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Sign Operator for Coping with Heavy-Tailed Noise: High Probability Convergence Bounds with Extensions to Distributed Optimization and Comparison Oracle	Reject	Summary: ### Motivation Heavy-tailed noise is a common issue in large-scale machine learning optimization, particularly for LLMs. Approaches like gradient clipping and normalization are common ways to mitigate this issue but require careful tuning or are simply not suitable for distributed settings. This paper explores the use of sign-based optimization as a simple and effective alternative. ### Key Contributions 1. Sign-Based Methods for HT Noise - The authors demonstrate that SignSGD achieves optimal convergence under HT noise without additional hyperparameters. - They provide the first high-probability convergence bounds for SignSGD for non-convex losses. 2. High-Probability Convergence Guarantees - SignSGD with minibatching achieves an optimal complexity for HT noise with a bounded $\kappa$-th moment $\kappa \in (1,2]$. - SignSGD with Majority Voting further improves convergence under symmetric noise. 3. Extension to Zeroth-Order Optimization - The paper introduces MajorityVote-CompSGD, an algorithm for optimization with comparison-based oracles. - It provides the first HP bound for zeroth-order optimization under HT noise. ### Highlights - Sign-based optimization is highly effective in handling heavy-tailed noise. - Majority Voting significantly reduces noise. - Sign-based methods outperform traditional approaches, making them particularly useful for LLM training and stochastic optimization. # Update After Rebuttal Dear Authors, You have shown great effort, and I am satisfied with your reply. I am sure you will: 1. Include your newly found results and compare them with the relevant literature ([1,2,3,4]). 2. Include your new experiments to validate your bounds. These can still be improved, e.g., larger and different settings, but they are a step in the correct direction. 3. Rectify your claims about your methods being somewhat uniformly better than AdamW or so, and rather being more precise about this type of claim. I appreciate your reply: I will follow the discussion with the other Reviewers. For the moment, I decided to raise my score to Accept (4), but not to Strong Accept (5). Claims And Evidence: While the theory looks sound, not all the theoretical insights are necessarily validated appropriately in meaningful setups. More details later. Methods And Evaluation Criteria: I honestly do not think the evaluation criteria are sufficient: Claiming that an optimizer is better than AdamW for LLMs is among the strongest claims one can make in this field. I believe training on such a small LLM is by no means representative, but certainly encouraging. Claiming to be better than AdamW requires extensive evaluations across multiple architectures and datasets. A good start could be validating this claim on "Pythia: A Suite for Analyzing Large Language Models Across Training and Scaling". And still, this would not be enough to say your algo is better than AdamW, but it would be a much more solid basis to say it is promising. Theoretical Claims: No, I did not check the proofs in detail: I skimmed over the main results and they seem fine. The results themselves make sense in light of the existing literature. Experimental Designs Or Analyses: As I discussed above, I believe the experimental setup is too limited to draw any meaningful conclusion. In LLMs, scale is THE challenge and different (and larger) scales bring different challenges. Not testing the behavior at different increasing scales of a model is not enough to claim that "Our theoretical findings are supported by the superior performance of sign-based methods in training Large Language Models". Supplementary Material: The code was not available. Relation To Broader Scientific Literature: While browsing for recent literature, I came across two concurrent works [1,2] that were recently published --- They contain some interesting results that deserve some comments as they are very much related to those derived in this paper: [1] Derives a convergence bound for SignSGD under Gaussian and Student's t gradient noise when the variance of the noise is unbounded; [2] Generalizes [1] to the distributed setting and studies also the case where the expected value of the noise is unbounded: Distributed SignSGD seems to converge even in this case and it is empirically verified across different architectures and datasets. I suggest: 1. Discussing results like Lemma 3.5 in [1] or Theorem 3.12 and Theorem 3.13 in [2] regarding the role of $\sigma$ and comparing these with the bounds derived in this paper. 2. Commenting on why the analysis in this paper requires the expected value of the noise to be bounded, while this is not necessarily necessary in Theorem 3.12 and Theorem 3.13 of [2] with $\nu=1$. [1] "Adaptive Methods through the Lens of SDEs: Theoretical Insights on the Role of Noise", Compagnoni et al. ICLR 2025. [2] "Unbiased and Sign Compression in Distributed Learning: Comparing Noise Resilience via SDEs", Compagnoni et al. AISTATS 2025. Essential References Not Discussed: See above. Other Strengths And Weaknesses: The main issue is truly the experimental side, which I discussed above. To build on that, I believe that it could be very educational to verify the bounds empirically on some simple settings: A straightforward approach to address this would be to train a small model—such as a shallow MLP—while injecting noise into the full gradient. This setup does not require a large-scale LLM while it allows for systematic testing of the theoretical predictions. By varying each parameter appearing in the derived bounds, one could assess whether the theoretical results align with empirical observations. For instance, training a small MLP while injecting noise of magnitude $\sigma$ could verify whether the L1 norm of the gradient truly scales linearly as predicted by Lemma 1. Similarly, other key hyperparameters could be ablated. Such an evaluation would give a bit of intuition on how tight the analysis is and how loose the bounds are. Other Comments Or Suggestions: # Conclusion From a theoretical standpoint, the paper seems solid and simply needs a bit of contextualization w.r.t. recent literature. The results are novel and the new optimizers show promising results from an experimental point of view. However, the experimental evaluation is too restrictive to draw any meaningful conclusion w.r.t. whether or not these new optimizers truly outperform AdamW. As this claim would have major repercussions for the DL community, it has to be thoroughly verified. IF you can show that your optimizers outperform AdamW (ofc AdamW would need first to be tuned to find optimal parameters!) on a variety of architectures and datasets (see at least my suggestions above regarding Pythia), this paper deserves a Strong Accept. For the time being, I think it is fair to give Weak Accept and I will follow the discussion during the rebuttal time: I see potential to give Accept. Questions For Authors: Can you somehow show linear speed-up in terms of the number of clients for your distributed optimizer? Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: Dear Reviewer 5Sbn, thank you for your questions and positive evaluation of our paper. Claiming that an optimizer is better than AdamW. By saying this in abstract, we did not mean to suggest that the sign-based method is the best possible method for language model pretraining, but rather that it can compete with other methods commonly considered in theory for dealing with heavy tails -- specifically, clipping and normalization. We sincerely apologize if our wording misled the Reviewer. We also do not claim that M-SignSGD is a new SOTA uniformly surpassing AdamW across a wide range of practically important tasks. However, our experiments, along with the results from [Zhao 2024], demonstrate that it can at least provide serious competition to well-tuned AdamW at small scales (up to 1B) of dense language model pretraining. To further explore the potential applicability of M-SignSGD in practically important tasks, we conducted additional experiments with the pretraining of a Mixture-of-Experts language model of larger size. The results can be found in reply 1 for Reviewer AScN. [Zhao 2024] Zhao, R. et al. Deconstructing what makes a good optimizer for language models, 2024. Related works. Indeed, in works [1] and [2], the authors work with Student's distributions which can have unbounded math expectation. Symmetric noises can break traditional lower bounds and guarantee convergence when noises have bounded $\kappa$-th moment, $\kappa > 0$, see [3, 4]. Therefore, for a fair comparison, we provide our rates for MajorityVote-SignSGD $\kappa \in (1,2]$ (Theorem 3): $$N = O\left(\frac{ \Delta_1 L_\delta d}{\varepsilon^2} + \frac{ \Delta_1L_\delta d} { \varepsilon^2} \left(\frac{a_\kappa\|\|\sigma\|\|_1}{ \varepsilon}\right)^2\right),$$ where $(a_\kappa)^\kappa := \frac{\kappa+1}{\kappa - 1}$. The dependence on $\kappa$ is only in a deteriating factor $a_\kappa$. We did not consider the case $0 < \kappa \leq 1$, however, after careful check, we proved that MajorityVote-SignSGD can work with any $\kappa >0$. We managed to eliminate the factor $a_\kappa$ and obtain high probability rates with $M = \max\left(\frac{(\kappa + 1)^{2\kappa - 1}}{\kappa^{\kappa + 2}}, (\frac{\|\|\sigma\|\|_1}{\varepsilon})^2 \right)$: $$N = O\left(\frac{ \Delta_1 L_\delta d}{\varepsilon^2\kappa^4} + \frac{ \Delta_1L_\delta d} { \varepsilon^2} \left(\frac{\\|\sigma\\|_1}{ \varepsilon}\right)^2\right).$$ Hence, MajorityVote-SignSGD can also operate under $1 \geq \kappa > 0$ and symmetric HT noise similar to the DSignSGD from [2]. We will add case $\kappa > 0$ in a revision. In our bounds, the dependence on $\sigma$ is quadratic, and, in [2], the dependence is linear. We are not aware of any lower bounds for symmetric HT noises. Thus, we cannot say whether the linear dependence on $\sigma$ is optimal or not. The linear dependency in [2] could have emerged since the authors consider only Student's distributions. [1] "Adaptive Methods through the Lens of SDEs: Theoretical Insights on the Role of Noise", Compagnoni et al. [2] "Unbiased and Sign Compression in Distributed Learning: Comparing Noise Resilience via SDEs", Compagnoni et al. [3] Puchkin, N.et al. Breaking the heavy-tailed noise barrier in stochastic optimization problems. [4] Armacki, A.et al. Large deviations and improved mean-squared error rates of nonlinear sgd: Heavy-tailed noise and power of symmetry. Validate theory in practice. Following your advice, we trained MLP on 'mushrooms' dataset to practically validate the dependence on noise. Lemma 1 states that SignSGD without batching or voting converges with rate $$\frac1T \sum\limits_{k=1}^{T} \\|\nabla f (x^k)\\|_1 \leq \frac{2\Delta_1}{T\gamma} + 16 Ld\gamma \log(\frac{1}{\delta}) + 4 \sigma \notag + 12\frac{d\\|\nabla f (x^1)\\|_1}{T} \log(\frac{1}{\delta}).$$ Figure 1: https://limewire.com/d/llU7f#n4qOoELVLI Figure 2: https://limewire.com/d/xf3xK#0fFssBjtev Figure 3: https://limewire.com/d/lm6Z3#CfR5OGQit4 If one takes a small batchsize $\gamma$ and a large number of iterations $T$, then method reaches $\sigma$ plateau despite $\kappa$. In Figure 1, we did this experiment, and one can see that plateau level in practice linearly depends on $\sigma$ and does not depend on $\kappa$. Theorem 3 and the updated rates from the above question state that batchsize $M$ in MajorityVote-SignSGD reduces achieved plateau level as $\frac{\sigma}{\sqrt{M}}$ for any $\kappa \in [1,2].$ In Figure 2, we took quadratically growing batchsizes $[1, 5, 17]$ and fixed $\sigma$, and plateau level actually drops linearly despite $\kappa$ (even $\kappa = 1$). Similarly, according to Theorem 2, simple batching theoretically drops plateau level as $\sigma/B^{\frac{\kappa - 1}{\kappa}}$. In Figure 3, we verified it for $\kappa = 2$ with quadratic batchsizes and for $\kappa = 1.5$ with cubic batchsizes. Therefore, we demonstrate that our theoretical bounds seem to be tight in practice. --- Rebuttal Comment 1.1: Comment: Dear Authors, you have shown great effort, and I am satisfied with your reply. I am sure you will: 1. Include your newly found results and compare them with the relevant literature ([1,2,3,4]). 2. Include your new experiments to validate your bounds. These can still be improved, e.g., larger $T$, and different settings, but they are a step in the correct direction. 3. Rectify your claims about your methods being somewhat uniformly better than AdamW or so, and rather being more precise about this type of claim. I appreciate your reply: I will follow the discussion with the other Reviewers. For the moment, I decided to raise my score to Accept (4), but not to Strong Accept (5).	Summary: In this paper, the authors consider the problem of minimizing a non convex function under two different oracle models. In the first case, the algorithm access to a noisy first order oracle obeying to an heavy-tailed distribution. In this model, authors analyze a number of version of the sign SGD method, and prove several sample complexity bounds. In the second model, the oracle returns zeroth order information corrupted by heavy tailed noise. Even in this case, authors consider a number of variants of sign SGD-like methods for which they prove sample complexity bounds. Preliminary experiments are provided. ## Update after rebuttal ## I thank the authors for the rebuttal, however I'll keep my score due to the following reasons: The authors have overlooked an important related work in their discussion and appear (perhaps unintentionally) biased toward earlier contributions in this area. The clarifications provided in the rebuttal should have been included in the original submission. Some contributions seem overstated. For instance, the claim that the numerical constants for sign SGD are smaller than those of alternative methods is not particularly meaningful. Since prior works did not focus on optimizing constants, and the minimax values are unknown, comparing constants in upper bounds across different methods lacks justification. Such a comparison would only be appropriate if the authors had improved the upper bound of an existing method — which is not the case here. Overall, the paper feels somewhat rushed in its current form. Authors use a somehow sloppy jargon in several point of the manuscript, as I highlighted in my review. Technical novelty is limited. This is not a major problem, as long as the results are interesting, but combined with a poor presentation and discussion of the related work, contribute to my low score. Sign SGD is an interesting and robust alternative to standard SGD. In that respect, this paper addresses a relevant problem. However, I believe that the present submission requires a major revision — not just a camera-ready version — incorporating the points raised in the rebuttal and presenting the material in a more polished and thorough manner, before it is ready for publication. Claims And Evidence: See discussion below. Methods And Evaluation Criteria: See discussion below. Theoretical Claims: See discussion below. Experimental Designs Or Analyses: See discussion below. Supplementary Material: No. Relation To Broader Scientific Literature: See discussion below. Essential References Not Discussed: See discussion below. Other Strengths And Weaknesses: The paper consider a problem which is relevant for the ICML community. Writing: The overall writing could be improved as currently it appear to be a bit rushed. In several point, authors use a rather informal prose, and some effort is required to put claims in context. As an example, I found Remark 2 quite confusing: what the authors mean by "the batched function values"? More examples of inaccurate claims or phrases will follow. References: The related work section for the first order method is lacking some important references and is inaccurate. For clipping on non-convex objective, the authors do not cite [Nguyen2023] = Improved Convergence in High Probability of Clipped Gradient Methods with Heavy Tailed Noise. Nguyen et al. NeurIPS 2023. In that paper authors prove rates of convergence (for the average gradient norm), in both the finite horizon (known number of iteration) and the any-time setting (unknown number of iteration), that are comparable, or better, to those prove in this paper. In the finite horizon setting, the authors show a rate of (the order of) $T^{(2\kappa-2)/(3\kappa-2)}$ with unit batch-size. This leads to a sample complexity of order $\bigg(\frac{1}{\varepsilon}\bigg)^{\frac{2\kappa-2}{3\kappa-2}}$ Notice that this is better of the results in (3) and (4) of the present paper . This rate is also better then that in (7) and (8) for every $\kappa < 6/5$. In addition, authors of it is worth noting that authors of [Nguyen2023] also consider the any-time setting, where they show similar results up to the introduction of additional logarithmic terms in $1/\varepsilon$. Finally, in the same work, Nguyen et al. also prove results for the convex setting, which the author of this works seems to not consider. Inaccurate claims/Clarifications: In section 1.1., clipping paragraph, authors mention a lower bound by Zhang et al. it would be useful to state the lower bound or include a table with the most important sample complexity bounds. In the same paragraph, and in other places in the paper, authors say that symmetric noise is a relaxation of the Heavy-Tailed noise. This is not true, not all heavy-tailed distribution are symmetric (e..g, the Pareto). Similarly there are symmetric distribution that do not have finite expectation. Thus the two classes are not in an inclusion relation. Authors should clarify what they mean by relaxation. Still in section 1.1. authors say that Liu et al. 2023, and Cutkosky & Metha 2021 obtains high probability bounds under heavy tailed noise for normalized SGD. How those bounds compare with that obtained in this paper? Authors define arbitrary the first type of tuning in all their results, but this tuning leave only a constant parameter free to the user. A real free tuning would have left the choices of the step-size and the batch-size completely free. Below Theorem 3, authors claim that:In comparison with (4) for minibatch-SignSGD, in expectation....but they are still close due to the norm relation (10). I'm not sure to understand that, there may still be a factor $\sqrt{d}$ between these quantities, and that can be large in high dimension. The discussion in section 2.6. is inaccurate. Comparing with clipping authors ignore the work of [Nguyen2023], and only refer to Sadiev et al. 2023. Even limiting to this latter work, one should notice that the authors do not make effort in optimizing the constants, and therefore it cannot be concluded that clipping suffers from worse constants... The parameter setting proposed by the authors for their variants of sign SGD also on the number of iterations, and then it is unclear what do they mean by The sign-based methods work well with constant, arbitrary parameters. Conclusion: The problem faced in this work is interesting, but I think that a major rework is needed to include a more comprehensive discussion of the related works (including the related paper [Nguyen2023]), a more extensive comparison with the existing results, and a more careful writing and presentation of the results. Other Comments Or Suggestions: In section 2.1. authors may add a comment on how their component wise assumption on the noise relate to the canonical norm assumption on the oracle. In section 2.4, paragraph Majority Voting, the $g_i$ are used without begin introduced. Please rephrase this sentence: Choosing the most frequent value from the sign...M Bernoulli trials. There is a typo in line 2 of Algorithm 3, $B_k$ should be replaced by $M_k$. In section 3.1 it should be $\mathbb{R}^d$ not $\mathbb{R}^D$. Questions For Authors: In section 1.2, first bullet point, authors says that they generalize their high probability bound to a bound in expectation. In which sense, their in expectation bound is a generalization? In eq. (3) where is the dependence on $\delta$? Below eq. (5) authors claim that it is not possible to obtain decreasing probability for $\sign(\nabla f(x^k))_j \neq \sign(\sum_{i=1}^M \sign(g_i^k)_j$, unless one place additional assumptions. Why is that? Could you add a reference for this claim? For example, the condition (6) is satisfied if the noise of the gradient estimate for each coordinate is unimodal and symmetric about its mean. In the experimental section, it is unclear to me how many repetitions have been performed in each experiment and what statistics authors reported. Could you clarify it? Code Of Conduct: Affirmed. Overall Recommendation: 1	Rebuttal 1: Rebuttal: Dear Reviewer 1isr, thank you for your valuable feedback. We sincerely apologize for overlooking certain important works. We will address these gaps in a revision. Nevertheless, we would like to emphasize that our main results remain competitive with or outperform mentioned methods. In this case, suggested presentation, typos and unclear moments can be quickly fixed. [Nguyen2023] The rates from [Nguyen2023] are given for the average SQUARED $l_2$-norm, i.e., to achieve $\\| \nabla f(x)\\|^2_2 \leq \varepsilon^2$ one needs $$\max \left(\left(\frac{8 \|\|\sigma\|\|_2^\kappa \log \frac{1}{\delta}}{\sqrt{\Delta_1 L}} \right)^\frac{3\kappa -2}{\kappa - 1} \left(\frac{720 \sqrt{\Delta_1 L}\log \frac{1}{\delta} }{\varepsilon^2}\right)^\frac{3\kappa - 2}{2\kappa - 2}, \left(\frac{720 \cdot 32^\frac1\kappa \|\|\sigma\|\|_2\log \frac{1}{\delta} }{\varepsilon^2}\right)^\frac{3\kappa - 2}{2\kappa - 2}, \left(\frac{1440\sqrt{90} \cdot L\Delta_1 \log \frac{1}{\delta} }{\varepsilon^2}\right)^\frac{3\kappa - 2}{2\kappa - 1}\right).$$ For the minibatch-SignSGD, the bound (4) is given in terms $\\| \cdot \\|_1 \leq \varepsilon$ (WITHOUT SQUARE): $$ \max \left(\frac{512 \Delta_1 L \log \frac{1}{\delta} d }{\varepsilon^2}, \frac{512 (16 \|\|\sigma\|\|_1)^\frac{\kappa}{\kappa -1} \Delta_1 L \log \frac{1}{\delta} d }{\varepsilon^\frac{3\kappa -2}{\kappa - 1}} \right) \quad \quad ().$$ Our bound has the same dependency on $\varepsilon$ for $\forall \varepsilon, \sigma > 0$ and even better one if $\sigma = 0$. The dependencies on $L,\sigma$ are much closer to the lower bound $\Omega \left( \frac{\Delta_1 L}{\varepsilon^2} + \frac{\Delta_1 L\|\|\sigma\|\|_2^\frac{\kappa}{\kappa - 1} }{\varepsilon^\frac{3\kappa -2}{\kappa - 1}} \right)$ from [Zhang2020]. Finally, the numerical constants with $\log \frac1\delta$ factors are milder in our bounds. Additional $\sqrt{d}$ factors* are inherent to sign methods, since they work with larger $l_1$ norm instead of $l_2$. We can derive bound $\|\|\cdot\|\|_2 \leq \varepsilon$ with the following density function $\phi(u) := \frac{\|\|u\|\|_1}{\sqrt{d}\|\|u\|\|_2}$ ($= 1$ for dense vectors and $=\frac{1}{\sqrt{d}}$ for sparse): $$O\left( \frac{\Delta_1 L_\delta } {\varepsilon^2\phi^2(g)} \left( 1 + \frac{\|\|\sigma\|\|_2 \phi(\sigma)}{\varepsilon \phi(g)}\right)^\frac{\kappa}{\kappa-1}\right),$$ where $\phi(g)$ is the average density of gradients. In practice, this density remains close to $1$ (see [1] (Section 3)), therefore, high dimensionality does not immediately imply slower convergence. Convex case. We left the convex case out of the scope of our work, since its primal goal is to effectively and robustly solve non-convex ML and DL tasks under HT noise. The sign-based methods can work with convexity (see, [2]). Infinite horizon. Sign methods can work with infinite horizon ([3] Theorem 1). For minibatch-SignSGD, we can provably take stepsizes $\gamma_k \sim 1/\sqrt{k}$ and $B_k \sim k^\frac{\kappa}{2\kappa-2}$ to obtain rates with extra $\log T$ factors and the same sample complexity to get $\min_k \\|\nabla f(x^k) \\|_1 \leq \varepsilon$. Clip Normalized SGD. In [Cutkosky Metha], the rates are obtained for the bounded gradient $\kappa$-th norm, and [Liu] generalizes it for the bounded $\kappa$-th moment: $$O\left(\frac{\sqrt{L\Delta_1}}{T^\frac{\kappa - 1}{3\kappa - 2}} + \frac{\sigma\log T/\delta}{T^\frac{\kappa - 1} {3\kappa - 2}}\right).$$ Compared to ours, these rates have extra $\log T$ factors and are not optimal for $\sigma = 0.$ Complexity table. For the sake of readability, we put lower bound in Section 2.6 line 272, where we discuss explicit formulas. Clipping Constants. We do not optimize constants as much as possible. However, constants in bound () are clearly better than the one from [Nguyen2023]. Our constants follows from proof lines 810-850. Parameter free.* We did not try to build parameter-free methods. We only mean that even without knowing anything about the problem, one can expect and evaluate convergence of sign-based methods using the proposed problem-agnostic parameters. Word "generalization". The word "generalization" is incorrect for in expectation bounds and symmetric HT noises. We will replace it. Eq3. There must be $L_\delta$ instead of $L$. Below eq. (5) There is a $1$-d counterexample: $\nabla f = 0.1$ and noise $\xi = -1$ with $99\%$ and $\xi=1$ with $1\%$. The probability of getting the right sign with 1 trial is $0.01$, and with $3$ trials $\leq 2 * 0.01 * 0.01$. Reference for this claim? It was proved for BV noise in [1](Theorem 2). For HT noise, we prove it in the beginning of Section C.5. Experimental section We ran all experiments with 3 different random seeds. For pretraining, we report validation perplexity, and for fine-tuning, we report target task test accuracy. References: [1] https://arxiv.org/pdf/1802.04434 [2] https://arxiv.org/abs/1901.09847 [3] https://arxiv.org/abs/1905.12938	Summary: This paper investigates the robustness of a series of sign-based stochastic optimization methods for handling heavy-tailed (HT) noise in smooth non-convex functions. The authors argue that leveraging the sign of gradient estimates, without introducing additional hyperparameters, effectively addresses HT noise. The key contributions include: 1. A family of methods including SignSGD, SignSGD with Majority Voting, and a novel zeroth-order method, MajorityVote-CompsSGD; 2. High-probability (HP) sample complexity bounds for these methods under HT noise, such as $\tilde{O}\left(\varepsilon^{-\frac{3\kappa - 2}{\kappa - 1}}\right)$ for SignSGD to achieve gradient norm accuracy $\varepsilon$; $\tilde{O}(\varepsilon^{-4})$ for SignSGD with Majority Voting under symmetric noise and $\tilde{O}(\varepsilon^{-6})$ for MajorityVote-CompsSGD in terms of comparison 3. Experimental validation on Transformer models (LLaMA pre-training and RoBERTa fine-tuning). The paper claims these methods collectively outperform clipping-based approaches by avoiding complex tuning. Claims And Evidence: The claims are generally supported by theoretical proofs and experimental results. The HP bounds for SignSGD (Theorem 1) and its variants (Theorems 2-4) are derived under clear assumptions (smoothness, lower boundedness, and HT noise with bounded κ-th moment), with proofs deferred to Appendix C. Experimental validation on Transformer models provides evidence of practical effectiveness. Methods And Evaluation Criteria: The proposed methods—SignSGD, SignSGD with Majority Voting, and MajorityVote-CompsSGD are well expressed. The evaluation criteria. The use of Transformer models (LLaMA pre-training and RoBERTa fine-tuning) as benchmarks is appropriate given their relevance to modern machine learning tasks. Expanding the evaluation with additional benchmarks could further enrich the findings and enhance their generalizability. Theoretical Claims: I reviewed the convergence theorems for the main proposed methods and their assumptions, as outlined in Section 2. The theorems' high-probability (HP) bounds appear to be correctly derived under the stated assumptions, balancing terms such as the smoothness constant L, noise magnitude σ, and failure probability δ. While the proofs are not included in the main text, the assumptions (e.g., L-smoothness, bounded κ-th moment noise) are standard and reasonable. I did not detect any obvious errors in the formulation, though I could not fully verify the proofs without access to Appendix C. Experimental Designs Or Analyses: The experiments involve pre-training LLaMA 130M on the C4 dataset and fine-tuning RoBERTa on NLP tasks. The design is sound, targeting real-world scenarios. Metrics (e.g., gradient norm reduction, task performance) are not fully specified, which reduces transparency. Supplementary Material: I reviewed the proofs for the proposed theorems in the supplementary materials, and no obvious flaws or errors were detected. Relation To Broader Scientific Literature: This paper presents work whose goal is to advance the field of Machine Learning. None of them must be specifically highlighted here. Essential References Not Discussed: N/A Other Strengths And Weaknesses: N/A Other Comments Or Suggestions: Can you provide a direct experimental comparison with ClipSGD under HT noise to substantiate the superiority claim? This could strengthen my confidence in the practical advantage. Questions For Authors: Can you provide a direct experimental comparison with ClipSGD under HT noise to substantiate the superiority claim? This could strengthen my confidence in the practical advantage. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Dear Reviewer AScN, thank you for your time and comments and positive evaluation of our paper: (1) Expanding the evaluation with additional benchmarks could further enrich the findings and enhance their generalizability. Thank you for raising this point. We complement our experiments with a new setup -- new architecture and data. Previously, we used a dense LLaMA model; now, we have switched to a Mixture of Experts (MoE) architecture based on the same LLaMA model, retaining RoPE and identical activation functions. Our MoE model follows the Switch Transformer [1] MoE variant with classical top k=2 gating and 8 experts, giving us approximately 520M parameters if we have the same configuration as 130M LLaMA. We conduct this experiments on the FineWeb dataset [1] a popular corpus for LLM pre-training. We run AdamW, M-SignSGD, M-NSGD and M-ClippedSignSGD optimizers following the best practices from our earlier setup on dense models. We train with a batch size of 256 and sequence length 512 for 42k (5.5B tokens)and 336k steps (44B tokens). That is for the second training horizon we go far beyond the Chinchilla optimal tokens-per-parameters ration. Perplexity of LLaMa-base MoE 520M model pre-trained on FineWeb for 42k steps. Lower is better AdamW: ppl 22.85 M-SignSGD: ppl 23.19 M-NSGD: ppl 23.32 M-ClippedSignSGD: ppl 23.30 Perplexity of LLaMa-base MoE 520M model pre-trained on FineWeb for 336k steps. Lower is better AdamW: ppl 18.68 M-SignSGD: ppl 18.87 We would like to highlight that M-SignSGD scales remarkably well with increasing model size, outperforming M-NSGD and M-ClippedSignSGD. Additionally, we encountered difficulties running M-ClippedSGD in this setting. Consequently, we decided to include a clipped version of M-SignSGD, which aligns with our approach since we consider only an EMA of momentum in the update. [1] https://arxiv.org/abs/2101.03961 [2] https://arxiv.org/abs/2406.17557 (2) Metrics (e.g., gradient norm reduction, task performance) are not fully specified, which reduces transparency. We thank the Reviewer for this note. Although we specify in the captions of Tables 1 and 2 the metrics being reported, the main text would benefit from a more detailed description of the target metrics. We will be sure to include this in a reversion. (3) Can you provide a direct experimental comparison with ClipSGD under HT noise to substantiate the superiority claim? This could strengthen my confidence in the practical advantage. Could you, please, clarify what kind of experiments and methods you would like to see? In the reply (1), we conducted additional experiments with LLMs, comparing M-ClipSGD and M-SignSGD methods. --- Rebuttal Comment 1.1: Comment: Thank you for your rebuttal; it cleared up my doubts.	Summary: This paper studies optimization under heavy-tailed noise. The authors assume that the noise affecting gradient estimates and function evaluations has bounded $\kappa$-th moments for (1,2]. This assumption is common in many large-scale deep learning scenarios. Under this assumption, they develop sign-based methods for both first-order and zeroth-order optimization. In the first-order setting, they introduce variants of SignSGD that incorporate momentum and majority voting. They provide high-probability convergence guarantees for these methods under standard assumptions such as L-smoothness and bounded-below objectives. In the zeroth-order setting, where only comparison feedback is available, they propose CompSGD and an improved version called Majority Vote-CompSGD. Under similar noise and random direction assumptions, they derive high-probability convergence results for these methods. The paper also includes experiments on large-scale language model pretraining and NLP fine-tuning tasks, as well as experiments on synthetic benchmarks, to demonstrate the practical behavior of the proposed algorithms. Claims And Evidence: The submission presents several claims about convergence under heavy-tailed noise, including high-probability convergence for sign-based first-order methods and comparison-based zeroth-order methods. The authors offer experiments on large-scale language model pretraining, NLP fine-tuning tasks, and synthetic benchmarks that appear to match the theoretical outcomes. Methods And Evaluation Criteria: The proposed methods and evaluation criteria are appropriate for the problem at hand. The authors develop sign-based optimization techniques designed for heavy-tailed noise scenarios and support their analysis with both theoretical derivations and practical experiments. For example, they test their algorithms on large-scale language model pretraining and NLP fine-tuning tasks, which are contexts where heavy-tailed noise is a recognized challenge. In addition, synthetic benchmarks are used to validate the theoretical claims under controlled conditions. Overall, the methods and evaluation criteria are reasonable for addressing robust optimization in heavy-tailed noise settings. Theoretical Claims: I did not carefully check the proofs but I believe the proof methodologies are known and should be correct in general. Experimental Designs Or Analyses: The experimental designs and analyses, including those for the large-scale language model pretraining, NLP fine-tuning tasks, and synthetic benchmarks for the zeroth-order methods, appear standard for the problem at hand. Supplementary Material: I did not review the supplementary material carefully Relation To Broader Scientific Literature: The paper draws on multiple threads in the literature related to gradient clipping (Pascanu et al., 2013; Goodfellow et al., 2016), normalization-based SGD (Hazan et al., 2015; Liu et al., 2023; Cutkosky & Mehta, 2021), and sign-based methods (Bernstein et al., 2018a). Prior works often examined these techniques under bounded-variance or symmetric noise assumptions, sometimes offering only expectation-based results. The current submission places these methods in a setting with heavy-tailed noise, which is handled via sign operations, clipping, or normalization. For zeroth-order methods, it references ideas such as the Three-Point method (Bergou et al., 2020; Gorbunov et al., 2022) and noisy comparison oracles (Saha et al., 2021; Lobanov et al., 2024a), extending them to heavy-tailed scenarios with high-probability guarantees. The paper integrates these methods for both first-order and zeroth-order cases, offering a unified approach to robust optimization under heavy-tailed noise. Essential References Not Discussed: NA Other Strengths And Weaknesses: The biggest weakness of the paper is that it mainly integrates existing techniques and extends them under already established assumptions. The work does not introduce fundamentally new ideas, and its contribution in terms of originality is somewhat incremental. Other Comments Or Suggestions: NA Questions For Authors: In Table 1, M-SignSGD is performing better than AdamW. Do you think this is a hyperparameter tuning issue or M-SignSGD is inherently better for pre-training? Also for paper like Galore[1], the reported perplexity for 130m models are around 25 (see Table 2 in [1]). How come the reported numbers here are so low? Seems that it's due to a larger number of training steps? References: [1] Zhao, Jiawei, et al. "Galore: Memory-efficient llm training by gradient low-rank projection." arXiv preprint arXiv:2403.03507 (2024). Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Dear Reviewer nio3, thank you for your feedback and positive evaluation of our paper. The biggest weakness of the paper is that it mainly integrates existing techniques and extends them under already established assumptions. The work does not introduce fundamentally new ideas, and its contribution in terms of originality is somewhat incremental. Research that provides new insights into already known methods is just as valuable to the community as other types of contributions. For instance, we provide a list of A* conference papers dedicated to the upper bounds for the existing methods: [1] Nguyen, T. D., Nguyen, T. H., Ene, A., & Nguyen, H. (2023). Improved convergence in high probability of clipped gradient methods with heavy-tailed noise. Advances in Neural Information Processing Systems, 36, 24191-24222. [2] Sun, T., Wang, Q., Li, D., & Wang, B. (2023, July). Momentum ensures convergence of signsgd under weaker assumptions. In International Conference on Machine Learning (pp. 33077-33099). PMLR. [3] Sadiev, A., Danilova, M., ... & Richtárik, P. (2023, July). High-probability bounds for stochastic optimization and variational inequalities: the case of unbounded variance. In International Conference on Machine Learning (pp. 29563-29648). PMLR. Furthermore, in the context of zeroth-order optimization, we propose novel methods together with their analysis approach via the sign operator. This approach helps uncover and explain the inherent robustness of these methods against noise. (2) In Table 1, M-SignSGD is performing better than AdamW. Do you think this is a hyperparameter tuning issue or M-SignSGD is inherently better for pre-training? We carefully tuned the hyperparameters (see Appendix D.1 for details) and believe that the results for all algorithms in Table 1 are close to optimal. Moreover, similar results were also obtained in the study [4] (see, e.g., Figure 1). We do not claim that M-SignSGD is inherently better than AdamW for language model pretraining. However, we believe that M-SignSGD can be a serious competitor to AdamW, at least for smaller model sizes. To further explore the potential applicability of M-SignSGD in practically important tasks, we conducted additional experiments with the pretraining of a Mixture-of-Experts language model of larger size. The results can be found in reply 1 for Reviewer AScN. [4] Zhao, R., Morwani, D., Brandfonbrener, D., Vyas, N., and Kakade, S. Deconstructing what makes a good optimizer for language models, 2024. (3) Also for paper like Galore[1], the reported perplexity for 130m models are around 25 (see Table 2 in [1]). How come the reported numbers here are so low? Seems that it's due to a larger number of training steps? As stated in Appendix D.1, we trained the model for 100k steps, unlike the 20k steps in GaLore [5]. Although the number of optimization steps in GaLore aligns with the empirical rule for scaling laws [6], the model remains far from convergence. Since, in practice, models are typically trained on significantly more tokens than suggested by scaling laws, we decided that longer training periods would be more representative. Moreover, since GaLore explores a memory-efficient setup, the authors trained the model in a pure bfloat16 format (meaning master weights are stored and updated in bfloat16) instead of the standard mixed precision approach for language model pretraining where master weights are kept in float32. This also degrades the model's performance. [5] Zhao, J., Zhang, Z., Chen, B., Wang, Z., Anandkumar, A., and Tian, Y. Galore: Memory-efficient llm training by gradient low-rank projection, ICML 2024. [6] Hoffmann, J., Borgeaud, S., Mensch, A., Buchatskaya, E., Cai, T., Rutherford, E., Casas, D. d. L., Hendricks, L. A., Welbl, J., Clark, A., et al. Training compute-optimal large language models, 2022.	null	null	null	null	null	null
Momentum-Driven Adaptivity: Towards Tuning-Free Asynchronous Federated Learning	Accept (poster)	Summary: This paper propose to adopt the server-client momentum with variance reduction technique in the Async FL framework. By using VR technology, the proof eliminates the heterogeneity assumption while maintaining the same efficiency as sync FL such as SCAFFOLD. The experiments validate the algorithm's efficiency in terms of test accuracy. Claims And Evidence: The theoretical proofs are complete, but the experiments are insufficient, lacking sensitivity studies on multiple variables and comprehensive ablation experiments. There is also no use of methods such as changing random seeds to verify robustness. For specific details, refer to 'Experimental Designs Or Analyses‘. Methods And Evaluation Criteria: 1. The approach has some originality, but its novelty is not high. Both server-client momentum and variance reduction techniques like scaffold have been widely studied. The approach adopts in this paper combines these two methods within the asynchronous FL framework without making significant modifications. 2. AdaMasFL requires to communcate an extra variable $\Delta$, this will increase the communication overhead. Theoretical Claims: 1. In theorem 3.1, the selection of momentum coefficient $\beta=\sqrt{SK/T}$ is not a constant. This usually does not occur in previous algorithms, because the number of training rounds $T$ can approach infinity, which also means that $\beta$ will consequently approach 0. This condition is stronger than previous methods. 2. The description in line 271 is inaccurate. On the general assumptions, the original FedAvg cannot achieve the full acceleration bound under partial participation, as discussed in reference [1]. The full acceleration bound $O(1/\sqrt{SKT})$ depends on variance reduction or additional bounded gradient assumptions. The related description needs to be revised and further discussed. [1] Achieving linear speedup with partial worker participation in non-iid federated learning Experimental Designs Or Analyses: 1. The experiments are partially tested on FMNIST and CIFAR10 on ResNet-18, with some improvements on the test accuracy, but there is a lack of systematic experiments to validate the findings. There is insufficient experimental validation for related variables, such as different local length $K$, data heterogeneity levels, and the duration of delay $\tau_i$. According to the description on page 29, most of the hyperparameters are selected as fixed values without additional sensitivity experiments, etc. I recommend that the authors conduct further extensive ablation experiments to determine the robustness of the proposed algorithm. 2. An experiment for a core variable is missing. One of the core contributions of this paper is the use of momentum-based weighting at both the server and client ends. Therefore, ablation experiments related to this scheme are essential. Necessary experiments, such as the benefits brought by only local momentum, global momentum, or variance reduction, should be included in the main text. 3. The experiments related to $\beta$ are missing. As an important hyperparameter, $\beta$ should be tested to determine the range in which it is effective. Although the theory sets it to be related to $T$, the practical role of $\beta$ in the experiments is still unclear. 4. The authors need to include a table to report the communication bits and wall-clock time of all methods in the baselines. Supplementary Material: There is no supplementary material. Relation To Broader Scientific Literature: It is helpful for the design of asynchronous federated learning frameworks. Essential References Not Discussed: The discussion is sufficient. Other Strengths And Weaknesses: Other strengths: Table 1 presents the convergence complexity and detailed conditions, which is great as it allows one to easily see the source of theoretical progress and the additional assumptions. Although the choice of $\beta$ depends on $T$ rather than being a constant, which makes the theory somewhat thin, the corresponding conclusions are still very clear in the comparison shown in Table 1. Other Comments Or Suggestions: see above for more details Questions For Authors: Main issues seen above. 1. What's the meaning of variables in line 153, e.g. $\sigma_h$? I did not see the relevant definition. 2. Can $\beta$ be set as a constant? If so, what effect does it have? Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We sincerely appreciate the reviewer for recognizing our contributions and for the constructive comments. Our point-to-point responses to concerns on Weaknesses and Questions are given below. Reply to Methods And Evaluation Criteria: 1. Thank you for your comment. Our work advances asynchronous federated learning (AFL) in the following key ways: - Eliminating Data Heterogeneity Bounds in the Asynchronous Regime: While server-client momentum has been explored in some prior AFL works, all existing approaches rely on data dissimilarity bounds to address non-iid data. In this work, we introduce a novel two-level momentum technique, making our approach the first to eliminate the need for such heterogeneity bounds in AFL. Although variance reduction technique has been explored in methods such as SCAFFOLD, they operate in synchronous frameworks, thus their analyses are inherently simpler compared to our asynchronous approach. - Tuning-Free AFL Approach: This paper also makes another significant contribution by introducing a completely tuning-free AFL approach, greatly simplifying algorithm deployment. As shown in Fig. 2, our method demonstrates exceptional robustness across varying levels of asynchrony. Based on the reviewer's suggestion, we have also included comparisons under different data heterogeneity levels and local training lengths ($K$). The results confirm that our method remains robust across diverse scenarios. These contributions go beyond combining existing techniques and addressing key challenges in AFL. 2. We agree with the reviewer that AdaMasFL requires the communication of an additional variable, $\Delta$, as the cost of achieving a tuning-free AFL. To address this communication overhead, information compression techniques can be incorporated as a potential solution. We acknowledge this as an important future work. Reply to Theoretical Claims: 1. Thanks for the comment. Using a $T$-dependent learning rate is standard in non-convex optimization to achieve theoretical guarantees. This predefined $T$ is reasonable since in real-world deployments, FL systems typically run for a pre-determined number of rounds due to resource constraints and practical considerations. The design also ensures momentum diminishes as $T$ increases, avoiding excessive staleness accumulation in asynchronous updates. 2. We sincerely thank the reviewer for pointing this out. We have removed the reference to the FedAvg algorithm in line 271. Reply to Experimental Designs Or Analyses: 1. Thanks for the comment. We have included sensitivity experiments with different local training lengths ($K$) as shown in https://github.com/anonymouslinkforrebuttal/for4415/blob/main/4-1-k.pdf, and data heterogeneity levels as shown in https://github.com/anonymouslinkforrebuttal/for4415/blob/main/4-1-noniid.pdf. Additionally, an ablation study on the impact of varying delay durations has already been presented in Fig. 2 of our main paper. Detailed information about the asynchronous setting can be found in our response to "Weakness 2" of reviewer JC6K. The results demonstrate the robustness of our approaches across various hyperparameter settings. 2. Thanks for your suggestion. We have included an ablation study analyzing the benefits of normalization, momentum, and control variate in our algorithms, shown as https://github.com/anonymouslinkforrebuttal/for4415/blob/main/4-2-ablation.pdf. 3. Thanks for the comment. We have included performance comparisons under different values of $\beta$ and compared with the momentum-based method FADAS as in https://github.com/anonymouslinkforrebuttal/for4415/blob/main/4-3-beta.pdf. 4. Thanks for the comment. We have added a table to report the wall-clock time of all baseline methods (in seconds) achieving a certain accuracy (CIFAR-10: 80%, FMNIST: 75%). Regarding information compression, as it goes beyond the scope of this work and we assume perfect communication in our paper, we leave this as an important direction for future research. \|Dataset \|Heterogeneity\|CA$^2$FL\|FADAS\|MasFL\|AdaMasFL\| \|-\|-\|-\|-\|-\|-\| \|CIFAR-10\|iid\|3485\|4171\|2033\|2323\| \|\|non-iid\|12593\|9372\|6679\|5333\| \|FMNIST\|iid\|1975\|1238\|832\|394\| \|\|non-iid\|2311\|1943\|1067\|514\| Reply to Questions For Authors: 1. Thanks for pointing this out! $\sigma_h$ should be $\sigma_g$ defined in eq. (1), which characterizes the level of data heterogeneity. 2. For a predetermined $T$, $\beta = \sqrt{SK/T}$ is a constant in our methods. As this momentum coefficient $\beta$ balances historical and fresh updates, it plays a crucial role in mitigating staleness in AFL. A larger $T$ results in a smaller $\beta$, ensuring stability and convergence by reducing the influence of stale updates. This design enables linear speedup by effectively balancing momentum and new gradient updates, ensuring strong theoretical guarantees and scalability. Thank you once again for your thoughtful review and constructive feedback. --- Rebuttal Comment 1.1: Comment: I have read the author's rebuttal and most of the concerns have been addressed. I suggest authors 1) state a table to show the communication bits and calculations for the proposed method. 2) according to the experiments of $\beta$, it appears that choosing $\beta=0.2,0.3$ yields the best performance, which aligns with expectations. However, since $\beta$ is not a constant in the theoretical analysis, this conclusion appears quite weak (as a decayed $\beta$, like the learning rate, can artificially weaken the influence of certain constant upper bounds). The authors' claim that $\beta$ can be treated as a constant in practice after pre-selecting $T$ is incorrect, because $T$ is generally not considered a constant in optimization complexity analysis. The current version does not seem to resolve this issue. 3) In Table 4, besides reporting the overall speedup, the authors should also provide the computation time per round. While the total time speedup is meaningful, the number of communication rounds may vary depending on the dataset, and reporting wall-time per iteration would more accurately reflect computational efficiency. I understand that this might make the algorithm appear computationally expensive and inefficient, but it represents the true performance of the method. 4) The experiments on $\beta$ suggest that the use of momentum provides only a minor improvement, as the performance curves in the experiment are quite uniform (except for $\beta=0.1$, where the performance is significantly worse). I suggest that the authors include a table comparing the AdaMasFL method with the baseline FedAvg method, showing how much each module improves performance separately. This would help highlight the most critical components of the proposed approach. Currently, the experiments suggest that $\beta$ may not be very important. How much improvement does normalized SGD and the server-side operations contribute? I believe I have fully understand this paper, and I will adjust my score based on the answers to these unresolved issues. --- Reply to Comment 1.1.1: Comment: Thanks for the reply! Our point-to-point responses are given below. 1. Thanks for the comment. Denote by $d$ the dimension of our training model $\theta$. At each global round $t$, our first algorithm, MasFL, requires uploading a vector $\mathbf{c}^t$ (of dimension $d$) from each client to the server and downloading two vectors ($\theta$ and $\beta\theta^t + (1-\beta)g^{t+1}$, both of dimension $d$) from the server to each client. For our second algorithm, AdaMasFL, an additional $d$-dimensional vector, $\frac{1}{\eta K}(\theta^{t-\tau_i^t} - \theta_t^{t,K})$, is required to upload, resulting in $2d$-dimensional information transformation for both uplink and downlink. We would like to clarify that this communication overhead is the same as that of SCAFFOLD-based algorithms, and our methods do not introduce any additional communication workload. For each real number, let $\delta$ represents the communication bits required to transmit each real number, the communication costs of our methods are as follows: \| MasFL \| Uplink \| Downlink \| \|-\|-\|-\| \| MasFL\| $d\delta$ \| $2d\delta$ \| \| AdaMasFL$\quad$ \| $2d\delta$ $\quad$\| $2d\delta$ \| In our experiments, the dimension of the training model for the CIFAR-10 dataset (ResNet 18) is $d=11689512$, and that for the FMNIST dataset (CNN) is $d=21840$. The calculation accuracy in of our experiment is $\delta=32$ bits. 2. Thanks for the comment. (1) In our work, the value of $\beta = \sqrt{SK/T}$ is preselected and remains constant for a given experiment. It is a fixed value and does not decay. Here, we would like to clarify that $T$ refers to the total number of algorithm iterations, not the variable $t$, which represents the current iteration. (2) Moreover, we would like to emphasize that this $T$-dependent step size setting is a common practice in nonconvex optimization, as seen in works such as [1] and [2]. For further details, please refer to the discussion on "SGD in nonconvex optimization" in the Related Work section of reference [2]. (3) Most importantly, such constant step sizes are generally preferred in practice for nonconvex optimization, especialy in large-scale optimization tasks like deep learning. [1] Cheng, Ziheng, et al. "Momentum benefits non-iid federated learning simply and provably." arXiv preprint arXiv:2306.16504 (2023). [2] Yang, Junchi, et al. "Two sides of one coin: the limits of untuned sgd and the power of adaptive methods." Advances in Neural Information Processing Systems 36 (2023): 74257-74288. 3. Thank you for this suggestion. The per-iteration wall-times of our approaches and all baselines are provided below: \|Dataset\|CA$^2$FL\|FADAS\|MasFL\|AdaMasFL\| \|-\|-\|-\|-\|-\| \|CIFAR-10\|25.47\|26.13\|26.85\|26.4\| \|FMNIST\|5.47\|6.61\|6.36\|6.35\| From this table, the per-iteration wall-times of all algorithms are quite similar. This is because they are all based on the FedAvg framework and do not involve computationally expensive operations, such as high-dimensional matrix multiplications. However, we would like to note that the computation time is significantly influenced by the computational resources and hardware configurations of the machine used to run the algorithms. While this metric is informative, it may vary across different environments. 4. Thank for the comment. (1) According to the simulation results in https://github.com/anonymouslinkforrebuttal/for4415/blob/main/4-2-ablation.pdf, momentum significantly improves the performance of our first algorithm, MasFL, while contributing only marginally to the second algorithm, AdaMasFL. This may be attributed to the robustness provided by the adaptive step size design in AdaMasFL. (2) We would like to emphasize that this stability to varying $\beta$ is a key advantage of our algorithm, highlighting its robustness and tuning-free nature. Notably, across the entire range of $\beta$ values depicted, our algorithm consistently outperforms the state-of-the-art baseline (FADAS approach). (3) We agree with the reviewer that adding the performance comparison with the FedAvg algorithm would better showcase the performance improvement of our approach. We have added FedAvg in the ablation study of AdaMasFL: https://github.com/anonymouslinkforrebuttal/for4415/blob/main/24-fedavg.pdf. The corresponding test accuracies are listed below: \|Method\|CIFAR-10\|FMNIST\| \|-\|-\|-\| \| FedAvg\|0.837\|0.819\| \| AdaMasFL\|0.880\|0.853\| \| AdaMasFL w/o norm\|0.844\|0.833\| \| AdaMasFL w/o control variate\|0.885\|0.835\| \| AdaMasFL w/o momentum\|0.868\|0.850\| (4) Finally, we emphasize that the primary focus of this paper is to design a tuning-free algorithm to simplify the deployment of AFL, which has never been realized before. We have provided thorough theoretical analysis to validate our results. In our algorithm design, we incorporate momentum, normalized SGD, and control variates because they are all indispensable components to achieving this tuning-free objective, not out of the performance improvement purpose.	Summary: This paper studies asynchronous federated learning and proposes a novel momentum-driven asynchronous FL framework that eliminates the need for data heterogeneity bounds. The authors provide theoretical analysis and conduct experiments to verify the effectiveness of the proposed method. Claims And Evidence: I think the claims in the submission are mostly clear. Methods And Evaluation Criteria: 1. I am wondering how asynchronicity is reflected in the proposed algorithm. In line 3 of Algorithm 1, the server randomly selects a set of clients $S_t$ , and in line 7, the aggregation also happens within this set $S_t$. This suggests that the clients in $S_t$ participate in the update within the same round, which seems to contradict the asynchronous scheme where clients update at their own pace. Although Algorithm 2 includes notations related to delay $\tau_i^t$, I believe this represents a semi-asynchronous approach. While clients may start from different global models, the server still waits for all aggregated information before proceeding. 2. Moreover, I am wondering whether the unbiasedness of the two-level momentum still holds when the correction term includes asynchronous delay (a similar issue arises regarding the sampling set $S_t$). 3. I think the proposed methods incur extra implicit memory on both the server and clients, i.e., the server need to maintain each clients' correction term $c$, and the client also need to maintain one copy of correct term $c$. Theoretical Claims: I have reviewed all the theoretical results in the main paper and briefly examined the theoretical results in the appendix. I have several questions regarding this: 1. Why is the left-hand side of Theorem 3.1 different from that of Theorem 4.1? What is the reason for using both $\|\|\nabla f(\theta^t))\|\|^2$ and $\|\|\nabla f(\theta^t))\|\|$ when presenting the convergence rate? 2. I think the constraint on the learning rate $\eta$ in Theorem 3.1 is not convincing. When the delay is large, e.g., $\tau_{\max} \geq \sqrt{T}/\sqrt{SK}$, the numerator in the constraint on $\eta$, i.e., $T - 4SK\tau_{\max}^2 < 0$ becomes negative, making the square root term undefined. Moreover, other related theoretical analyses on asynchronous FL, such as CA2FL and FADAS, do not include such a "minus term" in their learning rate conditions. Experimental Designs Or Analyses: 1. How was the asynchronous delay simulated/achieved in the experiments? 2. What does $M_c$ represent in the experiments? Does $M_c$ control the asynchronous delay, and does it share a similar concept with $S$ in your experiments? 3. I think providing more ablation studies on how the degree of asynchronous delay affects the proposed method would be helpful in verifying its effectiveness. Supplementary Material: I briefly examined the theoretical results in the appendix. Relation To Broader Scientific Literature: This paper may contribute to the privacy-preserving related machine learning applications. Essential References Not Discussed: N/A Other Strengths And Weaknesses: Strengths: 1. The empirical results seem convincing. 2. The paper is well structured and easy to follow. Most Weaknesses have been discussed in previous sections, particularly about the theoretical claims, the method, and the motivation. Other Comments Or Suggestions: N/A Questions For Authors: Please refer to previous sections. Addressing the issues in previous part would help me better understand and potentially change my evaluation of the paper. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We sincerely appreciate the reviewer for recognizing our contributions and for the constructive comments. Our point-to-point responses to concerns on Weaknesses and Questions are given below. Reply to Methods And Evaluation Criteria: 1. The asynchronicity of our method is reflected in the following two aspects: - Server-Side Asynchronicity: In Line 4 of Algorithm 1, the server maintains a buffer to store the latest updates from each client. When a client $i$ is selected for global aggregation ($i\in\mathcal{S}_t$), the server updates its control variate using the buffered (outdated) update rather than waiting for the client’s most recent update. This ensures the server does not rely on synchronized updates, enabling asynchronous behavior. - Client-Side Asynchronicity: On the client side (Algorithm 2), each client performs local updates continuously and uploads its results after $K$ iterations, then immediately begins the next update. Clients operate independently, and the global round index corresponds to the round when the client finishes its update, including a delay ($\tau_i^t$). This delay is reflected in the momentum term ($g^{t-\tau_i^t}$), capturing the asynchronicity. Semi-Asynchronous Behavior: Although the server aggregates update from the selected set of clients ($i\in\mathcal{S}_t$), these updates are generated at different times due to the clients’ independent schedules, distinguishing our approach from fully synchronous methods. Such an asynchronous mechanism is adopted in almost all existing AFL work to our knowledge, such as CA2FL and FADAS. 2. (1) The unbiasedness property does not hold in our two-level momentum. However, we achieve state-of-the-art convergence for our algorithm by carefully controlling the bias throughout the iterations. (2) The unbiasedness holds for the participating client set $\mathcal{S}_t$ because we sample clients randomly and uniformly at each round. 3. We agree with the reviewer that our method requires extra memory to maintain the control variate $c$ (with the same dimensions as the learning model) on both the server and client sides. This memory overhead is inherent to all SCAFFOLD-based algorithms, including ours. Reply to Theoretical Claims: 1. The differences in the left-hand sides of Theorem 3.1 and Theorem 4.1 arise from the distinct proof techniques used in each case: - Theorem 3.1: This theorem adopts the widely used squared gradient norm metric, i.e., $\|\|\nabla f(\theta^t)\|\|^2$, which is standard in analyzing convergence rates for optimization algorithms. - Theorem 4.1: To achieve problem-parameter-free convergence guarantees, we employ a novel proof technique that directly analyzes the gradient norm, i.e., $\|\|\nabla f(\theta^t)\|\|$. This direct analysis is essential for establishing problem-parameter-free results and requires a different approach compared to Theorem 3.1. 2. We agree with the reviewer that Theorem 3.1 suggests a sufficiently large $T$ such that $T \geq \Omega(\tau_{\max}^2)$. However, we would like to emphasize that imposing a lower bound on the number of iterations is a common practice in the literature. For example, the convergence bound of asynchronous SGD [1, Corollary 4] is established under a similar condition, $T \geq \Omega(\tau_{\max}^2)$. For AFL methods such as CA$^2$FL and FADAS, their asymptotic convergence rates of $\mathcal{O}\left(\frac{1}{\sqrt{T}}\right)$ are achieved when $T \geq \Omega(\tau_{\max}^2\tau_{\text{avg}}^2)$. Most importantly, we highlight that, unlike CA$^2$FL and FADAS, the unique contribution of Theorem 3.1 is that it does not impose any restrictions on data heterogeneity. [1] Lian, Xiangru, et al. "Asynchronous parallel stochastic gradient for nonconvex optimization." NIPS 2015. Reply to Experimental Designs Or Analyses: 1. Our implementation simulates practical asynchronous conditions using FedBuff's delay mechanism to account for varying client arrival times. Specifically: - At any given time, there are $M_c$ clients perform local updates concurrently; - Each client's execution time is sampled from a uniform distribution; - These varying execution times naturally create different delays in global aggregation participation; - Global aggregation occurs simultaneously with local updates. This design captures the realistic scenario of heterogeneous client completion times and asynchronous aggregation. 2. $M_c$ represents the number of clients performing local updates concurrently throughout the algorithm's runtime. Since the overall client participation rate remains fixed, a greater $M_c$ leads to larger system delays, and vice versa. 3. Thank you for this suggestion. An ablation study on the performance of our methods and all baselines under different asynchronous levels has already been presented in Fig. 2 of our original paper. Thank you once again for your thoughtful review and constructive feedback. --- Rebuttal Comment 1.1: Comment: Thank you to the authors for the rebuttal. Sorry for my late reply, as I originally replied to the “Official Comment” button. However, I still find somewhere a bit unclear to me. First, about the asynchronicity, as I point out in the review, "In line 3 of Algorithm 1, the server randomly selects a set of clients $S_t$ , and in line 7, the aggregation also happens within this $S_t$." There is no evidence showing that "these updates are generated at different times due to the clients’ independent schedules". According to the algorithm, the clients selected at round $t$ are also the ones whose updates are aggregated at that same round. I think this is not a fully asynchronous setting. About the learning rate conditions. I think the requirement $T\geq \Omega(\tau_{\max}^2)$ for achieving the desired convergence rate and the condition of $T-4SK\tau_{\max}^2 \geq 0$ should not be treated as equivalent, even though they share a similar direction, i.e., $T$ should be sufficiently large relative to $(\tau_{\max}^2)$. To me, it’s not clear that these conditions stem from the same underlying aspect, so I hope the authors can provide further clarification on this point. --- Reply to Comment 1.1.1: Comment: Thanks for the reply! 1. Asynchronous Setting: Thank you for the comment. In our algorithm, as described in Section 3.1 and Algorithm 1, the server maintains a buffer to store updates from clients that arrive asynchronously throughout the runtime. This means that at each global aggregation step, the updates used for aggregation from the selected client set $S_t$ are drawn from the buffer, not from their most recent updates. Instead, the updates could have been generated at different times due to the independent schedules of the clients. This is a key point that ensures the algorithm operates in an asynchronous manner. We follows the widely adopted asynchronous setting from the FedBuff [1], which captures practical scenarios with varying client availability and update arrival times. [1] Nguyen, J., Malik, K., Zhan, H., Yousefpour, A., Rabbat, M., Malek, M., and Huba, D. Federated learning with buffered asynchronous aggregation. In Proceedings of the 25th International Conference on Artificial Intelligence and Statistics, pp. 3581–3607. PMLR, 2022. 2. Thank you for the insightful comment. We agree with the reviewer that the requirement $T \geq \Omega(\tau_\max^2)$ and the condition $T - 4SK\tau_\max^2 \geq 0$ are not equivalent. Our Theorem 3 specifically relies on the condition $T \geq \Omega(\tau_\max^2)$, and we will clarify this distinction in the revised version of our paper. We would also like to emphasize that the requirement for a sufficiently large $T$ is a common condition for ensuring theoretical guarantees in asynchronous learning frameworks, as seen in works such as CA$^2$FL, FADAS, and [2]. Compared to these references, our requirement on $T$ is not particularly restrictive. [2] Lian, Xiangru, et al. "Asynchronous parallel stochastic gradient for nonconvex optimization." NIPS 2015. Thank you again for your valuable feedback!	Summary: This paper addressed the data heterogeneity and staleness in asynchronous federated learning (AsycnFL). The authors propose MasFL that introduces the control variates into AsyncFL to stabilize the model updates during local training and global aggregation. Further, they normalize the momentum-averaged gradients in local model training to eliminate the need for trial-and-error tuning or problem-parameter, e.g., the number of participating clients $S$, local update iterations $K$, and communication rounds $T$. The theoretical analysis is thorough, and the experimental results are promising, showing improvements over the state-of-the-art methods. 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: NA Essential References Not Discussed: One highly-related work [a] was missing. [a] Cheng Z, Huang X, Wu P, et al. Momentum benefits non-iid federated learning simply and provably[J]. arXiv preprint arXiv:2306.16504, 2023. Other Strengths And Weaknesses: Strength - High Writing Quality. The manuscript is well-organized and easy to read. - Technical Advantage. The authors first introduce the control variates into AsyncFL to tackle the challenges of data heterogeneity, gradient staleness, and complex hyperparameter tuning. Compared with another similar technique Scaffold, the authors additionally consider the global momentum to stabilize the model updates during model aggregation, improving the FL system's robustness to the stale clients in the context of asynchronous aggregation. Both theoretical and experimental results confirm the effectiveness of this strategy. - Theoritical Contribution. The paper provides strong theoretical guarantees for both MasFL and AdaMasFL. The convergence analysis is detailed, and the authors successfully prove that their methods achieve state-of-the-art convergence rates with linear speedup concerning the number of participating clients and local updates. Weakness - Overstatement. The claim that AdaMasFL "completely eliminates the need for tuning-free convergence" might be overstated. While the theoretical framework provides explicit hyperparameter settings, practical implementation might still require adjustments based on system-specific factors. In addition, the claim "tuning-free AFL approach" also suffers the risk of overclaiming since tuning the learning rate led to different empirical results as evidenced by the experiments. The authors should temper this claim and discuss the practical implications of their theoretical results. - Issues on Experiment Settings. The authors conducted experiments by directly assuming the degree of round-wise delaying of clients, which eliminated the necessity to consider the aggregation addition of clients (e.g., every $K$ arrivals in FedBuff). This issue also prevents a more practical setting that uses a virtual clock [b] to conduct asynchronous experiments. It's recommended to clarify the practical aggregation conditions of the proposed methods. - Missing Related Work. One important related work was missing. Although this work conducted the convergence of synchronous FL, they are the first to remove the dependency on the assumption of bounded data heterogeneity (i.e., bound gradient dissimilarity) and also confirm the impact of control variate in Scaffold. Since the main theoretical contribution of this work lies in removing the dependency of convergence on bounded data heterogeneity assumption and uses similar control variates, the authors should discuss their contributions and the relationship of this work to it. [a] Cheng Z, Huang X, Wu P, et al. Momentum benefits non-iid federated learning simply and provably[J]. arXiv preprint arXiv:2306.16504, 2023. [b] Lai F, Dai Y, Singapuram S, et al. Fedscale: Benchmarking model and system performance of federated learning at scale[C]//International conference on machine learning. PMLR, 2022: 11814-11827. Other Comments Or Suggestions: NA Questions For Authors: Please see the weakness. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We sincerely appreciate the reviewer for recognizing our contributions and for the constructive comments. Our point-to-point responses to concerns on Weaknesses and Questions are given below. Reply to Essential References Not Discussed: We sincerely thank the reviewer for bringing this conference to our attention. We have added a detailed comparison of our work with [a] in the revised manuscript, as cited below. > In the synchronous setting, [a] showed that momentum helps remove data heterogeneity bounds (i.e., bound gradient dissimilarity) for nonconvex FL, marking a first in the literature. However, integrating momentum into AFL introduces substantial challenges due to fundamental conflicts between momentum's historical gradient accumulation and the asynchronous nature of updates. In asynchronous settings, clients' delayed updates compromise the accuracy of momentum calculations, as stale gradients introduce biases into the optimization trajectory, as shown in [1]. To address this, we propose a two-level momentum mechanism: the server updates based on the latest global momentum, while each client performs local updates using an outdated global momentum. This inconsistency, while necessary to control bias, presents significant challenges in the theoretical analysis of our approach. [1] Yu, T., Song, C., Wang, J., and Chitnis, M. Momentum approximation in asynchronous private federated learning. arXiv preprint arXiv:2402.09247, 2024. Reply to Weekness 1: Thank you for pointing this out. We agree with the reviewer that different learning rates can influence the performance of our algorithm. However, we would like to clarify that the optimal learning rates for our algorithm can be directly calculated based solely on system-defined constants: the number of participating clients ($S$), local update iterations ($K$), and communication rounds ($T$). These are configuration parameters that are predetermined by the system administrator, rather than problem-specific factors that require estimation or tuning. That said, we acknowledge the reviewer's suggestion to adopt a more tempered statement. In response, we have revised the manuscript to replace "tuning-free AFL approach" with "problem-parameter-free" or "simplify the algorithm tuning process" throughout, which we believe better reflects the practical implications of our work. Reply to Weekness 2: Thank you for this important observation. We apologize for any confusion caused by not including the detailed experimental setup in the main paper. Due to space constraints, we placed the complete asynchronous implementation details in the supplementary material (page 29). We would like to clarify that our implementation does simulate practical asynchronous conditions using FedBuff's delay mechanism, which accounts for varying client arrival times rather than assuming fixed delay rounds. Specifically: - At any given time, there are a total of $M_c$ clients perform local updates concurrently; - Each client's execution time is sampled from a uniform distribution; - These varying execution times naturally create different delays in global aggregation participation; - Global aggregation occurs simultaneously with local updates. This design aligns with the virtual clock setting proposed in [b] to captures the realistic scenario of heterogeneous client completion times and asynchronous aggregation. We appreciate this feedback and will incorporate these important implementation details into the main paper for better clarity. Reply to Weekness 3: Thanks for pointing this out. The reference [a] has been properly cited in the revised manuscript, please refer to our response under "Reply to Essential References Not Discussed." Thank you once again for your thoughtful review and constructive feedback.	Summary: Previous works on asynchronous federated learning put strong assumptions (like bounded gradient assumption) in order to get theoretical guarantees. However, these assumptions are usually not realistic. In this paper, the authors propose a new asynchronous FL algorithm which novelly combines with global and local momentum. Due to the use of momentum, the authors remove the needs of strong assumptions in convergence analysis. Furthermore, they also design an adaptive version, which allows auto learning rate tuning. Experiments validate the effectiveness of proposed algorithms. Claims And Evidence: The authors claimed that they propose two novel training approaches MasFL and AdaMasFL. These algorithms incorporates two-level momentum. They provide not only theoretical guarantees with weaker assumptions but also experimental results to show advantages. Overall I think these claims are solid and well supported. Methods And Evaluation Criteria: The authors provide a standard convergence analysis to analyze their proposed method. The benchmark datasets in experiments are cifar and fmnist, which are relatively small. Theoretical Claims: I didn't check full details. Experimental Designs Or Analyses: Yes, the designs and analyses look good. Supplementary Material: No. Relation To Broader Scientific Literature: This paper may make asynchronous FL algorithm to be more practical and powerful. The analysis technique of two-level momentum may be also interesting to some readers. Essential References Not Discussed: No. Other Strengths And Weaknesses: NA Other Comments Or Suggestions: In the paper "Yu et al. Momentum approximation in asynchronous private federated learning." they also propose a method to improve async FL. The authors should also compare experiments with this paper. Questions For Authors: NA Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: We sincerely appreciate the reviewer for recognizing our contributions and for the constructive comments. Response to Comments Or Suggestions: Thanks for the suggestion. We have already discussed the reference Yu et al. (2024) in the Related Work section of our original manuscript (see Line 95), as cited below: > Yu et al. (2024) identified that asynchrony introduces implicit bias in momentum updates and proposed momentum approximation for AFL, which optimally weights historical model updates to approximate synchronous momentum behavior. In response to the reviewer's suggestion, we will include experimental comparisons of our work with [1] in the revised version. Thank you once again for your thoughtful review and constructive feedback.	null	null	null	null	null	null
Improving LLMs for Recommendation with Out-Of-Vocabulary Tokens	Accept (poster)	Summary: This paper focuses on the insufficiency of the LLM-based sequential recommendation tasks and proposes to enhance the tokenizers by introducing OOV tokens. A way of generating new tokens, namely META ID is proposed to characterize the users and items and provide token initializations for later finetuning process. Experimental results illustrate the effectiveness of META ID and introducing OOV tokens. Claims And Evidence: The claims made in the submission are supported by clear and convincing evidence. Methods And Evaluation Criteria: The chosen evaluation protocol and criteria are reasonable and follow the common practice. Theoretical Claims: NA. Experimental Designs Or Analyses: The experimental designs and analyses are valid and sound. Supplementary Material: NA. Relation To Broader Scientific Literature: This paper proposes a fundamental OOV token technique that could be applied in a wide range of LLM-based recommender systems. Essential References Not Discussed: NA. Other Strengths And Weaknesses: Strengths: + A simple yet effective token initialization method that is agnostic to model structures. + Comprehensive experiments support the effectiveness and necessity of introducing specifically-designed OOV tokens. Weaknesses: - The finetuning strategy of LLM is way too simplified, therefore might not be as effective on larger-scaled LLMs. The author could consider using other instruction tuning techniques enhance the framework. - The META ID method is only tested on old models with less than 7b parameters. The effectiveness of META ID on larger and latest LLMs (e.g. LLaMa3-42b) remain unexplored. Other Comments Or Suggestions: NA. Questions For Authors: Please refer to the weaknesses. Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: We sincerely thank the reviewer for the constructive and encouraging feedback. We are glad that the reviewer finds our method simple yet effective, the evaluation sound, and the overall contribution valuable. Below, we address the concerns: Q1: On the finetuning strategy being overly simplified A1: We appreciate the reviewer’s thoughtful feedback. We would like to clarify that our method does adopt LoRA (Low-Rank Adaptation) for finetuning in Line 312-314, which is a widely used and effective parameter-efficient finetuning strategy, especially designed for large-scale LLMs. LoRA significantly reduces the number of trainable parameters while maintaining strong performance, and has been successfully applied to models with tens or even hundreds of billions of parameters, such as GPT-3, LLaMA3, and Mixtral. Therefore, our finetuning strategy is not limited to small-scale models, and the proposed META ID token design is fully compatible with larger models under the same LoRA-based training paradigm. While our current experiments focus on models up to 7B due to resource constraints, we believe the scalability of both LoRA and META ID ensures that our approach can be extended to larger models. We are actively working on testing our method on models such as LLaMA3-13B and LLaMA3-42B. Q2: On testing with larger LLMs A2: As our primary goal was to evaluate the feasibility and utility of introducing META IDs, we chose small- to mid-sized models to ensure manageable training costs and reproducibility. We agree that testing on larger models like LLaMA3-42B or Mixtral-8x7B is important and could better demonstrate scalability. We are currently working on extending our framework to these larger models and will include these results in future versions or follow-up work.	Summary: The paper proposes META ID, an Out-Of-Vocabulary (OOV) tokenization mechanism for improving user/item ID representation in LLM-based recommendation systems. While traditional methods struggle with token diversity and semantic conflicts in token representation, the proposed META ID OOV tokens, generated through clustering meta-path representations of historical user-item interactions, improve both memorization and diversity. It's tested across various recommendation tasks (sequential, direct, rating prediction, explanation generation, and review summarization), outperforming traditional ID construction methods. Experiments also show that LLM-based recommenders incorporating META ID tokens show better performance than popular non-LLM recommenders. Claims And Evidence: 1. In Table 1 the authors compared their proposed method with other sequential recommenders to demonstrate their superiority. One issue is that the other methods are not LLM-based, which makes it hard to tell where the major gain comes from, i.e. the compute and world knowledge LLM offered, or the proposed META ID. The following data points should also be presented to justify the conclusion: 1) The training and inference efficiency related numbers of these methods 2) Comparisons with LLM-based recommenders Methods And Evaluation Criteria: - Theoretical Claims: - Experimental Designs Or Analyses: 1. See the first tip in "Claims And Evidence" 2. The effectiveness of certain parts of the model is not fully discussed, such as performance difference w/ and w/o the Linear Transformation layer. 3. As a tokenization method, more discussions on ID space collisions, the relationship of token size & #of distinct IDs would help validate the proposed method. Figure 4 only presents the performances of different token size on 3 categories of the dataset, which has the following limitations: 3.1 As shown in Table 9, the # of distinct IDs are similar across the 3 categories. How the required token size grows with # of distinct IDs is unclear 3.2 The experiments are done on each category separately. What will the proposed method perform when ID spaces get more complex (e.g. mixed categories)? Supplementary Material: - Relation To Broader Scientific Literature: - Essential References Not Discussed: - Other Strengths And Weaknesses: - Other Comments Or Suggestions: - Questions For Authors: Besides the questions in previous sections, 1. How much computational overhead does generating meta-paths and performing clustering introduce? Will it be too computationally intensive for extremely large datasets? Code Of Conduct: Affirmed. Overall Recommendation: 2	Rebuttal 1: Rebuttal: We thank the reviewer for the thoughtful comments and valuable suggestions. Below, we address each concern in detail. Overall, we emphasize that our method compares fairly with LLM-based recommenders using equivalent architectures, maintains high efficiency, and introduces minimal computational overhead. We have also added further explanation and data to clarify the role of token size, META ID contributions, and preprocessing costs. Q1：Comparisons with LLM-based recommenders A1：We would like to clarify that our method does compare against LLM-based recommenders. Specifically, in Line 300-303, we compare with TIGER (based on T5X arch.), as well as RID, SID[2] and CID[3] (all based on T5 arch.). For fairness, META ID also use T5 architecture, with only a 0.7% parameter increase over the vanilla T5 and achieve superior performance over these LLM-based recommenders. To further evaluate the feasibility and utility of META ID, we also include experiments using mid-sized LLMs (LLaMA2-7B), which strike a balance between performance and training cost. Additionally, tasks such as explanation generation and review understanding (in Tables 2 and 3) rely heavily on language comprehension, which non-LLM models are typically unable to handle. By leveraging the LLM, META ID effectively bridges structured and unstructured semantics—enabling multi-task capability beyond traditional non-LLM models.   Q2：The training and inference efficiency A2: We appreciate the reviewer’s suggestion regarding efficiency. While our primary focus is on inference (as it is critical for deployment), we report inference FLOPs for all LLM-based methods under the same input conditions: RID：7.74 GFLOPs SID：7.74 GFLOPs CID：7.77 GFLOPs TIGER：8.02 GFLOPs META ID(with T5 backbone): 7.83 GFLOPs Regarding training efficiency, we note that the computational graph is structurally similar between training and inference. As such, the relative efficiency trends are preserved during training.   Q3: Performance difference w/o the Linear Transformation layer A3: In Figure 6, removing the Linear Transformation layer (i.e., using random initialization) results in a performance drop. This confirms that the transformation layer contributes to more effective representation learning.   Q4: Token size, distinct ID space and scalability A4: We agree that token size is influenced by the number of distinct IDs. As the ID space expands, the representational demand increases, typically requiring more clusters. However, this relationship is not strictly linear, as token size also depends on: - The distributional structure of the ID space (e.g., density, sparsity) - The clustering resolution, which controls semantic separation granularity Table 1: Token size as a function of ID count (on Beauty dataset) \| portion \| ID count \| OOV Token size \| \|----\|-----\|---\| \| 30% \| 10,339 \| 711 \| \| 50% \| 17,232 \| 925 \| \| 80% \| 27,571 \| 1,156 \| \| 100% \| 34,464 \| 1,319 \| On testing the method under more complex ID spaces (e.g., mixed categories), our current setup isolates categories to study tokenization behavior in a controlled fashion. We agree that mixed-category evaluation is a valuable direction for assessing generalizability. Although such settings are not included due to scope constraints, we plan to incorporate them in future work, and our method is structurally capable of adapting via unsupervised clustering mechanisms.   Q5: Computational overhead of meta-path generation and clustering A5: We appreciate the reviewer’s concern about scalability. The proposed meta-path generation and clustering are offline preprocessing steps, performed once before training or inference, and thus do not affect runtime performance. On the Beauty dataset (~34K unique IDs): - Meta-path generation (using 32 walks × length 64) takes under 5 minutes - Clustering completes in 8.8 seconds using standard CPU implementations For larger datasets, our method is scalable via: - Parallel meta-path extraction (user/item paths are independent) - Mini-batch or streaming clustering (e.g., MiniBatchKMeans) Given the one-time nature and low cost, we believe the computational overhead is both acceptable and controllable, even for large-scale deployment.   [1] Recommender Systems with Generative Retrieval. NeurIPS 2023. [2] OpenP5: An Open-Source Platform for Developing, Training, and Evaluating LLM-based Recommender Systems. SIGIR 2024. [3] How to Index Item IDs for Recommendation Foundation Models. SIGIR-AP 2023.	Summary: This paper introduces META ID, a framework that improves LLM-based recommender systems using out-of-vocabulary tokens. The authors demonstrate that in-vocabulary tokens lack diversity when representing users/items and propose constructing OOV tokens from meta-path features extracted from user-item interaction histories. The approach uses clustering to create hierarchical tokens that capture relationship patterns while maintaining distinctiveness. Claims And Evidence: Yes. Methods And Evaluation Criteria: Diversity score as a metric is quite unstable, as each item basically requires more than 10^4 calculations, resulting in a very high computational complexity. Theoretical Claims: Yes. Experimental Designs Or Analyses: Yes. Supplementary Material: No submitted supplementary material. Relation To Broader Scientific Literature: Close to Generative Recommendation. Essential References Not Discussed: Essential References Not Discussed [1] ICML’24. Actions Speak Louder than Words: Trillion-Parameter Sequential Transducers for Generative Recommendations [2] AAAI’24. HLLM: Enhancing Sequential Recommendations via Hierarchical Large Language Models for Item and User Modeling. Other Strengths And Weaknesses: Strengths: 1. The topic of generative recommendation is interesting, and the optimization from an ID-based perspective is impressive. 2. The paper is well-written and easy to understand. Weaknesses: 1. The motivation lacks sufficient justification. 2. Some of the latest baselines are missing. 3. There is no discussion of scaling law, which is very important in GR. Other Comments Or Suggestions: 1. The motivation seems unreasonable. First, id-based approaches are not essential in GR. While some GR models like HSTU and SASREC still construct input sequences based on IDs, other methods such as TIGER and EAGER-LLM have proven the feasibility and effectiveness of token-based approaches. This paper only discusses id-based methods without analyzing the advantages and disadvantages compared to token-based approaches, nor explaining in which scenarios id-based approaches are more advantageous than token-based ones. Second, existing LLM vocabularies are already very large, for example, DeepSeek-V3's vocabulary has 129,280 tokens, which is sufficient to represent clustered items. Why add separate OOV tokens? It seems somewhat redundant. 2. Some important baselines are missing. For example: [1] ICML’24. Actions Speak Louder than Words: Trillion-Parameter Sequential Transducers for Generative Recommendations [2] AAAI’24. HLLM: Enhancing Sequential Recommendations via Hierarchical Large Language Models for Item and User Modeling. 3. What's the difference between your approach and traditional cold-start item solutions? The meta-path method is similar to traditional solutions - adding neighbors through meta-paths. The novelty is insufficient. 4. Why choose T5 and LLAMA 7B? The authors need to conduct a rigorous discussion on scaling laws, which is extremely important in GR. 5. How is the appropriate number of OOV tokens selected for each dataset? From Figure 4, this selection appears quite random. Questions For Authors: Please see the above comments and suggestions. Code Of Conduct: Affirmed. Overall Recommendation: 2	Rebuttal 1: Rebuttal: We thank all reviewers for their constructive feedback. Below, we provide a point-by-point response addressing key concerns. Q1: Stability of DS. A1: Although diversity score (DS) involves KL divergence, it is computationally efficient in practice. We avoid full pairwise comparisons (O(N²)) by sampling a fixed number of pairs (e.g., 1,000 or 10,000), reducing the complexity to O(S). Each KL divergence is fast and vectorized (via NumPy/PyTorch). For example, on the Sports dataset, computing 10,000 samples takes only 0.81 seconds on CPU, demonstrating that DS is lightweight and scalable. Q2: About the motivation A2: We thank the reviewer for raising this point. We would like to clarify a potential misunderstanding regarding the term "ID-based." Our method does not fully rely on traditional one-hot or raw ID embeddings, but instead tokenizes each ID into a unique, learnable sequence. This makes it fundamentally token-based in form while still preserving the ID-specific semantics—similar to TIGER 's subword compositions. Our method extends the token-based line by enabling OOV-aware, compositional ID encoding that bridges structured semantics with LLM-compatible inputs. Regarding vocab size concerns (e.g., DeepSeek-V3's 129K tokens), general vocabularies lack domain-specific tokens and might raise hallucination [3,4]. Our added OOV tokens (+0.7% params) cover this gap and yield measurable performance gains (Table 1).   Q3: On missing strong baselines such as EAGER [1] A3: Thank you for highlighting recent LLM-based methods. We have added direct comparisons with EAGER on Sports and Toys datasets: Table 1: Comparison with EAGER \| Dataset \| Method \| HR@10 \| NDCG@10 \| \|---\|---\|---\|---\| \| Sports \| EAGER \| 0.0441 \| 0.0236 \| \| \| Ours \| 0.0487 \| 0.0277 \| \| Toys \| EAGER \| 0.0714 \| 0.0505 \| \| \| Ours \| 0.0761 \| 0.0441 \| META ID achieves consistent gains in HR@10 on both datasets,and comparable NDCG@10. Regarding the HSTU[2], its trillion-scale architecture requires substantial resources beyond our scope. Instead of scaling size, our method emphasizes lightweight, structured ID-level representation (+0.7% params), benefiting OOV handling and multitask generalization. We will include these methods in the related work section to acknowledge their contributions and clarify our differences.   Q4: Comparison with traditional cold-start method A4: We appreciate the reviewer’s comment and agree that cold-start has been a long-standing challenge in recommendation. While our method does leverage graph-based neighbor information via meta-paths, it differs fundamentally from traditional cold-start solutions in several key aspects: - Tokenization instead of embedding fusion: instead of fusing neighbor features or adding graph edges, we tokenize meta-paths into ID-specific sequences and feed them into an LLM, enabling learnable, compositional representations. - Unified multi-task modeling: OOV tokens allow the model to perform both recommendation and text generation* (e.g., explanation) in a unified token space,which traditional methods cannot handle. Thus, our approach introduces a novel token-level representation strategy that integrates graph semantics into LLM-friendly inputs, a direction not explored in prior cold-start literature.   Q5: Backbones and scaling law A5: We thank the reviewer and agree that scaling laws are important in GR. We selected T5 (small-size) and LLaMA2-7B (mid-size) as representative backbones for the following reason: - Architectural diversity: T5 is encoder-decoder; LLaMA2 is decoder-only, covering both major LLM paradigms in GR. - Compute trade-off: Both support strong performance under realistic compute budgets. - Baseline alignment: Baselines (e.g., TIGER, RID, SID) are also built on T5, enabling controlled comparison. While we do not conduct a full scale-sweep, META ID is scaling-agnostic and can plug into larger LLMs (e.g., GPT-3, LLaMA2-13B) without modification.   Q6: Number of OOV tokens A6: The number of OOV tokens is explicitly controlled by the clustering hyperparameter (K), where each cluster maps to a token. In Figure 4, we vary K to analyze how token granularity affects performance. This mechanism offers a flexible way to adjust vocabulary size based on data complexity or computational budgets. For example, smaller K offers compact vocabularies, while larger K allows fine-grained modeling. [See also Q4 of Reviewer 8KDs]   [1] EAGER-LLM: Efficient Adaptive Generation for Recommendation. AAAI 2024. [2] Actions Speak Louder than Words: Trillion-Parameter Transducers for GR. ICML 2024. [3] Survey of Hallucination in Natural Language Generation. ACM Comput. Surv. 2023 [3] How to Index Item IDs for Recommendation Foundation Models. SIGIR-AP 2023.	null	null	null	null	null	null	null	null
Balancing Efficiency and Expressiveness: Subgraph GNNs with Walk-Based Centrality	Accept (poster)	Summary: This paper proposes a technique to reduce the computational complexity of subgraph-GNNs, which have higher expressivity than 1-WL but are often too computationally expensive to be used in practice. In particular, the method, called HyMN, relies on sampling subgraphs based on some node centralities, which can also be used as a structural encoding, akin to the RWPE. Experiments showcase the applicability of the prosed method, showing that the proposed method obtains a predictive performance that is comparable or better compared to full-bag subgraph GNNS, while having a significantly lower time complexity. Claims And Evidence: The (few) theoretical results on expressivity are correct. The experimental results are backed up by publicly available code. Methods And Evaluation Criteria: The proposed method to select the marked subgraphs for Subgraph GNNs is reasonable and effective, and motivated by some experimental results in section 3.2. However, there is a discrepancy between these observations and the proposed method itself (see W1). The method is benchmarked on relatively few datasets, all of which are molecular ones, except MalNet-Tiny. For a mostly experimental paper like this one, more datasets would be preferred. The results substantiate the validity of the method. Theoretical Claims: The (few) theoretical results on expressivity (Thm 4.1 and 4.2) seem to be correct. Experimental Designs Or Analyses: Apart from the lack of a diverse selection of real-world datasets, the experimental methodology is sound. The authors provide results on both synthetic and real-world datasets, they provide confidence intervals, and code for reproducibility. Supplementary Material: I checked the proofs and the provided code (but I did not run it). Relation To Broader Scientific Literature: The proposed method seems to produce accuracies on par with subgraph GNNs that consider all subgraphs, at a fraction of the cost. This is an important advance in the field, which was hindered by computational costs. Moreover, the proposed method is simple to implement, which would make it easier to be used by practitioners and to be improved upon by further research. Essential References Not Discussed: None. Other Strengths And Weaknesses: Strengths: 1) the proposed method seems to produce accuracies on par with subgraph GNNs that consider all subgraphs, at a fraction of the cost. This is an important advance in the field, which was hindered by computational costs. Moreover, the proposed method is simple to implement, which would make it easier to be used by practitioners and to be improved upon by further research. 2) the paper is well-written and very well motivated. The observations on which node makings impact the most the GNN output and the subsequent exploitation of these observations make for a compelling story that makes it easy to follow the paper. Weaknesses: 1) There seems to be a large discrepancy between the motivating observations and experiments of Section 3.2, and the proposed method itself. Indeed, in the section it is observed that, given a graph G, marking the node with highest walk-based centralities and obtaining a single graph G’ yields the highest change in the GNNs output \|f(G) - f(G’)\|. This however does not align with subgraph GNNs, where the graph is transformed into a bag of transformed (sub)graphs. I understand that one might want to diversify the embeddings of each of the subgraphs in the bag, and this could be the motivation for your choice, but this should be discussed explicitly in the manuscript. 2) The subgraph centrality structural encoding proposed in the paper is simply a rescaling of the RWPE, and can hardly be considered a contribution. This maybe should be stated more clearly. 3) The baseline of GIN + CSE should be added to the experiments on ogb data. 4) The method is benchmarked on relatively few datasets, all of which are molecular ones, except MalNet-Tiny. For a mostly experimental paper like this one, more datasets would be preferred. The paper, although somewhat incremental, seems to be solid and impactful, and it can be considered for acceptance. Other Comments Or Suggestions: 1) It would be useful to have a figure to illustrate node-marking-based Subgraph GNNs, with and without a subsampling approach like HyMN. Remark: I’d be open to raising my score (which is anyway mostly positive) if all my concern are properly addressed. Questions For Authors: Most real word datasets, especially molecular ones, don't really require expressive power higher than 1-WL, see for example Table 2 in [WL meet VC, ICML'23] or Table 2 in [Graph Neural Networks Can (Often) Count Substructures, ICLR'25]. Do you have an intuitive explanation on why Subgraph GNNs nonetheless show higher predictive performance compared to simpler baselines? It would be interesting to discuss this in the paper. . ----- ### Update I believe that during the rebuttal the paper has improved (e.g., new experiments, intuitive figures, and a stronger motivation). Therefore, I raised my score to 4 to suggest acceptance. Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: The reviewer found the paper “solid and impactful”, the method as “an important advance in the field”, “reasonable”, “effective” and “motivated” by experimental results. They manuscript is also found “well-written". We address comments below. --- “There seems to be a large discrepancy between the motivating observations and experiments of Section 3.2, and the proposed method itself. [...] this should be discussed explicitly in the manuscript.” In Section 3.2 we look at the optimal initial subgraph selection to (i) alter the base MPNN’s graph representation sufficiently and (ii) in a way that correlates with predictive information (e.g. subgraph counts). When only one subgraph is chosen (T=1), this approach exactly aligns with the proposed method, and we disagree there is a discrepancy in this case. Also, T=1 is, by far, the most compelling setting from a complexity perspective and our model attains very strong performance for this. Overall, we optimized for a sampling strategy that was efficient and non-learnable, and accordingly considered the case where every subgraph selection is made w.r.t. the original graph representation. We acknowledge that further theoretical insights could be gained on partially filled bags; we mention this in line 435 and will emphasize this more. --- “The subgraph centrality structural encoding proposed in the paper is simply a rescaling of the RWPE, [...] This maybe should be stated more clearly.” We acknowledge the similarity between RWSEs and CSEs. In fact, we devote Section F.4 to discuss their relation. Proposing CSEs as a new form of SEs is not the (main) contribution of our manuscript. CSEs emerge from the centrality computations required for subgraph sampling: we propose to retain them and show the benefit of this in terms of discriminative power. We will clarify this point further. --- “The baseline of GIN + CSE should be added to the experiments on ogb data.” We agree. We conducted these experiments during the rebuttal period and report the results below: \| \| molhiv \| molbace \| moltox \| \|--------------\|--------------\|--------------\|--------------\| \| GIN+CSEs \| 77.44 ± 1.87 \| 76.58 ± 2.29 \| 75.81 ± 0.39 \| \| HyMN (GIN, T=2) \| 81.01 ± 1.17 \| 81.16 ± 1.21 \| 77.30 ± 0.35 \| These results support the effectiveness of our centrality-based strategy. We will include them in Table 2. --- “The method is benchmarked on relatively few datasets, all of which are molecular ones, except MalNet-Tiny. For a mostly experimental paper like this one, more datasets would be preferred.” We note that, although effectively molecules, peptides differ substantially from the small drug-like molecules in ogbg datasets—in size, structure, and biological role. Actually, we argue this makes for three different data domains. That said, we agree broader benchmarking would strengthen our work. To this end, during the rebuttal period we additionally evaluated our method on the Reddit-binary (RDT-B) dataset—a fourth domain (social networks). RDT-B is significantly larger than ogbg graphs and is too large for full-bag Subgraph GNNs. Results, obtained under the setup from [1], are below: \| Method \| RDT-B Accuracy \| \|-------------------------\|-----------------\| \| GIN \| 92.4 ± 2.5 \| \| FULL \| OOM \| \| RANDOM (T=20) \| 92.6 ± 1.5 \| \| RANDOM (T=2) \| 92.4 ± 1.0 \| \| POLICY-LEARN (T=2) \| 93.0 ± 0.9 \| \| HyMN (T=2) \| 93.2 ± 2.2 \| HyMN matches the performance of the learnable POLICY-LEARN, coherently with results obtained on other datasets. We will add the above in the next paper revision. [1] https://arxiv.org/abs/1810.00826 --- “It would be useful to have a figure to illustrate node-marking-based Subgraph GNNs, with and without a subsampling approach like HyMN.” Thanks for the suggestion – we have accordingly prepared a figure currently hosted at [this](https://anonymous.4open.science/r/HyMN-ICML-Rebuttal-8A82/2.png) anonymous link. We plan to add it in the next paper revision (Section B). --- “Most real word [sic.] datasets, especially molecular ones, don't really require expressive power higher than 1-WL [...] Do you have an intuitive explanation on why Subgraph GNNs nonetheless show higher predictive performance [...] ?” This is an open question in graph learning. Higher separation power may not be needed, or even harmful if obtained by spurious features. Yet, expressive models like Subgraph GNNs often generalize better. A reasonable hypothesis is that these form a representation space with “more convenient” graph separation, one that makes solving the downstream task more amenable, e.g. by “aligning” with predictive motif counts. Some of these intuitions are echoed in our approach. --- We hope our responses clarify the raised concerns. We would kindly ask the reviewer to reconsider their scores in view of them. --- Rebuttal Comment 1.1: Comment: Thank you for your reply. I think the addition of the additional experiments further strengthens the paper. I am however confused about the figure you linked, as the bag of subgraphs does not contain the original graph with marked nodes, but rather subgraphs for the original graph. I think the figure should be more aligned with your methods. In fact, thinking about node markings made me realize that your method, especially with T=1, is closely linked with random node features/node individualizations literature, where nodes are marked in order to increase expressivity. You might want to consider discussing this relationship in the paper. Finally, I don't understand how the method setting T=1 aligns with the intuition give in Section 3.2. For example, you say that "subgraphs associated with low centrality nodes can be interpreted as redundant w.r.t. the original input graph". If you choose T=1 there is no redundancy whatsoever. To me it's also very unclear why one would want the representation of the marked graph (with T=1) to be as different as possible to the original graph, as this could lead to unpredictable behavior (although clearly this is not the case in practice, as the method performs really well). I think that providing a more convincing alignment between intuition and practice could make the difference between a good and a great paper. --- Reply to Comment 1.1.1: Comment: We are glad the reviewer appreciated our additional set of results. Let us reply to the outstanding points here below. --- “I am however confused about the figure you linked, as the bag of subgraphs does not contain the original graph with marked nodes [...]” Thanks for pointing this out – yes, the figure we had created refers to a generic Subgraph GNN with a bag-sampling approach. In the specific example, the subgraph selection policy was ego-networks. We agree this can cause confusion, as, in our paper, we assume to be always working with the (more general) node-marking selection policy. Accordingly, we improved the figure to better align it with our approach. Please find it here ([link](https://anonymous.4open.science/r/HyMN-ICML-Rebuttal-8A82/3.png)). Concretely, the figure represents the setting T=1, where only one marked subgraph is sampled (out of six possible ones). In particular, our approach chooses the subgraph associated with the maximum-centrality node. --- “I don't understand how the method setting T=1 aligns with the intuition give in Section 3.2. For example, you say that "subgraphs associated with low centrality nodes can be interpreted as redundant [...]” In the setting T=1, the sampling method picks exactly one node-marked subgraph out of all possible ones. For T=1, the downstream GNN will then effectively process a node-perturbed version of the original graph (as illustrated in the aforementioned figure). Now, the Observation we make in Section 3.2 is that if the marked node is a low-centrality one, then such a GNN will output a graph representation (necessarily) similar to the one it would have output when processing the original graph. We agree that the term “redundant” in line 196 is not fully rigorous to refer to this and we will remove it in the next revision. We will only leave the term “poor marking candidates” to refer to them (line 197). See more on this below. --- “[...] why one would want the representation of the marked graph (with T=1) to be as different as possible to the original graph, as this could lead to unpredictable behavior (although clearly this is not the case in practice, as the method performs really well).” Out of all possible node-marked subgraphs, our method prefers to sample those associated with higher-centrality nodes. This is because: - As mentioned above, low-centrality nodes perturb representations only up to a limited extent, causing the method to work in a “regime” close to a vanilla 1-WL GNN; - We empirically observe the perturbations induced by marking high-centrality nodes correlate much more with potentially predictive features, like subgraph-counts. According to our observations, thus, higher-centrality nodes are those which have the potential to perturb the original graph representation the most, and in a way that captures predictive features. As the reviewer correctly observes, marking these nodes does not lead to unpredictable behaviour in practice: ultimately, the downstream GNN will learn, via training, how to make best use of the additionally provided information. In principle it can learn to ignore this completely –should it not be predictive– or to leverage it to extract expressive features –in the case they correlate with targets. This flexibility is something that may not be effectively provided by marking low-centrality nodes, whose induced perturbations have a lower upper-bound. In order to further prove our point above, we have run additional experiments for counting triangle and 4-cycle substructures, studying the impact of sampling marked subgraphs associated with the minimum values of the Subgraph Centrality (SC). We report the results in the tables below, along with those of random and max-centrality sampling (MAE, the lower the better). Triangles \| Policy \| 10 subgraphs \| 20 subgraphs \| 30 subgraphs \| \|----\|----\|----\|----\| \| Min SC \| 0.78 \| 0.52 \| 0.43 \| \| Random \| 0.62 \| 0.48 \| 0.40 \| \| Max SC \| 0.20 \| 0.10 \| 0.03 \| 4-cycles \| Policy \| 10 subgraphs \| 20 subgraphs \| 30 subgraphs \| \|----\|----\|----\|----\| \| Min SC \| 0.74 \| 0.63 \| 0.41 \| \| Random \| 0.59 \| 0.45 \| 0.36 \| \| Max SC \| 0.38 \| 0.12 \| 0.08 \| We observe that min-centrality sampling is indeed outperformed by the two other strategies on all settings. --- “[...] with T=1, is closely linked with random node features/node individualizations literature, where nodes are marked in order to increase expressivity.” Thanks for pointing this out. For T=1, node-marking can be interpreted as the first call to a node-individualization algorithm. Also, in a way, node-marking breaks symmetries between nodes as random features would do. We will discuss these connections in the next revision. --- We will clarify all the points above based on our responses, hoping they have addressed your outstanding concerns.	Summary: The authors propose a centrality-based scheme for selecting expressive subgraphs for subgraph GNNs. Essentially, their idea is based on the observation that message passing themes and walks on graphs are the same thing, which makes using walk-based centralities a natural proxy for selecting nodes with high influence on the learning process of GNNs. The authors evaluate their approach on synthetic (Erdős–Rényi random graphs) and real-world graphs and demonstrate that their approach outperforms subgraph-GNN-based and transformer-based baselines both in terms of performance and runtime. ## update after rebuttal As mentioned during the rebuttal period, I am satisfied with the authors' responses and planned revisions to the manuscript. Hence, I maintain my score which I updated during the rebuttal period. Claims And Evidence: The claims made by the authors are supported by clear arguments and empirical evidence. Methods And Evaluation Criteria: I believe that the chosen evaluation datasets and measures are sufficient for supporting the authors' claims. As they point out, their approach focuses on learning graph representations with the intention to provide a basis for various downstream tasks. Theoretical Claims: I find that the authors' arguments are clearly formulated and convincing. I have read the proofs in appendix D and did not find any obvious issues, however, I am not trained as a mathematician and may have missed more involved subtleties. Experimental Designs Or Analyses: The experimental setup seems sound. However, I find that the authors should be more explicit regarding how the results of their evaluation should be interpreted. Specifically, they count sub-structures in Erdős–Rényi random graphs and measure the performance of their scheme in terms of Pearson correlation. But how should we interpret those values? Obviously a higher correlation is better, but what results do we expect? And what results does their proposed method return? Also, based on the datasets used in Table 2, I guess that the considered task is graph classification, I think it would be better to state the considered task explicitly in the text. Supplementary Material: I've read the supplementary material but did not carefully check it for correctness. Relation To Broader Scientific Literature: As the authors point out, current subgraph GNNs suffer from computational challenges when they consider full bags of subgraphs and, therefore, are limited to applications involving very small graphs. While the network science community has long considered walk-based measures as an extremely useful tool, I am happy to see that they are now also finding broader adoption in the deep learning community. Essential References Not Discussed: I am not aware of any essential references that the authors have missed to include. Other Strengths And Weaknesses: I find the paper extremely well written. The authors' arguments are clearly laid out. They are guiding the reader by asking and answering relevant questions on the reader's behalf. Overall, I found it enjoyable to read the paper. Other Comments Or Suggestions: I found the explanation regarding what effectiveness and efficiency are (Section 3.1, paragraph "Goal") very intuitive. Questions For Authors: 1. Are there any limitations regarding what kinds of graphs the proposed approach can be applied to? For example, do the graphs need to be connected or undirected? What about disconnected graphs or directed graphs that are only weakly connected? Or is the only requirement that the chosen centrality measure must be able to assign centrality scores to all nodes? 2. Why is there a difference between degree centrality and PageRank in Figure 3? In undirected graphs, the two should select the same nodes as the most central. Is the difference only due to the randomness in the initialisation of GNN weights? 3. What is the reason for the missing values in Table 2? 4. The paper title mentions "balancing efficiency and expressiveness", but I am wondering to what extent it can actually be claimed that the subgraph centrality addresses the expressiveness goal? Yes, selecting the nodes with the highest centrality values works better than random selection or selecting those nodes with low centrality values. But is there another set of nodes that should be preferred over those with the highest centrality values? My intuition tells me that this should be the case -- and I might be wrong with that. But given the relatively small number of chosen nodes in the empirical experiments, it should be possible to quantify how well the proposed selection scheme works in comparison to the optimal set of nodes of the same size that could be chosen. Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: We are very pleased to note the positive recommendation made by the reviewer. They have appreciated the proposed application of Network Science results to Deep Learning, and have found the paper “extremely well written”, with claims supported by “clear arguments and empirical evidence”. The reviewer had a clarity concern pertaining to tackled tasks and result interpretation, along with some questions. We address these points in the following. --- “I find that the authors should be more explicit regarding how the results of their evaluation should be interpreted. [...] they count sub-structures in Erdős–Rényi random graphs and measure the performance of their scheme in terms of Pearson correlation. But how should we interpret those values? [...] Also, based on the datasets used in Table 2, I guess that the considered task is graph classification [...]” Substructure counts: in Sections 3 we report results in terms of Pearson correlation. The aim of these experiments is to understand how much substructure counts are recapitulated by the perturbations induced by different marking strategies. We agree that absolute correlations may be difficult to interpret per se, but, in relative terms, it is very valuable to observe how the various marking strategies rank w.r.t. each other. Eventually, these rankings give us an indication on how the strategy will perform in the actual task of counting substructures, which we study in Section 5. This time, these results are quantified in terms of Mean Absolute Error, and are reported in Figures 3 and 7. We will better highlight these aspects in the next revision. As for results reported in Table 2 – yes, we confirm all the three benchmarks involve graph classification. We will make sure to state this clearly. --- “Are there any limitations regarding what kinds of graphs the proposed approach can be applied to? [...] is the only requirement that the chosen centrality measure must be able to assign centrality scores to all nodes?” Yes, this is correct. As long as the centrality measure ranks all the nodes in a graph, the method can be run without any caveat. Regarding directionality: our focus is mostly on undirected graphs, consistently with virtually all previous works on Subgraph GNNs. As such, our analysis does not specifically discuss the case of directed graphs, but one could clearly consider a centrality measure that is well-defined thereon. An interesting avenue for future research would be to extend perturbation analyses on directed graphs and study whether known centrality measures allow to well capture these effects, similarly to how we proceed in our manuscript. --- “Why is there a difference between degree centrality and PageRank in Figure 3? [...]” While it is true that the two centrality measures are often found to produce similar node rankings in undirected graphs, we note that they are not generally equivalent in this setting. The degree centrality only accounts for first-order node interactions, whereas Page-Rank also considers the effect of higher-order neighbours. In the latter case, two nodes with the same degree would, e.g., be ranked differently if they connect to a different number of high-degree neighbours. --- ”What is the reason for the missing values in Table 2?” We thank the reviewer for pointing this out. We chose these ogbg-molecular benchmarks to capture a good overlapping set of datasets on which previous sampling-based Subgraph GNNs were tested on. The results in Table 2 are directly taken from the original papers and, unfortunately, some methods were not uniformly benchmarked on these datasets. This explains the “missing numbers”. We will be more clear about this in the next revision. --- ”[...] Yes, selecting the nodes with the highest centrality values works better than random selection or selecting those nodes with low centrality values. But is there another set of nodes that should be preferred over those with the highest centrality values? [...] it should be possible to quantify how well the proposed selection scheme works in comparison to the optimal set of nodes of the same size that could be chosen.” This is an interesting point, and we agree that quantifying optimality could be particularly insightful. We also note, however, that optimality is ultimately defined with respect to a particular learning task. To find an optimal set which also accounts for learning would quickly become computationally challenging. We respectfully believe this experiment could not be run in a thorough manner within the rebuttal period. We will, either way, point out this interesting direction in the next revision. --- Rebuttal Comment 1.1: Comment: Thank you for your responses. I find that my concerns will be addressed by the planned revisions and have no further questions.	Summary: This paper explores subgraph GNNs as a way to overcome the expressivity limitations of standard Message Passing Neural Networks (MPNNs). In a subgraph GNN, a graph is transformed into a "bag of subgraphs," where each subgraph is processed independently using an equivariant architecture, and the results are aggregated for final prediction. While these methods enhance expressivity, they suffer from high computational costs due to the large number of subgraphs that need to be processed. To address this challenge, this paper proposes a hybrid subgraph selection and feature augmentation method. The key idea is to sample subgraphs centered around nodes with high Subgraph Centrality, which is a metric introduced in prior work that measures a node's importance based on walk-based connectivity patterns. Moreover, the paper introduces a feature augmentation technique that incorporates centrality scores as structural encodings. The paper provides some theoretical analysis to support the use of Subgraph Centrality. In the experiments, the method overall matches or outperforms some other Subgraph GNNs and Graph Transformers on some benchmarks, and is more scalable. Claims And Evidence: (S1) The authors claim that their method overcomes the expressive limitations of MPNNs while remaining scalable. Section 3.2 provides interesting progress toward substantiating these claims by establishing a connection between Subgraph Centrality and perturbation analysis. (However, I think this analysis could be refined/strengthened, as I describe in W1-W3 below.) Second the paper claims that the proposed method outperforms other subgraph selection strategies and achieves performance comparable to or better than full-bag Subgraph GNNs while sampling only one or two subgraphs. I'm not fully convinced about this claim, as I elaborate on in (W4) below. (S2) Finally, the paper claims that the proposed approach is competitive with Graph Transformers and SOTA GNNs while being significantly more computationally efficient. I think this is reasonably substantiated by Tables 3 and 4. Methods And Evaluation Criteria: Section 3.2 presents a combination of theoretical and empirical analyses to motivate the use of Subgraph Centrality. Observation 1 states that if a node has low centrality, training a GIN on its induced subgraph will have little impact on the GIN's prediction. The implication is that to improve expressivity, one should, at minimum, avoid selecting subgraphs centered around low-centrality nodes. Next, Section 3.2 presents two experiments: 1. Selecting subgraphs based on high-centrality nodes leads to large variations in the GIN's predictions. 2. Subgraphs centered on high-centrality nodes contain a higher prevalence of structural motifs, such as triangles and 4-cycles. Here are a few suggests for developing this section: (W1) The two experiments use very different types of graphs---real world TU datasets for the first and Erdos-Reyni for the second. It's not clear why there is this discrepancy and it would be helpful to standardize. (W2) While the theoretical results rule out low-centrality nodes as good candidates, they don't strongly establish that choosing high-centrality nodes is necessarily optimal. This makes this analysis interesting but not entirely conclusive. (W3) The discussion on why structural motifs are desirable could be expanded. The paper states that the “presence and number of strucutral ‘motifs’ are often related to graph-level tasks” but this doesn't explain why subgraphs with more motifs are desirable for improving GNN performance. Theoretical Claims: I have a question about observation 1: why don't node features come into play? Experimental Designs Or Analyses: (W4) The paper introduces many related subgraph GNN methods in its citations, but the experiments primarily compare the proposed method against POLICY-LEARN, not including the other potentially relevant baselines. Additionally, POLICY-LEARN is omitted from Tables 3 and 4, while it is included in other results. It would be helpful to provide a more comprehensive evaluation or explain why methods were omitted. Supplementary Material: I skimmed it and have nothing to comment on. Relation To Broader Scientific Literature: I think this paper would be of interest to the community interested in GNN expressivity, but I think the weaknesses I presented should be addressed first. Essential References Not Discussed: None that I'm aware of. Other Strengths And Weaknesses: None beyond those I described above. Other Comments Or Suggestions: None. Questions For Authors: Can you please address weaknesses (W3) and (W4)? Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: (W1) “The two experiments use very different types of graphs [...] it would be helpful to standardize.” We used TU datasets for perturbation analyses aligning with [1], but we agree standardization would be preferred. As suggested, we re-run them on the same ER graphs in the subgraph-count correlation study. The results ([link](https://anonymous.4open.science/r/HyMN-ICML-Rebuttal-8A82/1.png)) are consistent with our prior findings, and will be included in the new revision. --- (W2) “[...] theoretical results rule out low-centrality nodes [...] don't strongly establish that choosing high-centrality nodes is necessarily optimal. [...] analysis interesting but not entirely conclusive.” We agree that our approach is not necessarily optimal and, in fact, note that an optimal selection would also require access to targets and to account for learning. Our goal is to design an efficient subgraph selection that is run as preprocessing and achieves effective performance. Although our approach lacks optimality guarantees, it: - is theoretically grounded via the connection to perturbation analyses (found “interesting”); - leads to consistent empirical gains with contained overhead. Also, HyMN always performed at least as well as a learnt selection strategy, indicating its actual effectiveness once more. We think the above already provides an important contribution to the community, and believe further theoretical analyses on optimality warrant interesting future research. --- (W3) “The discussion on why structural motifs are desirable could be expanded.” Motif counts are widely recognized as important graph features: in Network Science, motif profiles have been used to compare and classify networks; the GNN community has also explored their utility due to message-passing limitations in detecting them. A seminal paper [2] even proposed to employ them as SEs, showing the significant expressivity and generalization boost they can provide. Starting from these premises, and provided that node-marking subgraphs enhances expressivity, we argue it would be preferable to choose those subgraphs which, amongst others, better enable the model to capture subgraph counts. We quantify this by studying the correlations between counts and the mark-induced graph perturbations. Our results indicate they are maximized when marking based on the highest Subgraph Centrality (see Table 1). These findings – as well as our more general argument – find supporting evidence in the experimental results reported in Figure 3. --- “[...] observation 1: why don't node features come into play?” Because we have to consider the TMD not between two generic graphs, but between a graph and the node-marked version thereof, where node feats. coincide. --- (W4) “[...] experiments [...] not including the other potentially relevant baselines. [...] POLICY-LEARN is omitted from Tables 3 and 4 [...]” In fact, Table 2 already includes additional efficient Subgraph-GNNs baselines beyond POLICY-LEARN: OSAN and MAG-GNN. These are in a separate table lane, likely causing confusion. We will improve the layout in the next revision. Either way, we agree that reporting the performance of other methods would strengthen our claim. In fact, molhiv is a reference test-bed for most full-bag methods. We will add these additional results: \| \| molhiv \| \|----\|----\| \| Reconstr. GNN \| 76.32±1.40 \| \| Nested-GNN \| 78.34±1.86 \| \| DSS-GNN \| 76.78±1.66 \| \| GNN-AK+ \| 79.61±1.19 \| \| SUN \| 80.03±0.55 \| \| HyMN (T=2) \| 81.01 ±1.17 \| HyMN competes with the best full-bag approaches with only two subgraphs. As for non-full-bag Subgraph GNNs, we will additionally include results (ROC-AUC) for CS-GNN [3], which we found has been benchmarked both on molhiv, and molbace. Note HyMN’s competitive performance compared to this method. \| \| molhiv \| molbace \| \|----\|----\|----\| \| CS-GNN (T=2) \| 77.72±0.76 \| 80.58±1.04 \| \| HyMN (T=2) \| 81.01 ±1.17 \| 81.16 ±1.21 \| \| CS-GNN (T=5) \| 79.09±0.90 \| 79.64±1.43 \| \| HyMN (T=5) \| 80.17 ±1.40 \| 80.64 ±0.48 \| Peptides, MalNet (Tables 3, 4): POLICY-LEARN was not originally evaluated thereon. We attempted this using the authors’ code. On MalNet-Tiny, memory usage exceeded our server’s capacity (1TB CPU RAM) due to the full bag materialization required by their implementation. Optimizations may be possible but infeasible within the rebuttal window. On Peptides, we obtained: \| \| peptides-func (AP ↑) \| peptides struct (MAE ↓) \| \|----\|----\|----\| \| POLICY-LEARN (T=1) \| 0.6336 ±0.0071 \| 0.2475 ±0.0008\| \| HyMN (T=1) \| 0.6857 ±0.0055 \| 0.2464 ±0.0013 \| \| POLICY-LEARN (T=2) \| 0.6459 ±0.0018 \| 0.2475 ±0.0011 \| \| HyMN (T=2) \| 0.6863 ±0.0050 \| 0.2457 ±0.0012 \| We finally refer to the response to Reviewer d9AX for additional results on Reddit-binary. --- We hope your concerns are clarified, while we are open to elaborate further. [1] https://arxiv.org/abs/2210.01906 [2] https://arxiv.org/abs/2006.09252 [3] https://arxiv.org/abs/2406.09291 --- Rebuttal Comment 1.1: Comment: Thank you for the clarification on the experiments, this helps alleviate some of my concerns.	Summary: The paper proposes HyMN (Hybrid Marking Networks), a combination of walk-based structural encodings and centrality-based subgraph marking strategies. The goal is to design a subgraph GNN which is simultaneously effective (sampled bags tend to optimal) and efficient (few operations / no learnable components). Claims And Evidence: C1: Centrality Measures can be conceptualized as graph perturbations. E: Analysis based on Chuang/Jegelka Tree Mover paper. Experiments to support the hypothesis. C2: A combination of SE and Centrality Measures works well. E: Ablation proofs, in the sense that they extend 1-WL in incomparable ways. Experimental support for HyMN. Methods And Evaluation Criteria: Yes. Theoretical Claims: Yes. The arguments seem correct. Experimental Designs Or Analyses: Yes. The experimental protocol are standard. Supplementary Material: Yes, entirely. Relation To Broader Scientific Literature: The paper forms a solid contribution to the existing work on Subgraph Sampling. The nice result of Chuang and Jegelka forms the real engine of the paper, though. Essential References Not Discussed: Not that I know of. Other Strengths And Weaknesses: Strengths 1) The paper is extremely well-written. The presentation is thorough. 2) Even though the paper is a bit light on theory, the paper cherry-picks the right ideas and puts them together nicely: Experimental support is provided wherever necessary. It was quite comfortable to grasp the essential ideas behind the model. 3) The idea of walk-centrality holds promise for spurring on further work in this area. Weaknesses 1) The use of both SE and Centrality Subgraph Sampling really makes HyMN a bit of a Swiss knife. This is not really a criticism, but this weakens the claims for the effectiveness of Centrality Marking as a technique. Other Comments Or Suggestions: - Questions For Authors: - Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We are very glad to note the reviewer found the paper “extremely well-written”, that it “picks the right ideas and puts them together nicely” and, importantly, that they believe the underpinning idea “holds promise for spurring on further work in this area”. The reviewer shared the view that the joint use of both SEs and Centrality-based sampling may weaken the claim for the effectiveness of the latter as an approach on its own. We understand that the hybrid nature of our approach may lead to this perception, but we believe it is important to underscore the effectiveness of the centrality marking alone. Even without our positional encodings (CSEs), on the ogbg-molecular benchmarks HyMN outperforms MPNN baselines and methods based on random subgraph sampling, while it matches the performance of the learnable approach Policy-Learn (see Table 2). HyMN without CSEs also attains successful results on the larger MalNet dataset, scoring the highest average test score in the configuration T=1 when compared to other HyMN variants and transformer-based baselines (see Table 4). We conclude by complementarily remarking how baselines methods like GIN and GCN, when augmented with CSEs, fail to match the full HyMN performance. We observe this in Table 3 on the peptides datasets and on the molecular ogbg benchmarks as well. We report, indeed, that we have additionally run GIN with CSEs thereon. We obtained the following results, which we report, for reference, along with the performance attained by HyMN in the configuration T=2: \| \| molhiv \| molbace \| moltox \| \|--------------\|--------------\|--------------\|--------------\| \| GIN+CSEs \| 77.44 ± 1.87 \| 76.58 ± 2.29 \| 75.81 ± 0.39 \| \| HyMN (GIN, T=2) \| 81.01 ± 1.17 \| 81.16 ± 1.21 \| 77.30 ± 0.35 \| We hope this clarifies the raised concern. We would kindly ask the reviewer to reconsider their scores in view of our response.	null	null	null	null	null	null
Improving Soft Unification with Knowledge Graph Embedding Methods	Accept (poster)	Summary: This paper presents the first integration of NTP and KGE, aiming to enhance the performance of NTP in terms of both effectiveness and efficiency. The experimental results demonstrate the synergy between these two lines of research. Claims And Evidence: To some extent, yes. There are a few claims in the introduction that are not entirely accurate, which I have outlined in the 'Other Weaknesses' section below. Methods And Evaluation Criteria: Yes. Theoretical Claims: N/A Experimental Designs Or Analyses: Yes, I believe the authors have provided sufficient details about the experiments, which are undoubtedly comprehensive. Additional comments can be found in the 'More Strengths' section. Supplementary Material: No I did not. Relation To Broader Scientific Literature: The integration of KGE to improve NTP is directly beneficial for scientific discovery, as NTP has become a key research focus for many logicians and mathematicians, particularly in areas like automated proof checking and broader scientific applications. Essential References Not Discussed: ### Inductive KGE/KGFMs on unseen relations [1]. Galkin, M., Yuan, X., Mostafa, H., Tang, J., and Zhu, Z. Towards foundation models for knowledge graph reasoning. In ICLR, 2024. [2]. Mao, H., Chen, Z., Tang, W., Zhao, J., Ma, Y., Zhao, T., Shah, N., Galkin, M., and Tang, J. Position: Graph foundation models are already here. In ICML, 2024. [3]. Lee, J., Chung, C., and Whang, J. J. Ingram: Inductive knowledge graph embedding via relation graphs. In ICML, 2023. ### Inductive GNNs on unseen nodes (there are more) [4]. Waikhom, Lilapati, Yeshwant Singh, and Ripon Patgiri. "PO-GNN: Position-observant inductive graph neural networks for position-based prediction." Information Processing & Management 60.3 (2023) Other Strengths And Weaknesses: ## Strengths 1. The paper is well-structured overall, and the integration of the two research areas is clearly demonstrated. 2. The experimental section is thorough, evaluating four potential methods for integrating KGE, while also comparing different KGE variants. The results show an overall improvement when integrating KGE, aligning with the authors' claims. Additionally, the increase in inference time is presented. ## Weaknesses 1. In the Introduction, it is initially stated that DL is limited by poor interpretability. However, later it is suggested that the transformation of discrete symbols into continuous vector space combines the strengths of both DL and symbolic AI. I wonder whether LLMs also fall under the category of NeSy AI, yet they still struggle with explanation abilities. Moreover, theorem proofs require significantly more interpretability than natural language, which raises the question of whether this approach is suitable for such domains. 2. The connection between NTP and KGE could be better introduced. Additionally, there are inductive KGE methods and GNNs that handle unseen entities or relations by defining local representations for unseen items. Knowledge graph foundation models also address such generalization issues [1-4]. 3. It would be valuable to explore the potential reasons behind the observed improvements and identify which types of proof structures could benefit most from KGE integration. This would provide further insight to the research community. Other Comments Or Suggestions: ## Weaker suggestions 1. More explanation of the 'sparse gradient perspective' in the Introduction is needed before shifting the focus to the embedding space. Questions For Authors: N/A Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: > *1. In the Introduction ... raises the question of whether this approach is suitable for such domains.* Thank you for your insights! While LLMs also transform discrete symbols to continuous space, the difference is NeSy approaches incorporate more explicit reasoning priors in their framework (e.g. backward chaining algorithm for NTPs), as compared to the generic next-token-prediction in LLMs. These structural priors allow NeSy models to have less hallucination and better interpretability (as one can trace the proof paths and localize errors). > *2. The connection between NTP and KGE could be better introduced / include works of inductive KGE/KGFMs on unseen relations* We will revise our manuscript to incorporate more corresponding details. Also, just to clarify, in this work we do not focus on inductive KGC, and hence we did not include these works initially. > *More explanation of the 'sparse gradient perspective'* We will rewrite the introduction to add more explanations. > *3. potential reasons behind the observed improvements* Improved Embedding space. First, we empirically find integrating KGE (paricularly CTP2) can notably improve the structureness of NTP embedding space. This is discussed throughout the paper. Explanation of why similarity-based KGEs work better with NTPs than translational-based KGEs. Please refer to section 2.why using similarity-based KGEs can achieve better performance in our reply to Reviewer Bi1c. Theoretical justification CTP1 vs. CTP2. We provide a theoretical justification from a gradient perspective of why CTP2 performs better than CTP1 (as CTP2 is different from CTP3 and CTP4 and mostly similar to CTP1). Due to space limit, we are only able to show essential steps. Let $\theta$ denotes the learnable embeddings, $\phi_N$ and $\phi_K$ denote the score function of KGE and CTP, the loss for CTP1 is $$\mathcal{L_1}(\theta) = -y \log \phi_N(\theta) - (1-y) \log(1-\phi_N(\theta)) - y \log \phi_K(\theta) - (1-y) \log (1-\phi_K(\theta)).$$ Applying the chain rule, the gradient of $\mathcal{L_1} \ \text{with respect to} \ \theta$ is $$\nabla_\theta \mathcal{L_1} = \left[-\frac{y}{\phi_N(\theta)} + \frac{1-y}{1-\phi_N(\theta)}\right] \nabla_\theta \phi_N(\theta) + \left[-\frac{y}{\phi_K(\theta)} + \frac{1-y}{1-\phi_K(\theta)}\right] \nabla_\theta \phi_K(\theta).\quad(1)$$ For CTP2, the score function is a combination (assume $\lambda = \frac{1}{2}$) of KGE and original NTP's similarity score, write as $$\phi_2(\theta) = \frac{\phi_N(\theta) + \phi_K(\theta)}{2}, $$ and the loss becomes $$\mathcal{L_2}(\theta) = -y\log\phi_2(\theta)-(1-y)\log(1 -\phi_2(\theta)).$$ the gradient for each individual score calculation in CTP2 is $$\nabla_\theta \mathcal{L_2}=\left[-\frac{y}{\phi_2(\theta)} + \frac{1-y}{1-\phi_2(\theta)}\right] \cdot(\nabla_\theta \phi_N(\theta) + \nabla_\theta \phi_K(\theta))\quad(2)$$ By comparing Eq.1 and Eq.2 we can see that CTP1's gradient only involve "self" terms, where the gradients of KGE and NTP are separately computed and then added. On the other hand, CTP2's gradient involves `cross' terms, such as $-\frac{y}{\phi_2(\theta)} \cdot \nabla_\theta \phi_N(\theta)$, which could potentially provide a more coherent gradient update. Further, assume both $\phi_{N}$ and $\phi_{K}$ are noisy estimates of an underlying true signal $$\phi_N(\theta) = \phi + \epsilon_N, \quad \phi_K(\theta) = \phi + \epsilon_K,$$ with independent zero-mean terms $ \epsilon_N, \epsilon_K $ each with variance $\sigma^2$. Assume $$\nabla_\theta \phi_N(\theta) \approx \nabla_\theta \phi_K(\theta) \equiv \nabla_\theta \phi.$$ Define $$g(\phi) = -\frac{y}{\phi} + \frac{1-y}{1-\phi} \quad \text{and} \quad g'(\phi) = \frac{y}{\phi^2} + \frac{1-y}{(1-\phi)^2}.$$ Using a first-order Taylor expansion, we can approximate$$g\bigl(\phi_N(\theta)\bigr) \approx g(\phi) + g'(\phi) \epsilon_N, \quad g\bigl(\phi_K(\theta)\bigr) \approx g(\phi) + g'(\phi) \epsilon_K. $$ The gradient for CTP1 becomes: $$\nabla_\theta \mathcal{L_1}\approx 2g(\phi)\nabla_\theta \phi+g'(\phi)(\epsilon_N+\epsilon_K)\nabla_\theta\phi.$$ The noise term is $\Delta_1 = g'(\phi)(\epsilon_N+\epsilon_K) \nabla_\theta \phi,$ with variance $$\operatorname{Var}[\Delta_1] \propto \left(g'(\phi)\right)^2\operatorname{Var}(\epsilon_N+\epsilon_K) = \left(g'(\phi)\right)^2 \cdot 2\sigma^2.\quad(3)$$ Similarly, for CTP2, the noise term is $$\Delta_2 = g'(\phi)\frac{\epsilon_N+\epsilon_K}{2} \nabla_\theta \phi, $$ with variance $$\operatorname{Var}[\Delta_2] \propto \left(g'(\phi)\right)^2\operatorname{Var}\left(\frac{\epsilon_N+\epsilon_K}{2}\right) = \left(g'(\phi)\right)^2\frac{1}{4}\cdot 2\sigma^2 = \left(g'(\phi)\right)^2\frac{\sigma^2}{2}.\quad(4)$$ By comparing Eq.3 and Eq.4 we can see the noise variance for CTP2 is reduced by a factor of 4 compared to CTP1's. This reduction could lead to smoother and more stable optimization dynamic, which is also what we observed empirically. --- Rebuttal Comment 1.1: Comment: Dear authors, Thank you for the rebuttal. I find most of my concerns have already been addressed. I will keep the positive score. Best, --- Reply to Comment 1.1.1: Comment: Dear Reviewer ck5p, Thank you very much for your feedback and for keeping the score. We truly appreciate your support and encouragement. Your positive evaluation of our work means a great deal to us, and we are grateful for your time and thoughtful review. We look forward to any further suggestions you may have in the future. Best regards, Authors of the Paper 7442	Summary: This paper proposes integrating Knowledge Graph Embedding methods into Neural Theorem Provers to address challenges in optimization and efficiency. Claims And Evidence: The claims made in the paper are well-supported by evidence. Methods And Evaluation Criteria: The proposed methods and evaluation criteria are appropriate for the problem at hand. Theoretical Claims: The paper does not present theoretical claims that require verification. Its primary contribution lies in proposing a practical framework for integrating KGE methods with NTPs, rather than theoretical innovation. Therefore, this section is not applicable. Experimental Designs Or Analyses: The authors provided detailed descriptions of their experimental designs, including dataset selection, model implementation, and hyperparameter tuning. The results comprehensively demonstrate the performance differences among various methods. Supplementary Material: No supplementary material was provided for review. Relation To Broader Scientific Literature: The authors mention most related work. Essential References Not Discussed: No Other Strengths And Weaknesses: Strengths: 1. The paper proposes an innovative framework for integrating KGE methods with NTPs to address the optimization challenges of NTPs. 2. The experimental results demonstrate the effectiveness and applicability of the proposed methods across multiple datasets. Weaknesses: 1. The reasons for the accuracy drop in CTP3 and CTP4 on large-scale datasets were not thoroughly analyzed. 2. The relationship with emerging multi-modal knowledge graph reasoning methods was not fully discussed, potentially limiting the understanding of the paper's innovation and limitations. Other Comments Or Suggestions: 1. Conduct a thorough analysis of why different KGE methods perform variably in CTP3 and CTP4, and propose corresponding improvements. 2. Include a comparative analysis with multi-modal knowledge graph reasoning methods to further highlight the innovations and advantages of the proposed approach. Questions For Authors: 1. What are the main reasons for the significant performance differences of different KGE methods in CTP3 and CTP4? 2. How do you view the relationship between this paper's approach and multi-modal knowledge graph reasoning methods? Is there potential for further integration? Code Of Conduct: Affirmed. Overall Recommendation: 2	Rebuttal 1: Rebuttal: > *The reasons for the accuracy drop in CTP3 and CTP4 on large-scale datasets, and propose corresponding improvements* For CTP3, we recognize two issues that limits its performance particularly on large-scale dastasets, and propose two approaches to improve its performance. Recall for CTP3 we replace top-$k$ retrieval by using translational KGEs ($e.g.$ TransE) to directly compute the unknown entity, which means we are effectively doing top-1 retrieval. This results in two main drawbacks: 1. Limited expressiveness due to the top-1 retrieval. 2. Susceptible to spurious proof paths where subject and object are connected but logically irrelevant. For example, consider the path $(s, born\_in, o_1)$, $(o_1, located\_in, o_2)$, $(o_2, notable\_people, o)$, where $s$ and $o$ are connected but irrelevant. These issues become more obvious when the size and complexity of the dataset increase. To mitigate the above issues, we additionally propose two methods. Filtering spurious relation paths. We consider using the Path Constraint Resource Allocation (PCRA) for calculating the path reliability by measuring how much resource flows from the head to the tail entity following a path, as inspired by PTransE [1]. Formally, for a pair of $s$ and $o$ and a path $p = (r_1, r_2, \dots, r_n)$, the flow path can be written as $s \xrightarrow{r_1} S_1 \xrightarrow{r_2} \dots \xrightarrow{r_n} S_n$, where $S_i$ are sets of entities, and $o \in S_n$. Following the notation in PTransE, given any entity $m \in S_i$, the resource flowing to $m$ is defined as $$R_p(m) = \sum_{n \in S_{i-1}(\cdot, m)} \frac{1}{\|S_i(n, \cdot)\|}R_p(n),$$ where $S_{i-1}(\cdot,m)$ are its direct predecessors in $S_{i-1}$, and $S_i(n, \cdot)$ is the direct successors of $n \in S_{i-1}$. By calculating $R_p(m)$ recursively from $s$ to $o$, we can obtain the final resource (reliability) of the path $p$ given $s$ and $o$. For more details please refer to~\cite{ptranse}. During training, we then mask out the path with lowest 10\% reliability score (we do not modify for evaluation stage). Learnable entity expansion module. To alleviate the issue with top-1 retrieval, we consider adding an additional learnable module which expands the resulting entity embedding obtained from the translational KGE function to $k$ neighboring entities. In other words, we learn a linear layer $\mathbf{W}$ with shape $(d, k)$ to encode a set of related entities $\\{S\\}_k$ given the calculated entity $s$, $i.e.$ $p(\\{S\\}_k\|s, \mathbf{W})$. In the table below we show the results for incorporating PCRA and Entity Expansion (EE) module with $k=10$ for CTP3. We can observe noticeable improvements, especially on larger datasets such as FB122 and WN18RR. \|\|UMLS\|Kinship\|Nations\|FB122\|WN18RR\|Codex-s\| \|-\|-\|-\|-\|-\|-\|-\| \|MRR \|0.65\|0.5\|0.53\|0.53\|0.37\|0.35\| \|w/ PCRA\|0.66\|0.50\|0.54\|0.55\|0.39\|0.38\| \|w/ EE\|0.67\|0.52\|0.54\|0.60\|0.41\|0.42\| \|w/ both\|0.67\|0.52\|0.55\|0.63\|0.42\|0.44\| For CTP4 the performance drop on larger dataset is mainly because of lack of negative samples during CTP training. Since in CTP4 we utilize KGE to rank entities, we rely heavily on the quality of the conditional probability $p(s,r\|o)$ learned through the KGE function. This is discussed in Section A.5 and Table 11 of the appendix. We show that by increasing the number of negative samples, we can dramatically improve the performance of CTP4 to be close to CTP (<0.01 difference on HITS@10 on FB122) despite being 1000x faster during evaluation. [1] Modeling Relation Paths for Representation Learning of Knowledge Bases, ACL 2015 > *Conduct a thorough analysis of why different KGE methods perform variably in CTP3 and CTP4* We provide an explanation on why similarity-based KGE methods work better with NTPs than translational KGEs because of the better alignment in their score function. Due to space limit, please refer to the section named 2.why using similarity-based KGEs can achieve better performance in our reply to Reviewer Bi1c. Additionally, we provide a theoretical justification for the better performance of CTP2 over CTP1 under the Theoretical justification CTP1 vs. CTP2. section under our reply for Reviewer ck5p. > *Include a comparative analysis with multi-modal knowledge graph reasoning methods. How do you view the relationship between this paper's approach and multi-modal knowledge graph reasoning methods?* We would like to clarify that we mentioned multi-modal KG reasoning in the introduction because it is one of our main motivations to study NTP and is our on-going research, yet it is not the focus in this work. Therefore, we feel it might be less coherent to conduct analysis regarding multi-modal KG reasoning in this work. However, since our proposed integration (in particular, CTP2) is a plug-and-play approach without introducing new parameters or significantly modifying model architecture, we believe it should be agnostic to the original modality behind the embedding.	Summary: The paper proposes to integrate Knowledge Graph Embedding (KGE) methods with Neural Theorem Provers (NTPs) to enhance neuro-symbolic reasonings, and hence. The author proposes 4 ways to use KGEs and explain the methodology, the most intuitive variant seems to be use the kge at each proof step. Then the paper uses extensive experiments to show the performance of newly proposed methodology in different datasets, the ablation studies is also provided. Claims And Evidence: Generally speaking, the paper provides empirical results as evidence for their claims. Methods And Evaluation Criteria: Yes. Theoretical Claims: This paper has no proofs. Experimental Designs Or Analyses: I think it's valid. Supplementary Material: No. Relation To Broader Scientific Literature: The paper studies Neural Theorem Provers. Essential References Not Discussed: No. Other Strengths And Weaknesses: Strengths 1. The approach to integrate KGEs to improve the NTPs is novel and reasonable for advancing the capabilities of neuro-symbolic systems. The four variants of CTPs shows the paper also offers detailed analysis on how to utilize the KGEs. 2. The paper provides extensive experimental results that not only compare them against a variety of benchmarks but also includes ablation study and case-study for detailed discussion of the empirical results. Weaknesses 1. The paper is dense with technical details as one can observe the paper uses a lot of spaces to talk about existing research and methods, make it less accessible to readers not familiar with the specific fields of NTPs or KGEs. In contrast, the newly proposed CTP may require more room for further illustrations. 2. The improvement of the method seems to be marginal, as the CTP generally falls behind previous methods like NBF-net, though the paper has argued it has stronger efficiency. Other Comments Or Suggestions: I recommend adding more grounded examples for illustrations at the start of the paper instead of just Figure 1. Questions For Authors: Why NBFNet is not included in Table 5. Thanks author, I have read your response and changed my ratings corrspondingly. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: > *The paper is dense with technical details as one can observe the paper uses a lot of spaces to talk about existing research and methods, make it less accessible to readers not familiar with the specific fields of NTPs or KGEs. In contrast, the newly proposed CTP may require more room for further illustrations.* Thank you for your advice. We will incorporate more description on CTP and modify the introduction/method section to be easier to follow. > *The improvement of the method seems to be marginal, as the CTP generally falls behind previous methods like NBF-net, though the paper has argued it has stronger efficiency.* First, out of the seven Knowledge Graph Completion datasets tested, we are only slightly behind NBFNet for 2 of them (Kinship and WN18RR). While CTP2 lags behind NBFNet on Kinship for 0.09 MRR, we note that Kinship is a special case where CTP2 has little effect as the dataset has little multi-hop proof paths, yet for CTP2 we specifically add KGE priors along the proof path. In addition, we show that CTP2 clearly outperforms NBFNet and all the other baselines on Cluttr dataset (Table 4). Second, we show that by incorporating KGE priors, we can achieve consistent performance improvement across most if not all (excluding Kinship) datasets (CTP2), without introducing any new parameters and with negligible additional computational overhead. While the improvements of CTP2 over baseline CTP on small statistical learning datasets (e.g. Nations, UMLS) are less significant (since the baseline CTP’s accuracy on these datasets is already relatively high). The improvement becomes much more obvious on WN18RR and CodEx, with an improvement on MRR of 0.07 and 0.16, respectively. Lastly, NBFNet has been a SOTA KGC method, and many more recent KBC works’ performances also do not surpass it (e.g. DiffLogic, LERP). > *I recommend adding more grounded examples for illustrations at the start of the paper instead of just Figure 1.* Thank you for the suggestion! We will modify the manuscript to incorporate a grounded CTP inference illustration. > *Why NBFNet is not included in Table 5.* Thank you for the question. We initially tried to run NBFNet on FB122 with various hyperparameters but the accuracy was all low compared to its performance on other datasets and we were uncertain if we missed something, therefore we did not include it. Below we show results on FB122 with NBFNet included. Additionally, we rerun Table 5 with larger retrieval size ($k=128$). This was done on WN18RR and CodEx datasets (L648-653) but not FB122 because the baseline GNTP was run on FB122 with $k=10$, and we want to draw a fair comparison with it. Due to space limit, we are only showing the Test-ALL split of FB122. \|\|\| H@3 \| H@5 \| H@10 \| MRR \| \|-\|----------------------\|------\|------\|------\|------\| \|With Rules\|\|\|\|\|\| \|\| KALE-P \| 61.2 \| 66.4 \| 72.8 \| 0.52 \| \|\| KALE-J \| 70.7 \| 73.1 \| 75.2 \| 0.67 \| \|\| ASR-D \| 71.7 \| 73.6 \| 75.7 \| 0.67 \| \|\| KBLRN \| 74.0 \| 77.0 \| 79.7 \| 0.70 \| \|Without Rules\|\|\|\|\|\| \|\| TransE \| 58.9 \| 64.2 \| 70.2 \| 0.48 \| \|\| DistMult \| 67.4 \| 70.2 \| 72.9 \| 0.63 \| \|\| ComplEx \| 67.3 \| 69.5 \| 0.72 \| 0.64 \| \|\| GNTP \| 61.5 \| 63.2 \| 64.5 \| 0.61 \| \|\| CTP \| 69.1 \| 70.5 \| 71.2 \| 0.68 \| \|\| NBFNet \| 57.2 \| 59.6 \| 70.6 \| 0.51 \| \|\|\|\|\|\|\| \|\| CTP₁ \| 65.4 \| 64.3 \| 65.0 \| 0.62 \| \|\| CTP₂ \| 76.1 \| 76.4\| 78.3 \| 0.75 \| \|\| CTP₃ \| 59.4 \| 60.8 \| 62.2 \| 0.53 \| \|\| CTP₄ \| 65.7 \| 66.3 \| 69.6 \| 0.64 \| As we can see, CTP2 achieves the best accuracy overall. NBFNet's accuracy, however, is significantly lower. Due to time limit we are not able to further search for hyperparameters as it takes more than a day to train NBFNet on FB122 with a V100 GPU. However we will keep experimenting and will update in the followup reply if we find better accuracy with NBFNet. > *Replies to other reviewers* Here we would like to refer to some questions from other reviewers and our replies that could potentially be of your interest. Theoretical justification of why CTP2 is better. We provide a theoretical justification for the better performance of CTP2 over CTP1 under the Theoretical justification CTP1 vs. CTP2. section under our reply for Reviewer ck5p. Explanation on why similarity-based KGEs perform better than translational KGEs on NTPs. Please refer to the section named why using similarity-based KGEs can achieve better performance in our reply to Reviewer Bi1c. Explanation on why CTP3-4's accuracy drop sharply on large-scale dataset, and methods of improvement. Please see our reply to Reviewer H1qZ, section The reasons for the accuracy drop in CTP3 and CTP4 on large-scale datasets, and propose corresponding improvements.	Summary: This paper investigates the integration of Neural Theorem Provers (NTPs) and Knowledge Graph Embeddings (KGEs) to enhance soft unification and reasoning efficiency. The paper systematically explores four strategies for integrating KGEs into NTPs: CTP1: Uses KGE as an auxiliary loss to support NTP training. CTP2: Injects KGE-based similarity scores score function into NTPs as an auxiliary score. CTP3: Replaces the topk retrieval with a translation-based operation to improve inference efficiency. CTP4: Replaces the final step of NTP’s proof evaluation with KGE-based ranking to reduce computational overhead. The paper demonstrates that these integrations can substantially improve NTPs in both accuracy and computational efficiency. Additionally, the paper provides detailed ablation studies. This work is the first systematic study of KGE integration into NTPs. Claims And Evidence: The paper makes several key claims, including: 1. Leveraging the properties of KGEs can drastically improve the inference and evaluation efficiency of NTPs. The paper reports that CTP2 achieves higher accuracy than existing NTP-based methods on multiple datasets, including FB122, Nations, and UMLS. 2. CTP3 and CTP4 significantly improve computational efficiency. This claim is well supported by experiments. The paper provides empirical runtime comparisons, demonstrating substantial speed improvements. However, a formal complexity analysis is missing. 3. This is the first systematic study of integrating KGE into NTP. The paper “End-to-End Differentiable Proving” has proposed the method that integrates KGEs into NTPs, but this paper is the first systematic study for the integration of KGEs into NTPs. Methods And Evaluation Criteria: Methods: The proposed methods which integrate KGEs with NTPs through different distinct strategies (CTP1–CTP4)—are well-motivated by the limitations of NTPs, such as the poorly structured embedding space. The integration choices are reasonable, as they directly address these issues by leveraging KGE’s structured representation learning. However, a more formal theoretical justification for why CTP2 work better than others is missing. Evaluation Criteria: The evaluation is conducted on standard knowledge graph reasoning benchmarks, including FB122, WN18RR, Nations, UMLS, Kinship, CLUTRR. These datasets are appropriate choices for evaluating reasoning tasks. The paper evaluates performance using standard metrics: Mean Reciprocal Rank (MRR) and Hits@m, which are widely used for knowledge graph completion tasks. Theoretical Claims: The paper does not provide formal theoretical proofs regarding the correctness of the proposed methods. The paper relies on experimental evidence to support its claims. Experimental Designs Or Analyses: The experimental using multiple benchmark datasets and standard metrics, including comparisons with baselines, efficiency evaluation, visualization, hyperparameter analysis and effect of using different KGEs. The experimental design is generally sound, lacks theoretical analysis for performance differences. In addition, there appears to be an error in the bolding of values in Table 2. For the HITS@10 metric on UMLS, the best result should be CTP1 rather than CTP2. Supplementary Material: The supplementary materials include dataset information, experimental settings, training dynamics, visualization of learnt rules, training NTPs with more negatives, settings for inference speed comparison, pseudo-code implementation and conditional theorem prover. These supplementary materials make the details of the experiment clearer. Relation To Broader Scientific Literature: This paper is the first systematic study for the integration of KGEs into NTPs and propose four integration strategies, improving both performance and efficiency. Using KGE as auxiliary was originally proposed in “End-to-End Differentiable Proving”, but it was only briefly mentioned without any further exploration, and is not used in any subsequent NTPs. Compared with NTPs: NTP, GNTP, CTP, and link predictors: ComplEx, DistMult, NEURALLP, MINERVA, DIFFLOGIC, LERP and GNN NBFNET, the method proposed in this paper achieved better results in most cases. Essential References Not Discussed: To the best of my knowledge, the paper discusses the most relevant prior work, and I did not identify essential references that are missing. Other Strengths And Weaknesses: Strengths： 1. The paper is well-written and clearly structured, making the key contributions and technical details easy to follow. The motivation for integrating KGE with NTPs is well-explained. 2. The authors have conducted comprehensive experiments, including comparisons with baselines, efficiency evaluation, visualization, hyperparameter analysis and effect of using different KGEs. Weaknesses: 1. There is no theoretical analysis for performance differences. Specifically, the experimental results indicate that CTP2 achieves the best performance, but the paper does not explicitly discuss why CTP2 can achieve the best performance? Can it be theoretically explained? 2. The “Effect of using different KGEs” part of experimental results indicate that similarity-based KGEs, ComplEx DistMult generally yields the best performance, whereas translation-based KGE TransE and RotatE often lag back by a large margin. The paper lacks an explanation for this phenomenon. Would it be possible to further analyze why using similarity-based KGEs can achieve better performance? Other Comments Or Suggestions: 1. There appears to be an error in the bolding of values in Table 2. For the HITS@10 metric on UMLS, the best result should be CTP1 rather than CTP2. 2. The capitalization of model names such as ComplEx and RotatE is inconsistent in the paper. For example, "COMPLEX" and "ComplEx" are both used. Questions For Authors: Please see the weaknesses above. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: > *Complexity Analysis:* Below we provide complexity analysis for the baseline CTP and the proposed variants. We particularly focus on the final step at each proof path during evaluation, since it is the computational bottleneck in the NTP framework. Let $\|\mathcal{E}\|$ be the number of entities, $k$ be the number of top facts retrieved per $(s, r,t)$ pair, $d$ be the embedding dimension, $N$ be the number of proof path templates, $D$ be the depth of the recursive proof tree. Baseline CTP retrieves top-k facts for each combination of the missing entity and the known predicate-object/subject pair, followed by the unification score calculation between two tensors of shape $(\|\mathcal{E}\|, k, 3d)$. Retrieval: we use the IndexFlatL2 index from FAISS library, which has linear complexity $w.r.t.$ number of items. Since we are retrieving for each entity combination, the complexity of retrieval is $O(\|\mathcal{E}\|^2)$ for the final step at each proof path. Score calculation: we employ the Gaussian RBF kernel as the similarity metric between two embeddings. The RBF kernel is defined as \begin{equation}\text{RBF}(x_i, y_i) = \exp\big(-\frac{\|\|x_i-y_i\|\|^2}{2\sigma^2}\big),\end{equation} which has approximately linear complexity $w.r.t.$ number of entities $\|\mathcal{E}\|$ and dimension $d$, $i.e.$ $O(\|\mathcal{E}\| \cdot kd)$. Since this has to be done at each individual proof path, the complexity becomes $O(ND(\mathcal{\|E\|}^2 + \mathcal{\|E\|} \cdot kd))$. $\textbf{CTP}_1$ adds the KGE objective only as a loss term. Therefore the evaluation complexity is the same as baseline $\text{CTP}_1$, which is $O(ND(\mathcal{\|E\|}^2 + \mathcal{\|E\|} \cdot kd))$. $\textbf{CTP}_2$ adds the KGE scoring function on top of baseline CTP's existing similarity function (RBF kernel). However, as we find the additional KGE scoring function is only necessary during training and can be omitted during evaluation time, the evaluation complexity is the same as baseline $\text{CTP}_1$. $\textbf{CTP}_3$ replaces retrievals with translational KGEs to directly compute the next unknown tail entity. This reduces the retrieval complexity from quadratic to linear $w.r.t. \mathcal{\|E\|}$. Therefore the complexity becomes $O(ND(\mathcal{\|E\|} + \mathcal{\|E\|} \cdot kd))$. $\textbf{CTP}_4$ replaces the final ranking step from baseline CTP's retrieval & unification score calculation with direct ranking based on the KGE score. Assume a linear complexity for the KGE function $w.r.t.$ number of entities ($e.g.$ ComplEx), the overall complexity is further reduced to $O(ND(\mathcal{\|E\|})$. > *1.Theoretical analysis for why CTP2 is better* We provide a theoretical analysis from the gradient perspective comparing CTP2 to CTP1 (since they are similar to each other compared to CTP3-4). Due to space limit, we kindly ask the reviewer to refer to the section named Theoretical justification CTP1 vs. CTP2. in our reply to Reviewer ck5p. We are only able to show essential steps in the derivation here, but we will add the full derivation to our manuscript. > *2.why using similarity-based KGEs can achieve better performance* We conjecture the score function of similarity-based KGEs align better with the similarity metric (RBF Kernel) used in NTP, as compared to translational KGEs, which use the negative distance between original and translated entity embedding as the score. Specifically, similarity-based KGEs like ComplEx or DistMult generally use an inner product (or bilinear form) $\langle \cdot, \cdot \rangle$ to score triplets: $$s_{\text{sim}} (s,r,o) = \langle (s,r), o \rangle,$$ while translational-based KGEs (such as TransE) use the distance as metric $$s_{\text{transE}} = -\|\|s+r-o\|\|.$$ On the other hand, since RBF kernel is defined as $$\text{RBF}(x, y) = \exp\big(-\frac{\|\|x-y\|\|^2}{2\sigma^2}\big).$$ For simplification, assume the embeddings are normalized, we have $$\|\|x-y\|\|^2 \approx 2 - 2\langle x, y \rangle,$$ therefore $$\text{RBF}(x_i, y_i) = \exp\big(-\frac{1 - \langle x , y \rangle}{\sigma^2}\big).$$ This means RBF kernel is essentially a monotonic function of the inner product $\langle x, y \rangle$, and therefore the gradient of the similarity-based KGE score is directly tied to inner product-based KGEs ($e.g.$ ComplEx and DistMult). In experiments, we also observe faster convergence and higher accuracy when using ComplEx and DistMult. > *Other Comments: bolding and capitalization errors* Thank you for pointing them out! We will correct them in our final manuscript. --- Rebuttal Comment 1.1: Comment: Thanks for solving my concerns, and I will keep my original score. --- Reply to Comment 1.1.1: Comment: Dear Reviewer Bi1c, Thank you very much for your feedback and for keeping the score. We truly appreciate your support and encouragement. Your positive evaluation of our work means a great deal to us, and we are grateful for your time and thoughtful review. We look forward to any further suggestions you may have in the future. Best regards, Authors of the Paper 7442	null	null	null	null	null	null
VIP: Vision Instructed Pre-training for Robotic Manipulation	Accept (poster)	Summary: The authors propose a pretraining strategy for robotic manipulation in which all inputs are visual, with no language descriptions required. 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: Good Essential References Not Discussed: No Other Strengths And Weaknesses: The paper is well-written, which is easy to follow. The real-world experiments are interesting, which include dual-arm setting. However, my main concern lies in the motivation of this work, as described in the introduction, which highlights the drawbacks of language descriptions and emphasizes the importance of visual observations: 1. The paper uses RoboFlamingo to argue that language-guided policy models struggle to follow instructions due to data scarcity. However, I do not find this example convincing, as RoboFlamingo is not pretrained on a large-scale robotic dataset paired with language descriptions. Other works, such as OpenVLA[1] and PI0[2], pretrain models on large-scale robotic demonstrations with language descriptions, enabling instruction following—at least in simple cases like the 'green block' example provided by the authors. While I partially agree with the claim made in the second paragraph of the introduction, I do not believe that RoboFlamingo and the 'green block' example are appropriate choices to support this argument. 2. In the third paragraph of the introduction, the authors claim that visual prompts provide a more comprehensive representation for the model, leading them to use only visual information for pretraining, supported solely by a human intuition example. While I acknowledge that visual prompts have advantages over language prompts, their advantage should not be described as 'comprehensive to the model.' A visual model may be more comprehensive for a vision-motor policy, but this does not necessarily hold for a vision-language-action model. Moreover, the intuition-based example does not sufficiently support the authors' argument. A citation to prior research would be more convincing. 3. If the claim that visual prompts provide a more comprehensive representation for the model is true, then how did the authors crop the image region of the object for manipulation during fine-tuning and inference without language guidance? If language is still used to guide the cropping process, then the claim that visual prompts alone are sufficient is inconsistent. The motivation should align with the expectation that the model fully leverages visual observations without relying on language descriptions. [1] Kim, Moo Jin, et al. "Openvla: An open-source vision-language-action model." arXiv preprint arXiv:2406.09246 (2024). [2] Black, Kevin, et al. "$\pi_0 $: A Vision-Language-Action Flow Model for General Robot Control." arXiv preprint arXiv:2410.24164 (2024). Other Comments Or Suggestions: Additional baselines focusing on pretraining models for robotic tasks should be considered, such as R3M[3], VC-1[4] and others. [3] Nair, Suraj, et al. "R3m: A universal visual representation for robot manipulation." arXiv preprint arXiv:2203.12601 (2022). [4] Majumdar, Arjun, et al. "Where are we in the search for an artificial visual cortex for embodied intelligence?." Advances in Neural Information Processing Systems 36 (2023): 655-677. Questions For Authors: Refer to weakness section Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We believe the Reviewer has significant misunderstandings of this work. In the following, we address the concerns one by one using more precise explanations and sufficient experiments. The paper will be revised accordingly to avoid these misunderstandings. ## Q1: Insufficient support for vision instruction We believe we do not mention RoboFlamingo in the paper. What we claim is in the current manipulation data status (very expensive to collect), vision instruction is more efficient for disclosing task information. We agree models like OpenVLA and PI0 can pick up the shown green box given text instruction We do not claim that text instruction cannot specify target. What we highlight is the efficiency difference between text and vision instructions. Robot manipulation data is expensive, and models like OpenVLA have used up most public data resources (Open X-Embodiment dataset covers most popular manipulation datasets). However, we find that OpenVLA overfits to specific text representation. For example, when we use the instruction ''grasp the cup", it works well. However, when we use ''pick up the cup'', the policy fails. This means even though we combine almost all public manipulation datasets, the data is still insufficient to cover common text instructions. By contrast, the shown generaliazation performance of our method is much better. To further support our claim, we compare the performances of the models pre-trained by OpenVLA, PI0, and our VIP. As the zero-shot manipulation results of OpenVLA and PI0 are limited, we tune them with the same data as our policy for fair comparison. Specifically, We use the pre-trained feature extractors to extract feature, and employ three Transformer decoders to decode the extracted feature as actions to execute. Each pre-trained policy is test in two settings, freeze or not freeze the feature extractor during tuning. Text instructions are provided to VLA-based policies. The success rates are as follows: Method \| Freeze \| Pour Blueberries \| Open Lid \| CLean Table \| Move Box \| Transport Box \| Stack Boxes \| \| :-: \| :-: \| :-: \| :-: \| :-: \| :-: \| :-: \| :-: \| PI0 \| Yes \| 0.07 \| 0.48 \| 0.14 \| 0.82 \| 0.44 \| 0.29 \| PI0 \| No \| 0.28 \| 0.60 \| 0.31 \| 0.84 \| 0.58 \| 0.55 \| OpenVLA \| Yes \| 0.14 \| 0.45 \| 0.19 \| 0.81 \| 0.45 \| 0.36 \| OpenVLA \| No \| 0.30 \| 0.67 \| 0.32 \| 0.88 \| 0.66 \| 0.60 \| VIP (Ours) \| Yes \| 0.32 \| 0.63 \| 0.34 \| 0.88 \| 0.69 \| 0.61 \| VIP (Ours) \| No \| 0.42 \| 0.71 \| 0.37 \| 0.92 \| 0.74 \| 0.68 \| According to the results, although PI0 and OpenVLA use much more pre-train data than VIP, VIP achieves better performance. This result supports our claim that vision instruction is more efficient than text instruction. The ablation study in Table 2 of the paper also supports this claim. In summary, our method achieves superior or at least similar performance as OpenVLA and PI0 based on much less data, which favors addressing the expensive data collection cost in robot manipulation. ## Q2: Vision instruction is more comprehensible In this work, "more comprehensible" means the policy can learn to follow instructions based on less training data. As reminded by the Reviewer, we will replace "comprehensible" as "easy to follow". We understand the concern of the Reviewer is VLA may can understand text instruction easily as it has been pre-trained using numerous image-text pairs. Actually, we have tried many VLAs during developing this work. The observation is large-scale image-text pre-train favors understanding text instruction in robot manipulation, but the required manipulation data volume required by text instruction is still significantly larger than vision instruction to learn to complete a task. This is due to the gaps between common image-text data and manipulation data. Image-text-action data is precious and far from being sufficient to train the policy to follow general text instruction following. The experiment results in the Reply to Q1 supports this observation. ## Q3: How the cropped region is obtained In test, we give a text instruction, and the text instruction is converted as vision instruction (cropped region) based on a 2D object detector. We do not claim we should not use text instruction. It is more convenient for human to give instructions based on text than taking a photo. What we claim is vision instruction is more efficient to serve as the direct input to the policy. Therefore, we convert the text instruction from human as vision instruction and input the vision instruction to the policy. The experiment results in Table 2 of the paper indicates this design leads to much better performance than inputting text instruction to the policy. ## Q4: Comparison with more pre-training methods As suggested by the Reviewer, we conduct more comparison with the recommended pre-train methods. Besides the results in the Reply to Q1, find more comparison results in the anonymous link: [Exp Result](https://anonymous.4open.science/r/VIP_rebuttal-9331/README.md). --- Rebuttal Comment 1.1: Comment: In the first question, in the first paragraph, I was misled by an incorrect citation. Upon further checking, the reference that the paper cited was actually Visual Instruction Tuning, not RoboFlamingo, though the point I intended to make remains the same. However, the authors’ response effectively addressed my concern, so I’m willing to improve the score to Weak Accept.	Summary: In this work, based on the observation that current policies cannot capture features from text instruction effectively, due to data scale, the authors propose a model named VIP which utilizes vision instructions to specify manipulation targets as an alternative. Specifically, the input of VIP is the current observation, future observation, and a corresponding sparse point flows between the current and future images. Since sparse point flows and future images are not available during inference time, they are progressively randomly masked during pre-training and future images are replaced with the cropped region of the object to manipulation in the current observation. The effectiveness of VIP is demonstrated with three tasks in the real world and three tasks in simulation(IsaacGym). Claims And Evidence: - This work claims that text-instructed policies cannot successfully capture the feature of manipulation targets because of the lack of sufficient manipulation data and image-text pairs. Figure 1, which displays the attention map of a text-instructed policy in a pick-and-place scenario, evidences this claim. - The effectiveness of vision instructions is supported by the policy attention map in Figure 1 and the strong performance in both real and simulated environments. Methods And Evaluation Criteria: The proposed vision-instructed pre-training method makes sense for the manipulation tasks. The evaluations involving both tasks in the real world and the simulation are comprehensive, and the evaluation criteria are the success rates of each task. Theoretical Claims: This work is mainly an ML application in robotic manipulation tasks, so there is no need to provide theoretical proofs. Experimental Designs Or Analyses: It is promising that VIRT has achieved all state-of-the-art performance in the tasks given in the paper. However, those tasks involved are still very simple, pick-and-place tasks in a clean background, which cannot genuinely demonstrate the advantages of vision instructions over text instructions as proposed in the paper. It would be better if you could add more distractions such as more positional randomness of your manipulation targets, and more complex tasks, such as articulated object manipulation tasks, to your evaluation suite. The robustness to simple image transforms is not persuasive enough of its generalization capabilities and the effectiveness of the vision prompts. Supplementary Material: I have watched the videos of evaluation tasks in the supplementary materials. Relation To Broader Scientific Literature: Current pre-training methods in robotics manipulation mainly apply text as the prompt, while using vision instructions is less explored. Essential References Not Discussed: Some works which pre-train on human demonstration datasets and are fine-tuned for robotic manipulation are not discussed in this work. These works involve but are not limited to: [1] Ilija Radosavovic, Tete Xiao, Stephen James, Pieter Abbeel, Jitendra Malik, and Trevor Darrell. Real-world robot learning with masked visual pre-training. In CoRL, 2022. [2] Suraj Nair, Aravind Rajeswaran, Vikash Kumar, Chelsea Finn, and Abhinav Gupta. R3M: A universal visual representation for robot manipulation. In CoRL, 2022. [3] Jia Zeng, Qingwen Bu, Bangjun Wang, Wenke Xia, Li Chen, Hao Dong, Haoming Song, Dong Wang, Di Hu, Ping Luo, Heming Cui, Bin Zhao, Xuelong Li, Yu Qiao, Hongyang Li. Learning Manipulation by Predicting Interaction. In RSS, 2024. [4] Arjun Majumdar, Karmesh Yadav, Sergio Arnaud, Yecheng Jason Ma, Claire Chen, Sneha Silwal, Aryan Jain, Vincent-Pierre Berges, Pieter Abbeel, Jitendra Malik, Dhruv Batra, Yixin Lin, Oleksandr Maksymets, Aravind Rajeswaran, Franziska Meier. Where are we in the search for an Artificial Visual Cortex for Embodied Intelligence? In arXiv, 2023. Besides, there are also some works supporting utilizing both vision and text instructions, such as: [5] Dibya Ghosh, Homer Walke, Karl Pertsch, Kevin Black, Oier Mees, Sudeep Dasari, Joey Hejna, Tobias Kreiman, Charles Xu, Jianlan Luo, You Liang Tan, Lawrence Yunliang Chen, Pannag Sanketi, Quan Vuong, Ted Xiao, Dorsa Sadigh, Chelsea Finn, Sergey Levine. Octo: An Open-Source Generalist Robot Policy. In RSS. 2024. are not discussed in this work. Other Strengths And Weaknesses: The clarity of this work is great. Other Comments Or Suggestions: It would be better if Table 1 could provide the parameter numbers of each method for direct comparison. Questions For Authors: Can VIRT also generalize to moving manipulation target scenarios? Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: We have addressed the concerns of the Reviewer one by one in the following. The paper will be revised accordingly. ## Q1: Experiments with more distraction. As suggested by the Reviewer, we have added experiments with stronger distraction in both simulated and real robot environments. For simulation, we select a set of challenging tasks in RLbench, and these tasks require challenging actions like insert, open, and screw. We compare our method with previous SOTAs using the same training data and testing protocol. The results are reported as follows: Method \| Insert Peg \| Open Drawer \| Place Cups \| Put in Cupboard \| Screw Bulb \| Stack Cups \| \| :-: \| :-: \| :-: \| :-: \| :-: \| :-: \| :-: \| ConvMLP \| 0.00 \| 0.04 \| 0.00 \| 0.00 \| 0.00 \| 0.00 \| PolarNet \| 0.04 \| 0.84 \| 0.00 \| 0.12 \| 0.44 \| 0.08 \| PerACT \| 0.06 \| 0.88 \| 0.02 \| 0.28 \| 0.18 \| 0.02 \| ACT3D \| 0.27 \| 0.93 \| 0.03 \| 0.51 \| 0.47 \| 0.09 \| RVT \| 0.11 \| 0.71 \| 0.04 \| 0.50 \| 0.48 \| 0.26 \| RVT-2 \| 0.40 \| 0.74 \| 0.38 \| 0.66 \| 0.88 \| 0.69 \| VIRT (Ours) \| 0.48 \| 0.79 \| 0.42 \| 0.68 \| 0.90 \| 0.73 \| We can see that our method outperforms all previous methods. In addition, we devise two new real robot tasks to verify the performance of our method. In both tasks, there are multiple targets randomly placed on a table. In the spoon deliver task, the robot hand needs to pick and deliver randomly placed spoons to a tray. This task is more challenging because spoons are smaller and the robot must learns to grasp the necks of the spoons in diverse poses. In the wire deliver task, the manipulation target is non-rigid and presents non-regular shapes. The policy must delivers all seen objects to achieve one successful trial. The success rates of different methods on these two new tasks are as follows: Method \| CNNMLP \| Diffusion \| ACT \| VIRT (Ours) \| \| :-: \| :-: \| :-: \| :-: \| :-: \| Spoon Deliver \| 0.00 \| 0.06 \| 0.14 \| 0.42 \| Wire Deliver \| 0.00 \| 0.00 \| 0.07 \| 0.39 \| We can find that VIRT outperforms other methods more significantly on these more complex tasks. Moreover, we present anonymous video links of our method on these two tasks here: [Spoon Deliver](https://drive.google.com/file/d/1sEOaJ9PwOs8aV7beUxLOJdWNAVCEzFXL/view?usp=sharing) and [Wire Deliver](https://drive.google.com/file/d/111Jbot6Skb1uRL7u-a40oGxNglf4OYLo/view?usp=sharing). ## Q2: Method for Moving Object Manipulation. Yes, our method supports moving object manipulation due to its fast response speed and precise manipulation operation. We design a new task that the robot needs to pick the moving spoons on a moving belt and delivers them to a box. This task is challenging because (1) The spoons are small and in diverse poses. The robot hand must grasps the necks of spoons for successful picking up. (2) The spoons are moving, which means the policy must learns to predict the positions of spoons at the grasp moment rather than the current moment. The success rate of VIRT arrives 0.82, while all the other test methods fail. This result attributes to two advantages of our VIRT: (1) VIRT shows very fast response speed. (2) The vision instruction helps VIRT focus on the moving spoons and better predict the future positions of these spoons. We present an anonymous video link of our method on this new task here: [Move Manipulation](https://drive.google.com/file/d/111juTCA0EHkfemDUYPoUj0xdHg2Y6ldC/view?usp=sharing). To the best of our knowledge, this is the first end-to-end imitation policy that can perform moving object manipulation. ## Q3: More discussion with relevant works. We thank the Reviewer for this reminder. As suggested by the Reviewer, we will add all the references mentioned by the Reviewer and discuss the relevance of our work with them in the paper. The papers mentioned by the Reviewer are mostly about using video data cheaper than robot manipulation data (like human ego-centric videos and web videos) to conduct pre-train. The advantage of these works is the data is easy to obtain, but their effectiveness is limited due to embodiment gaps. Differently, what we study is another setting: how to use robot manipulation data to conduct pre-train, where the data is more expensive to collect but provides more direct generalization. Notably, these two settings of pre-train do not conflict with each other. We can first pre-train a policy using cheap web data and then fine-tune the policy based on the robot manipulation data based on our proposed method. ## Q4: Parameter number. As suggested by the Reviewer, we will report the parameter numbers of these methods in the paper. For the convenience of review, we also list them as follows: Method \| CNNMLP \| Diffusion \| ACT \| VIRT (Ours) \| \| :-: \| :-: \| :-: \| :-: \| :-: \| Parameter Number \| 76.7M \| 142.8M \| 115.0M \| 38.6M \| According to the results, we can find that VIRT is the most lightweight model. This is mainly because VIRT adopts a very concise architecture consisting of only Transformer encoders and decoders. --- Rebuttal Comment 1.1: Comment: The authors' additional experiment results addressed my concerns about the method's capabilities of positional generalization and moving object manipulation. However, real-world experiments are still conducted in a clean and static environment without many distractions. So, I will accordingly increase my score to Accept.	Summary: This paper introduces a novel pretrained method designed for general robotic manipulation tasks. The authors argue that text-instructed policies often fail to effectively focus on target objects, and therefore, they propose integrating more interpretable features for pretraining visual-based policies. These features include sparse point flow and future visual observations, which enhance the model's ability to comprehend and predict environmental dynamics. To validate their approach, the authors have developed a series of tasks conducted in both real-world and simulated environments. These tasks are designed to rigorously evaluate the performance and robustness of the proposed method under various conditions. Claims And Evidence: The main claim regarding the drawback of text-instructed policies—that they may misinterpret the attention focus on the target object—is not sufficiently substantiated. While the authors provide a visualization in Figure 1 to compare text- and vision-instructed policies, two critical issues undermine the credibility of this comparison. First, the specifics of the text-instructed policy used for the visualization are not detailed, which raises questions about the validity and reproducibility of the results. Without transparency regarding the implementation and parameters of the text-instructed policy, it is difficult to assess the fairness of the comparison. Second, the claim appears to overlook the significant success and widespread adoption of text-instructed pretraining methods in the field. Text-instructed policies have demonstrated remarkable achievements across various pretraining tasks, making the assertion that they are inherently flawed seem overly subjective and potentially biased. Methods And Evaluation Criteria: Yes, integrating point cloud flows and future images into the pretraining framework could lead to more robust and generalizable policies. Theoretical Claims: This paper contains no theoretical claims. Experimental Designs Or Analyses: The soundness of the proposed method is not fully established. While the paper introduces a novel pretraining paradigm and, in Section 4, conducts experiments to validate the importance of individual components and the overall improvements for downstream tasks, it lacks a crucial comparison with other existing pretraining methods. This omission leads to the confusion about how the proposed method performs relative to previous pretraining methods. Without such comparisons, it is difficult to determine whether the claimed advancements are truly superior to state-of-the-art alternatives. Supplementary Material: The videos contain in the supplementary materials reveal the effectiveness of the proposed method. Relation To Broader Scientific Literature: The authors propose a novel pretraining method for robotic manipulation tasks. Unlike previous text-driven pretraining methods such as R3M and CLIP, this work shifts the focus to a vision-based paradigm. Text-driven methods typically align given prompts with current visual observations to generate conditional features for downstream policies. The authors identify potential limitations in text-instructed policies, like misinterpretations or illusions in aligning textual instructions with visual contexts. To address this, they design a novel vision-based pretraining framework. A key contribution of the proposed method lies in its explicit use of future images and point cloud flows, which clearly indicate the intended direction of target actions. By focusing on visual cues rather than relying on potentially ambiguous textual instructions, the proposed method could be able to overcome some of the inherent limitations of text-driven approaches. Essential References Not Discussed: This paper introduces a novel pretraining paradigm; however, it overlooks one of the most widely recognized and influential pretraining methods in the field, like R3M, which was published at CoRL 2022. Other Strengths And Weaknesses: Strength: 1.The integration of additional visual features, such as future images and point flows, for pretraining a robust feature representation network is a notable strength. This approach enhances the performance of downstream action policies without relying on text embedding networks like CLIP, offering a more direct guidance for robotic manipulation tasks. 2.The authors conduct experiments in both real-world and simulated environments, which helps verify the practical effectiveness and versatility of the proposed method. Weaknesses: 1.The claim regarding the drawbacks of text-instructed policies is not well-supported. Text-driven pretraining paradigms, such as R3M, are widely adopted in the field and have demonstrated strong generalizability in robotics. The lack of a fair comparison or evidence to substantiate this claim undermines its validity. 2.A significant limitation is the absence of experiments comparing the proposed method with other established pretraining approaches, such as CLIP-based or R3M-based methods. This omission weakens the confidence in the superiority or even the competitiveness of the proposed method against existing alternatives. 3.The presentation of the algorithm's details is insufficient. While the paper mentions the integration of images and point flows during training, it fails to provide a clear explanation of how these features are processed or combined, leaving critical implementation aspects unclear. 4.Although the authors propose a general pretraining method, they do not evaluate it on widely used benchmarks like RLBench or Robomimic. Such evaluations are essential to demonstrate the generalizability and robustness of the proposed method across diverse tasks and environments, which is a key expectation for a general pretraining framework. Other Comments Or Suggestions: 1. Why not incorporate masks directly into the pretraining stage? Utilizing masks during pretraining could enhance consistency between the pretraining and inference phases. If the mask image is validated to be effective, it seems like the current pretraining process can also rely on it instead of future images. 2. Is the pretraining model directly employed in the simulation environment? If so, the ability of the pretrained model should be avaluated in other imitation learning benchmark like RLBench or Robomimic. Questions For Authors: Please refer to the comments_suggestions and the strenghs_weaknesses sections. Code Of Conduct: Affirmed. Overall Recommendation: 2	Rebuttal 1: Rebuttal: We have addressed the concerns of the Reviewer one by one in the following. The paper will be revised accordingly. ## Q1: Visualization details of the teaser figure. In the teaser figure, we visualize the attention map between the action query $q_T$ at the last timestamp $T$ and image feature tokens $F$ in the last decoder. We use $q_T$ as query and $F$ as key to compute the attention map $A$. Then, we take the mean of $A$ across all channels and resize the obtained feature to the same shape of the input image. Finally, we visualize the feature and get the teaser figure. For fair comparison, the text and vision instructed policies adopt the same network except the input instructions are different. The policy parameter number is 38.6M. ## Q2: The success of previous text-instructed methods. * The mentioned pre-train methods like R3M are based on natural videos (like human hand operation videos). Although these models provide promising initialization weight for robot applications, their effectiveness is limited due to embodiment and task gaps. Differently, what we study is another setting: how to use robot manipulation data to conduct pre-train, where the data is more expensive to collect but provides more direct generalization. * There are text-instructed VLAs based on robot manipulation data, like OpenVLA. However, we find these methods overfit to specific text instructions. For example, OpenVLA behaves well given ''grasp the cup'' but fails given ``pick up the cup''. This is because manipulation data is expensive to collect and not diverse enough to cover common text instructions, although the works like OpenVLA have used up most public data resources. * We have added comparison experiments with previous pre-train methods. For fair comparison, we integrate their pre-trained backbone into VIRT in the same way as our VIP pre-trained backbone. If the pre-train method relies on text instruction, we provide the policy with text instruction during fine-tune and test. We report comparison results using all the simulated and real-robot tasks as follows: Method \| Pour Blueberries \| Open Lid \| Clean Table \| Move Box \| Transport Box \| Stack Boxes \| \| :-: \| :-: \| :-: \| :-: \| :-: \| :-: \| :-: \| R3M \| 0.26 \| 0.62 \| 0.25 \| 0.83 \| 0.68 \| 0.51 \| OpenVLA \| 0.30 \| 0.67 \| 0.35 \| 0.88 \| 0.66 \| 0.60 \| E-RADIO \| 0.34 \| 0.68 \| 0.32 \| 0.84 \| 0.69 \| 0.62 \| Theia-B \| 0.38 \| 0.65 \| 0.36 \| 0.85 \| 0.65 \| 0.64 \| VIP (Ours) \| 0.42 \| 0.71 \| 0.37 \| 0.92 \| 0.74 \| 0.68 \| According to the results, we can find that although the compared methods generally use more pre-train data than ours, our proposed method achieves better performance. ## Q3: Comparison with other pre-train methods. As suggested by the Reviewer, we have conducted more comparison between our pre-train method and other pre-train methods. Due to character limit, the results are reported in the above Table in the Reply to Q2. The results suggest that our pre-train method achieves the best performance on all tasks, which further reveals the superiority of our method. ## Q4: Comparison on public benchmarks. As suggested by the Reviewer, we compare our method with previous SOTAs using the ManiSkill-v3 and RLBench benchmarks. The training data and testing protocols are the same between VIRT and the compared methods. Refer to the reply to Q2 of Reviewer uDoz for more experiment details. The results on ManiSkill-v3 are as follows: Method \| Push Cube \| Pick Cube \| Stack Cube \| Draw Triangle \| \| :-: \| :-: \| :-: \| :-: \| :-: \| ConvMLP \| 0.32 \| 0.56 \| 0.00 \| 0.02 Diffusion \| 0.75 \| 0.81 \| 0.06 \| 0.55 ACT \| 0.84 \| 0.89 \| 0.20 \| 0.68 \| VIRT (Ours) \| 0.94 \| 0.96 \| 0.48 \| 0.80 \| For RLBench, we use the training data of PerACT and follow its testing protocol. The results on RLBench are as follows: Method \| Insert Peg \| Open Drawer \| Place Cups \| Put in Cupboard \| Screw Bulb \| Stack Cups \| \| :-: \| :-: \| :-: \| :-: \| :-: \| :-: \| :-: \| ConvMLP \| 0.00 \| 0.04 \| 0.00 \| 0.00 \| 0.00 \| 0.00 \| PolarNet \| 0.04 \| 0.84 \| 0.00 \| 0.12 \| 0.44 \| 0.08 \| PerACT \| 0.06 \| 0.88 \| 0.02 \| 0.28 \| 0.18 \| 0.02 \| ACT3D \| 0.27 \| 0.93 \| 0.03 \| 0.51 \| 0.47 \| 0.09 \| RVT \| 0.11 \| 0.71 \| 0.04 \| 0.50 \| 0.48 \| 0.26 \| RVT-2 \| 0.40 \| 0.74 \| 0.38 \| 0.66 \| 0.88 \| 0.69 \| VIRT (Ours) \| 0.48 \| 0.79 \| 0.42 \| 0.68 \| 0.90 \| 0.73 \| The results on the ManiSkill and RLBench benchmarks show VIRT achieves the best results, which further confirm the superiority of our method. ## Q5: How image and point flow are integrated. As shown in the pipeline of the paper, the images and points are encoded as tokens separately. Then, we directly concatenate them as the feature input to Transformer decoders. We will release our code publicly to help other researchers reproduce our work. ## Q6: Image random mask in pre-train. The image random mask improves the robustness of the pre-train policy but cannot directly enable the policy to learn useful representation. Therefore, the future action prediction task is necessary in pre-train.	Summary: This paper proposes VIP, a framework that uses visual signals as guidance for visual pre-training in robotic tasks. Instead of using language as the instruction (which is ambiguous), this work proposes using vision-instructed policy as an alternative. The vision-instructed policy uses visual cues to instruct the policy on what to do and where to pay attention, which helps policy learning. During training, the visual signals (sparse points) are masked and annealed gradually, which helps policy training by making the sparse points unnecessary at inference time. Experiments show that the policy is able to boost performance in both simulated and real-world robots. Claims And Evidence: This paper claims that using vision-instructed pre-training provides a performance boost to downstream tasks and proposes using target image + sparse key point as an effective pre-training strategy for simulated and robotic bi-manual manipulation tasks. The evidence in performance boosts backs up these claims. Methods And Evaluation Criteria: Three real-world and simulated robotic tasks are used to evaluate the proposed method. These tasks are household tasks that can evaluate the performance of the visual policy. There is a missing opportunity in evaluating in standard robotic benchmarks such as ManiSkill or RobotSuite. Theoretical Claims: No theoretical claims made. Experimental Designs Or Analyses: The experiment design and analysis are adequate to back up the claims. I appreciate the extensive ablations to show each component of the proposed method. Based on the success rate, it is clear that the proposed pre-training method is effective in boosting the performance of the policy. Supplementary Material: Supplementary videos show the performance of the real-world and simulated robot performance. Relation To Broader Scientific Literature: This work tackles the important question of how to use large-scale pre-training data for training visual encoders for robotic tasks. Due to the embodiment difference, it is important to train visual feature extractors that can extract useful information from the existing datasets. Essential References Not Discussed: Reference is adequately discussed. Other Strengths And Weaknesses: ### Strength - I find the idea of using visual signals and sparse key points as guidance an intuitive and useful idea for visual pretraining. Figure 1 shows the benefit of using vision-instructed policy well. The sparse point flow is an interesting idea to explore as a different modality to instruct policy learning. - Extensive ablations show that the combination of vision instruction and sparse keypoints achieves the best performance. - SOTA results achieved compared to baselines. - Robustness analysis shows that the policy learned with pre-training is robust to visual noises. ### Weakness - Most of the ablations are conducted in simulation but not in the real world. Real-world experiments can lead to different results than simulation. Other Comments Or Suggestions: I suggest testing the proposed method on standard benchmarks to better compare it with SOTA methods. Questions For Authors: None Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: We have addressed the concerns of the Reviewer one by one in the following. The paper will be revised accordingly. ## Q1: Ablation study in real-world experiments. In the paper, we conduct ablation study mainly in simulation as the environment is easy to control, which benefits to ensuring fair comparison. Our experience shows that the experimental results between our built simulation environment and real robot are consistent. As suggested by the Reviewer, we also conduct ablation study using the real robot and report the success rates on all the three our designed real-robot tasks. These three tasks evaluate the performance of robot manipulation policies from different perspectives. The real-robot experiment results corresponding to Table 2 of the paper are as follows. We can see that the improvments of our proposed designs are more significant in the real-robot experiments. Pre-train \| Inference \| Pour Blueberries \| Open Lid \| Clean Table \| \| :-: \| :-: \| :-: \| :-: \| :-: \| F \| Cropped \| 0.37 \| 0.63 \| 0.30 \| S \| Cropped \| 0.00 \| 0.02 \| 0.00 \| F+S \| Text \| 0.37 \| 0.63 \| 0.14 \| F+S \| Future \| 0.30 \| 0.57 \| 0.06 \| F+S \| Cropped \| 0.42 \| 0.71 \| 0.37 \| The real-robot experiment results corresponding to Table 3 of the paper are as follows: DINO \| Uncern \| Mask \| Pour Blueberries \| Open Lid \| Clean Table \| \| :-: \| :-: \| :-: \| :-: \| :-: \| :-: \| No \| No \| No \| 0.29 \| 0.56 \| 0.26 \| Yes \| No \| No \| 0.33 \| 0.63 \| 0.31 \| Yes \| Yes \| No \| 0.39 \| 0.65 \| 0.34 \| Yes \| Yes \| Yes \| 0.42 \| 0.71 \| 0.37 \| According to the reported results, all the designs in our proposed method are also effective on the real robot. ## Q2: Experiment on public simulator benchmarks. In the paper, we conduct experiments based on our own built simulation environment rather than previous public benchmarks because these public benchmarks usually generate demonstration data by rule-based motion control. Their generated data has a distribution gap with the real robot data collected based on teleoperation. Differently, our used training data in our own built simulation tasks is also obtained from teleoperation, so the experimental results are more convinicing. As suggested by the Reviewer, we compare our method with previous SOTAs using the ManiSkill-v3 and RLBench benchmarks. We select them because they provide unified training data generation protocol, which ensures fair comparison. The training data and testing protocols are the same between VIRT and the compared methods. The tasks in ManiSkill-v3 cover navigation, humanoid robot, manipulation, etc. We select the manipulation tasks in ManiSkill-v3 to conduct experiments. As mentioned before, the training data is generated based on classic motion control. The results on ManiSkill-v3 are as follows: Method \| Push Cube \| Pick Cube \| Stack Cube \| Draw Triangle \| \| :-: \| :-: \| :-: \| :-: \| :-: \| ConvMLP \| 0.32 \| 0.56 \| 0.00 \| 0.02 Diffusion \| 0.75 \| 0.81 \| 0.06 \| 0.55 ACT \| 0.84 \| 0.89 \| 0.20 \| 0.68 \| VIRT (Ours) \| 0.94 \| 0.96 \| 0.48 \| 0.80 \| For RLBench, although there are totally 100 tasks, many tasks are easy and previous methods have achieved very high success rates. Due to the reply character limit, we select six challenging and representative tasks that the success rate of the best method is still below 90%. We compare our method with the other methods that have reported their results in RLbench. We use the training data of PerACT and follow its testing protocol (the other compared methods also adopt this protocol). The results on RLBench are as follows: Method \| Insert Peg \| Open Drawer \| Place Cups \| Put in Cupboard \| Screw Bulb \| Stack Cups \| \| :-: \| :-: \| :-: \| :-: \| :-: \| :-: \| :-: \| ConvMLP \| 0.00 \| 0.04 \| 0.00 \| 0.00 \| 0.00 \| 0.00 \| PolarNet \| 0.04 \| 0.84 \| 0.00 \| 0.12 \| 0.44 \| 0.08 \| PerACT \| 0.06 \| 0.88 \| 0.02 \| 0.28 \| 0.18 \| 0.02 \| ACT3D \| 0.27 \| 0.93 \| 0.03 \| 0.51 \| 0.47 \| 0.09 \| RVT \| 0.11 \| 0.71 \| 0.04 \| 0.50 \| 0.48 \| 0.26 \| RVT-2 \| 0.40 \| 0.74 \| 0.38 \| 0.66 \| 0.88 \| 0.69 \| VIRT (Ours) \| 0.48 \| 0.79 \| 0.42 \| 0.68 \| 0.90 \| 0.73 \| The results on the ManiSkill-v3 and RLBench benchmarks show VIRT achieves the best results, which further confirm the superiority of our method. --- Rebuttal Comment 1.1: Comment: Thanks for the additional results! My concerns are addressed and I will maintain my acceptance rating.	null	null	null	null	null	null
Leveraging Online Olympiad-Level Math Problems for LLMs Training and Contamination-Resistant Evaluation	Accept (poster)	Summary: This paper created a new math dataset sourced from the Art of Problem Solving. It designed a pipeline that includes (1) raw data collection, (2) math question detection, (3) question-answer extraction, (4) solution rewriting, and (5) data decontamination. Steps 1 to 3 involve the use of LLMs in the processing. To provide an unbiased benchmark for evaluating the performance of LLMs on math, this paper collected discussions between January 2023 and September 2024 and processed them through a more complex procedure to ensure benchmark quality. The authors further used this dataset to evaluate the performance of open-source models. There is a clear decrease in performance concerning the time at which the discussions took place. ## update after rebuttal I maintain my view that this paper is suitable for acceptance. Claims And Evidence: Yes. Methods And Evaluation Criteria: Yes. Theoretical Claims: N/A. Experimental Designs Or Analyses: The design of the experiments is well-structured. The first part of the evaluation focuses on data quality. The authors randomly select 10% of the benchmark questions and have a group of graduate students evaluate their correctness. Additionally, they compare the correctness of models on the Olympiad benchmark and LiveAoPSBench, observing a clear positive correlation. An ablation study also confirms the necessity of solution rewriting. The second part examines the effectiveness of the math instruction fine-tuning dataset. The results indicate that AoPS-Ins improves the model more effectively than Numina. The third part evaluates the performance of open-source models on LiveAoPSBench. Dividing topics by time is a clever approach to avoiding contamination. The observed performance decline further indicates that benchmarking still suffers from data contamination to some extent. Supplementary Material: No. Relation To Broader Scientific Literature: This paper provides a new Math Instruction Fine-tuning dataset and a math benchmark. This effort contributes to the community of AI for math. Essential References Not Discussed: N/A. Other Strengths And Weaknesses: N/A Other Comments Or Suggestions: The short title at the top of each page exceeds the limit. Questions For Authors: 1. For question with 2 or 3 answers, how do you handle them? Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: We thank the reviewer for their positive comments. Below, we answer the main questions raised by the reviewer: Q1: For question with 2 or 3 answers, how do you handle them? A1: For the LiveAoPSBench evaluation set, we only retain questions with closed-form answers. If a solution provide multiple valid answers, they are summarized as a list of closed form answers. After this, we remove all questions that show discrepancies—i.e., different closed-form answers—between the community-provided solutions(see Section 3.2 LLM cross-checking). In the AoPS-Instruct training set, we include all recognized solutions based on forum discussions for two reasons: (1) Most of the Q-A pairs in training set either have no final answer (e.g., proof-based questions) or the answer is free form, making it hard to rely on voting mechanisms to resolve discrepency. (2) Prior works such as Alphacode[1], have successfully used partially correct solutions for training their models. Therefore, we choose not to apply majority voting filters, allowing users to customize the filtering according to their needs. [1] Li et al., Competition-Level Code Generation with AlphaCode, 2022	Summary: The paper introduces a scalable pipeline that leverages the Art of Problem Solving (AoPS) forum to construct two key resources for advancing Olympiad-level mathematical reasoning with LLMs. (1) AoPS-Instruct is a large-scale instruction-tuning dataset containing over 600k QA pairs, extracted and rewritten from AoPS forum posts. (2) LiveAoPSBench is a continously evolving, timestamped evaluation set intended to minimize overlap (contamination) with existing training corpora. Through extensive experiments, the authors demonstrate that (1) fine-tuning on AoPS-Instruct improves model performance on various math benchmarks, including Olympiad-level problems, and (2) older test sets often lead to inflated accuracy due to potential data contamination. Claims And Evidence: The authors claim that “Fine-tuning various LLMs on AoPS-Instruct lead to improved performance on standard benchmarks such as OlympiadBench, Omni-Math, and our LiveAoPSBench dataset, verifying the effectiveness of our dataset in enhancing math reasoning capabilities of LLMs.” However, their evaluation is limited to the LLMs with fewer than 7B parameters. To strengthen their claims, the authors should extend their experiments to larger-scale LLMs (exceeding 7B parameters) and provide a more comprehensive assessment of the proposed method’s effectiveness. Methods And Evaluation Criteria: The evaluation criteria are somewhat limited due to the lack of larger-scale LLMs (exceeding 7B parameters) used. Theoretical Claims: This paper does not include the theoretical claims. Experimental Designs Or Analyses: The experimental analysis is valid. However, expanding the experiments to include a broader range of LLMs with more than 7B parameters would further strengthen the findings. Supplementary Material: I briefly reviewed the supplementary materials, which primarily contain more details on the proposed benchmarks. Relation To Broader Scientific Literature: This paper is not connected to the broader scientific literature. Essential References Not Discussed: Regarding the mathematic benchmark for LLMs, the paper covers the necessary related works. Other Strengths And Weaknesses: Strengths: 1. The authors present a fully automated procedure—from extracting forum posts, filtering and rewriting answers, to building a “live” test set—showcasing a viable way to harness community-generated data for advanced math tasks. 2. By time-stamping problems and drawing from posts beyond a given cutoff date, LiveAoPSBench offers a valuable approach to reduce dataset leakage, giving a more faithful measure of actual LLM reasoning ability. 3. The authors provide a thorough set of experiments across multiple math benchmarks (Omni-Math, OlympiadBench, etc.) and demonstrate that training on AoPS-Instruct consistently boosts performance. They also show a strong correlation between LiveAoPSBench and a human-verified Olympiad dataset, indicating good dataset quality. Weaknesses: The paper is well-structured and effectively conveys its main points. Improving mathematical reasoning capabilities of LLMs is an important problem in the research field, and the authors propose the corresponding method to address this problem. However, the experimental validation presented in this paper is weak. 1. The evaluation is limited to the LLMs with fewer than 7B parameters. To strengthen their claims, the authors should extend their experiments to larger-scale LLMs (exceeding 7B parameters) and provide a more comprehensive assessment of the proposed method’s effectiveness. 2. The evaluation set primarily consists of problems with concrete numeric or symbolic final answers. This excludes a large portion of Olympiad problems that require more open-ended proofs, which the pipeline and automated evaluations currently do not fully capture. Other Comments Or Suggestions: Figure 1 contains too many plotted lines, which may impact visual clarity and overall readability. Questions For Authors: 1. Would you explore evaluating the results on larger-scale LLMs (7B+ parameters)? 2. Have you considered adapting your pipeline to handle open-ended proof-based questions with no single “boxed” answer? What modifications might be needed for verifying correctness in such contexts? Code Of Conduct: Affirmed. Overall Recommendation: 2	Rebuttal 1: Rebuttal: We thank the reviewer for their constructive feedback. Below, we answer the main concerns raised by the reviewer: Q1: The evaluation is limited to the LLMs with fewer than 7B parameters. To strengthen their claims, the authors should extend their experiments to larger-scale LLMs (exceeding 7B parameters) and provide a more comprehensive assessment of the proposed method’s effectiveness. A1: We do not currently have the resources to fine-tune larger than 7B models, but we believe we provide substantial evidence that we hope motivates the community to push this further. To reiterate on some of the evidence we show in the paper: * Table 2 presents results for two 7B math-specialized models, alongside Llama 1B and 3B models, all consistently demonstrating improved accuracy across the board. * Table 6 in the appendix shows that performance gains transfer from a smaller 1.5B rewriting model to a larger 7B model. * For evaluation, we tested models up to 72B on our LiveAoPSBench, highlighting the benchmark’s difficulty and its correlation with uncontaminated benchmarks (Figure 5a). Q2: The evaluation set primarily consists of problems with concrete numeric or symbolic final answers. This excludes a large portion of Olympiad problems that require more open-ended proofs, which the pipeline and automated evaluations currently do not fully capture. A2: Evaluating proof-based questions has remained a long-standing and persistent challenge in the mathematical reasoning community, with no widely accepted solution outside formal languages like Lean—which fall beyond the scope of our work. A key limitation is the lack of large-scale training data for informal proof-based problems. As noted in our paper, approximately 30% of our training dataset consists of proof-based questions. We are optimistic that this dataset will support the development of new methods for evaluating proof-based reasoning.	Summary: 1) The paper constructs a dataset for Olympiad-level mathematical reasoning with a large scale and diverse problems, which is significant for LLMs’ development in mathematical problem-solving. 2) Experiments demonstrate that the dataset can effectively improve LLM performance on benchmarks like MATH. Also, this dataset can serve as a benchmark with some resistance to contamination, effectively evaluating model performance Claims And Evidence: Yes Methods And Evaluation Criteria: 1) Insufficient methodological details: 1.1) No conflict resolution protocol for handling discreprancies in community-provided answers (e.g., voting mechanisms). 1.2) Lack of validation for each step in the dataset construction pipeline (e.g. whether LLM cross-cheching effectively removes incorrect answers). 2) The current approach detects duplicate data via substring matching but fails to identify semantically equivalent problems with different wording or multilingual translation issues (e.g., Chinese-to-English translations). Could semantic similarity be used instead? Theoretical Claims: N/A Experimental Designs Or Analyses: 1) The paper does not effectively demonstrate that timestamps mitigate contamination. There is no quantitative analysis of new problem duplication rates, such as statistics on overlap between different time periods and previous datasets. Supplementary Material: No. Relation To Broader Scientific Literature: Similar work (such as the NuminaMath dataset) has been done on this topic. The contribution of this paper is marginal. Essential References Not Discussed: N/A Other Strengths And Weaknesses: Constructing a large-scale and high-quality dataset for mathematical reasoning is an important task and will promote the research on mathematical reasoning. However, the contribution of this paper is marginal. It is somewhat weak technically. Other Comments Or Suggestions: N/A Questions For Authors: 1) NuminaMath also sources data from AoPS and rewrites solutions using GPT-4o. How does your approach compare to theirs, and what advantages does it offer? Code Of Conduct: Affirmed. Overall Recommendation: 2	Rebuttal 1: Rebuttal: We thank the reviewer for their constructive feedback. Below, we answer the main concerns raised by the reviewer: Q1: No conflict resolution protocol for handling discreprancies in community-provided answers (e.g., voting mechanisms). A1: For the LiveAoPSBench evaluation set, we only keep questions that have a closed-form answer, and we handle discreprancies between community-provided via LLM cross-check. In the AoPS-Instruct training set, we include all recognized solutions based on forum discussions for two reasons: (1) Most of the Q-A pairs in training set either have no final answer (e.g., proof-based questions) or the answer is free form, making it hard to rely on voting mechanisms to resolve discrepency. (2) Prior works such as Alphacode[1], have successfully used partially correct solutions for training their models. Therefore, we choose not to apply majority voting filters, allowing users to customize the filtering according to their needs. [1] Li et al., Competition-Level Code Generation with AlphaCode, 2022 Q2: Lack of validation for each step in the dataset construction pipeline. (whether LLM cross-cheching effectively removes incorrect answers.) A2: In Figure 5.b we show the effectiveness of LLM rewritting. The effectiveness of LLM cross-checking has been qualitatively verified by human annotators. In Section 4.4, a human-annotated error rate of 8% was reported, whereas we empirically observed an error rate of over 20% before applying LLM cross-checking. Q3: The current approach detects duplicate data via substring matching but fails to identify semantically equivalent problems with different wording or multilingual translation issues (e.g., Chinese-to-English translations). Could semantic similarity be used instead? A3: N-gram decontamination is a standard practice in math data. We follow the DeepSeek-Math [2] paper, which uses 10-gram decontamination. Qwen-Math also applies decontamination based on 13-grams [3]. [4] Leverages the LLM for semantic based decontamination, but is not widely adpoted due to its inefficiecy when scaling up, and high false-positive rate. [2] Shao, et al., DeepSeekMath: Pushing the Limits of Mathematical Reasoning in Open Language Models, 2024 [3] Yang, et al., Qwen2.5-Math Technical Report: Toward Mathematical Expert Model via Self-Improvement, 2024 [4] Yang, et al. "Rethinking benchmark and contamination for language models with rephrased samples." arXiv preprint arXiv:2311.04850 (2023). Q4 The paper does not effectively demonstrate that timestamps mitigate contamination. There is no quantitative analysis of new problem duplication rates, such as statistics on overlap between different time periods and previous datasets. A4: Thank you for the suggestion! We demonstrate the correlation of timestamps vs contamination by decontaminate against the massive Numnia Training set following the decontamination set up of Qwen2.5[3]. Below we report a change of contamination rate w.r.t to timestamp. We report the statistics of overlap against Numina CoT Traing dataset (released July.2024) as below: \| Time \| Jan-Apr 2023 \| May-Aug 2023 \| Sep-Dec 2023 \| Jan-Apr 2024 \| May-Aug 2024 \| \|:-------------------\|-------------:\|-------------:\|-------------:\|-------------:\|-------------:\| \| 10-gram Overlap Rate \| 13.24%\| 11.65%\| 12.82%\| 9.92%\| 6.88%\| \| Overlapped Question\| 229 \| 208 \| 218 \| 226 \| 109 \| \| Total Questions \| 1730 \| 1785 \| 1701 \| 2278 \| 1585 \| As we can see, the rate of potential contamination significantly decreases as timestamps increase. We will add this info to our revised manuscript. Q5: NuminaMath also sources data from AoPS and rewrites solutions using GPT-4o. How does your approach compare to theirs, and what advantages does it offer? A5: While Numina source some problems from AoPS contest pages, their problem-solution extraction mechanism is very simple, leading to very small number (30K QA pairs) of extracted solutions compared to our method. Their method only extracts problems from contest page (where the problems are formally written), and their solution extraction method takes the longest post which contains a black box at the end of the proof. Instead, we explore the entire AoPS forum discussions, where questions and solutions are shared in unstructured posts by community members. This requires extensive use of LLMs for data filtering and solution extraction, allowing us to extract 652K QA pairs (in contrast to Numina's 30K), resulting in a 21-fold increase in extracted data from AoPS. These improvements result in a stronger dataset, leading to higher performance gains as shown in Table 2 of our paper.	Summary: This paper introduces AoPS-Instruct, a dataset of 666K Olympiad-level math QA pairs, and LiveAoPSBench, a contamination-resistant benchmark, both sourced from the Art of Problem Solving (AoPS) forum. Using an automated pipeline, the authors extract and refine QA pairs, leveraging Qwen 2.5 72B to rewrite solutions into step-by-step explanations. Fine-tuning LLMs on AoPS-Instruct improves performance on benchmarks like OlympiadBench and Omni-MATH, while LiveAoPSBench reveals performance drops over time, indicating prior benchmark contamination and thus, highlights the importance of continually evolving datasets for fair LLM evaluation. Claims And Evidence: The paper provides sufficient empirical evidence for all the claims made. Methods And Evaluation Criteria: The description of methodology lacks details about the motivation behind certain design choices as well as other details. * Why is Llama-3.1-70B used for Question-Answer Extraction as compared to a chat variant of the Qwen-2.5 series. * In Step 3 (solution rewriting), how is the solution that is to be re-written selected out of all the solutions provided by different users as extracted from the forum. * Are any measures taken to remove the 5% incorrect and 3% no-answer category questions from the final evaluation set? Presence of these amounts of degenerate questions could cause significantly wrong judgements about the performance of models. Theoretical Claims: The paper does not make any theoretical claims Experimental Designs Or Analyses: I have cetain questions and suggestions about the experiments reported in the paper. * In Table 2, the size of the datasets on which the models have been finetuned have not been specified. I believe it would be important to ensure that the amount of data on which the models are finetuned is same across different datasets in order to ensure fair comparison * For the comparison in Table 2, it would be useful to have a comparison with a stronger baseline. Several powerful synthetic datasets (for eg. ScaleQuest [1] and DART-Math [2] are plausible candidates) * The number of seeds over which the performances are computed has not been reported. It is important to discuss the statistical significance of small differences (such as the difference in performance of models on AoPS-Ins and Numina+AoPS-Ins in Table 2. It would be useful to report the performances of some state of the art models such as o1, DeepSeek-R1, DeepSeek-R1 distilled series, etc. on LiveAoPSBench. This would give a better idea of the difficulty level of the benchmark. Supplementary Material: I have gone through some of the evaluation questions attached in the supplementary material attached with the submission. I have not gone through the code in detail. Relation To Broader Scientific Literature: This paper falls within the vast literature on developing novel benchmarks for evaluating mathematical reasoning abilities of LLMs. More specifically, this work focuses on developing contamination resistant evaluation benchmarks but continually collecting new olympiad level questions discussed on the AoPS forum. Another work which attempts to tackle the problem of evaluation data contamination includes [3] which uses an AI-Assisted approach for creating new and difficult mathematical questions. Essential References Not Discussed: I believe the following papers are worth discussing: Synthetically Generated Training Datasets for Math Reasoning [1] Ding el al., 2024; Unleashing Reasoning Capability of LLMs via Scalable Question Generation from Scratch; https://arxiv.org/abs/2410.18693 [2] Tong et al., 2024; DART-Math: Difficult Aware Rejection Tuning for Mathematical Reasoning; https://arxiv.org/abs/2407.13690 Connections with approaches for creating math evaluation benchmarks to address data contamination in existing benchmarks [3] Shah et al., 2024; AI-Assisted Generation of Difficult Math Questions; https://arxiv.org/abs/2407.21009 Other Strengths And Weaknesses: ### Strengths The paper is well motivated and presents systematic pipelines for creating olympiad level training datasets and contamination resistant evaluation datasets. The paper is generally well written and provides a good set of experiments and ablation studies to show the usefulness of the approach ### Weaknesses Please refer to Methods and Evaluation Criteria and Experimental Design and Analyses sections Other Comments Or Suggestions: I have mentioned all comments and suggestions that I have in previous sections. The paper attempts to tackle an important problem and proposes a pipeline which is more generally applicable. However, I believe it lacks certain important clarifications and details which I have highlighted previously. Questions For Authors: Please see Methods and Evaluation Criteria and Experimental Design and Analyses Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We thank the reviewer for their constructive feedback. Q1: In Table 2, the size of the datasets on which the models have been finetuned have not been specified. It would be important to ensure that the amount of data on which the models are finetuned is same across different datasets to ensure fair comparison A1: We used the full Numina dataset, decontaminated against our evaluation benchmarks, resulting in 824K data points. In comparison, our dataset contains 647K data points. Despite being smaller, our dataset demonstrates a greater performance improvement than Numina, as highlighted in Table 2. We will add this information to our revised manuscript. Q2: For the comparison in Table 2, it would be useful to have a comparison with a stronger baseline. Several powerful synthetic datasets (for eg. ScaleQuest [1] and DART-Math [2] are plausible candidates). A2: ScaleQuest: Thank you for bringing our attention to this very recent work. We will add a citation to this work as a concurrent work. DART-Math: Thank you for pointing this work out. Below, we take the DeepSeek model from the DART-MATH paper, and compare it with our DeepSeek-fine-tuned model: \| \| AoPS24 \| MATH \| OlympiadBench \| OmniMath \| \|-\|--\|--\|---\|--\| \| DART-Math \| 13.3 \| 53.6 \| 22.5 \| 15.2 \| \| AoPS-Ins \| 19.0 \| 58.8 \| 24.3 \| 17.8 \| We observe that our model outperforms the DART-MATH model on all benchmarks. We will add this table to our paper. Q3: The number of seeds over which the performances are computed has not been reported. A3: We measure the Pass@1 metric in all of our tables, and for non-R1 models, the common practice is to set a temperature of zero for performance measurement. Therefore, there is no stochasticity in the metric to repeat for multiple seeds. This is in line with other works in mathematical reasoning (e.g., see [2] and [3]) where there are no standard deviations to report for Pass@1. Q4: It would be useful to report the performances of some state of the art models such as o1, DeepSeek-R1, DeepSeek-R1 distilled series, etc. on LiveAoPSBench. This would give a better idea of the difficulty level of the benchmark. A4: We have reported the performance of R1-distilled models in Figure 8 in the Appendix. However, assessing the full R1 and o1 models is both computationally and financially prohibitive due to their high operational costs, which prevents us from including their results. Q5: Are any measures taken to remove the 5% incorrect and 3% no-answer category questions from the final evaluation set? The presence of these amounts of degenerate questions could cause significantly wrong judgments about the performance of models. A5: LiveAoPSBench is a dynamically evolving benchmark, and we continuously work to refine the pipeline as we identify failure cases. We should note that current large language models perform well below this error-rate threshold (e.g., DeepSeek distilled models achieve only 52.2% accuracy on our benchmark). Moreover, even the human-labeled GSM8K dataset is known to contain a small percentage of label errors [1], yet it remained a highly discriminative benchmark until state-of-the-art models began to saturate it. Thus, while we are committed to enhancing LiveAoPSBench, we believe it remains valuable and informative in its current state. Q6: In Step 3 (solution rewriting), how is the solution that is to be re-written selected out of all the solutions provided by different users as extracted from the forum. A6: We input the whole topic discussion to the LLM, and the LLM must infer correct post indexes that contain correct solution. This is done by analyzing the forum discussion to detect correct answers. We use few-shot chain-of-thougt prompt to extract these (see Figure 12 for the exact prompt, and our code for few-shot examples). Q7: Why is Llama-3.1-70B used for Question-Answer Extraction as compared to a chat variant of the Qwen-2.5 series. A7: We apologize for the typo. In fact, we utilize Qwen-2.5 across the entire AoPS-instruct pipeline (as illustrated in Figure 1 and Table 1). We will correct this mistake in our revised submission. Q8: Another work which attempts to tackle the problem of evaluation data contamination includes Shah et al., which uses an AI-Assisted approach for creating new and difficult mathematical questions. A8: Thank you for highlighting this relevant work. The work of Shah et al. aims to produce an evaluation dataset that tests compositional generalization by combining pairs of distinct mathematical skills extracted from the MATH dataset. This differs from our methodology, which emphasizes dynamically evolving, community-driven problem-solving data. We appreciate the suggestion and will include a citation to this work in our revised manuscript. [1] https://gradientscience.org/platinum-benchmarks [2] Yang et al., Qwen2.5-Math [3] Shao et al., DeepSeekMath --- Rebuttal Comment 1.1: Comment: I thank the authors for the detailed rebuttal and for clarifying my questions. DART-Math comparison If I understand correctly, the DART-Math-DSMath-7B model referred to in the rebuttal by the author was obtained by fine-tuning DeepseekMath-7B (base model) using DART-Math data where as the model reported in the paper is a obtained by fine-tuning DeepseekMath-7B-Ins (i.e., instruct tuned version) on the AoPSInstruct dataset. This is not a fair comparison since instruct tuned models usually lead to better fine-tuned models. The empirical evaluation of the effectiveness of AoPSInstruct seems limited in general. I would encourage the authors to include more base models and comparison with datasets such as ScaleQuest and DART-Math (a subset of size equal to AoPSInstruct, and if affordable within the compute budget of the authors) in the revised versions. Correctness of Data I also maintain my concern about the error rates in the eval dataset. While it is true that existing models do not saturate the dataset and that previous benchmarks have had errors as well, I believe that evaluation benchmarks should held up at the highest standards. Despite the above concerns, considering that the authors addressed my other concerns satisfactorily, and the general utility of the pipeline, I am increasing my score. --- Reply to Comment 1.1.1: Comment: We thank the reviewer for their continued engagement and for acknowledging the utility of our proposed pipeline. DART-Math Comparison: We appreciate the reviewer’s observation regarding the fairness of the comparison between DART-MATH and AoPS-Instruct. To address this concern, we took the DART-MATH-Hard dataset and fine-tuned it for three epochs on DeekSeek-Math-Instruct using our setup ensuring a more direct and fair comparison. The updated results are as follows: \| Dataset \|Size\| AoPS \| OlympiadBench \| Omni-MATH \| MATH \| \|----------------\|--\|------\|----------------\|------------\|------\| \| DART-MATH-Hard\| 585k \| 14.4 \| 21.8 \| 15.4 \| 52.5 \| \| AoPS-Ins \| 647k \| 19.0 \| 24.3 \| 17.8 \| 58.8 \| As shown, AoPS-Instruct fine-tuning still outperforms DART-MATH-Hard across all four benchmarks. We will add this experiment to our revised manuscript for further validation.	null	null	null	null	null	null
Portable Reward Tuning: Towards Reusable Fine-Tuning across Different Pretrained Models	Accept (poster)	Summary: The paper proposes Portable Reward Tuning (PRT), a fine-tuning pipeline to enable efficient and reusable fine-tuning across different foundation models (FMs). It is especially useful when the old FMs are replaced by new FMs with different pre-training dataset and even different model architectures. Previous fine-tuning methods, i.e. inference-time tuning methods or emulated fine-tuning (EFT) in this paper, require running multiple models during inference, increasing overhead. The proposed PRT claims to avoid this by training an explicit reward model instead of modifying the pretrained model for each fine-tuning task. Experiments on vision and language models show that PRT achieves comparable accuracy to EFT with lower inference costs (evaluated by memory usage and time usage). Claims And Evidence: As my understanding, with the proposed PRT method, this paper makes three claims and provides proof to support each claim. Claim 1: PRT maintains accuracy comparable to EFT. Claim 2: PRT reduces inference overhead compared to EFT. Claim 3: During inference, the reward model can be used with any foundation model (with the same set of vocabularies or labels). For Claim 1, Figures 2–4 and Appendix E,F show PRT matches EFT on vision and language tasks. For Claim 2, the authors provide Tables 2-3 in Appendix. For Claim 3, the above experiment results can prove it. For example, for CLIP, we see generalization across ResNet and ViT, for LLAMA we see results from 1B model to 8B model, and for Qwen (from 0.5 B to 72 B), etc. Methods And Evaluation Criteria: The proposed methods: PRT trains a reward model using cross-entropy loss, reformulating fine-tuning as reward maximization with KL regularization. The reward is combined with new models at inference via closed-form policy (Eq. 10). The experiments are designed on broad coverage of FMs and benchmarking datasets. The paper provides evaluation on proposed method, baseline methods (EFT) and FT for both vision tasks and language tasks. However, I believe the evaluation metrics are not sufficient. For example, for vision tasks, only one quantitative metric, accuracy (Figs. 2–4) is used. The accuracy focuses on means with no standard deviations or confidence intervals. Is it possible to have more metrics to provide statistical significance of differences between PRT and baselines? Theoretical Claims: Following are theoretical claims I have checked. Proposition 3.1: Establishes a one-to-one mapping between fine-tuned models and rewards. Comment: Valid, assuming rewards are scaled properly. Proposition 3.2: Bounds the KL divergence between inference models when source and target pre-trained models are ε-close. Comment: 1) When replacing a Resnet foundation model with ViT (just like the experiment does. See Figure 2 (a)), the ε should be larger than replacing a Resnet with a Restnet. I am not sure how drastic the ε could be in practice. 2) The authors assume that the maximum and mean value ratio of the exponential reward is bounded by some constant C. I am not sure how large the C could be and if this assumption is realistic for practice or not. Proposition 3.3: I am not familiar with the PAC Bayes framework so I lack understanding of this. Experimental Designs Or Analyses: 1. Quantitative experiments on Vision experiments and Language experiments a) The settings of baselines. For each experiment, the comparison is limited within FT, EFT and PRT, and there are other lightweight efficient fine-tuning methods available as baseline methods, such as LoRA and adapters. It weakens the point that PRT is a superior alternative to fine-tuning. b) FT method performs better than EFT and PRT in terms of accuracy and speed in most of the cases (Fig. 2 and 10. Table 1 and 2), yet FT is not a baseline. The impact is the same with the last issue. c) About the training and inference speed, the proof is provided in the Appendix. I feel it is also an important proof because it is one of the keys to proving the efficiency of the proposed method. Is it possible to have them or part of them in Section 4? 2. Qualitative experiments a) It lacks analysis of Figure 11 - 12 in HumanEval Results (Appendix F). For example, PRT underperforms on Falcon-3 models when the target model is 7B and 10 B. Things are different with other target models. What does this phenomenon mean? Does it imply that PRT’s reliance on source model quality, which is not discussed in the main paper? 3. Other issues not discussed in the paper a) The reward model scalability. What factors can impact the scale of the reward model and how costs would change with its scale? b) What are the limits of the "same label space" assumption? And what if the label is partially different? Supplementary Material: 1. Appendix.A: Proof of Proposition 3.2. I have discussed the issue in ‘Theoretical Claims’. 2. Appendix.B: Experimental Setup. Questions for Appendix.B.2: In Table 1, the memory usage of PRT is higher than FT, and the time usage of PRT is also longer than FT. I don’t think Table 1 provides useful information to support any claims of this paper. 3. Appendix. E to F. I have discussed the issue in ‘Experimental Designs Or Analyses’. Relation To Broader Scientific Literature: This work, if solid, may contribute to Foundation Models of both computer-vison and natural language processing. Essential References Not Discussed: To my knowledge, the current related work is comprehensive. Other Strengths And Weaknesses: S1. The paper provides an interesting idea to bridge an old FM and a new FM with a tuned reward, without training from the beginning every time for a new FM. W1. However I believe the motivation of using PRT is not persuasive enough because 1) the direct FM performs well. 2) Other efficient fine-tuning methods are not compared to prove the high efficiency of PRT. Other Comments Or Suggestions: 1. The ‘flower’ dataset used for experiments in Figure 2 is not mentioned in section 4 but only appears in the Appendix. 2. Section 4.4 ‘Tables 2 and 3 show that PRT successfully reduces both inference speed and memory usage’ should be ‘...increase inference speed’ (increase speed or reduce time). 3. For Table 1, and Table 2 in the Appendix, ‘Speed per batch’ should be ‘Time usage per batch’. Questions For Authors: Q1. We have seen PRT is capable of handling different datasets and even model architectures. Is it possible to test PRT method on different downstream tasks, and how to do that? For example, for vision tasks, there are different downstream tasks including object detection, image segmentation, etc. Q2. Is it possible to have a comparison of PRT with other latest effective fine-tuning methods? Q3. Could the trained reward model of PRT be ‘outdated’ and require re-training too? Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Thank you for your detailed feedback. Here we focus on answering major concerns/questions due to space limitation. However, we sincerely appreciate other feedback and will reflect them to our revisions, as well as discussions below. ### Methods And Evaluation Criteria > However, I believe the evaluation metrics are not sufficient. Due to the space limitation, please refer to our answer to Reviewer BmQN on standard deviations. ### Theoretical Claims > When replacing a Resnet foundation model with ViT, the ε should be larger than replacing a Resnet with a Restnet. I am not sure how drastic the ε could be in practice. > I am not sure how large the C could be and if this assumption is realistic for practice or not. The practical validity of our assumptions is indeed an important perspective. Thus we conducted additional experiments to measure $\epsilon$, KL-divergence between pretrained models, and the constant $C$ on CIFAR100: \|$\pi_{pt}$\|$\widetilde{\pi}_{pt}$\|ε\|C\| \|-\|-\|-\|-\| \|RN50 (OpenAI)\|RN50 (OpenAI)\|0.0\|19.41\| \|RN50 (OpenAI)\|RN101 (OpenAI)\|0.0016\|-\| \|\|ViT-B (OpenAI)\|0.0030\|-\| \|\|ViT-B (LAION-400M)\|0.0107\|-\| \|\|ViT-L (OpenAI)\|0.0044\|-\| \|\|ViT-L (LAION-400M)\|0.0158\|-\| Here we reported averaged results over inputs from the dataset. These results indicate that (1) KL divergences between similar models are surprisingly small, (2) KL divergences largely depend on pretraining datasets, rather than model structures, (3) the constant C is seemingly finitely bounded. ### Experimental Designs Or Analyses > [...] there are other lightweight efficient FT methods available as baseline methods, such as LoRA and adapters. It weakens the point that PRT is a superior alternative to FT. > FT method performs better than EFT and PRT in terms of accuracy and speed in most of the cases, yet FT is not a baseline. The impact is the same with the last issue. First of all, we would like to emphasize that our paper does not claim PRT is `a superior alternative to FT` unconditionally. If we have enough resources that we can ignore costs for training models or maintaining training data, we should employ repeated FT rather than one-time PRT. Rather, our paper claims that PRT is a better alternative in cases that we don't want to retrain new pretrained models for various reasons. In such cases, FT models are unavailable and thus should be viewed as unknown oracles for PRT/EFT. Hence the fact that FT is better than PRT/EFT in accuracy/efficiency does not diminish their motivation. Also, we consider that the lack of comparison with efficient FT methods like LoRA does not weaken our claims because: (1) Both PRT and EFT are not efficient FT methods. Rather, they enable us to reuse a once-tuned model for (inference-time) tuning other pretrained models with different sizes or updated knowledge. (2) Since efficient FT methods like LoRA are designed to apply to FT, they should also apply to PRT. The following additional experiments (instruct-tuned with LoRA, eval. on GSM8K) verify that LoRA actually works with PRT as well as FT. \|\|0.5B\|1.5B\|3B\|7B\|14B\| \|-\|-\|-\|-\|-\|-\| \|EFT+LoRA (0.5B)\|29.72%\|53.15%\|65.28%\|56.41%\|53.37%\| \|PRT+LoRA (0.5B)\|21.83%\|50.11%\|63.15%\|74.91%\|73.62%\| > It lacks analysis of Figure 11-12 in HumanEval Results (...). For example, PRT underperforms on Falcon-3 models when the target model is 7B and 10B. Things are different with other target models. [...] Actually, PRT performs well on the GSM8K benchmark even with Falcon3 7B/10B models, which implies PRT indeed transfer the instruction-tuned ability to these models. The problem on HumanEval is mainly due to the difficulty of controlling downstream accuracy in instruction-tuning in some models, since the instruction dataset contains many data irrelevant to downstream tasks. > Other issues not discussed in the paper a) The reward model scalability. [...] b) What are the limits of the "same label space" assumption? And what if the label is partially different?` a): Figure 13 shows the reward model scalability. Overall, a larger reward model leads to better accuracy with new pretrained models. Also, we additionally evaluated how inference time will be changed by scailing model sizes (1B → 3B). The results show the increase in average time per token is only 2% with PRT, while 25% with EFT. \|\|Llama3.2-1B w/ Llama3-8B\|Llama3.2-3B w/ Llama3-8B\| \|-\|-\|-\| \|EFT\|24.4 ± 0.2 ms\|30.4 ± 0.0 ms (× 1.25)\| \|PRT\|22.7 ± 1.8 ms\|23.1 ± 1.0 ms (× 1.02)\| b): See our answer to Reviewer BmQN. ### Questions: Q1: The instruction-tuned models are actually evaluated on downstream tasks like math and coding. However, as you pointed out, tasks that require feature extraction, rather than label distributions, are out of scope in this paper. This may be an interesting direction for future work. Q2: See above discussion. Q3: We confirmed that the reward model can be retrained and then reused with other pretrained models when input distribution changed. See our answer to Reviewer BmQN. --- Rebuttal Comment 1.1: Comment: Thanks for the detailed responses. The rebuttal is persuasive and add more details based on the original submission. I updated my rating accordingly. --- Reply to Comment 1.1.1: Comment: Thank you for taking the time and updating your evaluation. We again appreciate your detailed feedback, which led to the improved manuscript and a better understanding of our method.	Summary: This paper proposes Portable Reward Tuning (PRT), a new fine-tuning paradigm that decouples the “reward” from the foundation model itself, thereby making it “portable” to other foundation models of the same architecture family (with shared label or token vocabulary). Overall, the method aims to reduce repeated training costs and extra inference costs when one’s underlying foundation model is replaced or upgraded. Claims And Evidence: Overall, the paper offers sound conceptual reasoning plus decent experiments on a variety of image and NLP tasks. While the final accuracy typically remains below a fully re-fine-tuned new model, PRT competes well with the existing “emulated fine-tuning” baseline and indeed uses fewer inference resources. Methods And Evaluation Criteria: The authors design PRT by explicitly parameterizing a reward function r_\theta(x,y). They then train it via the same cross-entropy style objective normally used for fine-tuning, ensuring that the closed-form “max reward + KL constraint” policy solution matches the fine-tuned distribution. They measure classification accuracy in vision tasks, code generation pass rates, or language understanding metrics. The baselines are: (1) the original, non-fine-tuned “pretrained” model, (2) a normal “fine-tuned” model for that new architecture (oracle), (3) the existing “emulated fine-tuning” approach (EFT), and (4) PRT. The evaluation is thorough for a wide set of classification and NLP tasks. However, exploring truly large language models in real production settings or more open-ended tasks would bolster real-world relevance. Theoretical Claims: The authors rely on the standard derivation of KL-regularized maximum entropy RL. They show that “fine-tuning is the closed-form solution to a certain reward objective.” They provide a fairly standard PAC-Bayesian argument in the appendix to justify generalization. Experimental Designs Or Analyses: The paper’s results cover classification (eight standard fine-grained or broad datasets), instruction following tasks (GSM8k, IFEval, MMLU, etc.), and code generation (HumanEval). This breadth is good. The authors only do a certain limited ablation around, e.g., the effect of different source vs. target architectures or training stable reward networks. More discussions on how stable the training is across random seeds or large scale might be helpful. Supplementary Material: The appendix includes details on proofs, full hyperparameters, memory benchmarks, speed measurements, and additional dataset results. It adds clarity to the approach. Relation To Broader Scientific Literature: Fine-tuning with KL constraints is widely used in RL from human feedback. The authors cite prior works that interpret instruction tuning or RLHF in such terms. The authors position PRT as a solution for “cross-model generalization of fine-tuned solutions.” They might connect more with methods in model distillation or universal prompt offsets, but that is less critical. Essential References Not Discussed: No major references are obviously missing. Other Strengths And Weaknesses: Weaknesses: Some details about how robust the reward model is to massive distribution shifts remain underexplored. And the final performance is typically still below a real full re-fine-tune. If one can afford re-training, PRT is only partial. Overall, it’s a promising approach. Other Comments Or Suggestions: Could we do something approximate if the new model’s vocabulary is only partly changed? Another possible future direction is combining PRT with partial re-training to reduce any performance gap. Questions For Authors: How big a mismatch can we handle between old and new model vocabularies or label sets? Could partial alignment or token mapping methods mitigate that? Do you observe any stability concerns or require special hyperparameters to get consistent results in PRT training? Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Thank you for your valuable feedback. We are really encouraged by the positive feedback to our research direction. Here we would like to address your concerns or questions. > The authors only do a certain limited ablation around, e.g., the effect of different source vs. target architectures or training stable reward networks. More discussions on how stable the training is across random seeds or large scale might be helpful. Thank you for the suggestion. Indeed, in vision experiments (e.g. Fig 2), we have already plotted one standard deviation (by black bars) over three random seeds in training, which indicates very small variance in PRT training/inference. Moreover, although training language models with multiple seeds is computationally heavy and thus not standard in previous literature, we additionally conducted PRT/Instruct tuning of Qwen2.5-0.5B model with three random seeds, and evaluated them with other pretrained models. These results show the stability of PRT is at the same level as standard FT, also in language experiments. We would like to add such discussions on training stability with respect to random seeds in our revision. \|\|0.5B\|1.5B\|3B\|7B\|14B\| \|---\|---\|---\|---\|---\|---\| \|EFT\|$26.79\pm3.79\%$\|$45.94\pm4.40\%$\|$53.37\pm4.77\%$\|$66.14\pm2.43\%$\|$71.01\pm3.16\%$\| \|PRT\|$26.69\pm1.45\%$\|$51.73\pm1.84\%$\|$62.37\pm2.14\%$\|$71.34\pm0.60\%$\|$77.23\pm0.20\%$\| > The authors position PRT as a solution for “cross-model generalization of fine-tuned solutions.” They might connect more with methods in model distillation or universal prompt offsets, but that is less critical. Thank you for suggestions. We agree that automatic prompt tuning can also be considered as inference-time tuning (but only for language models), and thus we would like to add a discussion about them. Also we would like to survey related literatures from the field of model distillation. > Weaknesses: Some details about how robust the reward model is to massive distribution shifts remain underexplored. > [...] Another possible future direction is combining PRT with partial re-training to reduce any performance gap. Here we will proceed by assuming `massive distribution shifts` refers to input distributions. To examine this, we conducted experiments with noisy data, i.e., CIFAR100 with gaussian noise ($\sigma^2=0.01$). Here we employ a reward model (ResNet50, untuned) trained on clean data by PRT, and then additionally tune it by PRT on the noisy data (ResNet50, tuned) for only $1/10$ iterations. The results show that (1) PRT degrades its performance on noisy data (as well as standard FT) but (2) additional PRT training can recover its performance. \| \|ResNet50\|ResNet101 \|ViT-B-16\| \|---\|---\|---\|---\| \|PRT on clean data (ResNet50, untuned) \|71.70%\|72.36%\|79.5%\| \|PRT on noisy data (ResNet50, untuned) \|21.37%\|34.77%\|53.47%\| \|PRT on noisy data (ResNet50, tuned)\|71.60%\|72.18%\|78.06%\| > Could we do something approximate if the new model’s vocabulary is only partly changed? > How big a mismatch can we handle between old and new model vocabularies or label sets? Could partial alignment or token mapping methods mitigate that? We sincerely agree that such a research direction is important for inference-time tuning, i.e., for both EFT and PRT. We decided not to treat this topic in this PRT paper as it should be focused on questions specific to PRT. Also handling different vocabularies is actually a highly non-trivial problem in language models [1, 2, for e.g.], and thus it should deserve another paper, which may require to match different vocabularies using, for e.g., edit distance, optimal transport, etc. - [1] Xu et al. "Bridging the Gap between Different Vocabularies for LLM Ensemble" - [2] Wan et al. "Knowledge Fusion of Large Language Models" > Do you observe any stability concerns or require special hyperparameters to get consistent results in PRT training? As described in Appendix B, we basically used the same hyperparameters for both PRT and (E)FT in training and inference, for fair comparison. Some experiments (Fig.6, 7) includes EM regularization, but we found that the regularization coefficient does not affect the stability of final results. --- Rebuttal Comment 1.1: Comment: After reviewing the authors’ rebuttal, I appreciate the additional experiments. Given my limited expertise in this area, I maintain my original score, and the AC may weigh my evaluation accordingly. --- Reply to Comment 1.1.1: Comment: We sincerely thank you for taking the time to read our rebuttal and for acknowledging the additional experiments. As our paper appears to be on the borderline, we would greatly appreciate it if you could consider reassessing your evaluation in light of our clarifications to your concerns, or kindly let us know if there are any remaining concerns we could address in future work. Once again, we really appreciate your time and thoughtful review!	Summary: This paper introduces a novel approach to reward tuning that can be transferred across model architectures. Instead of modifying a model parameters directly, the proposed approach trains an explicit reward model using the same objective as fine-tuning. At inference time, the reward model can be applied to any compatible foundation model without additional retraining. Experiments on vision and language tasks demonstrate that the proposed algorithm achieves comparable accuracy to traditional fine-tuning. Claims And Evidence: The authors conduct convincing experiments and comparisons to support the strengths of their proposed algorithm. Methods And Evaluation Criteria: The experimental settings selected in the paper clearly support the claims made by the authors in the paper. Theoretical Claims: I quickly glanced the proofs for the theoretical claims to support the design of their algorithm and they look reasonable. Experimental Designs Or Analyses: The experiment designs are sound and valid, relevant to the claims made in the paper. Supplementary Material: I quickly glanced the proofs for the theoretical claims to support the design of their algorithm and they look reasonable. Relation To Broader Scientific Literature: The paper studies an important question on adaptable and reusable reward models that can utilized across pre-trained models. The proposed algorithm is simple, with a theoretical basis. Essential References Not Discussed: The authors have extensively discussed the important references. Other Strengths And Weaknesses: The strength of the paper lies in its motivation to make fine-tuning more efficient by introducing Portable Reward Tuning (PRT), which allows reward models to be reused across different pretrained models. The authors carefully discuss the key principles behind their approach, framing fine-tuning as reward maximization with KL regularization, which reduces inference costs while maintaining performance. Additionally, the paper provides theoretical insights into how reward models adapt to different pretrained models. Overall, this paper presents a promising direction for making model adaptation more efficient and reusable. Please find my questions below. Other Comments Or Suggestions: I don't find any typos. Questions For Authors: There are a few questions that I would like the authors to clarify during the rebuttal. - There is a mismatch between algorithm 1 and the text in lines 171-206. Reward models are simply fine-tuned on a given task with cross entropy loss. However, algorithm 1 seems to be training a reward model that trains on the difference between pre-training model's predictions and the true distribution from the task. In the first scenario, the reward function that will be used in algorithm 2 will be a log ratio of the fine-tuned model's prediction and original pre-trained model's prediction. On the other hand, in second scenario, the reward model can be used directly. Please clarify which version is used in the experiments. Furthermore, please clarify how many models need to be maintained to perform PRT at inference? - In figure 3, why is Instruct's performance lower than others? Isn't Instruct a model that has been fine-tuned on the task itself? Please clarify the differences between FT and Instruct in figures 2 and 3. - In proposition 3.1, when defining r(y\|x), shouldn't $\pi_{\text{ft}}$ be utilized for sampling y, i.e. $E_{y \sim \pi_{\text{ft}}} r(x, y) = 1$? - How is the regularization term applied? Is it simply applying an entropy regularization on the log likelihood ratio between the pre-trained model and the model that is being fine-tuned? What are the differences of this regularization term from the KL divergence loss between the pre-trained model and fine-tuned model's predictions? Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: Thank you for your valuable feedback, and finding our research direction promising. Here we would like to address the questions. > There is a mismatch between algorithm 1 and the text in lines 171-206. Reward models are simply fine-tuned on a given task with cross entropy loss. However, algorithm 1 seems to be training a reward model that trains on the difference between pre-training model's predictions and the true distribution from the task. Sorry for the confusion. We reviewed this part and confirmed there is actually no mismatch. Here let us explain that. From the text, we wrote `The reward model $r_\theta(x,y)$ is trained by simply optimizing the same loss function $L(p, y^)$ as in standard fine-tuning` and the loss function is expanded as $L(p, y) = ... = -\log \pi_\theta (y \| x)$. This description corresponds to line 8 in Algorithm 1. Also importantly, we note that $\pi_\theta (y\|x)$ is defined in eq. (6), as the product of the pretrained model $\pi_\mathrm{pt}(y\|x)$ and the exponential of the reward model $r_\theta(x,y)$. This corresponds to lines 6-7 in Algorithm 1, where we compute the product in the logarithmic space and then take softmax to obtain $\pi_\theta (y\|x)$. Nevertheless, as these correspondences are not explicitly described in the text, we would like to add such annotations in our revised paper. Thank you for pointing out them. > In the first scenario, the reward function that will be used in algorithm 2 will be a log ratio of the fine-tuned model's prediction and original pre-trained model's prediction. On the other hand, in second scenario, the reward model can be used directly. Please clarify which version is used in the experiments. Furthermore, please clarify how many models need to be maintained to perform PRT at inference? (cont.) Here we note that our reward model is expected to play the same role as the log ratio of the two models. In other words, Algorithm 1 automatically learns a single model $r_\theta(x,y)$ that implements this role, and that is the point of PRT. So the answer for the last question is: two models (new pretrained model & reward model) are used in PRT inference, while three models (new pretrained model & old pretrained model & old FT model) are used in the previous work. > In figure 3, why is Instruct's performance lower than others? Isn't Instruct a model that has been fine-tuned on the task itself? Please clarify the differences between FT and Instruct in figures 2 and 3. First of all, let us clarify the differences between FT (in vision experiments) and Instruct (in language experiments). FT means a model fine-tuned and evaluated on the same expert dataset (e.g., Cars, CUB, etc). On the other hand, Instruct means a model fine-tuned on a general dataset (i.e., the instruction-following data) and evaluated on other* expert datasets like math and coding. So the answer for the second question is yes. Thus, the performance of Instruct on each expert benchmark may degrade on some dataset due to implicit bias occurred in insturction tuning. > In proposition 3.1, when defining r(y\|x), shouldn't be utilized for sampling y, i.e. $E_{y\sim \pi_{\mathrm{ft}}} r(x,y) = 1$? Sorry for the confusion. Thanks to this comment, we have noticed a (non-crucial) typo. The probability for sampling y, $\pi_{\mathrm{pt}}$, is actually correct. However, we should write the condition for $r(x,y)$ should be $E_{y\sim \pi_{\mathrm{pt}}} \exp r(x,y) = 1$. Let us also explain about this condition briefly. By the mapping in proposition 3.1, $\pi_\mathrm{ft}$ is mapped to $r(x,y) := \log(\pi_\mathrm{ft}(y\|x) / \pi_\mathrm{pt}(y\|x))$. This satisfies $$E_{y\sim \pi_{\mathrm{pt}}} \exp r(x,y) = \sum_y \pi_{\mathrm{pt}}(y\|x) \exp r(x,y) = \sum_y \pi_{\mathrm{pt}}(y\|x) (\pi_{\mathrm{ft}}(y\|x) / \pi_{\mathrm{pt}}(y\|x)) = \sum_y \pi_{\mathrm{ft}}(y\|x) = 1,$$ i.e., $E_{y\sim \pi_{\mathrm{pt}}} \exp r(x,y) = 1$ rather than $E_{y\sim \pi_{\mathrm{ft}}} \exp r(x,y) = 1$. > How is the regularization term applied? Is it simply applying an entropy regularization on the log likelihood ratio between the pre-trained model and the model that is being fine-tuned? What are the differences of this regularization term from the KL divergence loss between the pre-trained model and fine-tuned model's predictions? The application of the regularization term is as described in eq. (12). The difference between the two KL divergence (eq. (5) and eq. (11)) is an important point. On one hand, KL divergence in eq. (5) measures discrepancy of two distributions over the label/vocabulary space. On the other hand, KL divergence in eq. (11) measures discrepancy of two (meta-)distributions over the set of probability models. As discussed in lines 267-274 and 220-229, since the latter KL divergence is computationally intractable, we proposed the entropy maximization regularization (eq. (5)). --- Rebuttal Comment 1.1: Comment: Hi, Thank you for the detailed responses. I have increased my scores accordingly. --- Reply to Comment 1.1.1: Comment: Thank you very much for taking the time and for your positive evaluation. We also appreciate your detailed feedback in the initial review, which should make our manuscript more precise and easier to follow.	null	null	null	null	null	null	null	null
Nonparametric Identification of Latent Concepts	Accept (poster)	Summary: The paper proposes that when there is an unknown concept-to-class matrix, the concepts can be identified under certain assumptions on the structure of the matrix. Namely, it formalizes in which sense each concept needs to have characteristic classes it belongs to, or vice versa, how every class needs to have characteristic attributes that distinguish it from the other classes. The paper is primarily theoretical, with some synthetical experiments. ## Update after the rebuttal I am raising my score to 3 because $f$ is non-linear (though still bijective), $z$ is continuous, and because of the inclusion of DCI/MIG, FID/PPL, and CUB/AWA experiments. Claims And Evidence: Under the given assumptions, concepts are identifiable * This seems to be theoretically backed, but I did not check the proofs The theoretical identifiability holds in practice * I have doubts here since the experimental setup is very small-scoped, see below. Methods And Evaluation Criteria: The paper uses only one metric to benchmark whether the captured concepts are ground-truth concepts, the ECC. While widely used, there are other popular metrics like the Disentanglement-Completeness-Informativeness score (DCI) or the Separated Attribute Predictability (SAP). It would be more convincing to test on multiple criteria, since they are known to all be noisy and imperfect. The paper does not compare to any baselines, except the base model. All quantiative experiments are only on synthetical datasets. Real datasets only have qualitative plots, without baselines. Theoretical Claims: I do not consider myself an expert in the very nuanced proofs of identifiability / nonlinear ICA, so I abstain from guaranteeing correctness of the proofs. Experimental Designs Or Analyses: Synthetical experiments lack metrics, models, and baseline approaches. The paper lacks quantitative real-life dataset experiments. Supplementary Material: I have read the experiments part of the appendix, I skipped the proof part. Relation To Broader Scientific Literature: The authors make connections between concept learning, nonlinear ICA, and structure learning. Essential References Not Discussed: The paper discusses most of the relevant works in nonlinear ICA. Other Strengths And Weaknesses: Strengths * Bridging concept learning literature with nonlinear ICA / identifiability literature is overdue * There are no distributional assumptions on the latent concepts, in particular no non-Gaussianity (though I am not sure, because the paper seems to exclude fully Gaussian data) Weaknesses * There are very strong assumptions / the space of generative processes this can be used for is very reduced * There is a very strong assumption that the generative process $f$ is bijective. * It may be that $f$ is linear (if it denotes M), though I am not sure, because the spaces that f works in are not defined (class to concept, class to image, image to concept, ...) and no comment on linearity / non-linearity is made * All concepts are binary * There is the structural diversity assumption, and I cannot judge how strong it is. It assumes that for each concept, there exists at least one class that has it (so far so good) and there exists a set of classes that does not have it, and this concept is the only concept that is not found in any of these classes. I understand that this prevents block matrices (which are by default non-identifiable) but cannot judge how many other realistic matrices it assumes away. * The experiments are on only one model, with one evaluation metric, and only on synthetical datasets (all evaluations on the real-life datasets are purely qualitative and without a baseline). It can thus be very overfitted to that setup, since, as put in the appendix “We generate the data following the process outlined in our theorems.”. Showing that the approach works on a synthetical setup which exactly follows its the paper’s assumptions is not a very general result, especially when the assumptions are as strict as in this paper. * The experiments do not compare to any baseline approaches, except the base model, see also below. * Code is not provided. Score justification: The paper seems to make progress on the exact matrix structure that is needed to allow identifiability, but I cannot quite judge how much it differs from current approaches since I know enough about ICA to not consider myself an expert. Hence, in terms of novelty and theoretical contribution, the score can be anywhere between 2-4. I am currently more on the sceptic end of this range for two reasons: 1) I believe the assumptions are rather strong / the applicability is limited to binary matrices (since f needs to be bijective and M binary). This is understandable for structure learning, but limiting for concept learning. I hope that the other reviewers can comment on the strength of the assumptions and novelty over previous approaches. 2) the experiments are very limited, to one evaluation metric and one model and only on synthetical datasets that exactly follow the assumptions the approach exploits. This limits the generality of the results. More results, as outlined above and below, can convince me otherwise here. Post rebuttal score: I have raise to score 3 due to the additional experiments and due to clarifications on the assumptions, which are still restrictive, but not as restrictive as I initially believed. Other Comments Or Suggestions: I did not find typos or formatting issues. Questions For Authors: If I understand correctly, your approach should work quite well on attribute-based classification, such as on CUB or AwA2? There you have a (binarizable) attribute-per-class matrix. Can you comment on whether it applies, and test your algorithm on it? This would help judge if it works in higher dimensions. I am concerned about how far the results span in terms of width of generative processes covered. Could you compare to the following two neighboring approaches (https://openreview.net/pdf?id=mGUJMqjDwE, https://proceedings.mlr.press/v216/leemann23a/leemann23a.pdf) in structural identifiability in terms of... * Theoretical scope, i.e., the assumptions placed on the generative process to guarantee identifiability * Practical applicability, i.e., which datasets it can currently discover concepts on Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We are genuinely grateful for your insightful comments. In light of these, we have introduced new experiments (https://anonymous.4open.science/r/0-518C/rebuttal_new_results.pdf) and new discussions. Please find our detailed response below: Q1: Strong assumptions / limited generative process space. A1: Thank you so much for the comment. It seems we may not be fully aligned on the core setting and assumptions. We sincerely appreciate the opportunity to clarify the following: - Q1.1: There is a very strong assumption that the generative process $f$ is bijective. A1.1: As defined in L129-136 left, $f$ is an unknown diffeomorphism onto its image—a very standard assumption in identifiability literature (e.g., most works mentioned in the survey [Hyvärinen et al. 2024]). It aligns with the manifold hypothesis, which posits that high-dimensional data (e.g., pixels) lie on a lower-dimensional latent manifold (e.g., concepts). In overcomplete settings (latent dim > observed dim), much stronger assumptions (e.g., linearity) are typically required. - Hyvärinen et al., Identifiability of latent-variable and structural-equation models: from linear to nonlinear, 2024 - Q1.2: $f$ may be linear (if it denotes $M$); unclear spaces that $f$ maps between. A1.2: Thanks for raising this. To clarify, $f$ and $M$ are unrelated. - As defined in L113–121 left, $f$ maps latent concepts $\mathbf{z}$ to observations $\mathbf{x}$ (Eq. 1: $\mathbf{x} = f(\mathbf{z})$) and is a general diffeomorphism, without any linearity constraint. - As defined in L159 left–133 right, $M$ is a binary structural mask between classes $\mathbf{c}$ and concepts $\mathbf{z}$, independent of $f$. - Q1.3: All concepts are binary. A1.3: As defined in L116 left, all concepts are continuous variables ($\mathbf{z} \subseteq \mathbb{R}^{n}$), with no restriction to binary values. - Q1.4: Unclear how strong the structural diversity is. A1.4: Thank you for the great question. In a general nonparametric setting (no functional/distributional constraints), identifiability is known to be ill-posed without additional assumptions. Structural diversity characterizes when every concept is identifiable in such settings. It is expected that ambiguous cases must be excluded, as in most prior identifiability theories. A key contribution of our work is going beyond this assumption. The local comparison framework (Thm. 1, Prop. 1) provides identifiability guarantees even when global condition is violated—allowing recovery of many concepts as groups (e.g., in FFHQ). In contrast, most prior work cannot provide any guarantees under any degree of violation. In light of your question, we have also added new experiments under partial violations (Figs. 1–2 in the link), confirming empirical robustness. Q2: Additional metrics for synthetic and real-world datasets. A2: Great suggestion. In light of it, we have added evaluations on DCI and Mutual Information Gap (MIG) for synthetic datasets (Figs. 1–2 in the link), and Fréchet Inception Distance (FID) and Perceptual Path Length (PPL) for real-world images (Table 1 in the link). Our method consistently outperforms baselines. Q3: More baselines. A3: Thanks for your advice. We have added two more baselines (Table 1 and Figs. 7-8 in the link), further supporting the effectiveness. Q4: Code is not provided. A4: Thanks. Due to rebuttal policy, we can only include figures in the link. Based on the flow-based method (L1372), we added an ℓ₁ norm (L369 right) since ℓ₀ norm is known to be indifferentiable. Q5: Test on CUB or AwA2. A5: Thank you for the advice. We have conducted new experiments on both datasets (Figs. 5–8, Table 1 in the link), showing that identifiable concepts remain recoverable. With these additions, we now have seven different real-world datasets to support the practical applicability. Q6: Comparison with two related papers. A6: Thanks for the suggestion. Please find the detailed comparison below: - Brady et al., 2023: (This work has been discussed in the introduction (L62-76 left).) - *Theory:* Assumes each observed variable (pixel) maps to only one latent slot. - In contrast, we allow arbitrary mixing. - *Practice:* Targets recovering concrete objects as pixel groups, assuming no occlusion or overlap among them. - In contrast, we focus on general concepts (concrete or abstract), with no constraints on observed object composition. - Leemann et al., 2023: - *Theory:* Assumes linear generative process or orthogonal Jacobians. - In contrast, we allow general nonlinear generative process, where the identifiability is much harder. - *Practice:* Targets post-hoc explanation assuming access to linear combinations of latent factors. - In contrast, we focus on general concept learning from observation in a nonparametric setting. --- Rebuttal Comment 1.1: Comment: Thank you for clarifying the points. I am raising my score to 3 because $f$ is non-linear (though still bijective), $z$ is continuous, and because of the inclusion of DCI/MIG, FID/PPL, and CUB/AWA experiments. --- Reply to Comment 1.1.1: Comment: Thank you very much for your kind encouragement! We're delighted that your concerns have been addressed. We deeply appreciate your time, thoughtful feedback, and valuable suggestions, which have greatly helped us improve our manuscript.	Summary: The paper studies the identifiability of latent concepts. The key assumption is that we observe class labels $c$ and observations $x$ which are mediated through concepts $z$, i.e., $c\to z\to x$ and they in addition allow for class independent features. Then they show that the difference in concepts for different classes can be identified and under a diversity condition the class dependent features are identifiable and the remaining features are block identifiable. Then they conduct experiments on synthetic and real data using established methods to investigate their identifiability results. ## update after rebuttal As explained in the rebuttal comment, I maintain my (overall positive) opinion Claims And Evidence: The key contributions of the paper are theoretical, see below. Methods And Evaluation Criteria: Yes, the datasets make sense, for evaluation see below. Theoretical Claims: The results generally seem plausible. However, I have one question/complaint. The treatment of the $\theta$ variable is a bit unclear. So the initial relation $(4)$ is clear. But then a relation for $g$ is used in (5) but $g$ is not injective and depends on $\theta$. In my opinion this part needs to be clarified. I did not check the rest of the argument in detail but it seems to follow the standard arguments. Experimental Designs Or Analyses: My understanding is that the authors do the following: They use (up to minor changes) a method from prior work and the comparison is not to another method but to a setting where their assumptions are violated. Is this correct? In this case (especially the second part) should be made a bit clearer in the text. Supplementary Material: I skimmed through the proofs and read the additional information on the experiments. Relation To Broader Scientific Literature: The specific setup of the paper is novel to my knowledge and I find it quite convincing, essentially it seems to be, loosely spearking, a combination of the iVAE paper with structural sparsity. The theoretical results are also new, but the used techniques date back to the first works on identifiability of linear ICA and the iVAE work and the sparsity approaches have also similarly appeared before. Essential References Not Discussed: One could consider citing more works from the causal representation learning literature that relies on similar techniques, but the key original works seem to be cited. Other Strengths And Weaknesses: Strengths: The paper is well motivated and overall well written. The examples are well-chosen, and it combines a setting of relevance (concept learning) with rigorous theoretical results that rely on reasonable assumptions. In particular, the results do not rely on parametric assumptions which makes them quite general. The discovered concepts in the experiments are quite convincing. Weakness: The technical novelty is limited. The experimental methodology is not new. The results require quite some supervision (class labels) this is a weakness compared to some existing work. Other Comments Or Suggestions: l 117 left: There seems to be something missing. The set $A$ and the matrix $M$ should be related explicitly $\theta$ in Definition 1 is a abuse of notation because $\theta$ was used before l.197 Definition of $T$ is unclear. Do you define $\mathbf{T}$ by the equation that follows? Make this clearer Proposition 1 might be renamed to Corollary 1 l 266 left: This is hard to understand, do you mean 'and which cannot be expressed as'? Do you allow singular distributions on $z_A$? l 360 right: How exactly are the $c^{(i)}$ created? What is a multi-hot vector? Is is sufficient to use one-hot vectors? Learning by comparison could be connected closer to the experimental methodology and the literature Questions For Authors: See theoretical claims and experimental design. Depending on the answer to the former my assessment would change. Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: We deeply appreciate your valuable insights. In light of these, we have carefully added several new discussions and conducted new experiments (https://anonymous.4open.science/r/0-518C/rebuttal_new_results.pdf). Please find our detailed responses below: Q1: More clarifications on Eq. 5. A1: Thanks for your suggestion, we have added further clarifications accordingly. $\mathbf{T}$ in Eq. 5 is invertible because the mapping $t$ is invertible. The invertibility of $t$ follows from Eq. 4 (L743-746), independent of $g$. Eq. 5 simply represents the derivatives w.r.t. $\mathbf{c}$, and $\theta$ denotes other factors independent of $\mathbf{c}$. Q2: Is the comparison based on the same method under violated assumptions? A2: Yes. The estimation method (previous work + regularization) is unchanged; only the data-generating process is altered to violate structural conditions (L407 left). We have now emphasized this more explicitly in light of your great question. Q3: The technical relation to previous methods such as iVAE and sparsity approaches. A3: Thanks a lot for the insightful comment. iVAE (and related methods) require sufficient distributional change (e.g., $2n+1$ environments), while we focus on how classes affect concepts—structure, not magnitude, of change. Our theory is closer in spirit to sparsity-based methods, as both leverage structural relationships. However, there are two key differences: - We study class–concept structures, while prior work focuses on concept–measurement structures. This relaxes assumptions on mixing function by weak supervision from class labels. - Our pairwise comparison framework supports identifiability under partial violations, unlike prior work that requires full structural assumptions. We hope this makes the distinctions clearer and would be more than happy to further refine it based on your feedback. Q4: Possible missingness in L117 left. A4: Thanks. We were not certain we understood correctly, so we assumed you suggested moving L124-125 ($p(\mathbf{z}\|\mathbf{c}) = p(\mathbf{z}_A\|\mathbf{c}) p(\mathbf{z}_B)$, $\mathbf{z}_A \coloneqq g(\mathbf{c}, \theta)$) alongside L117 (Eq. 1). We've made this change, but please let us know if this wasn't your intention. Q5: The set $A$ and the matrix $M$ should be related explicitly. A5: Thank you–we now explictly highlight that $A_i$ is the support of $M_{i,\cdot}$ in the updated manuscript. Q6: Abuse of notation with $\theta$ in Defn. 1. A6: Addressed—we removed $\theta$ in Defn. 1, keeping only $(g, p_{\mathbf{z}}, M)$, and likewise for $\theta’$. Thanks for raising this. Q7: More clarification on $\mathbf{T}$ and $\mathrm{T}$. A7: Thank you for your suggestion. We have added further highlights as follows: - $\mathbf{T}$: a matrix-valued function in $D_{\mathbf{c}} \hat{g} = \mathbf{T} D_\mathbf{c} g$. - $\mathrm{T}$: a matrix with the same support as $\mathbf{T}$. Q8: Rename Prop. 1 to Cor. 1. A8: Thanks, we have renamed it accordingly. Q9: L266 left — Do you mean “and which cannot be expressed as”? Do you allow singular distributions? A9: Thanks for the suggestion. We meant “and which cannot be expressed as” and have revised the wording. The condition excludes singular distributions by requiring the subset $A_{\mathbf{z}} \subseteq \mathcal{Z}$ to have non-zero probability measure. Q10: L360 right — How exactly are the $\mathbf{c}^{(i)}$ created? What is a multi-hot vector? Is it sufficient to use one-hot vectors? A10: Thank you for the great suggestions. Accordingly, we have added a detailed explanation in the updated manuscript. Specifically, $\mathbf{c}^{(i)}$ denotes the classes of sample $i$: a one-hot vector if single-labeled, or a multi-hot vector if multi-labeled (e.g., $[0,1,1]$ for two active classes). Q11: Learning by comparison could be connected closer to the experimental methodology and the literature A11: Thanks for the helpful advice. We have rewritten L82–99 left for closer grounding: > We address this question by grounding our approach in a fundamental cognitive mechanism: humans learn concepts by contrasting diverse classes of observations. Classic studies have shown that concept formation relies on detecting distinctions across examples—Bruner et al. (1956) emphasized learning through contrasts between exemplars and non-exemplars; Gibson (1963, 1969) proposed differentiation as a basis of perceptual learning in infants; and Gentner & Namy (1999) demonstrated that direct comparison enables children to abstract category-defining features. This principle is further supported by extensive literature across cognitive science, reinforcing that learning by comparison is the key underlying engine. Experimentally, FFHQ (Figs. 13–15) illustrates the need for local comparisons due to entangled concepts. We also added new experiments on two new datasets (see anonymous link), in light of your great insights. --- Rebuttal Comment 1.1: Comment: - There is no need to praise any minimal suggestion. - There was a typo in the review: There is a typo in line 147 left (at least missing bracket), not in 117, please apologize. - After reading the rebuttal and the other reviews, I still think that this is overall a solid contribution. --- Reply to Comment 1.1.1: Comment: Thank you for the clarification—indeed, L147 left should read $\operatorname{supp}(\mathbf{S}) \coloneqq \\{(i,j) \mid \exists \theta \in \Theta, \mathbf{S}(\theta)_{i,j} \neq 0 \\}$. We appreciate your feedback and are glad you consider the contribution solid.	Summary: This paper proposes a nonparametric framework for identifying latent concepts by leveraging structural diversity across observation classes, inspired by human cognitive mechanisms of learning through comparison. The authors establish theoretical guarantees for concept identifiability without relying on parametric assumptions about concept types, functional relationships, or generative models. Key contributions include: 1. Pairwise and local comparison theorems (Thm. 1, Prop. 1) showing that unique concepts in classes can be disentangled when sufficient diversity exists. 2. Global identifiability (Thm. 2) under structural diversity conditions, recovering class-dependent concepts up to permutation/element-wise transforms. 3. Structure recovery (Prop. 3) of class-concept relationships. 4. Empirical validation on synthetic data and real-world datasets (Fashion-MNIST, AnimalFace, FFHQ), demonstrating alignment between identified concepts and semantic attributes. ## update after rebuttal Thanks for the authors' rebuttal which addressed my concern. So I increase my score to clear accept. Claims And Evidence: The proofs for Thm. 1 (pairwise disentanglement) and Thm. 2 (global identifiability) were examined. While the linear algebra arguments and Jacobian-based reasoning are logically structured, two concerns arise: - Thm. 1 assumes linear independence of Jacobian vectors (Eq. 6). The proof does not address whether this holds in high-dimensional spaces or under noisy observations, potentially limiting practical applicability. - Thm. 2 relies on the structural diversity assumption (Assump. 1), which requires each concept to be uniquely tied to a class subset. The proof does not quantify how often this condition fails in real-world scenarios (e.g., overlapping concepts like "furry" for cats/dogs). Methods And Evaluation Criteria: Methods: The nonparametric framework is novel and well-motivated by cognitive mechanisms. However, the paper does not provide an explicit algorithm for estimating concepts (e.g., how to enforce ℓ0ℓ0 regularization in practice). This limits reproducibility. Evaluation: - Synthetic experiments validate identifiability under ideal conditions but do not test robustness to structural assumption violations (e.g., partial failures of Assump. 1). - Real-world evaluations rely on qualitative interpretation (e.g., heatmaps in Fig. 8–9) without quantitative metrics for concept interpretability (e.g., concept-accuracy scores via human trials or downstream tasks). - The MCC metric measures alignment but does not assess disentanglement quality (e.g., mutual information between recovered concepts). Theoretical Claims: I checked the correctness of proofs. All proofs are correct. Experimental Designs Or Analyses: Experiments on synthetic data validate identifiability under controlled structural conditions. However: - Real-world results (e.g., FFHQ in Fig. 13–15) show entangled concepts (e.g., "age" involving skin/eyes), yet the paper claims partial identifiability via local comparisons. This discrepancy is not rigorously analyzed. - Baseline comparisons (e.g., "Base" models) lack details on architecture/optimization parity, raising questions about fairness. - The MCC metric measures alignment but does not assess semantic interpretability, a critical aspect of concept learning. Supplementary Material: The appendix was reviewed, including: - Proofs: Detailed derivations for Thm. 1–2 and Prop. 1–3 (Appx. B). While comprehensive, some steps (e.g., Eq. 82–83 in Thm. 2) lack intuitive justification. - Additional experiments: Extended results on EMNIST/FFHQ (Figs. 12–15) highlight entangled concepts but do not address mitigation strategies. Relation To Broader Scientific Literature: The work extends identifiability theory in concept learning, contrasting with parametric approaches (e.g., linear ICA [Hyvarinen & Morioka, 2016], additive models [Lachapelle et al., 2023]). It aligns with cognitive-inspired methods [Brady et al., 2023] but diverges by eliminating parametric constraints. The structural diversity condition parallels sparsity assumptions in nonlinear ICA [Zheng et al., 2022], though the focus on class-concept relationships is novel. Essential References Not Discussed: No essential references are not discussed. Other Strengths And Weaknesses: see above. Other Comments Or Suggestions: 1. Include a discussion on how structural diversity could be measured/validated in practice (e.g., via concept-class mutual information). 2. Compare with concurrent work on concept bottlenecks (Delfosse et al., 2024) to highlight differences in identifiability guarantees. 3. Release code for reproducibility, especially for Jacobian regularization and synthetic data generation. Questions For Authors: The questions are listed above. Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: We are profoundly thankful for your insightful feedback. In light of it, we have included new discussions and conducted new experiments (https://anonymous.4open.science/r/0-518C/rebuttal_new_results.pdf). Please find our point-by-point responses below: Q1: Thm. 1 in high-dimensional space or under noisy observations. A1: Thank you for the question. Theoretically, the assumption only requires Jacobians to be linearly independent at some points to ensure meaningful variation—which can be expected from large populations. We have also added new experiments in light of your suggestions: - High-dimensional space: Beyond the five image datasets used before, we added two more (Figs. 5–8, Table 1 in the link). Since images are naturally high-dimensional, these results across seven datasets support applicability in such settings. - Noisy observations: We added experiments with noisy images (Figs. 3-4 in the link), showing meaningful concepts remain identifiable. Q2: Practical applicability of structural diversity. A2: Thanks for the suggestion. We have added new experiments under partial violations (Figs. 1–2 in the link), showing robustness. Intuitively, if a concept (e.g., “furry”) is absent in some classes, it can be disentangled. If all classes share it, it is unidentifiable under Thm. 2. However, our local comparison framework (Thm. 1, Prop. 1) still ensures identifiability even without global structural diversity. Q3: Reproducibility details for Jacobian regularization and synthetic data. A3: In light of your suggestion, we have highlighted details further in the updated version. Due to the rebuttal policy, we can only include figures in the anonymous link. We approximate ℓ₀ regularization with an ℓ₁ norm (L369 right) since ℓ₀ norm is known to be indifferentiable. We use a flow-based estimator (Sorrenson et al., 2020) to recover latent concepts (L365–367 right), though our theory is estimator-agnostic—as long as the observed distribution is matched and regularization applied. For synthetic data, we randomly construct a class-concept structure satisfying our conditions and sample each latent variable conditioned on its class labels. Q4: Suggestions on empirical evaluations. A4: Thank you so much. We added the following new experiments accordingly: - Q4.1: Partial violation of structural diversity. A4.1: Evaluated in Figs. 1–2 in the anonymous link; results show robustness. - Q4.2: Quantitative metric for real-world evaluations. A4.2: We added Fréchet Inception Distance (FID) and Perceptual Path Length (PPL). As shown in Table 1 in the link, ours consistently outperforms baselines. - Q4.3: More metrics for simulation. A4.3: We added DCI score and Mutual Information Gap (MIG) (Figs. 1–2 in the link); same conclusion holds. Q5: Entangled concepts on FFHQ. A5: Thanks for your question. Learning by local comparisons focuses on the unique part of each class (e.g., a group of dependent concepts), enabling partial identification even when full disentanglement is impossible. FFHQ illustrates this: despite global violations, concept groups remain identifiable (L1460–1467). In addition to the full identifiability (shown in other datasets), this partial identifiability is also one of our main focuses. Q6: Baseline comparisons lack details. A6: Thanks. As noted in L407 left, all models share the same setting except the data-generating process. We have highlighted this further in the updated manuscript. Q7: Some steps (e.g., Eqs. 82–83) lack intuition. A7: Thank you—we have added more intuition accordingly. For any $i \in \\{1,\ldots,n_A\\}$ and $v \in \\{1,\ldots,n_A\\} \setminus i $, $(\pi(i), v) \notin \mathcal{T}$ (apologies for a typo—$k$ in L1053 should be $v$) implies that all entries in row $\pi(i)$ of matrix $\mathrm{T}$ are zero except possibly at index $i$. Since $\mathrm{T}$ is inveritble, each row must have a non-zero entry, implying $(\pi(i), i) \in \mathcal{T}$. Q8: Measuring structural diversity in practice. A8: Thanks for the excellent point. We have added a discussion in the updated version. Structural diversity can be assessed via concept–class mutual information (as you kindly suggested) and domain knowledge (e.g., “sunshine” may be universal, “furry” is class-specific). Even if violated or unsure, our local comparison framework ensures alternative identifiability. Q9: Compare with Delfosse et al., 2024 on differences in identifiability guarantees. A9: Thanks for the suggestion. For Delfosse et al. (2024), did you mean “Interpretable concept bottlenecks to align reinforcement learning agents”? We are not sure if we understood correctly, as we did not find identifiability theories in that paper. Please let us know if we missed or misunderstood anything—we would be more than happy to include a discussion accordingly.	Summary: The authors tackle the important problem of identifying latent classes from data. They claim that given some constraints, it should be possible to do given that different classes (e.g. different animals), will produce different sets of observable concepts (i.e. different shapes, colors, etc); and that as long as there is at least one difference, it should be possible to identify them. The formalize these notions via several theorems and definitions. Finally, they validate these empirically by fitting simple non-parametric matrices corresponding to each pair of class and related concepts. Specifically, they fit a sparse model that attempts to fit concepts that are generated according to their theoretical assumptions by each class. The compare these to other data generating mechanisms that are entangled or do not have sparse structure and show they are harder to fit. Claims And Evidence: Yes. The authors theoretically define their model and compare it empirically to one that does not follow their regularization schemes. Methods And Evaluation Criteria: Yes. The authors extensively test their theoretical approach on several datasets. Theoretical Claims: I didn't check all the theorems. Some are intuitive, while I admit that others are a bit hard to follow given the notation. For example, theorem 2 and the corresponding figure (Figure 4), were not completely clear to me. Experimental Designs Or Analyses: For the most part yes. The simple toy experiments are easy to follow. I have questions about the real world datasets. Specifically, what models did the authors use? I could not find this. Supplementary Material: Only skimmed it. Mostly focused on the last section with real-world dataset. Relation To Broader Scientific Literature: I think the authors do a good job to refer to the related literature. I feel like some of their theoretical claims are very similar to previous work, especially in the ICA literature, but they are very thorough about formalizing their ideas. Essential References Not Discussed: Not that I can think of. Other Strengths And Weaknesses: The main strength of the paper is rigorous the authors try to be. I don't know if all the theorems are correct though. Main weakness is that for the real world datasets it is not clear how the concepts related to each class are extracted. A common story I see in these articles is that they abstract away the process of extracting the relevant entities (in this case the class-related concepts) and operate directly on those. If that is what's happening here then that makes the whole article much less useful since part of what makes this task hard is that we need to extract these concepts from raw input. Other Comments Or Suggestions: I suggest the authors re-write the paragraph in lines 82-92. If two classes of observations share an identical set of concepts are they really two different classes? It seems like the very set of concepts in the observation is what defines a class (from the perspective of the AI/Human) and not the other way around. To put it another way, if the observations are really generated by different classes, eventually they should differ, if they don't they are effectively the same (assuming we can observe the differences). Also, add a reference from the cogsci literature to the actual mechanisms you are taking inspiration from. I really like that the authors explain the intuitions behind their theorems and definitions. My only suggestion would be to introduce these intuitions first and the theorems later. A general structure could be: "Intuitively, structural diversity is important ...." and then "We can formalize this notion through theorem ....". I feel like this is a more natural way to read things than just suddenly having to wade through formulas. Questions For Authors: Can you provide more details about the models used to test on real world data? Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: We sincerely appreciate your constructive feedback. Accordingly, we have included several new discussions in the updated version. Please see our point-by-point responses below: Q1: More intuition on Theorem 2 and Figure 4. A1: Thanks for the suggestion. We have added more discussion in the revised version. Theorem 2 guarantees the identifiability of each class-dependent concept under the structural diversity condition. Figure 4 illustrates this condition: for example, for concept $\mathbf{z}_1$, there exist classes $\mathbf{c}_1$ and $\mathbf{c}_3$ s.t. $\mathbf{z}_1$ is unique to $\mathbf{c}_1$, allowing that concept to be disentangled. Meanwhile, class-independent concepts can also be disentangled as a block by leveraging distributional variety. Q2: What models did the authors use for the real-world datasets? A2: Thanks for the question. We used a general incompressible-flow network (GIN) following Sorrenson et al., 2020, with an additional sparsity regularization (L365-370 right). We have further highlighted this in the updated manuscript according to your constructive comments. Q3: Relation of theoretical claims with previous work, especially in the ICA literature. A3: Thank you for the insightful comment. We truly appreciate the opportunity to further illustrate how our theoretical results relate to prior work. While Thm. 2 shares ICA’s goal of identifying latent variables, it differs in assumptions, techniques, and scope. We would be very grateful for any further feedback if any part of the following differences is unclear or could be better articulated. - *Objective:* While ICA aims to recover all latent variables individually, our focus is on identifying which concepts are reliably recoverable, grounded in the cognitive process of comparison. Our main contribution lies in learning by local comparisons—showing that unique concepts can be disentangled from any class pair. This naturally extends to global identifiability (Thm. 2), but the local view enables more flexible, practical analysis. In contrast, most previous work in ICA cannot provide any guarantee with partial violation of their assumptions for some latent variables. - *Techniques:* ICA methods are built on elegant and powerful assumptions—such as auxiliary variables or sparse mixing—that enable strong identifiability results. For example, iVAE needs more than 2n+1 environments with sufficiently varying distributions; sparsity-based methods assume sparse concept–observed mixing structure. Our method avoids these by relying on class–concept structures, offering partial identifiability when global assumptions may not fully apply. In summary, our theory targets a different question: determining which concepts are identifiable under minimal, localized assumptions. We do not claim generality over ICA, but rather provide complementary insights, especially in settings where global assumptions may be partially violated. Q4: How to extract the concepts from raw input? A4: Thank you for the great question, and we have added more details in the updated version. After estimation (detailed in A2), we recover a latent vector from observed data and class labels. Each dimension of this vector corresponds to a concept. To aid interpretation, we rank dimensions by their variances—based on the heuristic that higher-variance components are often more semantically meaningful. Q5: Rewrite the paragraph in lines 82-92, and add a reference from the cogsci literature. A5: Thanks so much for the great suggestion. We have rewritten the paragraph as follows and added a line of references. > We address this question by grounding our approach in a fundamental cognitive mechanism: humans learn concepts by contrasting diverse classes of observations. Classic studies have shown that concept formation relies on detecting distinctions across examples—Bruner et al. (1956) emphasized learning through contrasts between exemplars and non-exemplars; Gibson (1963, 1969) proposed differentiation as a basis of perceptual learning in infants; and Gentner & Namy (1999) demonstrated that direct comparison enables children to abstract category-defining features. This principle is further supported by extensive literature across cognitive science, reinforcing that learning by comparison is the key underlying engine. --- References: Bruner, J. S., Goodnow, J. J., & Austin, G. A. (1956). A Study of Thinking. Wiley. Gibson, E. J. (1963). Perceptual learning. Annual Review of Psychology. Gibson, E. J. (1969). Principles of perceptual learning and development. Appleton-Century-Crofts. Gentner, D., & Namy, L. L. (1999). Comparison in the development of categories. Cognitive Development. --- Q6: Move intuitions before the theorems. A6: Thank you very much for the helpful suggestion. We have revised the layout accordingly, placing the intuitions before the theorems for better flow.	null	null	null	null	null	null
Comparing Few to Rank Many: Active Human Preference Learning Using Randomized Frank-Wolfe Method	Accept (poster)	Summary: This paper considers an N-item-ranking problem with K-way comparisons, where K<<N. The goal is to determine the optimal K-subset selection strategy to minimize the worst-case ranking error. Previous approaches to this problem are computationally infeasible due to the exponentially large number to consider. To address this, the authors propose an improved Frank-Wolfe algorithm that incorporates randomization, memorization, and sparse updates, making the computation tractable. Claims And Evidence: The claims in the paper are thoroughly supported at both the theoretical and experimental levels. Methods And Evaluation Criteria: Yes. Theoretical Claims: No mistakes were found in the proofs. Experimental Designs Or Analyses: The experiments include two small-scale text retrieval datasets and one LLM alignment dataset, along with multiple baselines, both synthetic and real feedback settings. The appendix also provides additional ablation experiments and runtime comparisons. I believe the experimental setup is thorough and reliable. Supplementary Material: I have reviewed the appendix. Relation To Broader Scientific Literature: The key contribution is related to the K-way feedback selection strategy in N-item ranking problems, which is highly relevant to RLHF and LLM alignment. Essential References Not Discussed: No. Other Strengths And Weaknesses: Strengths: - The paper is well-written, with a clear and rigorous logical structure. Despite the extensive mathematical theory, it remains easy to follow. - The theoretical section is very thorough, with both theoretical and experimental evidence supporting the claims, making the results highly credible. - The problem addressed by the paper is highly meaningful, and DopeWolfe makes the previously intractable algorithm with exponential computational complexity practically usable. Weaknesses: - If the paper included experiments on RLHF fine-tuning with LLMs, it would enhance the practical applicability and make the paper's findings more convincing. Other Comments Or Suggestions: - page 15, line 3, missing citation. - page 7, section 6.1, line 5, missing reference. Questions For Authors: I have no questions. Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: We want to thank the reviewer for a positive review, and recognizing both benefits and shortcomings of our paper. Our rebuttal is below. We will incorporate all comments of the reviewer in the next version of our paper. If you have additional concerns, please reach out to us to discuss them. We agree with the reviewer that LLM experiments would increase the appeal of the paper. However, we could not conduct them due to limited computational resources. To further support our claims and partially address your comment, we contacted Mukherjee et al. (2024) and implemented DopeWolfe on the Anthropic RLHF dataset in their paper. The plot of the experiment is at [Anthropic plot](https://anonymous.4open.science/r/DopeWolfe-ICML-anon-1AD6/DopeWolfe_Anthropic_ICML_rebuttal.png). We observe that the ranking losses of DopeWolfe and Dope are comparable. This means that DopeWolfe beats all baselines in Mukherjee et al. (2024). However, in terms of the wall-clock time, DopeWolfe is about $4$x times faster than Dope ($6.046$ seconds on average versus $24.924$). See Section Additional Baselines of the rebuttal to Reviewer Z4RR for more details.	Summary: This paper investigates how to select the optimal data points to learn the ground-truth reward model in RLHF. Specifically, compared to previous work [1], this paper extends the result from learning the ranking of $K$ actions from $K$-way feedback to learning the ranking of $N\geq K$ actions from $K$-way feedback. [1] Mukherjee, Subhojyoti, et al. "Optimal design for human preference elicitation." Advances in Neural Information Processing Systems 37 (2024): 90132-90159. Claims And Evidence: Yes. The proof sketch is clear and convincing to me. Methods And Evaluation Criteria: The synthetic feedback and real feedback seem to be reasonable. Theoretical Claims: I checked the proof sketch in the main text but did not go through the proof in the appendix. The proof seemed to make sense according to the proof sketch in the main text. Experimental Designs Or Analyses: I've checked Section 6 and it sounds reasonable to me. Supplementary Material: No. Relation To Broader Scientific Literature: This paper could complement previous papers about how to compute the ground-truth reward from a dataset of rankings, such as [2]. Specifically, the previous paper considers how to compute the reward form a given dataset, while this paper focuses on how to collect the data to make the computation efficient. [2] Zhu, Banghua, Michael Jordan, and Jiantao Jiao. "Principled reinforcement learning with human feedback from pairwise or k-wise comparisons." International Conference on Machine Learning. PMLR, 2023. Essential References Not Discussed: I do not find any essential references not discussed. Other Strengths And Weaknesses: Compared to [1], this paper does not include the scenario when multiple lists exist. [1] Mukherjee, Subhojyoti, et al. "Optimal design for human preference elicitation." Advances in Neural Information Processing Systems 37 (2024): 90132-90159. Other Comments Or Suggestions: There is a missing reference on lines 358-359. Questions For Authors: Compared to [1], may you also compare the baselines including Dope, Avg Design, Clustered Design, and APO? Additionally, I would appreciate a comparison in the Anthropic dataset [3] used in [1]. I would raise the score if the authors could provide additional experiments. [1] Mukherjee, Subhojyoti, et al. "Optimal design for human preference elicitation." Advances in Neural Information Processing Systems 37 (2024): 90132-90159. [3] Bai, Yuntao, et al. "Training a helpful and harmless assistant with reinforcement learning from human feedback." arXiv preprint arXiv:2204.05862 (2022). Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We want to thank the reviewer for acknowledging the contributions of our work and putting it in the context of prior works. Our rebuttal is below. We focus on major issues and will incorporate all comments of the reviewer in the next version of our paper. If you have additional concerns, please reach out to us to discuss them. ### We Do Not Handle Multiple Lists This is a writing issue. We sketch how to represent multiple lists in the last paragraph of Section 2. However, we failed to explicitly state that the algorithm remains unchanged when solving such problems. This is because it does not matter how the plausible subsets of items in DopeWolfe arise. They can be $K$-subsets of a single list or multiple. In fact, we already conducted an experiment like this in our paper. The Nectar dataset in Section 6.1 has $30000$ lists, each with $7$ choices. For $K$-way comparisons, we optimize over $30000 {7 \choose K}$ subsets of items. This is what $K = 2$ and $K = 3$ in Figure 1 are. Even for $K = 2$, this is $630000$ subsets and two orders of magnitude more than in Mukherjee et al. (2024). We describe this in lines 949-953 (Appendix D.1). ### Additional Baselines To alleviate your concerns about the lack of comparison to Dope and baselines in Mukherjee et al. (2024), we contacted Mukherjee et al. (2024) and obtained their code. The code differs from their paper as follows: * Dope is implemented using the Frank-Wolfe method where the linear maximization oracle (LMO) is a linear program. * The Nectar experiment is on $500$ lists. The code crashes for $2000$ lists used in Mukherjee et al. (2024) and they did not resolve this issue before we submitted this rebuttal. We implemented DopeWolfe in their code base as follows: * LMO is solved greedily, as in (8), on 10% of randomly sampled subsets of items. * Line search is implemented using golden-section search. The plots for the Anthropic and Nectar experiments are at [Anthropic plot](https://anonymous.4open.science/r/DopeWolfe-ICML-anon-1AD6/DopeWolfe_Anthropic_ICML_rebuttal.png) and [Nectar plot](https://anonymous.4open.science/r/DopeWolfe-ICML-anon-1AD6/DopeWolfe_Nectar_ICML_rebuttal.png), respectively. We observe that the ranking losses of DopeWolfe and Dope are comparable. This means that DopeWolfe beats all baselines in Mukherjee et al. (2024). However, there is a difference in the wall-clock time: * Anthropic: DopeWolfe is about $4$x times faster than Dope ($6.046$ seconds on average versus $24.924$). * Nectar: DopeWolfe is about $3$x times faster than Dope ($0.571$ seconds on average versus $1.826$). --- Rebuttal Comment 1.1: Comment: Thank you for your response! I will raise the score to 3.	Summary: This paper focuses on the problem of RL using human ranking feedback. In particular, the goal is to learn the ranking of N items using K-way ranking feedback. To solve such a problem in an active learning fashion, the learner needs to first compute a design via Frank-Wolfe (FW), sample queries according to the design, estimate utility for each item, and estimate the ranking. Previous work by Mukherjee et al. (2024) solved the problem where N=K. This paper extends Mukherjee et al. (2024) to the case when N>>K. The key challenge in this extension is that the FW gradient has a dimension of (choose N K), which is computationally challenging for modern computers. There are 2 contributions: (1) analyzing the ranking loss by extending Mukherjee et al. (2024) to show that the original method from Mukherjee et al. (2024) is still valid for the case when N>>K if ignoring the computation challenge; (2) proposes a computationally efficient method, called "DopeWolfe" by integrating randomized FW (Kerdreux et al., 2018) and golden-section search method (Kiefer, 1953) to approximately solve FW and reduce the computation with a factor of (choose N K) to (choose N 2). Also, the authors prove that after O(max(1, (choose N K)/R)/ε) iterations, the error is upper bounded by ε. The authors tested the proposed method vs 3 baseline methods on 3 real-world datasets. In the first experiment, the human preference vector, θ, is randomly sampled, and human feedback is simulated accordingly. In the second experiment, there is no ground truth θ (which makes the proposed method using the PL model misspecified), and the human feedback is taken from the dataset. The result shows that the proposed method with the MLE estimator achieves the lowest ranking loss. ## update after rebuttal I appreciate the authors' Rebuttal in addressing my concerns. I have adjusted my score accordingly. Claims And Evidence: * Claim 1: Mukherjee et al. (2024) is valid for the case of N>>K when ignoring the computation challenge. * This is theoretically justified by bounding the ranking loss in Sec.3.3 and empirically justified in experiments to show that the pipeline achieved higher performance than others. * I have one concern about the empirical result. In the result in Sec.6.1 (using synthetic feedback), the proposed method significantly outperformed baselines (Fig.1). However, in the result in Sec.6.2 (using real feedback), the advantage of the proposed method, in comparison to the baseline is less than 0.1 for mean ranking loss (Fig.2). It might be helpful to justify this by explaining that this difference can be significant in real-world systems. * Claim 2: when extending Mukherjee et al. (2024) to the case of N>>K, the FW is computationally challenging due to the computation complexity factor (choose N K). The proposed method resolves this by getting rid of the (choose N K). * This is theoretically justified by analyzing the computation complexity in Sec.5.1 and 5.2, by showing e.g., (choose N K) is reduced to (choose N 2). This is also empirically justified in experiments to show that the proposed method is able to solve the FW while vanilla FW won't work. * I have one concern about the theoretical result. Cor.4 shows that to solve the proposed algorithm to reach small error ε, it would need O(max(1, (choose N K)/R)/ε) iterations. So essentially, in each iteration, the proposed method is able to get rid of the (choose N K), but the overall optimization still needs (choose N K) iterations. I understand that there is no free lunch, and the empirical result seems to be working well, but it might be helpful for the authors to clarify this. Methods And Evaluation Criteria: Yes. The empirical study is based on 3 real-world datasets about text retrieval and LLM alignment. The synthetic-feedback experiment randomly selects θ, which makes sense because the problem is too complicated to identify the θ from the dataset. The real-feedback experiment directly uses human feedback and benchmarking the ranking loss, which makes sense. Theoretical Claims: I didn't check the proofs. Prop.1 adapts from Thm.5 of Mukherjee et al. (2024), and Prop.2 adapts from Thm.6 of Mukherjee et al. (2024). One concern is that Assumption 1 assumes that \|\|θhat\|\|_2<=1. I am wondering how this can be ensured during the MLE? Experimental Designs Or Analyses: The experiment design and analysis make sense. Supplementary Material: App.D about experiment and extra result. Relation To Broader Scientific Literature: The result can be useful for learning human preferences from ranking feedback for modern AI systems, such as LLMs, if the set of prompts is fixed and known, as demonstrated by the empirical result. Essential References Not Discussed: No. Other Strengths And Weaknesses: This paper is well written, with good theoretical and empirical justification. The technical contribution is not so "surprising" as it integrates several existing FW variations to solve an optimal design problem computationally efficiently. But the extension is well-motivated and the proposed method performed empirically better than baselines. So I think it is a good contribution. Other Comments Or Suggestions: Typo in Sec.6.1: `form sampling (see ??)` Questions For Authors: In Prop.2. I am curious why there is the extra additive d in the exponent. I checked that it also appears in Thm.6 in Mukherjee et al. (2024) (https://arxiv.org/pdf/2404.13895). Mukherjee et al. (2024) said that `This dependence is similar to Theorem 2 of Azizi et al. [6] for fixed-budget best-arm identification in Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We want to thank the reviewer for a positive review that discusses both the new aspects of our work and potential shortcomings. Our rebuttal is below. We focus on major issues and will incorporate all comments of the reviewer in the next version of our paper. If you have additional concerns, please reach out to us to discuss them. ### Empirical Concern in Claim 1 We acknowledge that the setting of real feedback is potentially more challenging because the optimized model is misspecified (unrealizable). However, we do not think that Figure 2 shows significantly worse results than Figure 1. First, note that the figures are plotted differently: all plots in Figure 1 are functions of a sample size for fixed $K$, while Figure 2 is a function of $K$ for a fixed sample size ($500$ in TREC-DL, for instance). Therefore, they are not comparable. Second, the corresponding experiments use different embeddings. Given all the differences, the relative difference in ranking losses of Uniform and DopeWolfe in the same plot is one natural metric. This is consistently 20% in Figure 2 and similar to many relative differences in Figure 1. ### Theory Concern in Claim 2 Thank you for understanding the computational feasibility perspective that we tried to convey in the last two paragraphs of Section 5. We reiterate that DopeWolfe was designed to address the concern that the naive implementation of Dope is infeasible even for small problems (Section 4). ### Ensuring Assumption 1 During MLE We can ensure $\\|\\|\hat{\theta}\\|\\|_2 \leq 1$ during MLE as follows. First, note that $\Theta = \\{\theta \in \mathbb{R}^d: \\|\\|\theta\\|\\|_2 \leq 1\\}$ is a convex set. Second, the MLE in (3) is a convex optimization problem. Therefore, we can minimize (3) on $\Theta$ using gradient descent with a projection step to $\Theta$. ### Additive $d$ in Proposition 2 The additive $d$ in Mukherjee et al. (2024) arises at the end of the proof of Theorem 6 (Appendix A.6), because a high-probability upper bound on the model parameter error is $O(d + \log(1 / \delta))$. See their Lemma 9 (Appendix B) for the statement and proof of the bound.	Summary: This paper proposes an algorithm to rank N items from K-way comparisons (K<<N), formulated through a D-optimal design objective. The authors develop “DopeWolfe,” a randomized Frank-Wolfe variant with sparse and low-rank updates to avoid high complexity of naive approaches. They prove a sublinear convergence rate for this randomized method under a logarithmically-homogeneous self-concordant barrier analysis. Empirical results on both synthetic and real IR datasets suggest that the proposed design framework improves ranking accuracy compared to uniform sampling or clustering-based methods. Claims And Evidence: Claims are supported by theoretical analysis. Methods And Evaluation Criteria: A key assumption in the paper is that a global ranking over N items can be inferred solely by issuing multiple K-ranking queries—i.e., repeatedly asking annotators to compare small subsets of items. However, this setup becomes questionable when N is large and the total number of queries T times K exceeds N. In real-world systems, it may be more natural and cost-effective to collect absolute (or per-item) feedback for high-dimensional or large-scale ranking tasks, rather than repeated sampling of the same few items in multiple queries. The results in the experiment gets small ranking error when T times K exceeds. Theoretical Claims: The theorems appear consistent with known self-concordance analyses. Experimental Designs Or Analyses: Data/Setup Concerns. The paper’s experiments primarily center on two information-retrieval datasets, each with N=100≫K=2. While these retrieval tasks do involve preference judgments, they may not accurately reflect the complexities of human-generated comparisons found in large-scale response-based RLHF settings, where user preferences can be more nuanced or subjective. Moreover, for the LLM-alignment dataset, the paper mentions N=7 items across multiple lists—a rather small scale. In such a scenario, it seems more prior baselines (e.g., DOPE) could be applied and compared, since the problem size is not computationally prohibitive. Baselines. On the “real data” setting, the paper omits the two baselines in synthetic setting, even though K remains small. Also, including baselines that is “smarter” than uniform sampling yet still computationally manageable would be more convincing. For instance, iterating through all data in random order and pairing. Hyperparameter Analysis. More tuning or ablation studies on key hyperparameters will be helpful. Supplementary Material: A code link is provided. Relation To Broader Scientific Literature: The paper situates itself in the broader context of RLHF and preference-based ranking. Its approach to active preference learning for K-wise feedback is connected to D-optimal design, a classic concept in statistics but still underexplored in RLHF or large-scale ranking tasks. It generalizes prior active ranking work (some of which focuses on pairwise or small-scale scenarios) to the more general Plackett-Luce model for K-way comparisons. The use of a randomized Frank-Wolfe variant for log-determinant objectives extends earlier results on Lipschitz smooth objectives, bridging a gap in the continuous optimization literature. Essential References Not Discussed: None. Other Strengths And Weaknesses: The problem setting is interesting but may not be very practical. The proposed algorithm nicely solve the problem and theoretical analysis is provided. But more real-world experiments are needed to support practical use. Other Comments Or Suggestions: Line 358 right column has a reference error (??) Questions For Authors: In practice, K-way queries might arrive in a sequential setting with noisy or incomplete feedback. How could DopeWolfe incorporate incremental updates as partial responses come in? Code Of Conduct: Affirmed. Overall Recommendation: 2	Rebuttal 1: Rebuttal: We want to thank the reviewer for detailed feedback, and recognizing that we solved the problem that we set out to solve well. Our rebuttal is below. We focus on major issues and will incorporate all comments of the reviewer in the next version of our paper. If you have additional concerns, please reach out to us to discuss them. ### Practical Motivation $K$-wise comparisons naturally arise in many large-scale systems. For instance, online marketplaces frequently display a handful of items selected from a catalogue of billions of items to a user, and the user’s choice among those items can be viewed as a noisy ranking observation. These real-world interactions are well-modeled by the Plackett–Luce model used in our work (Negahban et al., 2018; [Buchholz et al., 2022](https://arxiv.org/pdf/2205.06024)). Recent developments in reinforcement learning with human feedback (RLHF) also suggest that relative feedback can yield better alignment than absolute feedback ([Christiano et al., 2017](https://arxiv.org/abs/1706.03741); [Bai et al., 2022](https://arxiv.org/abs/2204.05862)). It has also been shown that comparisons on longer lists ($K > 2$) can improve downstream reward models (Zhu et al., 2023b; [Liu et al., 2024](https://arxiv.org/abs/2402.01878)). This is one motivation for collecting the Nectar dataset used in Mukherjee et al. (2024). ### Absolute Versus Relative Feedback We acknowledge the concern that repeated $K$-wise comparisons may become costly. However, it is known that absolute feedback has its shortcomings as well ([Shah et al., 2014](https://arxiv.org/abs/1406.6618)). First, annotators often exhibit variable calibration when assigning absolute scores, making cross-annotator aggregation difficult. Second, comparison of items is often more natural and faster for humans. Finally, often we only have access to proxy signals (ad clicks or video watch time), which have an approximately monotonic relation to the real preference. A relative comparison requires only ordering rather than judging the precise value, mitigating calibration and proxy issues. Ultimately, whether the absolute or relative feedback is used is a design choice, and we believe that both should be studied. ### Data and Setup Concerns We would like to clarify that our Nectar experiment is not small scale. The dataset has $30000$ lists, each with $7$ choices. For $K$-way comparisons, we optimize over $30000 {7 \choose K}$ subsets of items. Even for $K = 2$, this is $630000$ subsets and two orders of magnitude more than in Mukherjee et al. (2024). We describe this in lines 949-953 (Appendix D.1). ### Additional Baselines To alleviate your concerns about the lack of comparison to Dope and baselines in Mukherjee et al. (2024), we contacted Mukherjee et al. (2024) and obtained their code. The code differs from their paper as follows: * Dope is implemented using the Frank-Wolfe method where the linear maximization oracle (LMO) is a linear program. * The Nectar experiment is on $500$ lists. The code crashes for $2000$ lists used in Mukherjee et al. (2024) and they did not resolve this issue before we submitted this rebuttal. We implemented DopeWolfe in their code base as follows: * LMO is solved greedily, as in (8), on 10% of randomly sampled subsets of items. * Line search is implemented using golden-section search. The plots for the Anthropic and Nectar experiments are at [Anthropic plot](https://anonymous.4open.science/r/DopeWolfe-ICML-anon-1AD6/DopeWolfe_Anthropic_ICML_rebuttal.png) and [Nectar plot](https://anonymous.4open.science/r/DopeWolfe-ICML-anon-1AD6/DopeWolfe_Nectar_ICML_rebuttal.png), respectively. We observe that the ranking losses of DopeWolfe and Dope are comparable. This means that DopeWolfe beats all baselines in Mukherjee et al. (2024). However, there is a difference in the wall-clock time: * Anthropic: DopeWolfe is about $4$x times faster than Dope ($6.046$ seconds on average versus $24.924$). * Nectar: DopeWolfe is about $3$x times faster than Dope ($0.571$ seconds on average versus $1.826$). Note that both Anthropic and Nectar are well-established RLHF datasets.	null	null	null	null	null	null
The Limits of Tractable Marginalization	Accept (poster)	Summary: This paper defines three computation classes inclusing PM for tractable marginalization, PHM for Hamming marginalization and PVM for virtual evidence marginalization. The authors manage to show that class UFMAC is in all three classes mentioned before. Further, the authors show that PVM \subseteq PHM \subseteq PM. With the two conclusions above, the authors manage to provide a hierarchy of complexity class between UFMAC and FP. Claims And Evidence: The authors provide proves for all their claims. 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: I think the paper is nicely written, and the result is clear and easy to understand. The three ways of marginalization are also interesting and intuitive. However, it is unclear how the paper relates to the theme of this conference. It seems to me the paper fits better for a conference like CCC. I wonder if the authors could explain more about why complexity classes relate to marginalization, which is interesting for people who work in learning theory or even machine learning. Other Comments Or Suggestions: N/A Questions For Authors: I wonder if there are any possible implications or applications of the result in machine learning or learning theory. I think it would be helpful if the authors could give some explanation on why PVM, PHM, and PM are important complexity classes. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Thank you for your considered review. On our paper’s relation to the conference theme, we recall that ICML has recently featured other papers entirely focused on the theory of tractable marginalization [0, ICML 2023; 1, ICML 2024] (with similarly focused papers appearing at closely related conferences [8,9,10]). Moreover, we emphasize the fruitful tradition of a close connection between the theory and practice of tractable models, with theoretical insights inspiring practical breakthroughs. For example, [4, ICML 2024] leveraged theoretical expressivity theorems to inform the design of state-of-the-art tractable models (with similar examples appearing at closely related conferences [5,6,7]). More generally, we remark that marginalization is an essential task (i.e., computing the normalizing constant or partition function) for any probabilistic model; the question of tractable marginalization is therefore as old as probabilistic reasoning as a field. As for appeal to the broader community, we note that tractable models, in addition to quickly developing as performant probabilistic models in their own right [3], also appear as integral components in recent proposals for control and alignment of deep generative models [11,12,13] as well as numerous other applications [2,14]. We therefore view our work as fundamental and relevant to ICML, developing our understanding of tractable models by formalizing (and making progress in answering) the most basic questions about when marginalization is and isn’t computationally tractable. As reviewer jvgm writes, our work “substantially enhances our understanding of tractable marginalization” while managing to remain “neat,” “precise,” and “elegant,” at times even “refreshingly simple”. We hope this further context is helpful in addressing your questions and concerns, and we welcome any further discussion. [0] Bläser. Not all strongly Rayleigh distributions have small probabilistic generating circuits. ICML 2023. [1] Agarwal et al. Probabilistic Generating Circuits - Demystified. ICML 2024. [2] Wedenig et al. Exact Soft Analytical Side-Channel Attacks using Tractable Circuits. ICML 2024. [3] Liu et al. Scaling Tractable Probabilistic Circuits: A Systems Perspective. ICML 2024. [4] Zhang et al. Probabilistic Generating Circuits. ICML 2021. [5] Loconte et al. Subtractive Mixture Models via Squaring: Representation and Learning. ICLR 2024. [6] Wang et al. On relationship between monotone and squared circuits. AAAI 2025. [7] Loconte et al. Sum of Squares Circuits. AAAI 2025. [8] Martens et al. On the expressive-efficiency of sum-product networks. NeurIPS 2013. [9] Wang et al. A Compositional Atlas of Algebraic Circuits. NeurIPS 2024. [10] Vergari et al. A Compositional Atlas of Tractable Circuit Operations for Probabilistic Inference. NeurIPS 2021. [11] Zhang et al. Tractable Control for Autoregressive Language Generation. NeurIPS 2023. [12] Zhang et al. Adaptable Logical Control for Large Language Models. NeurIPS 2024. [13] Liu et al. Image Inpainting via Tractable Steering of Diffusion Models. ICLR 2024. [14] Saad et al. SPPL: Probabilistic Programming with Fast Exact Symbolic Inference. PLDI 2021. --- Rebuttal Comment 1.1: Comment: Thanks to the authors for the detailed mention of related work. I am less familiar with tractable marginalization, and this answer provided by the authors is a good tutorial. I understand the conference has a page limit, but it would be nice for the authors to include this in the related work section in the final version for general audiences if the paper is accepted. I raised my score accordingly. --- Reply to Comment 1.1.1: Comment: Thank you for your prompt response. We will incorporate further context along these lines into the final version of our paper. If you have any remaining questions or concerns, we welcome further discussion.	Summary: The paper "The Limits of Tractable Marginalization" explores the computational complexity of marginalization, a fundamental operation in probabilistic inference and formal verification. The authors focus on the relationship between functions with tractable marginalization and their representation using uniform finally multilinear arithmetic circuits (UFMACs)—a class encompassing known probabilistic models like hidden Markov models, determinantal point processes, and sum-product networks. They show that while all known tractable models can be captured by UFMACs, not all functions with efficient marginalization necessarily admit such circuit representations. Beyond standard variable marginalization, the authors examine two stronger forms of marginalization: Hamming weight marginalization and virtual evidence marginalization. Claims And Evidence: ### Claim 1: Not all functions with polynomial-time marginalization (PM) can be efficiently represented by uniform finally multilinear arithmetic circuits (UFMACs). - Evidence: The paper constructs a function $ f_{\text{aff}} $ that has tractable marginalization but does not belong to UFMAC, assuming FP ≠ #P. The function $ f_{\text{aff}} $ is defined using constraint satisfaction problems (CSPs) with parity constraints. --- ### Claim 2: UFMACs allow more powerful forms of marginalization than standard variable marginalization, such as Hamming weight marginalization. - Evidence: The authors show that any function in UFMAC can efficiently compute Hamming weight marginalization (HMAR) queries using a transformation to network polynomials. They prove that for any function $ f $ represented as a UFMAC, its Hamming weight marginalization can be computed via polynomial-time interpolation. --- ### Claim 3: There exists a strict separation between PM and PHM (assuming FP ≠ #P). - Evidence: The function $ f_{\text{aff}} $ is used as a separating example. It is shown to be in PM (tractable for variable marginalization) but not in PHM, since computing Hamming weight marginalization on $ f_{\text{aff}} $ is #P-hard. --- ### Claim 4: UFMACs allow efficient computation of virtual evidence marginalization (VMAR). - Evidence: The paper proves that any function in UFMAC can efficiently compute virtual evidence marginalization via standard polynomial evaluation. --- ### Claim 5: UFMACs are complete for virtual evidence marginalization in the real RAM model. - Evidence: The paper proves that if a function has a polynomial-time real RAM algorithm for virtual evidence marginalization, then it has an efficient UFMAC representation. --- ### Claim 6: The class of functions tractable for virtual evidence marginalization (PVM) is at least as large as the class of functions tractable for Hamming weight marginalization (PHM). - Evidence: The authors prove PVM ⊆ PHM by showing that Hamming weight marginalization can be efficiently computed via virtual evidence marginalization. Methods And Evaluation Criteria: This paper is purely theoretical, so no benchmark data is proposed and no empirical evaluation is conducted. Theoretical Claims: Yes. I have checked the proof of theoretical claims: - Claim 1: Not all functions with polynomial-time marginalization (PM) can be efficiently represented by uniform finally multilinear arithmetic circuits (UFMACs). - Claim 2: UFMACs allow more powerful forms of marginalization than standard variable marginalization, such as Hamming weight marginalization. - Claim 3: There exists a strict separation between PM and PHM (assuming FP ≠ #P). - Claim 4: UFMACs allow efficient computation of virtual evidence marginalization (VMAR). - Claim 5: UFMACs are complete for virtual evidence marginalization in the real RAM model. - Claim 6: The class of functions tractable for virtual evidence marginalization (PVM) is at least as large as the class of functions tractable for Hamming weight marginalization (PHM). Experimental Designs Or Analyses: NA. No experiments are conducted in this paper. Supplementary Material: Yes. I have read through the appendix. Relation To Broader Scientific Literature: This paper addressed an important problem of computing marginalization of probabilistic models. 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: Thank you for your considered review. We see no questions or concerns in your review needing response. We nonetheless welcome any further discussion, e.g., as prompted by the other reviews.	Summary: This paper tackles the problem of characterizing the class of functions on which marginalization can be performed in polynomial time. Previous work describes a construction with polynomial size arithmetic circuits computing multilinear polynomials. The authors demonstrate that this construction is incomplete and produce a broader class of functions with polynomial marginalization. Claims And Evidence: Claims are supported by propositions, lemmas, theorems, etc. Methods And Evaluation Criteria: Not applicable since the paper is theoretical. Theoretical Claims: Regrettably, I haven't got the background to easily follow the theorems and proofs so defer to other reviewers on this. Experimental Designs Or Analyses: There are no experiments since the paper is theoretical. Supplementary Material: N/A Relation To Broader Scientific Literature: With theoretical papers like this it is difficult to assess contributions to the broader scientific literature, as they may only become apparent in the future when the results are used in a more applied context. 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: Thank you for your considered review. We see no questions or concerns in your review needing response. We nonetheless welcome any further discussion, e.g., as prompted by the other reviews.	Summary: This paper proposes and studies UFMAC, a unifying arithmetic circuit formalism for representing functions that support tractable marginalization. It shows that UFMACs subsume prior such tractable classes, proves that all UFMACs support polynomial time marginalization, and also shows that the reverse isn't true -- that not all funcations with tractable marginalization have UFMACs. There are some additional contributions as well. This work substantially enhances our understanding of tractable marginalization. Additionally, the paper is carefully written (modulo some small typos in a later part) and uses neat and elegant arguments in all major proofs. E.g., the argument that UFMACs support tractable marginalization (Prop 3.7) is refreshingly simple, leveraging an earlier observation of Juma et al (2009). Similarly, while I wasn't quite sure what the motivation for studying Hamming Weight Marginalization is, it became evident later that this tool (besides being of interest by itself) will help prove that not all tractable functions have UFMACs --- because if they have a UFMAC, then even HMAR would be tractable, which conflicts with standard complexity assumptions on certain specific problems. I enjoyed reading the arguments, even though I am not very familiar with the area. Claims And Evidence: Yes. As noted above, the arguments are made very clearly and the proofs generally precise and elegant. Methods And Evaluation Criteria: The paper is theoretical and provides appropriate definitions, formalisms, and proofs. Theoretical Claims: Mostly yes, except I only lightly skimmed the proof of Theorem 4.10 (hardness of HMAR(f_aff) and the material in section 5 (virtual evidence marginalization). The findings in section 5 are a useful addition the main paper, though I think the paper is already strong even by the end of section 4. Experimental Designs Or Analyses: N/A Supplementary Material: Only lightly skimmed. Relation To Broader Scientific Literature: The proposed formalism of UFMACs generalizes, to my knowledge, all prior classes for which tractability of marginalization was known. Essential References Not Discussed: None to my knowledge. Other Strengths And Weaknesses: One thing I felt the paper doesn't motivate or revisit enough (other than in the initial part of section 2.3) is the "finally" part of UFMACs. The motivation of allowing polynomial degree at the intermediate nodes is good -- but even the fact that determinants would be hard (impossible?) to cover without it is only lightly mentioned within a paragraph. Later sections don't refer to the "finally" part at all (I suppose it's not directly relevant anymore for tractability bounds? But then it must make the proofs a little bit harder / more general than assuming linearity even on internal nodes. So it feels to me that something can still be said about it.) I wonder if even a proposition can be stated that UFMACs are strictly more expressive than UMACs. Fig 1 is useful to have but doesn't seem to be discussed directly after the appropriate notions have been defined and/or results stated. Other Comments Or Suggestions: Some typos to revisit: * page 5, defn 4.1: "f \in PHM is HMAR(f) is..." => should this be "f \in PHM if FMAR(f) is..." ? * page 8, defn 5.1: similar note as above * page 5, 2nd line after defn 4.1: should M_{m,k} be X_{m,k}? * page 5, line after prop 4.3: should FMACs be UFMACs? Similarly in the paragraph after lemma 4.4 and the proof of prop 4.5. Questions For Authors: I didn't look carefully but with a quick pass, I couldn't quite connect with section 5, virtual evidence marginalization, in part because Defn 5.1 defines a "marginalization" problem without any "summation" in it. Compare, e.g., to defns. 3.1 and 4.1, which both have a clear summation as expected. Can you clarify what exactly is the marginalization problem here? Which variables are we marginalizing over, under what setting? Code Of Conduct: Affirmed. Overall Recommendation: 5	Rebuttal 1: Rebuttal: Thank you for your considered review. We are glad you found our work “neat,” “precise,” and “elegant,” even sometimes “refreshingly simple.” We provide answers to your questions below and welcome any further discussion. [The “finally” in UFMAC] The choice to allow polynomial degree (i.e., the “Finally” in UFMAC) has indeed been made to allow for flexible circuits like those known for the determinant. The question of separating finally multilinear circuits from multilinear circuits is currently still an open problem [1, Open Problem 3], and we agree that this can be stated more clearly in the paper and we will do so. [Virtual evidence marginalization] This is a good question; we will clarify this in the paper. The point is as follows. On the one hand, multiplying the inputs by arbitrary rationals can be viewed as updating the distribution given virtual evidence, but on the other hand, we have observed (Lemma 3.6) that marginalization of f can be reduced to evaluating the multilinear polynomial for f at 1/2,…,1/2. Therefore the evaluation of p at arbitrary rational points a_1,…,a_n can be viewed as first applying virtual evidence corresponding to 2a_1,…,2a_n to x_1,…,x_n to get 2a_1x_1,…,2a_nx_n and then evaluating at x_1=…=x_n=1/2, i.e., marginalizing. Thus there is, in a sense, an implicit summation in every evaluation of the multilinear polynomial at rational points, i.e., in every VMAR(f) instance. In particular, to observe some virtual evidence and then compute a marginal probability, a VMAR(f) query suffices. We thank you for your other notes on minor typos. [1] Shpilka and Yehudayoff. Arithmetic Circuits: a survey of recent results and open questions. Foundations and Trends in Theoretical Computer Science, 2010.	null	null	null	null	null	null
Guided Zeroth-Order Methods for Stochastic Non-convex Problems with Decision-Dependent Distributions	Accept (poster)	Summary: This paper a new zero-order optimization algorithm for a new algorithm for a special optimization problem. The theoretical results show the proposed method converge to the stationary point and the step of steps to converge is also provided. The covariant matrix as estimated is a type of CMA-ES method (Eq. 6). Claims And Evidence: This paper proposed two methods in zero-order optimization with decision-dependent distributions. All results are well validated by theoretical proofs and simulations. Methods And Evaluation Criteria: The using evaluation criteria are training loss, testing loss and AUC. All are all pretty standard criteria. Theoretical Claims: This paper proposed two main theorems, . Experimental Designs Or Analyses: 1. The testing problems multiproduct pricing and strategic classification are a bit simple. Consider using more complex realworld problem. 2. Why the other three methods perform so poorly. Are these methods fair benchmarks? 3. Where the the error bar in Figure 1? Supplementary Material: The supplementary material provide plenty of theoretical proofs of the main proof as provided in the main paper. Relation To Broader Scientific Literature: This paper is related to zero-order optimization method as proposed by Powell. Essential References Not Discussed: 1. Z. Zhang, Scalable Derivative-Free Optimization Algorithms With Low-Dimensional Subspace Techniques, arXiv:2501.04536, 2025 [pdf] 2. T. M. Ragonneau and Z. Zhang, PDFO: A Cross-Platform Package for Powell’s Derivative-Free Optimization Solvers, Math. Program. Comput., 16:535–559, 2024 [pdf]. Consider compare with some zero-order methods in this lib. Other Strengths And Weaknesses: 1. The theoretical results in this paper are strong. 2. The notation section is clear, which is admirable. 3. The related work regarding to Decision-Dependent Distributions is very informative. Other Comments Or Suggestions: 1. Lemma 4.4, the constant 5488 is strange. Is 5488 too large? 2. Is using e as an all vector standard? It is usually used as 1 in previous literature. 3. The notation $\gamma \in R_{>0}$ is a bit too complex. Consider using $\gamma > 0$. 4. In Table 1, the data information is not necessary and takes too much space. Questions For Authors: 1. For some tasks, GZO-NS performs better and some tasks GZO-HS perform better. Why? Is there a statement which algorithm will be better under certain condition? 2. Is assumption 4.3 proper? I think for Wasserstein distance, it is easy to bound the lipschize constant. So it is better to calculate this constant directly rather than using an assumption. 3. Consider adding an error bar in experiments. 4. The testing problems are too simple and the benchmarks methods have not converged. What is the main reason? 5. Line 282 right. Why only this loss function f is considered, will other functions also work? Ethical Review Flag: Flag this paper for an ethics review. Ethics Expertise Needed: ['Discrimination / Bias / Fairness Concerns', 'Other expertise'] Ethical Review Concerns: NA. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We thank the reviewer for the general appreciation of our work as well as constructive comments. ### Questions For Authors. 1: If the distribution $D(x)$ does not change significantly with respect to $x$, GZO-HS, which uses samples from past iterations, is likely to perform better. This is because the distribution $D(x_i \pm \mu_i u_i)$ at past iteration $i$ is similar to the current distribution $D(x_k)$, improving the reliability of past samples. Conversely, when $D(x)$ varies greatly with $x$, GZO-NS, which leverages current partial gradient information, tends to outperform due to its increased accuracy in reflecting the current distribution. 2: Since we were unable to ascertain the exact subject of your Lipschitz constant, we interpreted your question as follows. Please let us know if our understanding is incorrect: ``Is it easy to compute a constant that bounds $\theta$ in Assumption 4.3? It is better to calculate this constant directly rather than relying on the assumption on the Wasserstein distance." To find such a constant ($\theta$ or higher) that makes Assumption 4.3 valid, we must obtain samples from $D(x)$ at all $x$ since $D(x)$ is unknown, which is impractical. Moreover, without Assumption 4.3, such a constant may not exist. For example, consider a discrete distribution $D(x)$ over $\xi \in$ {$0,1$}, where $\xi=0$ with probability $1$ if $x > y,$ and $\xi=1$ with probability $1$ if $x \le y$. (This setting corresponds to the situation where the seller determines the price $x$ of one product and the buyer buys it ($\xi=1$) with probability 1 if the price $x$ is less than $y$.) In this case, for any $\theta>0$, there exists $\epsilon>0$ such that $W(D(y), D(y+ \epsilon)) > \theta \\|\epsilon\\|$. Therefore, $\theta$ in Assumption 4.3 does not exist. This is due to the discontinuity of the probability distribution $D(x)$. Hence, Assumption 4.3, which imposes continuity on $D(x)$, is necessary. 3: Since Fig. 1 shows convergence in a single instance, we did not include error bars. To add error bars to Fig. 1, we would need to show results averaged over multiple instances. However, when describing averaged results, it becomes difficult to understand how the methods converge. For example, even a method that decreases the function value non-monotonically may appear to decrease it monotonically when averaged values are presented. For this reason, we have included the convergence of each method for one instance in the figures and summarized the statistical information in tables. Note that Tables 1 and 2 include that not only single-dimensional results of performance (i.e., average) but also measures of variation (i.e., standard deviation). On the other hand, since each table shows the statistical results at the final iteration, it is currently not possible to see the statistical results during the iterations. Therefore, we will add the figures that include averaged curves and error bars across multiple instances to the appendix. 4: Although our baselines are based on recent studies (Ray et al., 2022), (Hikima & Takeda, 2024), and (Liu et al., 2024a), they fail to converge for different reasons: - ZO-OG suffers from high variance and instability at each iteration. While increasing the number of samples $m_k$ may improve stability, it would also increase total sample size. - ZO-OGVR and ZO-TG do not include partial gradient information in the update direction $u$, which delays convergence. If you have other baselines, we would be happy to add them. 5: We adopted the loss function used in (Levanon \& Rosenfeld, 2021, Section 4)) in order to align our experimental setup with that of the existing study. Moreover, cross-entropy is a widely used and standard loss function for binary classification. We could have tried other loss functions in our numerical experiments, but we preferred to vary the coefficient $\gamma$ of the agent's cost function to see the performance of the proposed method for different probability distributions (which depends on $\gamma$). However, our method is applicable to other loss functions if they are differentiable. ### Other Comments Or Suggestions. 1: We consider 5488 to be an appropriate coefficient. This large number arises from the sixth power of the expected value of $u$ in Eq. (12) of Lemma C.7. Look at the equation transformation in lines 697 to 708. In the first inequality, the norm is decomposed, where number 32 occurs in the coefficients. Furthermore, in the third inequality, from (Nesterov \& Spokoiny, 2017, Lemma 1), i.e., Eq. (10) in our appendix, number $7^3$ appears in the coefficients. These transformations account for the magnitude of this constant. 2, 3, and 4: Thank you for the multiple suggestions about the description. We will correct them accordingly. ### Essential References Not Discussed. We will cite these references and clarify the differences from our study. Thank you for the suggestion.	Summary: This work proposes new zero-th order methods for nonconvex performative prediction problem (i.e. optimization with decision-dependent distribution) which improve the theoretical sample complexity of the state of the arts when the function variation $G=\sup_{x,\xi}\|f(x,\xi)\|$ is large compared with the dimensionality of the decision variable. The experimental results also demonstrate faster convergence of these new methods. ## update after rebuttal Reviewer Vnz2 is satisfied with the authors' responses and keeps rating 4. Claims And Evidence: The claims above are well supported by theorems and experimental results. Methods And Evaluation Criteria: The proposed zero-th method looks reasonable but the advantage of using guidance is still not intuitive and clear, as will be elaborated later. In the theoretical results, using the gradient norm as the evaluation metric is standard and reasonable. In the experiments, the evaluation metrics including objective function value, classification accuracy and AUC are also standard and reasonable. The experiment scenarios are good since they fit the studied performative prediction problem and directly come from applications. Theoretical Claims: I checked the proof of Lemmas C.2, C.4, C.5, C.7, C.10, C.11, C.12, 3.2, 4.6 and the general proof logic of Theorems 4.7 and 4.8, and did not find any mistakes. Experimental Designs Or Analyses: The experiment scenarios are good since they fit the studied performative prediction problem and directly come from applications. The evaluation metrics including objective function value, classification accuracy and AUC are standard and reasonable. The basic information for reproducibility is clear to me, including the objective function, data distribution, algorithms and their hyperparamter choices. The results also demonstrate the faster convergence of the proposed methods than that of the existing methods. Supplementary Material: Yes. I read Appendix A about experimental details. I also checked the proof of Lemmas C.2, C.4, C.5, C.7, C.10, C.11, C.12, 3.2, 4.6 and the general proof logic of Theorem 4.7. Relation To Broader Scientific Literature: This work is among the very few papers on theoretical complexities to converge to a stationary point of the objective function (instead of the performative stable point as an approximation), and improves these complexities using a new zero-th order gradient estimator when the function variation $G=\sup_{x,\xi}\|f(x,\xi)\|$ is large compared with the dimensionality of the decision variable. Essential References Not Discussed: [1-5] on convergence results of performative prediction are not cited. [1] Li, Qiang, and Hoi-To Wai. "Stochastic optimization schemes for performative prediction with nonconvex loss." Advances in Neural Information Processing Systems (2024): 8673-8697. [2] Khorsandi, Pedram, et al. "Tight Lower Bounds and Improved Convergence in Performative Prediction." OPT 2024: Optimization for Machine Learning. [3] Izzo, Z., Ying, L., and Zou, J. How to learn when data reacts to your model: Performative gradient de- scent. In Meila, M. and Zhang, T. (eds.), Proceed- ings of the 38th International Conference on Machine Learning, volume 139 of Proceedings of Machine Learning Research, pp. 4641–4650. PMLR, 18–24 Jul 2021 [4] Roy, A., Balasubramanian, K., and Ghadimi, S. Projection- free constrained stochastic nonconvex optimization with state-dependent markov data. In Advances in neural information processing systems, 2022. [5] Mehrnaz Mofakhami, Ioannis Mitliagkas, and Gauthier Gidel. Performative prediction with neural networks. In International Conference on Artificial Intelligence and Statistics, pages 11079–11093. PMLR, 2023. Other Strengths And Weaknesses: Strengths: This work studies an emerging and significant problem called nonconvex performative prediction (i.e., optimization with decision-dependent distribution), with important applications. There are only few existing works on theoretical complexities to converge to a stationary point of the objective function (instead of the performative stable point as an approximation), and this work improves these complexities using a new zero-th order gradient estimator in the case of large function variation $G=\sup_{x,\xi}\|f(x,\xi)\|$ compared with the dimensionality of the decision variable. The experiments are application-driven, clear, reproducible and demonstrate the faster convergence of the proposed algorithms. I can understand the clear presentation well. Weaknesses: The major weakness is that the intuition and benefits of using the gradient guidance $hh^{\top}$ in Eq. (6) are not clear, especially given that the proof of Theorem 4.7 does not depend on $s$ and thus $h$. This major weakness corresponds to my questions (1) and (8) in "Questions For Authors". Some works on performative prediction are not cited as listed above. Some other details are to be clarified as listed below. Other Comments Or Suggestions: (1) You could stress your contribution in the abstract that your theoretical sample complexity improves the state of the arts in the case of large function variation $G=\sup_{x,\xi}\|f(x,\xi)\|$ compared with the dimensionality of the decision variable. (2) You could cite the works listed in "Essential References Not Discussed" above, and compare (Liu et al., 2024a) with yours in terms of setting and complexity. (3) You may mention the name "performative prediction" of this optimization problem. (4) You could use "an unbiased" instead of "the unbiased" right before Eq. (3). Questions For Authors: (1) Could you provide intuition why using the guidance $hh^{\top}$ in Eq. (6), and the benefit of using $\alpha_k\to 1$ in Algorithm 1? For example, can Lemma 4.6 imply that the variance of the stochastic gradient is small if $\alpha\approx 0$ for large $\|\|\nabla F(x)\|\|$, and $\alpha\approx 1$ for small $\|\|\nabla F(x)\|\|$ (usually near the final iterates)? In this way we balance bias-variance trade-off? (2) The gradient estimator (2) has Gaussian variable $d{\bf u}$ with covariance $d^2I_d$, while in Eq. (6), the first part is $\frac{I_d}{d}$. Why is there a such scale difference in $d$? (3) At the beginning of Section 5.1, should $x\in\mathbb{R}^d$ instead of $x\in\mathbb{R}^n$? What is the value of the dimensionality $d$ and $\theta_i$ for the price experiment? (4) Do Tables 1 and 2 involve only the final iterate of each problem instance? You could explain that in the caption. Near the final of Section 5.1, should "Table 2" be changed to "Table 1"? In Table 1, does each data ID correspond to a problem instance? If yes, why not using data IDs 1-20? (5) In Lemma C.2, should it be $L_F=L_x+\theta L_{\xi}$? (6) In the proof of Lemma C.10, what does $n$ mean? Should it be changed to the dimensionality $d$? Also, (21) can directly imply (22) by replacing $u$ with $-u$ as they follow the same distribution $\mathcal{N}(0,\Sigma)$. (7) In the proof of Lemma 3.2, the second $x+\mu u$ in the second row could be changed to $x-\mu u$. (8) In the proof of Theorem 4.7, what will be the complexity result if $\alpha_k=1$? Since the proof does not depend on $s$, what if we use arbitrary $s$? (9) In the proof of Lemma C.12, if we replace all $L_F$ with $\|\|\nabla F(x)\|\|$, will this yield tighter result? It is fine if there is not enough time to explore this question in the discussion period. Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: We thank the reviewer for positive comments and constructive suggestions. ### Questions For Authors. (1): Since we make no assumptions on $h$ except that it is normalized, the sample complexities of our methods are derived in the worst-case scenario for $h$. In this case, by letting $\alpha_k \to 1$, as in our Algorithms 1 and 2, the effect of $h$ (, which is adverse in the worst-case scenario) is reduced, allowing us to achieve the stated sample complexity. For Lemma 4.6, note that $L_f \ge \|\|\nabla F(x)\|\|$; the upper bound is smaller when $\alpha=1$, unless $d$ is very small. Therefore, there is no trade-off in the worst-case scenario. As noted in ``Claims And Evidence and Essential References Not Discussed'' in the response to reviewer homv, our contributions are: (i) an improved sample complexity over (Hikima \& Takeda, 2024b) through tighter convergence analysis, and (ii) the introduction of partial gradient information $h$ without degrading the sample complexity, even in the worst-case scenario for $h$. Regarding (ii), (Maheswaranathan et al.,2019) assumes a confidence level for the partial gradient information ($\rho$ in Section 3.3 in their paper) and establishes a trade-off between the unbiasedness and variance of the gradient estimator. In contrast, we make no such assumptions on $h$, yet successfully construct methods that preserve sample complexity. We deliberately avoid assuming any correlation between $h$ and the true gradient because we adhere to the existing problem setting (Perdomo et al., 2020; Mendler-Dunner et al., 2020) where $D(x)$ is unknown for application requirements. If we assumed such correlation, the weight of first term in (3) would have to be known, which requires information on $D(x)$. Moreover, to the best of our knowledge, our paper is the first study to apply the concept of guided evolutionary strategy to problem (P). Thus, our goal is to first establish a highly general method under minimal assumptions. We believe our convergence analysis lays a foundation for future work that makes additional assumptions tailored to specific applications. (2): You are correct that the scales differ between Eqs. (2) and (6). In Eq. (2), when $u$ is sampled from the unit sphere, it is common to include $d$ in the numerator; when $u$ is sampled from a Gaussian distribution, $d$ is typically not included. This is done to align the scale of the gradient estimator with that of the true gradient (see [1], Eqs. (2.14) and (2.33)). Although we did not explicitly specify the distribution of $u$ in Eq. (2), we will remove $d$ from the numerator since we use a standard Gaussian distribution as an example. In Eq. (6), the scale is aligned with that of the existing study (Maheswaranathan et al., 2019). Although multiplying the right-hand side of (6) by $d$ would match the scale in (2), we used this scale to facilitate comparison with the previous study. (3): $\mathbb{R}^d$ is correct. Thank you for the comment. We set $d=10$ to match (Hikima \& Takeda, 2024b). (4): Tables 1 and 2 show the mean and standard deviation of the metric at the final iteration across 20 problem instances. Therefore, each value in the table does not represent the result of a single problem instance. In Section 5.1, ''Table 2'' should be ''Table 1.'' We apologize for the typo. In Table 1, the data ID corresponds to the week of data used. Therefore, ``data ID`` and ``date`` in Table 1 represent the same information. To avoid confusion, we will remove the ``data ID`` column from Table 1. (5), (6), and (7): You are correct in all comments. Thank you. (8): The same sample complexity can be derived when $\alpha_k=1$ for all $k$. In other words, the results of Theorems 4.7 and 4.8 hold for any $s$ (and normalized $h$). This is because we performed worst-case analysis on $s$ (and $h$), as described in our response to (1). (9): Thank you for the valuable suggestion. In the proof of Lemma C.12, replacing $L_F$ with $\|\|\nabla F(x)\|\|$ does not yield tighter result. However, we realized that it simplifies the proof. Specifically, the left side of equation (29) becomes $$\left(\beta \alpha_k d^{-1} -\frac{24 H_F\beta^2 \alpha_k^2 (d+4)^2}{d^2}-24H_F\beta^2(1-\alpha_k)(25-23\alpha_k) \right) E_{\zeta_{[0,k-1]}} \left[\|\|\nabla F(x_k)\|\|^2\right],$$ and the sixth term on the right side (i.e., $24H_F\beta^2(1-\alpha_k)(25-23\alpha_k) L_F^2$) is eliminated. This shortens the right-hand side of (29), and also makes (31) unnecessary. Then, if we set $$\beta:= \min \left(\frac{\alpha_0 d}{48H_F( (d+4)^2 + 25d^2)},T^{-\frac{2}{3}} d^{-\frac{1}{3}} \right),$$ Theorems 1 and 2 hold. ### Essential References Not Discussed. We will add these references in Section 2 and clarify the differences from our study. [1] Berahas, Albert S., et al. ``A theoretical and empirical comparison of gradient approximations in derivative-free optimization." Foundations of Computational Mathematics 22.2 (2022): 507-560. --- Rebuttal Comment 1.1: Comment: Reviewer Vnz2 is satisfied with the authors' responses and keeps rating 4.	Summary: The authors explore zeroth-order methods to solve stochastic problems where the distribution of stochastic variables depends on the decision x. By incorporating partial information in the construction of gradient estimators, they demonstrate improved convergence rates compared to existing works. Claims And Evidence: Compared to [1], the main improvement stems from replacing Assumption 3.2 with Assumption 4.1 and using two-point zeroth-order estimation. The authors should provide a clearer explanation of how partial information improves convergence compared to [1]. [1] Haitong L I U, Qiang L I, Wai H T. Two-timescale Derivative Free Optimization for Performative Prediction with Markovian Data[C]//Forty-first International Conference on Machine Learning. Methods And Evaluation Criteria: yes Theoretical Claims: I briefly go over the proof of main result in the last section. According to the proof from lines 1284 to 1303, when $\alpha_0 = 1$ (meaning no partial information is used), there is no negative impact on the theoretical results. In fact, the results are slightly better since both the first and last terms in line 1290 decrease. Experimental Designs Or Analyses: For the experimental validation, it would be valuable to include an experiment running Algorithm 1 with scaled gradient (setting $\Sigma_k=I_d/d$ in ZO-TG) to demonstrate the effectiveness of incorporating partial information in gradient estimation. The legend box obscures a significant portion of the figure, making it difficult to verify the authors' claim that a small $\alpha$ promotes a faster initial decrease in the objective value. Please relocate the legend box outside the figure. Supplementary Material: See Theoretical Claims part Relation To Broader Scientific Literature: NA Essential References Not Discussed: More discusssion and comparison with Hikima & Takeda, 2024b is needed, such as which part of the algorithm contributes to the improved rate? This should be clarified in the main file Other Strengths And Weaknesses: Strength: The paper constructs a central difference type gradient estimator, which proves superior to the result in previous work (Hikima & Takeda, 2024b), with better complexity dependence on $d$. Additionally, incorporating partial information into the covariance matrix is an innovative approach that shows promising results in the experiments. Weakness The presentation of Assumptions in section 4.1 is dense and difficult to follow, and the purpose of Assumption 4.3 needs clarification since it appears only in the appendix. Moreover, the paper heavily relies on the boundedness variance assumption 4.1. While this assumption relates to the $G$ constant in line (204), the constant sigma is not explicitly included in the complexity bound. This makes it difficult to compare the guided zeroth-order method with Liu et al.'s work, which depends on G. Minor: - The range of $\alpha_0$ is incorrect in both Algorithm 1 and Theorem 4.7. According to the proof, $\alpha_0$ should be in (0,1] rather than [0,1). Other Comments Or Suggestions: NA Questions For Authors: NA Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We thank the reviewer for valuable and constructive feedback. ### Weakness. > The presentation of Assumptions in section 4.1 is dense and difficult to follow, and the purpose of Assumption 4.3 needs clarification since it appears only in the appendix. In response to your comment, we will add the following explanations for each assumption: - Assumption 4.1 is required for approximating $F(x)$ by $f(x,\xi)$ with sample $\xi$. Since the objective function involves random variables, such an assumption is essential to evaluate the objective value by its sample. - The purpose of Assumptions 4.2 and 4.3 is to guarantee the Lipschitz continuity of the objective function. It is used to derive the properties of the Gaussian smoothing function. (See Lemma C.8.) - Assumption 4.4 is standard in convergence analysis, ensuring the accuracy of the first-order approximation via Taylor expansion. This is because descent methods with (estimated) gradients can be seen as optimizing a first-order approximation of the objective function at each iteration. > Moreover, the paper heavily relies on the boundedness variance assumption 4.1. While this assumption relates to the $G$ constant in line (204), the constant sigma is not explicitly included in the complexity bound. This makes it difficult to compare the guided zeroth-order method with Liu et al.'s work, which depends on $G$. In response to your comment, we will include $\sigma$ in the expression of the sample complexities. While some studies (Iwakiri et al., 2022; Hikima \& Takeda, 2024b) omit constants other than error tolerance $\epsilon$ and dimension $d$ in their theorems, several studies (Perdomo et al., 2020; Mendler-Dunner et al., 2020; Ray et al., 2022) include such constants, and we agree that your suggestion is valid. In this paper, including $\sigma$ leads to a sample complexity of $O(\sigma^2 \epsilon^{-6} d^4)$. However, we argue that Assumption 4.1 is much looser than the assumption of constant $G:=\sup_{x,\xi}\|f(x,\xi)\|$ in existing studies (Ray et al., 2022; Liu et al., 2024a). Assuming the existence of $G$, we cannot handle even a simple loss function. For example, $G$ is unbounded even if $f$ is the squared error $f(x,(A,b)):=\|\|A x-b\|\|^2$, where $\xi=(A,b)$. This fact is a weakness in the one-point gradient estimator, which is also pointed out in (Hikima \& Takeda, 2024b). In contrast, Assumption 4.1 requires only that $F$ can be approximated by samples, which is a fundamental and minimal requirement; if $\sigma=\infty$, the objective value cannot be estimated by sampling, making such assumptions unavoidable. ### Claims And Evidence and Essential References Not Discussed. > Compared to [1], the main improvement stems from replacing Assumption 3.2 with Assumption 4.1 and using two-point zeroth-order estimation. The authors should provide a clearer explanation of how partial information improves convergence compared to [1]. > More discussion and comparison with Hikima \& Takeda, 2024b is needed, such as which part of the algorithm contributes to the improved rate? Compared to (Liu et al., 2024a), the reason why $G$ does not appear in the sample complexities of our methods is that our methods use a two-point gradient estimator. This improvement has already been made in (Hikima \& Takeda, 2024b) and is therefore not the main contribution of this paper. The main contribution is the difference from Algorithm 2 in (Hikima \& Takeda, 2024b). Our contribution is two-fold: - We achieved a tighter convergence analysis compared to (Hikima \& Takeda, 2024b) by modifying settings such as mini-batch size and step size. - We proposed zeroth-order methods incorporating the partial gradient information, without making any assumptions on the information or worsening the convergence rate. Regarding the second contribution, please see our responses to reviewer Vnz2's question (1) for more information. ### Theoretical Claims. > According to the proof from lines 1284 to 1303, when $\alpha_0=1$ (meaning no partial information is used), there is no negative impact on the theoretical results. You are right. Since we consider the worst case for the partial gradient information $h$, the same sample complexity can be achieved with $\alpha_0=1$. Please see our responses to reviewer Vnz2's questions (1) and (8) for more information. ### Experimental Designs Or Analyses. > For the experimental validation, it would be valuable to include an experiment running Algorithm 1 with scaled gradient (setting in ZO-TG) to demonstrate the effectiveness of incorporating partial information in gradient estimation. In the experiments, we already used scaled gradients in ZO-TG by adjusting the step size $\beta$. See lines 532–536 for details. Compared to GZO-NS and GZO-HS, the updating distance in ZO-TG is scaled by reducing the step size by $d^{-1/2}$. Sorry for the confusion. We will clearly state in the experimental section that the scale of each method is aligned. --- Rebuttal Comment 1.1: Comment: Hi, thanks for your reply. I will raise my score as the authors resolve some of my concerns.	Summary: This paper studies zeroth-order methods with partial gradient guidance for solving the performative prediction problem. Specifically, the proposed algorithm leverages the gradient information of the known function $f(x, \xi)$ to refine the update direction. The authors establish a rigorous worst-case convergence bound and analyze the sample complexity. Simulation results are provided to validate the theoretical findings. Claims And Evidence: Yes, the claims made in the submission are supported by clear and convincing evidence. Methods And Evaluation Criteria: Yes, the methods used in this paper are appropriate for the performative prediction problem, but the motivation is unclear, see Weakness part. Theoretical Claims: Yes, I have checked the proof of Theorem 4.7, and it looks fine to me. Experimental Designs Or Analyses: 1. For the multiproduct pricing application: In Fig. 1, the author plots the loss function as a metric. However, in Theorem 4.7, the convergence metric is the expectation of gradient. From the current figure, we cannot observe the convergence speed information. 2. For strategic classification with an unknown agents' cost function: Regarding the setting with unknown $D(x)$, according to the best response function shown in line 301, right column, I wonder how to get $\xi_F$ in closed-form solution in simulation and whether this settings satisfy smoothness assumption A4.3. Supplementary Material: Yes, I check the appendix A, B, C. Relation To Broader Scientific Literature: In the zeroth-order methods literature for performative prediction, [Miller et al., 2021] and [Zrinc, 2024] consider the two-stage approaches, i.e., first estimate the shifted distribution and then optimize it. But neither of them use partial gradient information. Essential References Not Discussed: All realted works are well discussed. Other Strengths And Weaknesses: ### Strengths: 1. This paper is well written and easy to follow. Meanwhile, the proof is clearly presented. 2. Simulations are conducted to support the theorem. ### Weaknesses: 1. Motivation: Could the authors clarify the positioning of Algorithm 1 and Algorithm 2 within the existing literature on performative prediction? Specifically, how do these algorithms compare to prior approaches? If one only has access to the stochastic loss function $f(x,\xi)$ and seeks to quickly find the performative optimal solution, the two-stage method in [Miller et al., 2021] may be a more natural choice. On the other hand, if only loss values are available, existing zeroth-order methods such as [Roy et al., 2022] could be used. Given these alternatives, what specific problem setting or advantages motivate the development of the proposed algorithms? 2. Algorithm: Could you explain the definition of the distribution $D_{R}$? For Algorithm 2, is there any theoretical guidance on the historical sample size $\hat{p}$ to achieve better performance? 3. Gradient Estimator: In equation (6), the gradient estimator is affected by an important factor $\alpha$. How should it be chosen properly in practice? Additionally, we would like to see its effect on convergence behavior. Other Comments Or Suggestions: I listed some typos in this paper: 1. Line 298, 299: "Table 2" should be "Table 1." 2. Line 1125, 1126: The expectation notation $E$ should be $\mathbb{E}$. Questions For Authors: See the weakness part. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We thank the reviewer for the constructive suggestion. We answer each of the questions in the ''Weaknesses'' and ''Experimental Designs Or Analyses'' sections. ### Weaknesses. 1. Motivation. The motivation for our study is clear, and we clarify the positioning of our methods in relation to existing methods. First, as already mentioned in Section 2.2, the motivation of our method for the two-stage method by [Miller et al., 2021] is to find a stationary point without making strong assumptions about the distribution or loss function. Specifically, in section 4.2 of [Miller et al., 2021], they assume that the distribution $D(x)$ (denoted $D(\theta)$ in their paper) is included in the location-scale family, i.e. $D(x)$ needs to satisfy $$\xi \sim D(x) \Leftrightarrow \xi := \xi_0 + A x,$$ where $\xi_0$ is a random variable independent of $x$ and matrix $A$ is constant. This implies that the randomness is decision-independent, which limits practical applications. For example, in the multiproduct pricing (strategic classification) application in Section 5 of our paper, the demand (data) distribution does not satisfy this assumption. Moreover, [Miller et al., 2021] assumes that the function $f$ is strongly convex (see (A.3a) and (A.3b) in their paper). However, in the context of price optimization (machine learning), non-convex revenue (loss) functions are widely used. In contrast, we develop our method under milder assumptions; our assumptions do not require strong convexity of $f$ or any specific form of the distribution $D(x)$. In response to your comments, we will add these detailed explanations to Section 2.2. Next, the motivation for our method in relation to existing zeroth-order methods lies in leveraging the gradient information of $f$, as mentioned in the introduction section. In existing methods, $f$ is treated as a black box, and the gradient information is not used. However, in many applications, $f$ is a known function. This study speeds up the existing zeroth-order methods by using the gradient information of $f$. 2. Algorithm. Definition of $D_R$. It is a probability distribution over \{$1,2,\dots,T$\}. In Algorithms 1 and 2, the iteration to terminate is determined probabilistically using this distribution. As shown in Theorem 4.7, the convergence of our method can be guaranteed by setting $D_R$ as in the theorem. Such termination schemes are common in stochastic optimization to ensure convergence guarantees. For example, see (Ghadimi \& Lan, 2013; Theorem 3.2). Guidance for $\hat{p}$. Theoretically, the constant $\hat{p}$ can be any natural number. This is because we have derived the sample complexities of our methods in the worst-case for $h$, and $\hat{p}$ only affects the partial gradient information $h$. (Details are in the response to reviewer 2's question (1).) On the other hand, a future issue is to provide appropriate guidance for $\hat{p}$ depending on the distance between the past and current iterates. This is because as the distance increases, the past distribution may deviate significantly from the current one. In response to your comment, we will add this content to the conclusion section as a future issue. 3. Gradient Estimator. As shown in line 14 of Algorithm 1, we proposed a rule that updates $\alpha_{k+1} := 1-\gamma (1- \alpha_k)$. As noted in lines 195-199 in the left column, this updating rule promotes a faster decrease in the objective value initially and reduces the bias of the gradient estimate $g_k$ in later iterations. The updating rule of $\alpha_k$ is important to guarantee the theoretical convergence of our methods. (Details are in the response to question (1) of reviewer 2.) For the empirical setting of $\gamma$ and $\alpha_0$, if $\alpha_0$ is near 1 or $\gamma$ is too small, $\alpha$ rapidly converges to 1, resulting in behavior similar to existing methods. We set $\gamma=0.98$ and $\alpha_0:=0$ to prevent this. ### Experimental Designs Or Analyses. 1. Evaluation of the gradient norm in the experiment. In response to your comment, we will add figures that show the norm of the gradient. However, since we believe the function value better reflects the goal of the application, we will retain Fig. 1 as it is. 2. Response function of agents in strategic classification. We calculated the optimal response of the agent by the following procedure: (i) calculate the cost required for each agent to be judged as positive (the cost is $0$ for agents that have already been judged as positive), and (ii) if the cost is less than the gain from being judged as positive, the agent will change its own feature values so that it is judged to be positive. This setting does not satisfy the smoothness in Assumption 4.3. This is because the data distribution changes discontinuously at the point where the cost exceeds the gain for some agents. Despite this unfavorable setting for our methods, the experimental results show that they still perform well numerically. --- Rebuttal Comment 1.1: Comment: Dear authors, Thanks for your reply. I will raise my scores to 3 as the authors resolve my concerns.	null	null	null	null	null	null
Compressed Image Generation with Denoising Diffusion Codebook Models	Accept (poster)	Summary: This paper introduces a novel approach called the Denoising Diffusion Codebook Model, which replaces the standard Gaussian noise sampling in the reverse diffusion process with a codeword from a predefined codebook. This method enables the development of new lossy image codecs and, more broadly, compressed image restoration schemes. Claims And Evidence: Variants of the proposed Denoising Diffusion Codebook Model have a wide range of applications. This paper demonstrates them through image compression, compressed image restoration, and compressed text-based image editing, among others. Overall, the experimental results are quite convincing. Methods And Evaluation Criteria: Yes, the proposed method, which replaces continuous Gaussian samples with discrete codewords, is intuitively clear. Theoretical Claims: I have reviewed the theoretical analyses in the supplementary material. The analyses are relatively straightforward, and I have no concerns about their correctness. Experimental Designs Or Analyses: The experimental designs are well aligned with the proposed theoretical framework. Supplementary Material: Yes, I have reviewed the theoretical analyses and experimental results in the supplementary material. Relation To Broader Scientific Literature: This work is related to several areas, including generative models, image compression, and image restoration. Essential References Not Discussed: When it comes to compressed image restoration, the following paper should be cited and discussed. H Liu, G Zhang, J Chen, AJ Khisti, Lossy compression with distribution shift as entropy constrained optimal transport, International Conference on Learning Representations, 2021 Other Strengths And Weaknesses: Overall, the proposed method is highly promising and has numerous potential applications. However, as noted at the end of the paper, several aspects of the method can be further improved. Additionally, there is a lack of theoretical understanding regarding its effectiveness. Other Comments Or Suggestions: The current version is acceptable. However, the paper would be stronger with a deeper analysis of a specific topic, such as image compression, rather than providing a uniform treatment of multiple applications. Questions For Authors: In image compression, is there any benefit to adjust the codebook size K over the timesteps? Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: # Essential Reference We thank the reviewer for highlighting the insightful work by Huan Liu et al. (ICLR 2022). It is compelling to address tasks such as compressed image restoration by formalizing them as a distribution shift (via optimal transport) with an informational bottleneck. We will include a discussion of this important reference in the related work section of our revised manuscript. # Codebook Size Adjustment in Different Timesteps Dynamically adjusting the codebook size across timesteps may indeed offer potential benefits. A positive indication of this can be seen in Appendix B.3, where using different (fixed, not dynamically adjusted) codebook sizes for different timesteps leads to improved performance. However, identifying the “optimal” codebook size for each step can be challenging, as modifying the codebook size at some timestep can affect the outcomes of all subsequent timesteps. We will include this in the discussion as an interesting option for future research. --- Rebuttal Comment 1.1: Comment: I have no further comments and will maintain the original rating.	Summary: This paper introduces Denoising Diffusion Codebook Models (DDCM), a approach that replaces standard Gaussian noise sampling in Denoising Diffusion Models (DDMs) with selections from fixed codebooks of i.i.d. Gaussian vectors. Despite using a discrete and finite noise representation, DDCM preserves the sample quality and diversity of standard DDMs. The method enables state-of-the-art perceptual image compression by selecting optimal noise samples for a given image and generalizes to other conditional generation tasks, such as image restoration. Additionally, the paper provides a mathematical interpretation linking DDCM to score-based posterior sampling. Claims And Evidence: Without rigorous inspection, it can be considered that the claims in this paper are all supported by evidence. Methods And Evaluation Criteria: The paper defines bit rate based on the codebook size and the number of sampling timesteps, with the bit-stream length determined by their logarithmic relationship. This approach is closer to VQGAN-style methods rather than traditional compression metrics based on actual file size. While this provides a useful measure within the proposed framework, it would be helpful to clarify how this definition translates to real-world storage and transmission costs, and how it compares to standard rate-distortion metrics used in compression research. Theoretical Claims: The theoretical part of this paper is fine. Experimental Designs Or Analyses: Just from the text expounded in this article, the experimental designs and analysis are somewhat reasonable. Supplementary Material: I have reviewed the supp. Relation To Broader Scientific Literature: The paper is situated within the broader literature on diffusion models, generative modeling, and neural compression. Essential References Not Discussed: No essential references are not discussed. Other Strengths And Weaknesses: The idea of using discrete noise representations in diffusion models is intriguing, but the experimental setup and results are somewhat unclear. While the approach offers a novel take on generative modeling, its compression performance does not appear particularly strong when compared to traditional methods. As a generation method, it would benefit from more comprehensive evaluation using non-reference metrics, which could provide a clearer picture of its capabilities. The strength lies in the concept, but the execution in terms of compression and performance metrics needs further refinement. Other Comments Or Suggestions: See above. Questions For Authors: See above. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: # DDCM Bitrate and File Size Clarification Please note that the reported bitrate is precisely that of the compressed file size, as in traditional compression methods. Indeed, the mentioned logarithmic relationship $T\cdot log_{2}(K)$ between the codebook size $K$ and the number of sampling steps $T$ directly calculates the file size (in bits). This holds since each DDCM-generated image corresponds to a sequence of $T$ integers, each in $[0,K-1]$, that represent the indices of the codebook entries chosen during the generation (as depicted in Fig. 2). This sequence is then represented in a binary format and saved as a file. E.g., for $T=3,K=4$, the indices sequence [1,3,0] translates to the bitstream “011100”. We compare our method against previous compression approaches (including traditional ones) according to their file size (using BPP). # Experimental Setup and Results Clarification We apologize for any confusion about our experimental setup and results. Our paper contains multiple different experimental settings (starting at lines 157(R), 188(R), 309(R), and 368(R)), involving image generation, compression, and restoration, following common practices in each of these fields. Let us clarify. ### Section 4 in the paper This section shows that DDCM maintains competitive generation capabilities relative to DDPM, even with small codebooks (lines 158(R)). Specifically, we show that DDCM achieves comparable performance to DDPM as measured by standard generative metrics like FID (Fig. 3, main text), KID (Fig. 8, App. A), and through visual inspection (Figs. 9 & 10, App. A) across two distinct datasets: ImageNet and MS-COCO. This experiment is intended to validate our hypothesis regarding the redundancy of the continuous Gaussian representation space utilized in traditional DDMs (lines 016(R) & 182(L)). ### Section 5 in the paper This section introduces our perceptual image compression method, based on DDCM. We compare our method to prior approaches using standard rate-perception-distortion evaluations [R2], assessing perceptual quality (FID) and distortion (LPIPS, PSNR) across multiple bitrates (BPP). These quantitative comparisons are provided in Fig. 5, complemented by qualitative assessments in Fig. 4, following common evaluation practices. Both our quantitative and qualitative results demonstrate the superiority of our proposed method over existing techniques (lines 243-258(L)). In Appendix B, we also include additional qualitative results, as well as additional quantitative results for higher-resolution images (Figs. 11-16). ### Section 6 in the paper Here, we propose extending our compression framework to handle more general compressed conditional generation tasks, such as compressed image restoration. Our experiments in the main text cover two tasks: zero-shot posterior sampling (Sec. 6.1) and blind face image restoration (Sec. 6.2). We compare our method with previous state-of-the-art approaches, assessing both distortion (PSNR) and perceptual quality (FID), thus adhering to established evaluation protocols in image restoration [R1]. The qualitative and quantitative results, presented in Figs. 6 & 7, show that our method achieves superior perceptual quality compared to previous methods (lines 353-357(L) & 421-428(L)). Apps. C.3 & C.4 provide additional results (Figs. 17-22). We hope this clearly addresses the concerns raised regarding the clarity and comprehensiveness of our experimental setup and results. # Superior Perceptual Compression Performance Kindly note that our image codec is designed for perceptual image compression, meaning that we aim to achieve best output perceptual quality. Due to the rate-perception-distortion tradeoff [R2], this is expected to compromise the distortion (e.g., PSNR, LPIPS) of our method. Indeed, since our method achieves the lowest (best) FID (perceptual quality) for almost all bitrates and datasets (Figure 5), the rate-perception-distortion tradeoff explains why our method does not always achieve the best distortion. However, note that we do achieve better distortion compared to previous perceptual image compression methods such as PerCo (SD), while also achieving better perceptual quality. # Generation Evaluation Using No-Reference Metrics We kindly note that it is not common practice to evaluate image generation methods with no-reference quality measures (e.g., NIQE [R3]), since the goal in image generation is to sample from a data distribution. No-reference quality measures only assess the quality of the generated images and not their diversity, whereas metrics such as FID and KID (which we report in the paper) assess quality and diversity simultaneously. ## References [R1] Yochai Blau & Tomer Michaeli. The perception-distortion tradeoff. CVPR 2018. [R2] Yochai Blau & Tomer Michaeli. Rethinking lossy compression: The rate-distortion-perception tradeoff. ICML 2019. [R3] Anish Mittal et al. Making a ‘completely blind’ image quality analyzer. ACCSC 2012. --- Rebuttal Comment 1.1: Comment: The rebuttal addressed most of my concerns.	Summary: This paper presents a novel approach, DDCM, to represent an image by DDPM procedure using a set of gaussian noise (codebook) indices. In other words, this paper shows that it is possible to "discretize" the "z" at every step of DDPM to approximate a high-quality diffusion procedure. DDCM can also be leveraged to solve various tasks, like text-to-image and image-to-image problems, which shed a light for codebook-based diffusion sampling procedure. Claims And Evidence: Claims in this submission are fully supported by clear and convincing evidence. Methods And Evaluation Criteria: The proposed method, DDCM, is suitable for the visual generative problem, especially for compressed image generation. The evaluation criteria, computing several metrics on validation set like ImageNet, makes sense for visual generation. There are some minor points and see experiment design parts. Theoretical Claims: I am not an expert on mathematical proof on diffusion theory but proofs in C.2 seem sound and correct to me. Experimental Designs Or Analyses: The experimental designs and analyses are sound but some points and result presentation seem confusing. 1. In Figure 3 left, is the FID scale 10^1? Then it means that FID only decreases from 10.5 to 9.5 when increasing K from 2 to 64, which is not significant. Additionally, what is the exact FID value for DDPM in this figure? In my view, an FID of approximately 9.0 on ImageNet for DDPM or DDCM is not that strong. However, the visualizations do show high-quality samples. I'd like to see the authors' insights on this. 2. Relevant to P.1, what is the scale in Figure 5 FID, is it linear scale or log scale? Why show VAE bound instead of DDPM bound in Figure 5? 3. Can authors include the computing time of Equ (7)? Is the method efficient? Supplementary Material: I reviewed the supplementary A to C.3. Relation To Broader Scientific Literature: I think that the key contribution of this paper is discretization of the z noise in DDPM procedure, which is indeed novel and unexplored before. Essential References Not Discussed: I have not found essential references not discussed in this submission. However, I feel it is necessary to include discrete visual tokenization methods in the discussion since the proposed DDCM essentially does the discretization on images using diffusion models. The authors can discuss DDCM and discrete tokenization methods in a paragraph but not experiments needed. Other Strengths And Weaknesses: Overall, this submission is a good and novel paper on discretizing the z noise in diffusion steps and representing images by compressed noise indices. For other minor concerns, please see Questions For Authors. Other Comments Or Suggestions: Suggestions: the authors can provide absolute metric values in numeric forms in figure or table presentation, which could make results of DDCM more clear. Questions For Authors: I'd like to see insights for several open-end questions listed below from authors. No experiments needed. 1. Flow matching/rectified flow generative models are gaining popularity in the research community and have demonstrated competitive results. However, there is no random noise in ODE process behind FM except for initial point. Given this, can DDCM be applied to recent flow matching models like FLUX? 2. Is DDCM limited to the fixed-resolution generation process, given that the codebook fixed after intialization? Can noise codebook generalize to other resolutions with minimal efforts? 3. For better performance, is it doable to make noise map codebook learnable? Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: # Fig. 3 FID Yes, the FID scale in Fig. 3-L is $10^1$. The FID of DDPM is 9.21 (black dashed line). Indeed, some prior works with the same DDM reported lower FID on ImageNet 256x256, when using 50k generated samples [R2]. However, we use only 10k generated samples (see L171-L) to reduce computation time, similarly to [R3,R4]. Decreasing the number of samples is known to increase the FID [R1]. To validate this, we computed the FID between the same 50k reference images and two random subsets from the ImageNet 256x256 training set, consisting of 10k and 50k images. These subsets obtained FID=4.934 and FID=1.968, respectively. Note that this experiment only aims to demonstrate DDCM's competitiveness with DDPM, specifically for small codebooks. Indeed, the modest decrease in FID from 10.5 to 9.5 (when increasing $K$) is a strength of our method rather than a limitation: even for $K=2$, DDCM achieves FID$\approx$10.5 (competitive with DDPM). This supports our hypothesis (L016-R & L182-L) that the Gaussian representation space used by standard DDMs is redundant. # Fig. 5 & VAE Bound The FID scores for the compression results in Fig. 5 are in log scale. Regarding the “VAE bound,” we apologize for the misunderstanding, this term was not clarified in the paper. In some experiments we employ a latent DDM (specifically, SD 2.1), so we are compressing the latent VAE encoding of a given image, rather than the image itself. Since encoding-decoding an image using a VAE typically does not yield perfect image reconstruction, the distortion of any VAE-latent-space-based compression method (e.g., ours, PerCo, PSC) is bounded by that of the VAE encoder-decoder. The “VAE bound” in the figure corresponds to the distortion resulting from encoding and decoding the original images using only the VAE, without any additional compression. This bound is important to present since it allows to distinguish the distortion caused by the VAE from that caused by the compression scheme. Thanks for these important points. We will clarify them in the revised paper and replace the term “VAE-bound” with “SD 2.1 Encoder-Decoder bound.” # Eq. (7) Efficiency Please note that Eq. (7) does not involve any gradient computation, iterative optimization, or use of a neural network. It involves a straightforward matrix multiplication followed by picking the maximum out of K scalars. Empirically, on an L40S GPU with $K=8192$ and 256x256 images, this operation takes 0.357ms on average (over 100 trials). This is negligible compared to the DDM’s forward pass, which takes 57.2ms on average. # Tokenization Methods We appreciate this suggestion. Viewing DDCM-based compression as an image tokenization method with random noises acting as the tokens is interesting. We will discuss this in our paper revision. # Numerical Results Thanks for this valuable suggestion. We will add numerical comparisons to the appendix. # Applying to Flow Matching Models Although flow-matching models typically generate samples by solving an ODE, several works (e.g., [R5,R6]) have shown they can also generate samples by solving an SDE, which involves adding noise at each generation step. Thus, we believe that such flow-matching SDEs may be discretized as well, similarly to DDCM. # Resolution Generalization DDCM is easily generalizable to any resolution. Instead of pre-sampling the codebooks with a particular resolution, one can rely on a shared-seed random generator to dynamically generate codebooks for different resolutions. Specifically, one can store/transmit the resolution as part of the bitstream and, before compressing/decompressing an image, randomly sample the codebooks for the given resolution. Using the same seed for compression and decompression ensures that both would rely on the same codebooks. If no shared-seed random generator is available, one can pre-sample the codebooks for a maximal allowed resolution, store/transmit the resolution of the image, and dynamically slice smaller codebooks from the pre-sampled ones. Therefore, the generalizability of DDCM to different resolutions is determined only by that of the pre-trained DDM. # Learnable Codebooks Learning the codebooks may indeed enhance DDCM’s performance (as noted in L433-R), particularly in compression. We investigate this in our future work. ## References [R1] Mikołaj Bińkowski et al. Demystifying MMD GANs. ICLR 2018. [R2] Cheng Lu et al. DPM-solver: A fast ode solver for diffusion probabilistic model sampling in around 10 steps. NeurIPS 2022. [R3] Cheng Lu et al. DPM-Solver++: Fast solver for guided sampling of diffusion probabilistic models. arXiv:2211.01095. [R4] Kaiwen Zheng et al. DPM-Solver-v3: Improved diffusion ODE solver with empirical model statistics. NeurIPS 2023. [R5] Jeongsol Kim et al. FlowDPS: Flow-driven posterior sampling for inverse problems. arXiv:2503.08136. [R6] Litu Rout et al. Semantic image inversion and editing using rectified stochastic differential equations. ICLR 2025.	null	null	null	null	null	null	null	null
Riemann Tensor Neural Networks: Learning Conservative Systems with Physics-Constrained Networks	Accept (poster)	Summary: This paper is within the setting of learning physical systems from PDE equations. The authors propose a neural network architecture that outputs a divergence-free symmetric tensor (DSFT). By adding this constraint, the neural network is guaranteed to enforce conservation of mass and momentum. In multiple experiments, the authors describe how to recover the solution from the DSFT output, after training the model on a loss function comprising PINNs loss, energy loss, and supervised L2 loss at some points. The authors compare their method to PINNs and Neural Conservation Laws (NCL), the latter of which is a similar method that only enforces conservation of mass. They also use their method to augment and compare to separable physics informed neural networks S-PINNs. # Post rebuttal response I raised my score from 2 to 3 after the authors' rebuttal (see my comment below). Claims And Evidence: The method is presented in a straightforward way and makes sense that it would be an improvement over unconstrained PINNs and NCLs which only conserve mass. The experiments appear sensible and show a marked improvement over the selected baselines. Methods And Evaluation Criteria: Yes, the evaluation criteria make sense. They compare to other common problems and show an order of magnitude improvement in each case. My expertise is not in PDEs, so I cannot attest to whether these problems are meaningful to that domain; this would be something I would defer to other reviewers on. Theoretical Claims: I did not check the proofs of the theoretical claims. Experimental Designs Or Analyses: I read through the design and setup of the experimental designs. I have a concern with how the competing methods are constructed. For example, in section 3.2, the loss function used to train the method is defined in terms of isotropic loss and energy conservation, rather than the PDE system described in (11)-(13). It seems that a different loss function is used for PINNs and NCL (line 247, column 2). Thus, it is unclear whether the performance increase is due to a different loss function or due to the novel architecture (the author's contribution). Supplementary Material: No, the supplementary material was code which I did not review. Relation To Broader Scientific Literature: This method offers a novel architecture to provide hard constraints on conservation of mass and momentum. It builds on methods like NCL by hard-coding physical invariants into the architecture. Essential References Not Discussed: I am not aware. Other Strengths And Weaknesses: I think the idea to build constraints into the architecture makes sense and is a good approach. If my concern about the experimental section is addressed, I would consider raising my score. Other Comments Or Suggestions: N/a Questions For Authors: Please see my comments under "Methods and Evaluation Criteria". While the results of your method appear strong, for the comparison to be fair the only difference between each comparator should be the architecture (i.e., PINNS=unconstrained, NCL=mass only, DSFT=mass and momentum). Please clarify whether this is the case in your experiments. If not, I request that you provide the results showing differences in architecture. Otherwise, it is unclear whether your method does better simply by using a specialized loss function for each problem (while NCL and PINNs do not). Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We thank the reviewer for their time reviewing the manuscript and their feedback that will contribute to improving the clarity of our work. Below we address the reviewer's concern: Methods and Evaluation Criteria: PINN and NCL were both trained using the full system (11)--(14), which includes the conservation of mass, momentum, and energy equations. For NCL , the mass conservation equation is satisfied by construction and cancels up to machine precision. For RTNN, the continuity equation similarly cancels out and the energy equation (14) is also included in the loss. The only apparent difference is that RTNN replaces the explicit momentum residual with an isotropic loss term. However, this isotropic loss term naturally emerges when substituting the RTNN-predicted fields into the flux-form momentum equation. Imposing the zero-deviatoric condition on the stress tensor is numerically equivalent to enforcing the momentum equation directly in its expanded form (12--13). This equivalence can be evidenced following the reasoning below: Consider the compressible Euler system in (11)--(14): In our RTNN parametrization, the network outputs a flux tensor \$S\$ defined as: $$ S = \\begin{pmatrix} \\rho & (\\rho u)^T \\\\ \\rho u & \\rho u \\otimes u + \\sigma \\end{pmatrix}, $$ with \$\\rho = S_{0,0}\$ and \$\\rho u = S_{0,1:n}\$ . The stress tensor is then defined by: $$ \\sigma = S_{1:n,1:n} \\; - \\; \\rho\\, u \\otimes u. $$ We impose a zero-deviatoric constraint on \$\\sigma\$, meaning its deviatoric part vanishes: $$ \\sigma_{\\mathrm{dev}} \\;=\\; \\sigma \\; - \\; \\frac{1}{n}\\,\\operatorname{tr}(\\sigma)\\,I \\;\\triangleq 0. $$ This forces: $$ \\sigma \\triangleq \\frac{1}{n}\\,\\operatorname{tr}(\\sigma)\\,I \\quad \\triangleq \\quad pI, $$ with the pressure defined as: $$ p =\\ \\frac{1}{n}\\,\\operatorname{tr}(\\sigma). $$ Substituting \$\\sigma \\triangleq pI\$ back into the flux tensor, we obtain: $$ S = \\begin{pmatrix} \\rho & (\\rho u)^T \\\\ \\rho u & \\rho u \\otimes u + pI \\end{pmatrix}. $$ Our architecture enforces that \$S\$ is divergence-free: $$ \\nabla \\cdot S = \\begin{pmatrix} \\partial_t \\rho + \\nabla \\cdot (\\rho u) \\\\[6pt] \\partial_t (\\rho u) + \\nabla \\cdot (\\rho u \\otimes u + pI) \\end{pmatrix} = 0. $$ The first row yields the continuity equation: $$ \\partial_t \\rho + \\nabla \\cdot (\\rho u) = 0. $$ The second row yields: $$ \\partial_t (\\rho u) + \\nabla \\cdot \\Bigl(\\rho u \\otimes u + pI\\Bigr) = 0, $$ which when expanded yields the following equations: $$ \\partial_t \\rho + \\nabla \\cdot (\\rho u, \\rho v) = 0 \\tag{11} $$ $$ \\partial_t (\\rho u) + \\nabla \\cdot (\\rho u^2, \\rho u\\,v) = -\\partial_x p \\tag{12} $$ $$ \\partial_t (\\rho v) + \\nabla \\cdot (\\rho u\\,v, \\rho v^2) = -\\partial_y p \\tag{13} $$ This is exactly the system in (11--13). A similar reasoning can be applied when adding viscous terms (or magnetic terms), for instance. Furthermore, to address the reviewer's concern numerically, we conducted an experiment in which the velocity and pressure fields extracted from a single RTNN were trained using the expanded momentum (12)--(13) equation rather than the simplified condition on the stress tensor. In this setting, the only difference among the experiments is the architecture. Although this process is more computationally expensive --- owing to the necessity of computing a fourth-order derivative --- the RTNN-trained fields still demonstrate similarly superior accuracy compared to those obtained with PINN and NCL. We summarize the obtained results below for the two unsteady Navier--Stokes problems: flow around a cylinder and the Beltrami flow for five different initialization seeds: \| Method \| Beltrami rL2 (Median ± IQR) \| Cylinder rL2 (Median ± IQR) \| \|---------------------------------------\|-------------------------------------\|-------------------------------------\| \| RTNN (expanded momentum equation) \| 4.55e-04 ± 8.1e-05 \| 5.13e-03 ± 4.2e-04 \| \| RTNN (stress tensor condition) \| 4.28e-04 ± 5.9e-05 \| 5.70e-03 ± 4.3e-04 \| \| NCL \| 1.73e-03 ± 8.5e-05 \| 2.54e-02 ± 1.9e-03 \| \| PINN \| 1.41e-03 ± 3.1e-04 \| 2.99e-02 ± 7.9e-04 \| We acknowledge that the derivation of the condition on the stress tensors from the momentum equations could have been made clearer in the manuscript. We will appropriately make this link clear in the camera-ready version and provide the direct derivation in the appendix. We hope we have addressed the reviewer's main concerns and remain at their disposal should further clarifications be needed. --- Rebuttal Comment 1.1: Comment: I appreciate the author's response. I appreciate the additional table showing the performance of RTNN using the same loss function as PINNs and NCL. I think this highlights the benefit of the architecture, because the error improvement is mostly the same. Also, your response implicitly shows the benefit of your RTNN reparameterization in avoiding the fourth-order derivative computation. I'm willing to raise my score, since my main concern from the review is addressed.	Summary: In this paper, a method for learning divergence-free symmetric tensors is proposed. As neural network architectures that maintain conservation laws, a typical approach is learning divergence-free vector fields by using the exterior calculus. The proposed method is another approach based on a different geometric structure. As far as I know, the use of this structure is certainly new. In numerical experiments, it is shown that the proposed method achieves higher accuracy than a method for learning divergence-free vector fields. I think that the proposed approach is very interesting and powerful. Claims And Evidence: The method is clearly explained with its theoretical background. Methods And Evaluation Criteria: I believe that the proposed method is evaluated in an appropriate manner. Theoretical Claims: I checked the outline of the proofs, but I did not check them thoroughly. Experimental Designs Or Analyses: I believe that the experiments are designed appropriately; however, it seems strange that NCL performs worse than ordinary PINNs as seen in Table 1. In my understanding, similar to the proposed method, NCL is designed to satisfy conservation laws. However, the performance of one method (the proposed method) improves greatly while the other (NCL) declines, even though they are trying to maintain similar properties. Supplementary Material: I have checked Supplementary Material to a certain extent, but I did not check the details. Relation To Broader Scientific Literature: This paper proposes a new structure for neural networks that preserves conservation laws. In previous papers, the property d d = 0 of the exterior derivative has been mainly used. The approach in this paper is different from those in the existing papers and has a potential to improve neural networks for physics. Essential References Not Discussed: Perhaps discussing the following paper, which is an operator learning method that is based on a similar approach to CLN, is not essential but helpful for understanding the contributions of this paper. Ning Liu, Yiming Fan, Xianyi Zeng, Milan Klöwer, Lu Zhang, Yue Yu, Harnessing the Power of Neural Operators with Automatically Encoded Conservation Laws, https://arxiv.org/abs/2312.11176 Other Strengths And Weaknesses: Overall, I think that this is a very interesting paper. Other Comments Or Suggestions: None. Questions For Authors: I want to confirm the main difference between NCL and the proposed method. In my understanding, it is difficult for NCL to preserve multiple conservatoin laws simultaniously, but the proposed method can preserve them. Is this understanding correct? Also, why did NCL perform so poorly in the numerical experiment? Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: We would like to thank the reviewer for their time and feedback. Below we address some of the raised points: Main Difference between NCL and RTNN: NCL enforces only the continuity (mass-conservation) equation, whereas our approach reformulates the conservation laws in flux form, constraining each flux tensor to be both divergence-free and symmetric. This flux representation allows us to extract primitive fields—density, momenta, and stress tensors—that are geometrically coupled and, by construction, satisfy both mass and momentum conservation. In fact, when the RTNN-derived fields are substituted into the flux-form momentum equation, the momentum conservation learning problem is reduced to an optimization problem on the stress tensors. On NCL’s Performance in the Compressible Experiment: In our compressible experiment, NCL underperformed compared to other approaches. In this case, we have variable density and an additional energy equation, a scenario that differs from the incompressible cases where NCL performed well (both in our experiments and in the original NCL paper). Upon investigation we observed that, in the compressible setting, the NCL architecture struggled to simultaneously satisfy the PDE residual and the initial condition, likely due to imbalances in the loss terms. To verify this hypothesis, we transformed the ansatz to the following form: $$ F(t, x) = \text{NCL}(t, x) - \text{NCL}(0, x) + u_0(x) $$ Here, \$ u_0(x) \$ represents the initial condition. This formulation enforces both the continuity and initial conditions by design, resulting in significantly improved accuracy and confirming our conjecture, and also supports the argument that hard constraint satisfaction leads to simpler optimization problems. Related References: We reviewed the reference by Liu et al. [1] and find it both interesting and relevant to our work, we thank the reviewer for bringing it to our attention. We will add it to the related work section of the camera-ready version. We hope to have addressed the reviewer's question sufficiently and remain at their disposal throughout the review process. References: [1] Ning Liu, Yiming Fan, Xianyi Zeng, Milan Klöwer, Lu Zhang, Yue Yu, Harnessing the Power of Neural Operators with Automatically Encoded Conservation Laws, https://arxiv.org/abs/2312.11176	Summary: This paper concerns preserving certain structure properties when using neural networks to solve partial differential equations. The method uses an inductive bias by enforcing a certain form of the tensor field approximation, and the final form is called "Riemann Tensor Neural Network" (RTNN) involves some non-trainable final layer, plus an "differentiation layer" where the Hessian of the output from the previous layers is computed. Claims And Evidence: The authors show that RTNN is constructed to satisfy the divergence-free form of systems of conservation laws. This is shown by straightforward calculation. In numerical experiments, the authors illustrate that RTNN can be used in a collocated PDE-related loss minimization framework similar to Physics-Informed Neural Networks (PINNs) framework to solve various PDEs. Methods And Evaluation Criteria: The evaluation criteria is relative L2 error against reference solution, which is reasonable. Theoretical Claims: The RTNN is constructed to theoretically satisfy the DSFT constraints, and the proof is straightforward. So numerically the fields satisfy the constraints to machine precision. Experimental Designs Or Analyses: The tested set of PDEs is significant that can be challenging for standard PINNs. However, it is not easy to see what kind of singular behaviors (sharp gradients) the solution has. Perhaps the authors can describe more in detail what kind of features are challenging to learn in these problems for existing methods like PINNs, and what contributes to the high errors for these methods (as opposed to RTNNs). There are some details in the current form of the manuscript, but it is hard to infer what the challenge is for the individual problems. Supplementary Material: The error plots show great improvements in accuracy over a couple existing methods. Relation To Broader Scientific Literature: Structure preservation is a major theme in classical numerical schemes, perhaps the authors can mention a few references (texts, survey papers). Essential References Not Discussed: This type of embedding of conservation laws appear to be new, as far as I know. Other Strengths And Weaknesses: The PDEs that appear in numerical examples are challenging PDEs for PINNs. The results show a clear advantage compared to standard PINNs. The universal approximation theorem (Theorem 2.4) appears to be a very generic result, however, and does not shed a lot of light into why RTNNs have superior numerical performance. Other Comments Or Suggestions: I suggest the authors show a few of the solution plots (rather than the error plots only) so the readers can infer the difficulty in PINNs solution Questions For Authors: Is there any numerical issues for approximating the solution that contains what is essentially a "differentiation layer"? Repeated differentiations can result in loss of significant digits, and can be a source of instability. Code Of Conduct: Affirmed. Overall Recommendation: 5	Rebuttal 1: Rebuttal: We thank the reviewer for the detailed comments and suggestions. We appreciate them and hope to address some of the questions below: Suggestions: We agree that including representative solution plots would help the reader infer the difficulty in PINNs solution. We also appreciate the suggestion to cite relevant literature on structure-preserving numerical methods. Both additions will be included in the camera-ready version. Why do RTNNs perform better than PINNs: PINNs are notoriously difficult to optimize despite their recent success [1] . From the very advent of PINNs, several authors have advocated modifying machine learning models such that the boundary conditions or conservation laws are exactly zero. This has been empirically shown to improve training accuracy, including in our own work. The work in De Ryck et.al [2] links the training dynamics of PINNs to the condition number of a Hermitian operator A that depend both on the PDE operator and the boundary operator. They show that hard-imposing constraints within the architecture reduces the condition number of A, which in turn improves the training dynamics and accelerates convergence. Another way of explaining the superior performance of RTNNs relative to unconstrained networks is their ability to capture and exploit the intrinsic relationships between physical fields. In many fluid dynamics problems, one must simultaneously model a scalar density field, a vector velocity field, and a scalar pressure field. Conventional unconstrained models typically treat these components as independent scalar output channels, thereby ignoring the important geometric and physical correlations—such as the interdependence between the directional components of the velocity field, or the influence of pressure gradients on both density and velocity. By contrast, RTNNs treat these quantities as a unified field coupled through a shared conservation-law-based flux, this in turn leads to superior accuracy during the training. We believe this discussion will improve the quality of our manuscript. We will include a dedicated paragraph on this topic in the final version, and we thank the reviewer for raising this point. Question on Differentiation Layer: In our implementation, we compute at most third-order derivatives, and all experiments were conducted in double precision (we will state this explicitly in the revised manuscript). While repeated differentiation can in principle lead to numerical issues, we did not observe any instabilities or degradation in constraint satisfaction. The resulting tensors remained divergence-free and symmetric to machine precision throughout. In fact, we also verified that this property holds under single precision as well (although naturally this leads to degradations in accuracy for all methods). We hope that we addressed the reviewer's questions and we will stay attentive for further questions throughout the review process. References: [1] Wang, S., Yu, X., & Perdikaris, P. (2020). When and why PINNs fail to train: A neural tangent kernel perspective. arXiv preprint arXiv:2007.14527. [2] De Ryck, T., Bonnet, F., Mishra, S., & de Bézenac, E. (2024). An Operator Preconditioning Perspective on Training in Physics-Informed Machine Learning. ICLR 2024.	Summary: The paper proposes RTNNs, which can encodes the divergence-free constraints in neural networks within the PINN framework. The divergence-free constraint is satisfied by computing the hessian matrix of a feed-forward MLP network and combining with a special-designed basis. The method is evaluated on a range of PDE tasks requiring the divergence-free condition. Claims And Evidence: - Although understanding the theorem in section 2.1 seems to be beyond my knowledge, the description of divergence-free construction using hessian matrix is clear and convincing. - The experimental results look strong compared to PINN and NCL, although I am not familiar with the latter one. Methods And Evaluation Criteria: - The benchmarked problems are reasonable and diverse. - In line 270 left it says "$L_{data}$ incorporates supervised learning by penalizing the discrepancies between the model predictions and observed data labels". But in line 236 right it says "training is performed entirely without labeled data". It seems to be inconsistent. Theoretical Claims: - I did not check the correctness of math but the theory seems to be sound. Experimental Designs Or Analyses: - Line 243 right: "Both methods use similar MLP architectures for fairness." Are they exactly the same? - Is NCL supposed to be a strong baseline? The results of NCL in table 1 seems to be worse than PINN. Supplementary Material: - I did not check the appendix in detail. Relation To Broader Scientific Literature: - They are adequately discussed. Essential References Not Discussed: - Not I am aware of. Other Strengths And Weaknesses: - The paper is well written. - The method still requires other soft constraints to satisfy other constraints. - The use neural network model is rather simple. Other Comments Or Suggestions: - I did not notice typo. Questions For Authors: - Will computing Hessian matrix affect the scaling of computation cost? - What does the parentheses in equation 2 and 3 in subscripts mean? - Is there any intuitive way to understand theorem 2.1? For example, what does it mean in terms of quantities on the simulation grid? Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We would like to thank the reviewer for their time and feedback. Below we address the reviewer's questions: Label Data Inclusion While we can incorporate labeled data to penalize discrepancies between predictions and observations, for this experiment we did not. We acknowledge the inconsistency between line 270 and line 236 and will correct it in the final version. Both methods use similar MLP architectures for fairness. Are they exactly the same? Both methods share identical hidden-layer configurations (depth, width, activation). The only difference is the final output layer, where each architecture produces the specific number of scalars required by its formulation. Is NCL a Strong Baseline? We address the NCL performance issue for the compressible case in our response to reviewer G2wL. Will computing the Hessian matrix affect the scaling of computation cost? A key contribution of our work is the formulation of a computationally tractable ansatz that scales well in the 2D+1 and 3D+1 cases of interest. Rather than naively parameterizing a (0,4)-tensor— which would require outputting \$ \mathcal{O}(N^4) \$ , where N is the number of spacial components components — we exploit an isomorphism with two-forms to reduce the number of scalar outputs to \$ \tfrac{N(N+1)}{2} \$, thereby limiting the number of second-order derivatives that must be computed. Computing the Hessian is inherently expensive; however, we address this challenge through two derivative evaluation strategies: - Taylor-mode Automatic Differentiation: We compute second derivatives using Taylor-mode AD, which efficiently propagates truncated Taylor expansions ("jets"), thereby sharing repeated derivative computations across different orders through the network. For a scalar-output MLP, the complexity scales as \$ \mathcal{O}(L d W^2) \$, where \$ L \$ is the number of layers, \$ W \$ is the layer width, and \$ d \$ is the order of the derivative. This ensures that, for typical 2D+1 and 3D+1 PDEs, the cost of higher-order derivatives remains within a modest constant factor of a standard forward pass. - SPINNs for Magneto-Hydrodynamics: In Section 3.4, we take advantage of the SPINN architecture[1] to decompose multi-dimensional derivative evaluations into per-axis components, reducing the cost from \$ \mathcal{O}(N^d) \$ to \$ \mathcal{O}(N\ d) \$, where \$ N \$ is the number of collocation points per axis and \$ d \$ is the order of the derivative. Together, these strategies ensure that while computing the Hessian is expensive, our approach remains scalable and computationally tractable for the 2D+time and 3D+time problems of interest. What do the parentheses in equation 2 and 3 in the subscripts mean? In tensor algebra, a pair of indices enclosed in round parentheses denotes symmetrization with respect to those indices. For example: \\[ T_{(ab)\dots} = \frac{1}{2} \left( T_{ab\dots} + T_{ba\dots} \right) \\] Intuition Behind Proof 2.1: At each grid point, we must generate a flux tensor that satisfies the DSFT condition exactly. Theorem 2.1 provides a systematic way to achieve this. We take advantage of the fact that the divergence of a second derivative of a four-tensor naturally vanishes under certain symmetries (2)--(4). Specifically, if we define $S_{ab}$ in terms of a second derivative of some four-tensor $K_{abcd}$, the divergence-free condition is automatically satisfied due to the symmetry properties of partial derivatives. This is reminiscent of how potentials are used in physics to impose constraints on derived quantities. For example, in electromagnetism, introducing a four-potential \$ A_\mu \$ ensures that the field strength tensor \\[ F_{\mu\nu} = \partial_\mu A_\nu - \partial_\nu A_\mu \\] automatically satisfies the Bianchi identity: \\[ \partial_\lambda F_{\mu\nu} + \partial_\nu F_{\lambda\mu} + \partial_\mu F_{\nu\lambda} = 0 \\] We hope that we addressed the reviewer's questions sufficiently and we will stay attentive for further questions throughout the review process. References : [1] Cho, J., Nam, S., Yang, H., Yun, S.-B., Hong, Y., & Park, E. (2023). Separable Physics-Informed Neural Networks. Advances in Neural Information Processing Systems 36 (NeurIPS 2023).	null	null	null	null	null	null
An Augmentation-Aware Theory for Self-Supervised Contrastive Learning	Accept (poster)	Summary: This paper explores the role of data augmentation from the perspective of theoretical research. It for the first time propose an augmentation-aware error bound for self-supervised contrastive learning, showing that the supervised risk is bounded not only by the unsupervised risk, but also explicitly by a trade-off induced by data augmentation. It also discuss how certain augmentation methods affect the error bound. Some experiments verify its proposed theoretical results. Claims And Evidence: Yes. Methods And Evaluation Criteria: Yes. Theoretical Claims: Yes. I have carefully check the correctness of all proofs in this paper. Some issues I found are listed behind. Experimental Designs Or Analyses: No. Their experiments are intuitive. Supplementary Material: No. There is no supplementary material. Relation To Broader Scientific Literature: Please see the above Summary. Essential References Not Discussed: No. Other Strengths And Weaknesses: Strengths: 1.This paper for the first time proposes an augmentation-aware error bound for self-supervised contrastive learning, which is quite interesting. Weaknesses: 1.In the lines 103-105, the symbol of the set of all possible data points should be $\bar{X}$ instead of $P_{\bar{X}}$. 2.In the second paragraph of Section 2.1, the first sentence should be “In unsupervised contrastive learning, we select the different data augmentations of the same input image as the positive samples, and select the data augmentations of different input images as negative samples”. 3.On the right head of the line 82, there lacks a period between “assumption”and “Moreover”. 4.The equation between the line 138 and 139 lacks a minus sign in the exponential function. 5.There are some mistakes in proof. For example, (1) the decomposition at the beginning of Proof of Theorem 2.7 should have $p_{K-1}(...) r_{K-1}(...)$; (2) the last equation of Equation (31) should be $\sum_{m=1}^k$. 6.The setting of Equation (26) is not very rigorous. Therefore, Equation (25) and Equation (29) are not strictly equivalent. Besides, it may be necessary to make some modifications to Theorem 2.6 and its proof. 7.On the right head of the line 309, “likewise” should be “Likewise”. 8.Equation (21) exceeds the page margin. Other Comments Or Suggestions: Because of Question 6, I have not read the analysis of Section 3 carefully. If the authors provide some reasonable explanations for my concerns, I will improve my score. Questions For Authors: 1.In the third paragraph of Introduction, the authors state that the augmentation overlap assumption is still barely realistic, because in practice, it is unlikely for two different real images to share exactly the same augmented views. However, in my opinion, if an image has an augmented view having the same semantics as another image, we can say that these two images are augmentation overlapping. 2.What is the relationship between the distributions $P_X$ and $P_{\bar{X}}$? 3.Which results in Arora et al., 2019 and Nozawa &Sato, 2021 does Lemma 2.8 represent? 4.The authors state that they derive a novel decomposition of unsupervised contrastive risk. However, from my perspective, it is just a detailed expansion of unsupervised contrastive risk. What are the advantages of this decomposition? 5.What is the purpose that the authors provide the generalization bound in Theorem 2.4? It seems to be not essential. Please have more discussions about Theorem 2.4. 6.Assumption 3.1 is very confusing. Generally, Lipschitz continuity condition is $\\|f(w) - f(w^\prime)\\|\leq \\|w-w^\prime\\|$, where $w,w^\prime$ represent model parameters. Some works denote model parameter as $x$. However, in this paper, $x$ represents sample (image). Therefore, I suggest the authors carefully explain this assumption (it is better to give some examples) and check their subsequent analysis. Code Of Conduct: Affirmed. Overall Recommendation: 2	Rebuttal 1: Rebuttal: We express our sincere gratitude to Reviewer Do5D for appreciating the novelty of our theory. We address your concerns below. --- Weaknesses. W1,W2,W3,W4,W7,W8. A. We will revise the typos as suggested. W5. Mistakes in proof. (1) the decomposition at the beginning of Proof of Theorem 2.7 should have $p_{K-1}(\ldots)r_{K-1}(\ldots)$; (2) the last equation of Eq(31) should be $\sum_{m=1}^k$. A. (1) The typo $r_K$ in the second line should be $r_{K-1}$, so that $p_{K-1}r_{K-1}$ appears in the second term of the decomposition. This typo does not affect the overall correctness of the proof. (2) No, the summation should be $\sum_{m=k+1}^K$. According to the definition of $r_k$, there are $k$ different-class negatives, so the summation $\sum_{m=1}^K$ here breaks into two groups: the negatives $\bar{x}\_m$ having different classes from the anchor $\bar{x}$ ($\sum_{m=1}^k$) and the negatives $\bar{x}\_m$ sharing the same classes as the anchor $\bar{x}$ ($\sum\_{m=k+1}^K$). By fixing the abuse of notation $k$, Eq(31) becomes $$ \log(1+\sum_{m=1}^k\exp(-\mathbb{E}\_{\bar{x}\_m\sim\rho_{i_m}}\mathbb{E}\_{a',a_m}f(a(\bar{x}))^\top[f(a'(\bar{x}))-f(a_m(\bar{x}\_m))])+\sum_{m=k+1}^K\exp(-\mathbb{E}\_{\bar{x}_m\sim\rho_c}\mathbb{E}\_{a',a_m}f(a(\bar{x}))^\top[f(a'(\bar{x}))-f(a_m(\bar{x}\_m))])), $$ which simplifies the expectations and separates the two groups. W6. Eq(26) not rigorous, making Eq(25) and Eq(29) not strictly equivalent. Necessity to modify Theorem 2.6. A. (1) Eq(26) is rigorous according to the commutative law of addition. It holds for any $\\{i_1,\ldots,i_K\\}$ being a rearrangement of $[K]$. Eq(26) ensures that e.g. $\mathbb{E}\_{\bar{x}_1\sim\rho_1}\mathbb{E}\_{\bar{x}_2\sim\rho_2}\mathcal{L}=\mathbb{E}\_{\bar{x}_1\sim\rho_2}\mathbb{E}\_{\bar{x}_2\sim\rho_1}\mathcal{L}$, and therfore Eq(27) can all be represented by the same $r_k$, making Eq(25) and Eq(29) strictly equivalent. (2) Theorem 2.6 is correct. Typos will be fixed according to W5(2). --- Questions. Q1. Understanding of augmentation overlapping. A1. We respectively disagree from a mathematical viewpoint. In the original paper (Wang et al., 2021), augmentation overlap is formulated as $\mathcal{T}$-connectivity (Definition 4.3), where $x_i$ and $x_j$ are $\mathcal{T}$-connected if $\mathrm{supp}(p(x_i^+\|x_i))\cap\mathrm{supp}(p(x_j^+\|x_j))\neq\emptyset$, or equivalently, $\exists t_i,t_j \in \mathcal{T}$ s.t. $t_i(x_i)=t_j(x_j)$, meaning that $x_i$ and $x_j$ sharing exactly the same augmented views $t_i(x_i)=t_j(x_j)$, which is unrealistic. --- Q2. Relationship between $P_X$ and $P_{\bar{X}}$. A2. $\mathrm{P}_X$ is the distribution of $a(\bar{x})$, where $a\sim\mathrm{P}_A$ and $\bar{x}\sim\mathrm{P}\_{\bar{X}}$. --- Q3. Which results does Lemma 2.8 represent? A3. Lemma 2.8 is part of Proposition 6 in Nozawa & Sato, 2021 and Lemma 4.3 in Arora et al., 2019. Compared with Proposition 6 in Nozawa & Sato, 2021, Lemma 2.8 does not have the $d(f)$ term and shows an equation because the left hand side is $\bar{\mathcal{R}}^{\mathrm{sup}}$ instead of $\bar{\mathcal{R}}^{\mathrm{un}}$ (without the need of using Jensen's inequality). --- Q4. Advantages of decomposition. A4. The decomposition makes separation between same-class and different-class negative terms possible. Specifically, it decomposes the contrastive risk according to the number of negative samples having different labels from the anchor sample. The decomposition is non-trivial, as it only works for contrastive losses that treat negative samples equally (Eq(26)). With this decomposition, we further decompose the risk into different-class negative terms and same-class negatives terms (Eq(31)). Then respectively investigating the two types of terms (Eq(33) and Eq(37)), we reach our main theorems. --- Q5. Discussions about Theorem 2.4. A5. Theorem 2.4 shows the finite-sample error bound as a complement to the other theorems based on the population distribution. It also shows the compatibility of our bound with generalization bounds in previous works. --- Q6. Explain Lipschitz continuity. A6. The Lipschitz continuity condition concerning $f$ with respect to the image $x$ for convolution neural networks has been widely made in previous works, see e.g. [1] On Lipschitz Bounds of General Convolutional Neural Networks. TIP, 2019. [2] Intriguing properties of neural networks. ICLR, 2014. Moreover, the consistency between our pixel-level (Figure 2) and representation-level (Figures 3 & 4) experiments also verifies the assumption. --- Thanks for your insightful and constructive comments. According to our answers, we have clarified that our proofs have no factual mistakes (only typos to be fixed). We sincerely suggest the reviewer continue reviewing Section 3 and reconsider the overall recommendation score. We welcome any further questions during your follow up reviews. --- Rebuttal Comment 1.1: Comment: Thanks for the authors' response. Firstly, I want to explain W5 (2). There is a misunderstanding that $\sum_{k=1}^k \rightarrow \sum_{m=1}^k$ rather than $\sum_{m=k+1}^K \rightarrow \sum_{m=1}^k$. Besides, I still have some questions. 1. For W6, Eq (28) not Eq (26) is not very rigorous. For example, $c_{j_k}=i_k$ and $c_{j_{k+1}=\cdots=c_K=c}$ in Eq (28). While $c_j=i_j$ in Eq (25). Therefore, the symbol settings are a bit messy. So, it may be necessary to make some modifications to Theorem 2.5 (not Theorem 2.6) and its proof. 2. The author's requirement for augmentation overlap is too strict. I really can't accept this viewpoint. Taking Fig 1 (b) in Wang et al., 2021 as an example, do the authors think that the two augmented views related to tires are not-overlap? If so, the two areas of tires in Fig 1 of this paper have different semantics. It is contradictory. 3. For Q3, I still don't understand how $\bar{\mathcal{R}}^{un}$ became $\bar{\mathcal{R}}^{sup}$. And, I didn't find $\bar{\mathcal{R}}^{un}$. Could the authors provide a detailed demonstration? --- Reply to Comment 1.1.1: Comment: We thank the reviewer's timely reply. We address your concerns as follows. --- Q1. For W6, Eq (28) not Eq (26) is not very rigorous. For example, $c_{j_k}=i_k$ and $c_{j_{k+1}}=\ldots=c_K=c$ in Eq(28). While $c_j=i_j$ in Eq (25). Therefore, the symbol settings are a bit messy. So, it may be necessary to make some modifications to Theorem 2.5 (not Theorem 2.6) and its proof. A1. Eq (28) is a rigorous definition. The condition on the right hand side means that there exist $(K-k)$ negative samples sharing the same class $c$, and the other $k$ negative samples having classes $\{i_1,\ldots,i_k\}$. The notation $p_k(i_1,\ldots,i_k)$ depends only on $\{i_1,\ldots,i_k\}$, and does not depend on any specific $\{j_1,\ldots,j_k\}$. Besides, Eq (25) rigorously equals to Eq (29). For example, let us examine $k=1$ (the second last line in Eq (25)), $$ \mathbb{E}_c \mathbb{E}\_{\bar{x}\sim\rho_c}\mathbb{E}_a\sum\_{i_j\neq c} \sum\_{j=1}^K \mathrm{P}(c_1=c)\cdots\mathrm{P}(c_j=i_j)\cdots\mathrm{P}(c_K=c) \mathbb{E}\_{\bar{x}_k\sim\rho_c,k\neq j} \mathbb{E}\_{\bar{x}_j\sim\rho\_{i_j}} \mathbb{E}\_{a',\\{a_k\\}\_{k\in[K]}} \mathcal{L}(a(\bar{x}),a'(\bar{x}),a_k(\bar{x}_k);f) $$ $$ =\mathbb{E}_c\mathbb{E}\_{\bar{x}\sim\rho_c}\mathbb{E}\_a \sum\_{i_j\neq c}\sum\_{j=1}^K\mathrm{P}(c_1=c) \cdots\mathrm{P}(c_j=i_j)\cdots\mathrm{P}(c_K=c) r_1(i_j) $$ $$ =\mathbb{E}_c\mathbb{E}\_{\bar{x}\sim\rho_c}\mathbb{E}\_a \sum\_{i_j\neq c} p_1(i_j)r_1(i_j), $$ where the first equation holds because of Eq (26) and Eq (27), and the second equation holds because by Eq (28) $$ p_k(i_j)= \mathrm{P}(\exists j, \text{ such that } c_j=i_j \text{ and } c_\ell=c \text{ for } \ell\neq j) $$ $$ =\mathrm{P}(c_1=i_j)\mathrm{P}(c_2=c)\cdots\mathrm{P}(c_K=c) + \mathrm{P}(c_1=c)\mathrm{P}(c_2=i_j)\cdots\mathrm{P}(c_K=c) +\ldots + \mathrm{P}(c_1=c)\mathrm{P}(c_2=c)\cdots\mathrm{P}(c_K=i_j) $$ $$ := \sum_{j=1}^K \mathrm{P}(c_1=c)\cdots\mathrm{P}(c_j=i_j)\cdots\mathrm{P}(c_K=c). $$ The calculations of other lines in Eq (25) are similar, only with a bit more complicated notations required. --- Q2. The author's requirement for augmentation overlap is too strict. I really can't accept this viewpoint. Taking Fig 1 (b) in Wang et al., 2021 as an example, do the authors think that the two augmented views related to tires are not-overlap? If so, the two areas of tires in Fig 1 of this paper have different semantics. It is contradictory. A2. We would like to clarify more on the understanding of augmentation overlap. Firstly, in the 4th paragraph of the introduction in Wang et al., 2021, the two views in Figure 1(b) are commented as "very much alike that we could even hardly tell them apart", and augmentation overlap is defined as "there will be support overlap between different intra-class images through aggressively augmented views of them". The term "support overlap" indicates the existence of the same augmented views between different intra-class images. Secondly, if two views are similar but not exactly the same, they can still have the same semantics, e.g. two similar but not exactly the same wheels taken from different car figures share the same semantics of "wheel". (Perhaps the reviewer has different understandings of "semantics". Here, by "semantics", we refer to the semantic labels illustrated in Section 3.1 of our submission.) Thirdly, if augmentation overlap is interpreted as two images having the same semantics, one cannot mathematically explain how the model recognizes the semantics without making additional assumptions. Nonetheless, to avoid possible confusion, we will tone down our remark about augmentation overlap, and remove the statement from our next version. --- Q3. For Q3, I still don't understand how $\bar{\mathcal{R}}\_{\mathrm{un}}$ became $\bar{\mathcal{R}}\_{\mathrm{sup}}$. And, I didn't find $\bar{\mathcal{R}}_{\mathrm{un}}$. Could the authors provide a detailed demonstration? A3. $\bar{\mathcal{R}}_{\mathrm{sup}}$ defined in our paper equals the first term of Eq (7) in Nozawa & Sato, 2021, and also Inequality (b) in the proof of Lemma 4.3 in Arora et al., 2019. According to the proof of Proposition 6 in Nozawa & Sato, 2021 and the proof of Lemma 4.3 in Arora et al., 2019, it further decomposes into $(1-\tau_K)\cdots +\tau_K\cdots$. In previous works, the relationship between $\mathcal{R}\_{\mathrm{un}}$ and $\bar{\mathcal{R}}\_{\mathrm{sup}}$ is built via Jensen's inequality (Eq (7) in Nozawa & Sato, 2021, and Inequality (b) in the proof of Lemma 4.3 in Arora et al., 2019). In our submission, it is presented in Theorem 2.7. The typo $\bar{\mathcal{R}}\_{\mathrm{un}}$ should be $\mathcal{R}\_{\mathrm{un}}$ (defined in Eq (3)) in our last reply. --- Thanks again for the timely reply. We hope our response solves all your additional concerns, as this is the last rebuttal we can post. We strongly suggest the reviewer finish reviewing the rest of Section 3 and reconsider the recommendation score.	Summary: In this paper, the authors theoretically study how augmentations affect supervised risk, an unexplored area in self-supervised learning. Furthermore, they conduct some experiments to verify the theories. Claims And Evidence: Yes, the claims are supported by evidence. Methods And Evaluation Criteria: There is not a new method in this paper. Theoretical Claims: No, I am not familiar with it. Experimental Designs Or Analyses: After reviewing the experiments, I think the findings are reliable. Supplementary Material: No Relation To Broader Scientific Literature: None Essential References Not Discussed: None Other Strengths And Weaknesses: Strengths 1. This paper supports the augmentation study and highlights its important role in self-supervised learning. Weakness 1. The error bound is not directly correlated with the final performance. 2. The paper lacks empirical guidance, making it unhelpful for selecting appropriate augmentation parameters. Other Comments Or Suggestions: None Questions For Authors: 1. When selecting augmentation parameters, only suitable values lead to good performance. Could the authors explain why this occurs based on these theorems? Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We express our sincere gratitude to Reviewer 6JLt for appreciating the significance and reliability of our findings. We address your concerns below. --- Q1. The error bound is not directly correlated with the final performance. A1. We respectfully disagree. As shown in Section 4.2, we show that the optimal data augmentation parameter minimizing the distance sum also leads to the best downstream accuracy, indicating that lower downstream error bounds highly correlate with better downstream performance. Specifically, in Theorem 2.3 we show that the supervised error bound depends not only on the unsupervised loss but also on the maximum distance between augmentations and the minimum distance between samples of the same class. Typically, efforts focus on minimizing the unsupervised error to reduce the supervised error bound. However, the two distance terms, which depend on the augmentation parameter, are also crucial and must be minimized to improve classification accuracy. This is empirically verified by Figures 5 and 6, which show that classification accuracy is inversely proportional to the sum of these two distance terms. --- Q2. The paper lacks empirical guidance, making it unhelpful for selecting appropriate augmentation parameters. A2. On the one hand, our theoretical results in Section 2.2 show that the downstream classification risk depends not only on the unsupervised loss but also on the sum of two distance terms related to data augmentation, which provides empirical insight that the selection of data augmentation parameters is also vitally important. On the other hand, Section 3 demonstrates a theoretical trade-off between the two distance terms, indicating the existance of the optimal data augmentation parameters. Empirical varifications show that the optimal range of crop size should be large enough, with the upper bound being 1.0; the optimal probability of color jitter is around 0.6-0.8. (See Figures 5 & 6 and also the additional experiments on Imagenet100 in the response A2 to Reviewer Xxrg.) Furthermore, for future works, our theoretical results also guides a possible direction for designing new data augmentation methods to deliberately minimize some unsupervised surrogate of the two distances. --- Q3. When selecting augmentation parameters, only suitable values lead to good performance. Could the authors explain why this occurs based on these theorems? A3. In Theorems 2.1 and 2.3, we show that the supervised error bound depends not only on the unsupervised loss but also on the maximum distance between augmentations and the minimum distance between samples of the same class. Through model training, the unsupervised error can be reduced to a very small value. However, the impact of these two distance terms on classification performance is often overlooked. In fact, these distance terms are highly influenced by the augmentation parameter values. The augmentation parameter values that minimize the sum of these two distances may also yield the smallest classification error bound, as verified by Figures 5 and 6. --- Thanks for your insightful and constructive comments. Hope our explanations and additional experiments can address your concerns. --- Rebuttal Comment 1.1: Comment: Thank you for addressing my concerns. I will maintain my original score.	Summary: Self-supervised contrastive learning effectively extracts representations from unlabeled data. Despite its success prompting theoretical studies, the impact of specific data augmentation techniques is still under-explored. To address this, the authors proposed an augmentation-aware error bound for self-supervised contrastive learning, showing that the supervised risk is bounded not only by the unsupervised risk, but also explicitly by a trade-off induced by data augmentation. Furthermore, the authors discussed how certain augmentation methods affect the error bound. ## Update after rebuttal After reviewing the author's rebuttal and the reviews from another reviewer, I will keep my current weak accept rating. Claims And Evidence: The authors aim to formulate the problem and motivation using different scenarios: 1. Directly establishing a relationship between unsupervised contrastive risk and supervised risks through statistical modeling. 2. Relying on the assumption of an augmentation graph and borrowing mathematical tools from unsupervised spectral clustering. 3. Exploring other explanatory works of contrastive learning from the perspective of feature geometry. With these three scenarios, the authors attempt to formulate the problem, which remains under-explored. Thus, they propose an augmentation-aware theory for self-supervised contrastive learning, decomposing the unsupervised contrastive risk in relation to the number of negative samples sharing the same label as the anchor. Furthermore, they analyze specific types of data augmentation and discuss the existence of a trade-off between the two distance terms concerning the strength of data augmentation. Methods And Evaluation Criteria: In Section Two, the authors introduce a mathematical formulation for unsupervised contrastive learning and downstream classification, accompanied by a detailed analysis of the proposed approach. Following this, an augmentation-aware error bound is presented, supported by intriguing mathematical theory. This section offers a compelling theoretical explanation of how the authors address the issue with clear formulations. However, the organization of Section Two is lacking. For instance, in the middle of the theoretical explanation, the authors introduce a discussion that feels disconnected from the main theoretical idea. The authors design two types of experimental settings: pixel-level and representation-level, to validate the proposed approach. However, there is a lack of discussion regarding the contributions of the proposed method(in tense of ablation, comparison). In Section 2, the authors explain the main theoretical concepts with a strong promise of performance improvement. However, I cannot find a thorough discussion in these two experiment settings with different scenarios (impact of augmentation, augmentation-aware error bound). Furthermore, it is necessary to evaluate the proposed approach against state-of-the-art papers and to highlight its main contributions across different settings, as mentioned by the authors. Theoretical Claims: The authors provide a solid theoretical formulation of the proposed approach, clearly outlining how they intend to address the issues with precise mathematical formulations. However, the organization of the paper still needs some modifications. In certain sections, the authors introduce theoretical concepts alongside mathematical formulations, while simultaneously discussing experimental performance (Section 2.3). This structure can be confusing and may benefit from clearer separation. Experimental Designs Or Analyses: The experimental design needs reorganization and more discussion based on the theoretical formulation (augmentation-aware error bound, impact of different augmentation, some downstream tasks). As noted, some experimental settings lack sufficient discussion and analysis in relation to the theoretical framework. The experimental results should be presented with different augmentation strategies based on their formulations, the Augmentation-Aware Error Bound compared to other approaches (as discussed in Section 2.3). These aspects should be addressed more thoroughly, as they represent a significant weakness of the paper. Supplementary Material: Yes, I reviewed the supplementary materials, which include additional proofs and related papers on self-supervised and contrastive learning. Additionally, I examined the extra experimental results on the TinyImageNet dataset. Relation To Broader Scientific Literature: Their formulation is very interesting, particularly in relation to contrastive and self-supervised learning, as it addresses the risks associated with different augmentation techniques. Furthermore, the approach is intriguing for utilizing unlabeled samples in downstream classification tasks. Essential References Not Discussed: Some of the recent papers are discussed in the theoretical sections, but these discussed papers need to be addressed in the experimental section as well. It would be beneficial to compare their performance with the proposed approach and analyze how they affect performance in downstream tasks. Other Strengths And Weaknesses: I found the theoretical aspects of the paper is good. The problem formulation, arguments, and claims about how the approach is addressed in their work are interesting. Furthermore, their mathematical formulation is somehow fine. However, there are some weaknesses in the paper, particularly in the organization of Section 2 and the lack of detailed discussion in the experimental section. Specifically, the experimental section needs a more thorough discussion, including comparisons with different variations and settings, as well as a comparison of the proposed approach with existing works related to their approach. Other Comments Or Suggestions: The authors need to check the entire paper and proofread it thoroughly. Some sentences without proper punctuation. For example: "That means, we no longer need the conditional independence assumption Moreover, we formulate the data..." Questions For Authors: Most of the comments and questions have been mentioned in the sections above. However, these issues still need to be addressed: 1. Do the authors analyze and discuss the impact of different augmentations and augmentation-aware error bounds in the two experimental settings? 2. How does the proposed approach compare against state-of-the-art papers, and can the authors highlight its main contributions across these different settings? 3. Since the paper serves as a foundation for further theoretical exploration of data augmentation (self-supervised and contrastive learning), it needs a detailed analysis of the experiments and discussions. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We express our sincere gratitude to Reviewer cGdD for appreciating the soundness of our theoretical formulations and results. We address your concerns below. --- Q1. Organization of Section 2. A1. As suggested, we will make the discussions in Section 2.3 an independent section following Section 2 in our next version and also add a roadmap in the introductory section to enhance readability. --- Q2. Lack of discussion regarding the contributions and comparisons with SOTA. A2. The discussions of our contribution locate mainly in Section 2.3, where we compare our bound with previous theoretical works. Besides, we also conduct verification experiments in Section 4 to verify our new theoretical claims proposed in Sections 3.2 and 3.3. As the main contribution of this paper is to theoretically explain the role of data augmentation in self-supervised contrastive learning, the significance of the proposed error bound is not necessarily verified by ablations or experimental comparisons. Nonetheless, we could compare empirically the bound value with previous theoretical works. In detail, as shown in Figures 5 and 10, the sum of the two distance terms is around 1 (1.3 for TinyImagenet and 0.8 for CIFAR100) after 1000 epoch training, whereas we additionally measure the contrastive loss value to be around 42 (41.6 for TinyImagenet and 41.2 for CIFAR100). This indicates that compared with previous bounds, our bound relax the data generation assumption with the bound value increases less than 3% (1/42). See also A6. --- Q3. Some experimental settings lack sufficient discussion and analysis in relation to the theoretical framework. A3. The experimental section 4.1 is specifically in relation to theoretical analysis in Section 3 verifying the trade-off between the two distance terms, and the experimental section 4.2 is in relation to the error bound of Theorem 2.3, where the optimal augmentation parameter leads to the minimum distance sum and also the highest downstream accuracy. To further enhance the relation of experiments to the theoretical framework, we here present an additional experiment about the formulations of data augmentation strategies. This experiment verifies the theoretical analysis in Section 3.3 about the combination of random crop and color distortion. Specifically, we present the pixel-level distances between data augmentations using only random crops and that using random crops plus color jitter on CIFAR100. As shown in the figure https://imgur.com/a/aj3Xp4i, on top of random crop, color distortion further reduces the minimum same-class different-image distance and enhances the maximum same-image different-augmentation distance. --- Q4. Missing punctuation. A4. We will fix the typo in our next version. --- Q5. Do the authors analyze and discuss the impact of different augmentations and augmentation-aware error bounds in the two experimental settings? A5. Yes, in both settings, we show that stronger augmentations, e.g. smaller range of crop size and higher probability of color jitter, lead to larger maximum same-image different-augmentation distance and smaller same-class different-image distance, which coincides with the theoretical analysis in Sections 3.2 and 3.3. From the perspective of our error bound, there exists a trade-off between the two distance terms w.r.t. the strength of data augmentation, indicating the existance of the optimal augmentation parameters. Related discussions can be found in Section 4.1.1 2nd paragraph, Section 4.1.2 2nd paragraph, and Section 4.2 2nd paragraph. --- Q6. How does the proposed approach compare against state-of-the-art papers, and can the authors highlight its main contributions across these different settings? A6. In fact, instead of proposing a new contrastive learning methods that competes against the state-of-the-art,, the aim of our error bound is to explain their working mechanisms. Our bound applies for any contrastive learnin methods as long as they use the InfoNCE loss function regardless of the backbones or other architectural techniques. It builds upon a more realistic data generation process described in Section 2.1 without relying on any further assumptions (Theorem 2.1). That is, compared with other theoretical papers deriving the error bound, our bound can easily adapt these previous bounds under our more realistic data generation, only with two additional trade-off distance terms added to these bounds. See also the third paragraph of Section 2.3 for more details. --- Q7. The paper needs a detailed analysis of the experiments and discussions. A7. See A2 and A3. --- Thanks for your insightful and constructive comments. Hope our explanations and additional experiments can address your concerns.	Summary: This paper theoretically examines the role of data augmentation in contrastive learning. It demonstrates that supervised risk is bounded not only by unsupervised risk but also by a trade-off introduced by data augmentation. The analysis is further extended using Lipschitz continuity, providing insights into how changes in input data or augmentations affect the model's output and error bounds. Experimental results validate the theoretical findings, reinforcing the impact of augmentation on contrastive learning performance. Claims And Evidence: Claims made in the submission are supported by clear evidence. Methods And Evaluation Criteria: There are no new methods proposed. Evaluation criteria make sense for the problem of the theoretical analysis. Theoretical Claims: I believe the analysis in Sections 2 and 3 is correct. However, Assumption 2.2 could benefit from some empirical verification. The radius $R$ in Theorem 2.4 seems to be not formally introduced and explained. Experimental Designs Or Analyses: The experiments are sound for evaluating the theorems introduced. Supplementary Material: I scanned through it but did not examine it in detail. Relation To Broader Scientific Literature: Contrastive learning is a key self-supervised learning approach with numerous real-world applications. Augmentation plays an integral role in contrastive learning, often determining the quality of learned representations. Gaining a theoretical understanding of augmentation's impact could have significant implications for the broader scientific literature, shaping future advancements in self-supervised learning and representation learning. Essential References Not Discussed: Most papers are discussed. Other Strengths And Weaknesses: Strength: 1. This work extends previous theoretical analyses by making assumptions that may not fully align with real-world scenarios. This work does not assume that anchor and positive samples are conditionally independent or that two different real images share exactly the same augmented views. These assumptions, while useful for theoretical exploration, may not always hold in practical applications. 2. The experimental results validate the new theoretical results. Weakness: 1. The experiments are conducted only on small-scale datasets such as CIFAR-10/100. Since image resolution and dataset complexity could influence the theoretical results, an evaluation of larger, high-resolution datasets would provide a more comprehensive validation. 2. The study focuses exclusively on InfoNCE loss, which may limit the generalization of the theoretical findings. Other Comments Or Suggestions: Page 1, top right: The statement “we usually use only two views in training instead of using multiple ones.” may be misleading for readers unfamiliar with SSL. While many traditional contrastive learning methods use two views, several recent approaches, such as MMCR and DINO, leverage multiple views. Questions For Authors: Please address the questions regarding the assumptions and evaluations, as these concerns could impact my assessment of the paper. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We express our sincere gratitude to Reviewer Xxrg for appreciating our practical theoretical assumptions and novel theoretical results. We address your concerns below. --- Q1. Empirical verification of Assumption 2.2. A1. For each input image in the CIFAR100 dataset, we generate 100 different random augmentations, and plot the tsne visualizations of the random augmentated views, the mean of the augmented views, and the original input sample in the embedding space. We show the tsne plots of 4 randomly selected samples in https://imgur.com/a/NadpBSl. We see that the mean of augmented views lie near the embedding of the original input sample, which verifies Assumption 2.2. Besides, we also measure the $l$-2 distance between the mean of augmentations and the original sample in the embedding space. We show that on CIFAR100, the average distance is 0.083, which is small enough considering that the embeddings are normalized to have unit l-2 norm, indicating that the mean of augmented embeddings $\mathbb{E}_a f(a(\bar{x}))$ is close enough to input embedding $f(\bar{x})$. --- Q2. The experiments are conducted only on small-scale datasets such as CIFAR-10/100. Since image resolution and dataset complexity could influence the theoretical results, an evaluation of larger, high-resolution datasets would provide a more comprehensive validation. A2. Following your advice, we conduct additional verification experiments on Imagenet100, which contains 224224 high resolution images from 100 classes. Due to time limitation, we run experiments with ResNet-18 with batchsize 64 for 50 epochs on 2 24G RTX 3090 GPUs. (The other settings follow those of TinyImagenet in our submitted paper.) The pixel-level verifications are shown in https://imgur.com/a/UcVPXwS, and the representation-level verification w.r.t. crop size is shown in https://imgur.com/a/jl00TVn, where the results conincides with that in Sections 4.1.1 and 4.1.2, i.e., as the augmentation strength increases, the max same-image different-augmentation distance increases and the min same-class different-image distance decreases. Besides, in the figure https://imgur.com/a/wPs9WOO, we verify that the optimal augmentation parameters with the smallest distance sum also leads to the highest downstream accuracy, which coincides with Section 4.2. --- Q3.* The study focuses exclusively on InfoNCE loss, which may limit the generalization of the theoretical findings. A3. On the one hand, as one of the mainstream contrastive losses, InfoNCE-based contrastive learning still achieves state-of-the-art performances e.g. SimCLR, MoCo, etc. The extensive applications of InfoNCE loss partly demonstrate the generalization of our theory. On the other hand, although our theoretical results focus on the InfoNCE loss, we strongly believe that our analysis can potentially be generalized to other contrastive losses, e.g. BYOL, BarlowTwins, etc. Specifically, our analysis theoretically explains the effect of data augmentation to contrastive learning based only on the data generation procedure described in Section 2.1, with mild (Theorem 2.3) or even no further assumptions required (Theorem 2.1) and regardless of the network architectures. As long as a contrastive learning method selects positive/negative samples using random data augmentations, we can adapt the two trade-off distance terms to any error bound revealing the relationship between contrastive and downstream risks. --- Q4. Page 1, top right. The statement “we usually use only two views in training instead of using multiple ones.” may be misleading for readers unfamiliar with SSL. While many traditional contrastive learning methods use two views, several recent approaches, such as MMCR and DINO, leverage multiple views. A4. We will replace this statement with "we usually use only two views in training instead of using multiple ones in popular methods such as SimCLR and MoCo". --- Thanks for your insightful and constructive comments. We sincerely hope you can reconsider the recommendation score if our explanations and additional experiments solves your concerns. We also welcome further questions and discussions. --- Rebuttal Comment 1.1: Comment: Thank you for addressing my concerns. After carefully reviewing the authors’ responses and the discussions from other reviewers, I am happy to revise my original recommendation from a 2 to a 3. That said, I continue to share the concerns raised by Reviewer 6JLt regarding Questions 2 and 3. --- Reply to Comment 1.1.1: Comment: Thank you very much for your timely reply, and for raising the recommendation score. To address your further concerns, aside from the original reply to Q2&Q3 of Reviewer 6JLt, we provide additional elaborations as follows. --- Q2 of Reviewer 6JLt. The paper lacks empirical guidance, making it unhelpful for selecting appropriate augmentation parameters. A. The theoretical results in Section 2.2 and Section 3 provide empirical guidance that the downstream performance depends on the trade-off between the two distance terms related to data augmentation. For augmentations such as random crop and color distortion, the two distance terms are specifically related to the augmentation strength. To theoretically guide the selection of augmentation parameters, we refer to Theorem 3.2, indicating that the upper bound of supervised risk is related to the sum of the pixel-level distances. As suggested by Theorem 3.2, the augmentation parameters having the minimum pixel-level distance sum lead to the best downstream performance. We conduct additional validation of this empirical guidance by comparing the pixel-level sum of distances and the downstream linear probing accuracy. In Figure https://imgur.com/a/b99SQBr, we show that on all three benchmark datasets, the smaller pixel-level distance sum leads to better downstream accuracy. In other words, Theorem 3.2 provides the theoretical guidance that we can roughly select appropriate augmentation parameters by comparing the pixel-level distance sum before training. --- Q3 of Reviewer 6JLt. When selecting augmentation parameters, only suitable values lead to good performance. Could the authors explain why this occurs based on these theorems? A. "Only suitable values lead to good performance" because inappropriate parameters lead to a large distance sum, and consequently result in a worse downstream error bound (according to Theorems 2.1 and 2.3). For example, on Imagenet100, the worst-performed crop size parameter [0.08,0.4] has a representation-level distance sum of 1.69, whereas the distance sum of the best-performed parameter [0.08,1.0] is only 1.53. The larger distance sum leads to a worse downstream error bound and accordingly a worse downstream accuracy. The results on other datasets are similar, as evidenced by Figures 5, 6, 10, and 11. --- Thanks again for the reply. We hope our response solves all your additional concerns.	null	null	null	null	null	null
Cape: Context-Aware Prompt Perturbation Mechanism with Differential Privacy	Accept (poster)	Summary: This paper introduces Cape, a DP prompt perturbation mechanism aimed at enhancing the privacy-utility trade-off in LLM-based inference services through context-aware utility function and bucketized sampling function. The proposal is motivative and provides promising solutions to the long-tail dilemma in private selection over large NLP vocabulary. This paper provides comprehensive experimental validation showcasing Cape’s effectiveness. Claims And Evidence: Technically solid moderate-to-high impact paper Methods And Evaluation Criteria: with no major concerns with respect to evaluation, resources, reproducibility, ethical considerations. Theoretical Claims: with no major concerns with respect to theoretical claims. Experimental Designs Or Analyses: with no major concerns with respect to soundness/validity of any experimental designs or analyses. Supplementary Material: The proposed solution causes inevitable utility loss to enhance prompt privacy with high efficiency. However, this paper indeed achieves a better privacy-utility trade-off against prior works. Relation To Broader Scientific Literature: [1]: Permute-and-Flip: A new mechanism for differentially private selection Essential References Not Discussed: [1]: Permute-and-Flip: A new mechanism for differentially private selection Other Strengths And Weaknesses: Strengths: 1. The direction of enhancing prompt privacy in LLM inference services is promising. 2. The idea is neat and straightforward. 3. The writing is good and easy-to-understand. 4. Extensive experiments, along with ablation studies showcase the effectiveness of proposed approach. 5. The utility improvements are promising against prior works in both text classification and text generation tasks. Weakness: The proposed solution causes inevitable utility loss to enhance prompt privacy with high efficiency. However, this paper indeed achieves a better privacy-utility trade-off against prior works. Other Comments Or Suggestions: 1. It would be better if the authors could align the theoretical privacy budgets of different works in Table 3 for better understanding. 2. I recommend the authors to move the ablation of model distillation into main body. Besides, quantization could be discussed to further improve the efficiency and memory consumption. Questions For Authors: 1. See weakness above. I think on-device model acceleration is promising, especially for privacy concerns. 2. Is the proposed mechanism applicable to other DP mechanisms? E.g., more recent private selection mechanisms like permute-and-flip mechanism[1]? 3. The calculation of mean(b_i) uses b_{i, k}, does it refer to u_{i, k}? [1]: Permute-and-Flip: A new mechanism for differentially private selection Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: We thank the reviewer jdXq for the positive feedback on "The proposal is motivative and provides promising solutions". We hereby answer the specific questions below and provide detailed explanations. > Paper polishment Thanks for your suggestion. We acknowledge that on-device generation and acceleration are receiving increasing attention. In this regard, we conduct experiments of device model distillation, which are deferred to Appendix B.6 due to page limit. In the final version, we will supplement a detailed discussion on accelerating on-device computation using other SOTA techniques like quantization, sparsity, etc. Regarding Table 3, as explained at the beginning of Section 5.2, prior work uses distinct formal privacy definitions, making alignment challenging. Furthermore, we believe that empirical privacy, as indicated by privacy attacks, better reflects actual privacy protection. > Extensibility to other DP mechanisms Thanks for your suggestion. The permute-and-flip mechanism can be regarded as a variant of private selection algorithm, which we consider orthogonal to our work. We believe the permute-and-flip mechanism could be incorporated into Algorithm 2 as a replacement for the Exponential mechanism, and we can explore this as part of future work. > Typos Thanks for your careful reading. We have corrected the typos in the mean calculation. We will review the entire paper and check for any additional typos in the final version.	Summary: The paper introduces Cape, a DP mechanism designed to protect user privacy when interacting with LLM inference services. The authors identify an issue in current LLM services: users need to submit their prompts in plaintext for inference, exposing sensitive information. The paper proposes a context-aware approach that perturbs user prompts before sending them to the server while maintaining reasonable utility, including: a hybrid utility function that combines both token embedding distance and contextual information to better measure semantic similarity, and a bucketized sampling mechanism to handle the large vocabulary space in NLP tasks. The authors evaluate Cape on both text classification and text generation tasks, demonstrating improved privacy-utility trade-offs compared to prior methods like SANTEXT, CUSTEXT, and InferDPT. Claims And Evidence: The authors claim that Cape achieves a better privacy-utility trade-off than existing approaches, which is supported in the experiments section through the adversarial attacks. The empirical results demonstrate that Cape provides stronger defense against privacy attacks (KNN and MTI attacks) while maintaining competitive utility compared to baselines. The ablation studies validate design choices like the hybrid utility function and bucketing strategy. Methods And Evaluation Criteria: The authors evaluated both utility metrics (accuracy for classification, coherence and alignment for generation) and privacy metrics (attack success rates, effective mapping set size, retention ratio). The authors use multiple datasets (SST-2, QNLI, Wikitext-103) to validate their approach across different task types. While the paper uses KNN Attack and MTI Attack as evaluation metrics for privacy leakage, these methods may not capture all potential forms of information leakage in the perturbation process. For example, there's a possibility of semantic leakage that goes beyond token-level. The composition of multiple perturbed words in context could still reveal meaningful patterns that might enable adversaries to infer sensitive information, even when individual tokens appear adequately protected. A more comprehensive evaluation framework that considers semantic composition effects and contextual meaning reconstruction would improve the privacy analysis. Furthermore, it might be interesting to use additional utility metrics, such as LLM as a judge, or comparing the difference between perturbed response and the ground truth response. Theoretical Claims: I did not check the correctness of Theorem 4.1 whose proof is in the appendix. At a glance, the proof looks sound to me. Experimental Designs Or Analyses: I reviewed the experiments and have questions regarding section 5.1.2, which I mention in the questions for authors section. Supplementary Material: I reviewed the prompts used and the perturbed results. The perturbed results appear quite short and potentially unusable in practice, despite the improved method. I attribute this limitation to the fundamental constraints of the problem setup. Relation To Broader Scientific Literature: The paper contributes to privacy-preserving LLM inference techniques. The authors reviewed cryptographic solutions, client-server hybrid execution approaches, and previous DP-based techniques (SANTEXT, CUSTEXT, InferDPT). Essential References Not Discussed: There are some additional literature that offers less privacy protection but potentially better utility for minimizing disclosure risks: Dou, Yao, Isadora Krsek, Tarek Naous, Anubha Kabra, Sauvik Das, Alan Ritter, and Wei Xu. “Reducing Privacy Risks in Online Self-Disclosures with Language Models.” arXiv, June 23, 2024. http://arxiv.org/abs/2311.09538. Staab, Robin, Mark Vero, Mislav Balunović, and Martin Vechev. “Large Language Models Are Advanced Anonymizers.” arXiv, February 21, 2024. http://arxiv.org/abs/2402.13846. Other Strengths And Weaknesses: Strengths The paper addresses an important area of privacy protection for LLM. The authors improve DP token perturbation algorithms through two novel improvements: the hybrid utility function and bucketized sampling mechanism. Weaknesses While the author bridged some part of the gap, the output text remains difficult to interpret and use in practice. Other Comments Or Suggestions: If you have any important questions for the authors, please carefully formulate them here. Please reserve your questions for cases where the response would likely change your evaluation of the paper, clarify a point in the paper that you found confusing, or address a critical limitation you identified. Please number your questions so authors can easily refer to them in the response, and explain how possible responses would change your evaluation of the paper. On line 335 that the authors mention: 'When receiving the noisy generation yˆ from S, C uses the extraction model to de-noise the response as y′ ← Me(x, yˆ).' Does this step introduce potential privacy leakage? Since the extraction model has knowledge of prompt structures such as syntax or grammar, could this denoising step help adversaries recover the original prompt? It would be valuable to know if the authors performed privacy analyses (such as KNN attacks) against the extracted text, not just the perturbed prompts. It seems like the text from the appendix, though after extraction, is still unusable given the short length and the often ungrammatical nature. Could you please comment on the scalability of your method in the actual deployment of a sanitization framework? Questions For Authors: On line 335, the authors state: "'When receiving the noisy generation yˆ from S, C uses the extraction model to de-noise the response as y′ ← Me(x, yˆ)." Could you clarify the type of server model in this setup? The extraction model, a 1.5B model, appears to be strong enough to handle continuation tasks on the Wikitext103-v1 dataset. Have you conducted control experiments measuring the performance of text generation using unperturbed prompts directly with the extraction model? This would help distinguish whether the reported performance stems primarily from the extraction model's capabilities rather than the privacy-preserving pipeline. Have you considered designing experiments where the task completion explicitly requires the server's involvement, such as scenarios where the server possesses privileged information unavailable to the client? This would better demonstrate the necessity and effectiveness of your privacy-preserving approach in real-world applications. The text samples in the appendix exhibit limited length and grammatical issues that raise concerns about practical usability. Could you address the scalability of your method in real-world deployment scenarios? Specifically, what additional techniques might improve the quality of sanitized outputs while maintaining privacy guarantees? Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We thank the reviewer pKo2 for the positive feedback on "achieves a better privacy-utility trade-off than existing approaches". We hereby answer the specific questions below. > A more comprehensive evaluation for semantic privacy leakage and utility. Thanks for your suggestions. For privacy evaluation, we follow prior works and try our best to measure the empirical privacy comprehensively, including attack success rates, effective mapping set size and retention ratio. In this work, we primarily focus on single-token-level privacy leakage, such as name, age, etc. We clarify that more coarse-grained, semantic-level leakage like intent recognition (involving multiple token compositions), is out of our current scope. However, it is an interesting topic that could be explored in future work. For utility evaluation, we use commonly-used metrics like accuracy and alignment for a fair comparison, which yields better interpretability. We believe it would be interesting to use LLM-as-a-judge in more complext tasks like multi-candidate ranking. > Additional literature references These two works use LLMs to detect and anonymize sensitive attributes in an innovative way, which we perceive as complementary to our approach for improving utility. We will reference these papers and discuss their potential incorporation in Related Work. > Privacy concern on extraction model We clarify that there is no potential privacy leakage on using extraction model. In our setting, the extraction model is deployed locally on the client-side. Therefore, the adversary only has access to the perturbed prompt $\hat{x}$ and noisy generation $\hat{y}$ and cannot launch attacks on the extraction model without additional knowledge. > Clarification on perturbed text generation pipeline We follow InferDPT [1] to perform perturbation-then-extraction text generation pipeline, with Qwen2-1.5B-Instruct serving as both the server model and extraction model. We clarify that the choice of the models is actually orthogonal to our work. As illustrated in Figure 6, with models fixed and varying perturbation mechanisms, our method yields better trade-off than baselines. Besides, the effectiveness of this privacy-preserving pipeline is evidenced by Table VII in InferDPT paper [1]. The perturbation-then-extraction scheme (with Vicuna-7b-4bit model as the extraction model) yields better coherence scores against generation with Vicuna-7b-4bit alone. > Scenario where the server possesses privileged information. Thans for your suggestion. The scenario you mentioned resembles RAG-based applications, where server possesses an external knowledge database, which helps generate better responses. We will include this scenario in Introduction to better highlight the necessity of invoking privacy-preserving ML services. > Practical scalability and usability We first clarify that the two sample texts in Appendix are taken from the validation split of SST-2 dataset, providing a real-world example. Our method is also applicable to long-text scenarios, as demonstrated by the text generation experiments on Wikitext-103-v1 dataset. As shown in Figure 6, similar trade-offs are observed in long-text generation, not just in short-text classification. Below, due to words limitation, we present a sample text from the Wikitext-103-v1 dataset. Some tokens (marked in bold), such as numerical values for length and weight, and words like "homarus" -> "hortus", "large" -> "small", "weighting" -> "measuring" are perturbed. However, the overall semantics and grammatical structure are well preserved. More fine-grained sensitive data taxnomy level perturbation shall greatly improve real-world usability, which is complementary to our work. - $\epsilon=14$: hortus gammarus is a small crustacean, with aak length up to 95 centimetres ( 30 in ) and measuring up to 5 – 6 kilograms ( 11 - 15 lb ), although the lobsters caught in lobster pots are usually 23 – 35 cm ( 9 – 15 in ) long and weigh 0 @.@ 7 – 2 @.@ 2 kg ( 1 @.@ 5 – 4 @.@ 9 lb ) . In terms of usability, we acknowledge the inevitable trade-off between privacy and utility in DP-based methods—privacy comes at a cost. However, our approach manages to achieve a better balance than previous work. In real-world applications, we believe that an application-specific or user-specific taxonomy of sensitive data can guide the development of more refined privacy mechanisms. For instance, we could use separate sampling spaces for location, name, etc. to constrain sampling space while preserving semantics. Additionally, perturbation-aware fine-tuning in SANTEXT[2] could further enhance utility. Although the perturbed prompts may not be human-readable, they can be effectively understood by the fine-tuned model (e.g., extraction model). [1]: InferDPT: Privacy-preserving Inference for Black-box Large Language Models. [2]: Differential Privacy for Text Analytics via Natural Text Sanitization.	Summary: The paper proposes a new approach to perturb the tokens in user prompts to preserve local differential privacy in an efficient and utility-friendly way. For this, the authors utilize a secondary model, called device model, to generate logits for each token and use exponential mechanism (weighted by these logits) to randomize the token. The experimental results suggest better privacy-utility tradeoffs compared prior work in this area. Claims And Evidence: - In the introduction and related work sections, the paper talks about "efficiency", claiming that their work is more efficient that cryptographic solutions. But it is not clear what kind of efficiency this refers to or why their approach is more efficient at least at a high level. I suggest adding a brief discussion on why cryptographic solutions are less efficient. - The paper proposes the new approach as a black-box technique. But it would be better to clarify that it needs another model, called device model, to generate the logits. It's also not clear from the experiments how the results would be affected when there is a vocabulary or tokenizer mismatch between the black box model and the device model. Methods And Evaluation Criteria: - What does the privacy axis in Figure 5 refer to? How was it measured and what unit is this? Theoretical Claims: - In the definition of exponential mechanism, the sensitivity is given as $max_{x, y, y'}\\| u(x, y) - u(x, y') \\|$ but it should be $max_{x, x', y}\\| u(x, y) - u(x', y) \\|$. Experimental Designs Or Analyses: The experimental setup seem reasonable. It would be nice to try a few more pairs of pre-trained models and device models to understand the impact of vocabulary and tokenizer mismatches better. Supplementary Material: I checked the supplementary to find out more about what "privacy" refers to in Figure 5 but couldn't find a clear explanation. Relation To Broader Scientific Literature: The proposed approach would be useful to improve privacy preserving inference on LLMs. Essential References Not Discussed: I can't think of a key missing reference. Other Strengths And Weaknesses: - Clarity of Algorithm 1 could be improved. For instance, the operation on line 6, $\vec{u} \{ b_i \} $, was not defined. Minor: - "where exists a trade-off" in Related Work Other Comments Or Suggestions: An example on how the mechanism would work step by step on a toy setup would improve the clarity significantly. Questions For Authors: Please see above. Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: We thank the reviewer Mrs5 for the positive feedback on "proposed approach would be useful to improve privacy preserving inference on LLMs", which is quite encouraging for us. We hereby answer the specific questions below and provide detailed explanations. > Q1: Clarity of low efficiency of cryptographic solutions. We measure efficiency by the average inference runtime cost. For cryptographic solutions, take the SOTA 3-party computing work Ditto [1] as an example, the average runtime for generating one token with a sequence length of $128$ on Bert-base model requires about 30 seconds, which is far more expensive than our method. As shown in Appendix B.5, DP-based methods typically incur less than 1 second overhead for perturbation after an initial setup. We will supplement a brief description on the concrete runtime numbers in the Introduction section for better clarity. [1]: Ditto: Quantization-aware secure inference of transformers upon MPC. https://arxiv.org/pdf/2405.05525 > Q2: Effect of vocabulary or tokenizer mismatch. We first clarify that by "black-box," we mean that no knowledge of or modification to the server model is required in our work. We will add this description in Section 4.1 for better clarity. We list the vocabulary configuration in Appendix A. Notably, the device models (i.e., Bert and GPT-2) actually use different vocabularies compared to the server model (i.e., Qwen2-1.5B-Instruct, with a vocabulary size of 151,936). As shown in Table 3, while Bert (with a vocabulary size of 30,522) exhibits a larger vocabulary mismatch compared to GPT-2 (with a vocabulary size of 50,257), it still achieves higher sentence similarity. The possible reason could be that the perturbation using device model produces semantically-close natural language tokens. Consequently, although the tokenization granularity differs, the composition of sub-tokens still yield similar embeddings in the black-box model. For example, if device model perturbs 'unhappy' to 'un pleasant', although separated by space, its semantics can still be recognized by the black-box model. However, we believe that partial knowledge of the server model, such as its vocabulary, could further enhance semantic similarity, making it an interesting topic for future work. > Q3: What does the privacy axis in Figure 5 refer to? How was it measured and what unit is this? Apologies for the misunderstanding. "privacy" here refers to privacy score, which is defined at the beginning of Section 5 (at the bottom of Page 5). We will unify the notation and modify the axis label to "Privacy Score" for better clarity. We first calculate the attack success rate ($asr$) using KNN Attack and Masked Token Inference Attack. The privacy score is then defined as $1 - asr$. > Q4: Clarity of Algorithm 1 could be improved. Thanks for your suggestion. We will provide more detailed description in the final version. In Algorithm 1, $b_i$ denotes the token set that maps to the $i$-th bucket. Correspondingly, $\vec{u}_{b,i} = \vec{u}\\{b_i\\}$ denotes the score vectors for these tokens. Then, we can calculate the mean score for this bucket. > Q5: Typos Thanks for your careful reading. We have corrected the typos in Related Work and Preliminaries. We will review the entire paper and check for any additional typos in the final version. > Q6: Toy example of the overall mechanism Thanks for your recommendation. We will supplement a section in the Appendix to give a step-by-step example to ease understanding. --- Rebuttal Comment 1.1: Comment: Thank you for the response. I have increased my rating to 4. --- Reply to Comment 1.1.1: Comment: Dear Reviewer Mrs5, We'd like to thank you once again for the thoughtful feedback. We are glad to hear that our rebuttal has resolved your concerns. Best regards.	null	null	null	null	null	null	null	null
Learning Fused State Representations for Control from Multi-View Observations	Accept (poster)	Summary: The paper proposes a novel method called Multi-view Fusion State for Control (MFSC) to improve Multi-View Reinforcement Learning (MVRL). MFSC's main contribution is its integration of bisimulation metric learning into the MVRL framework, allowing for the extraction of task-relevant representations from multi-view observations. Additionally, the authors introduce a multiview-based masking and latent reconstruction auxiliary task to enhance the robustness of representation learning, notably when views are missing or noisy. The MFSC framework utilizes a Self-Attention Fusion Module that fuses multi-view representations using a learnable state fusion embedding. The bisimulation metric guides the learning of task-relevant features, while the auxiliary masking task helps the model deal with missing views by learning shared representations across different views. Key results show that MFSC outperforms existing MVRL methods in several tasks, including robotic manipulation and locomotion tasks, demonstrating superior performance in environments with missing or noisy views. The method is remarkably robust to interference and can handle incomplete observations effectively. The paper also includes visualizations and ablation studies that validate the effectiveness of each component, such as the bisimulation constraint and the self-attention mechanism, in improving task performance. Claims And Evidence: Yes, the paper's claims are generally supported by clear and convincing evidence. However, one potential area for further clarification is the handling of complex scenarios with significant occlusions or highly incomplete views. While the method shows robustness in many cases, some views may still contain critical information that is difficult to reconstruct, especially in tasks involving complex state transitions. This limitation could affect the performance in very challenging real-world environments, and further research into addressing these edge cases would strengthen the overall claims. Methods And Evaluation Criteria: The comparison methods are all model-free multiview reinforcement learning approaches, lacking a comparison with model-based methods, which makes it difficult to fully convince us of the performance superiority of this method. Theoretical Claims: Yes, the proof of Value Function Bound is convincing. Experimental Designs Or Analyses: Baselines and Comparisons Strengths: The authors compared MFSC with several baseline methods, including Keypoint3D, LookCloser, F2C, MVD, RAD, and Vanilla PPO. These baselines cover a range of approaches to MVRL, providing a robust comparison. The results show that MFSC consistently outperforms these baselines in most tasks, demonstrating the effectiveness of the proposed method. Potential Issues: Missing Baselines: As mentioned earlier, the comparisons do not include some recent MBMVRL methods. Including these methods would strengthen the validity of the results. Hyperparameter Tuning: The paper does not provide detailed information on the hyperparameter tuning for the baselines. If the baselines were not tuned to their optimal settings, the comparisons might be unfair. Performance Metrics and Evaluation Strengths: The authors evaluated the performance of their method using various performance metrics, including episode return, environment steps, and success rates. Using multiple seeds and confidence intervals in the results helps assess the statistical significance of the findings. Potential Issues: Limited Metrics in CARLA: In the CARLA environment, the evaluation metrics primarily focus on driving performance (e.g., distance traveled, success rate, steering amplitude, braking intensity, and collision severity). Including additional metrics, such as the number of collisions or the time taken to complete the task, could provide a more comprehensive evaluation. Reward Normalization: The paper uses reward normalization to stabilize the learning process. While this is a common practice, it could mask some of the nuances in the reward signal. The authors should discuss the impact of reward normalization on the results. Supplementary Material: Yes, all parts. Relation To Broader Scientific Literature: Bisimulation Metric Learning: Extends the concept of bisimulation metrics to the multi-view setting, providing a novel approach to learning task-relevant representations. Application to Real-World Scenarios: Evaluates the method in a real-world autonomous driving environment, highlighting its potential for practical applications. Essential References Not Discussed: Multiview Dreaming[1] extends the Dreaming algorithm to achieve integrated recognition and control from multiple perspective observations. This method utilizes contrastive learning to train a shared latent space between different views and integrates the latent state distributions from multiple perspectives through an expert mixture approach, thereby addressing the limitations of single-view observations in traditional reinforcement learning methods. MOSER[2] is a model-based approach that actively seeks the optimal perspective for learning task representations under multiple views to enhance performance. References [1] Kinose, A., Okada, M., Okumura, R., & Taniguchi, T. (2023). Multi-view dreaming: Multi-view world model with contrastive learning. Advanced Robotics, 37(19), 1212-1220. [2] Wan, S., Sun, H. H., Gan, L., & Zhan, D. C. (2024, August). MOSER: learning sensory policy for task-specific viewpoint via view-conditional world model. In Proceedings of the Thirty-Third International Joint Conference on Artificial Intelligence (pp. 5046-5054). Other Strengths And Weaknesses: Strengths - The paper presents a novel approach integrating bisimulation metric learning with a multi-view-based masking and latent reconstruction auxiliary task. - The paper is well-structured and clearly presents the methodology, experiments, and results. - The authors conducted extensive experiments to validate the effectiveness of MFSC. Weaknesses - The lack of comparison with model-based methods makes it impossible to fully validate the superiority of this approach. - There is a lack of quantitative analysis and presentation regarding the Bisimulation metric, not just ablation experiments. Other Comments Or Suggestions: Please see the Questions. Questions For Authors: 1. Could you provide more comparisons with model-based methods, such as MV-MWM, Multiview Dreaming, and MOSER? 2. Will conducting reinforcement learning from multiple perspectives lead to increased time and storage costs, and how can this issue be mitigated? Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: Thanks for your comments, and we will address your concerns in the following. ------ Potential Issues: hyperparameter tuning Thank you for your valuable feedback. For all baseline methods with publicly available implementations, we directly used their officially released code and default configurations to ensure they achieve the performance reported in the original papers. We will include a clarification of this in the experimental details section. ------ Potential Issues: limited metrics in CARLA Thank you for your suggestion. Our choice of evaluation metrics in CARLA is consistent with previous works. In addition, we would like to clarify that our evaluation metrics not only focus on driving performance (e.g., distance traveled, success rate of reaching 100 meters), but also take driving safety into account, including steering amplitude, braking intensity, and collision severity. ------ Potential Issues: reward normalization We acknowledge the reviewer’s point that reward normalization may mask certain nuances in the reward signal. In our experiments, whether to apply reward normalization under different benchmarks depends on the implementation of the methods we compare against. We also conducted ablation studies on MetaWorld tasks, where reward normalization is required, to analyze the impact of reward normalization. Detailed results can be found at this [link](https://anonymous.4open.science/r/MFSC-1488/rebuttal.pdf) (Fig.2). The results show that without reward normalization, the performance of our method degrades significantly. This is because the large scale of raw rewards causes large gradients during Q-value updates, leading to oscillations in Q-value loss and overall instability in training. Additionally, reward normalization constrains the reward signal to a feasible range, which helps stabilize the optimization of the bisimulation objective, further improving the quality of the learned representations. ------ Essential References Not Discussed We appreciate the additional references provided and are pleased to include Multi-view Dreaming and MOSER in our manuscript, as they significantly enhance the completeness and relevance of our work. ------ W1 and Q1: the lack of comparison with model-based MVRL We appreciate the reviewer’s suggestion to compare our method with MB-MVRL algorithms. Since MV-MWM relies on additional expert demonstrations and Multiview Dreaming does not release its implementation code, we chose to compare our method with the MB-MVRL algorithm MOSER. MOSER seeks the optimal viewpoint for learning task representations under multiple views. Its implementation code is available at https://github.com/yixiaoshenghua/MOSER, and the corresponding experimental results can be found at this [link](https://anonymous.4open.science/r/MFSC-1488/rebuttal.pdf) (Fig.3). Our experimental results show that our approach outperforms the MOSER algorithm in both tasks, demonstrating the effectiveness of our method. We believe these additional comparisons help validate the superiority of our method. ------ W2: quantitative analysis on bisimulation metric Thanks for your insightful comment. To provide a more quantitative analysis of the bisimulation metric, we include the training curve of the bisimulation loss and additionally measure the mutual $I\left( z_{L}^{0};s \right)$ information between the final fused embeddings $z_{L}^{0}$ and the ground-truth states $s$ using the MINE [1] method. The results can be found at this [link](https://anonymous.4open.science/r/MFSC-1488/rebuttal.pdf) (Fig.4). As training progresses and the bisimulation loss converges, we observe a consistent increase in mutual information. This indicates that the model not only optimizes the bisimulation criterion but also gradually constructs a task-relevant representation space aligned with the true environment states. [1]Belghazi, et al. Mutual information neural estimation. ------ Q2: Will conducting reinforcement learning from multiple perspectives lead to increased time and storage costs, and how can this issue be mitigated? While multi-view observations provide a more comprehensive understanding of the environment, they may lead to increased computational time, storage cost. To mitigate this, we can leverage pretraining techniques to reduce training costs. Additionally, inspired by MOSER, we can train a view selector to dynamically choose the most relevant views for decision-making, thus may potentially minimize unnecessary computational and storage demands. ------ Please do not hesitate to let us know if you have any additional comments. --- Rebuttal Comment 1.1: Comment: Thanks for the author's reply. My problems have been solved, and I will raise the score from 3 to 4.	Summary: The paper proposes a novel framework for Multi-View Reinforcement Learning (MVRL). The key contributions include: - Integrating bisimulation metric learning into MVRL to extract task-relevant representations from multi-view observations. - Introducing a multiview-based masking and latent reconstruction auxiliary task to enhance robustness against missing or noisy views. - Demonstrating superior performance over existing methods in robotic manipulation (Meta-World, PyBullet) and autonomous driving (CARLA) tasks, especially in scenarios with interference or missing views. Claims And Evidence: Yes, the claims are generally supported by clear and convincing evidence. Methods And Evaluation Criteria: Yes. The methods are largely appropriate for addressing the challenges of multi-view reinforcement learning. Theoretical Claims: Yes. The theoretical claims are sound. Experimental Designs Or Analyses: The experimental designs and analyses are largely sound but exhibit minor validity concerns in specific benchmarks and theoretical assumptions. For example, on DeepMind Control Suite environment, temporal stacking conflates temporal and spatial multi-view learning, undermining conclusions about MFSC’s multi-view fusion capabilities. Supplementary Material: Yes. The supplementary material further provides the experimental details and the results on DeepMind Control Suite and CARLA. Relation To Broader Scientific Literature: The paper advances MVRL by integrating bisimulation metrics and masking-driven reconstruction into a cohesive framework. MV-MWM (Seo et al., 2023a) relies on pixel-level reconstruction and expert demonstrations, which may retain redundant details. In this paper, the latent reconstruction loss avoids reconstructing irrelevant details, improving efficiency. Essential References Not Discussed: No, the essential references are discussed in the paper. Other Strengths And Weaknesses: Strengths: - This paper is clearly written and easy to follow. - It introduces a novel framework by integrating bisimulation metrics with multi-view fusion and masking-based reconstruction, addressing critical gaps in task-relevance and robustness for MVRL. - The work is supported by extensive experiments across diverse benchmarks (Meta-World, PyBullet, CARLA), including ablation studies and robustness tests under noisy/missing views. Weaknesses： - Using sequential frames as different views in the DeepMind Control environment is an invalid design choice. A more reasonable approach might involve training with three identical images as inputs to isolate multi-view fusion setting. Other Comments Or Suggestions: - The paper fixes the number of views to 3. How does the number of views impact the experimental results? An ablation study on varying view counts would strengthen the analysis. If performance with 1 view is comparable to multi-view setups, it raises questions about the necessity of multi-view learning or whether the method fails to extract useful cross-view information. - In Fig.1, the symbol $\tilde{z}^n_L$ was mistakenly written as $\tilde{x}^n_L$. Questions For Authors: In Fig.1, I would like to understand the model’s design details: How does the architecture ensure that $z_L^0$ the fused state embedding) integrates features from all views? Is this achieved by blocking gradient propagation from $z_L^{1-3}$, and is there theoretical justification for this design? Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: We sincerely thank the reviewer for thoughtful and constructive feedback. We are pleased that our proposed framework for Multi-View Reinforcement Learning (MVRL), including the integration of bisimulation metric learning and masking-based latent reconstruction, was well-received. We appreciate the recognition of our theoretical formulation, experimental design, and the robustness of our method across diverse benchmarks. We truly appreciate your insightful feedback and constructive suggestions, and we will address your concerns in the following. ------ W1: experimental setup of Deep Mind Control Suite We would like to clarify that our primary goal is to explore how multi-view information can be leveraged to enhance decision-making efficiency. While we focus on spatial multi-view in the paper, as demonstrated in our experiments with environments like Metaworld, PyBullet, and CARLA, we also recognize that "multi-view'' can manifest in both temporal and even multi-modal forms. Hence we further explore the temporal information fusion in DeepMind Control environments. To address the potential confusion, we will clarify the distinction between these two experimental setups in the next version of the paper. ------ Other Comments Or Suggestions 1: ablation study on varying view counts We appreciate the reviewer’s insightful suggestion. In response, we have added an ablation study that varies the number of views, and the results are presented in Fig. 1 at the following link [link](https://anonymous.4open.science/r/MFSC-1488/rebuttal.pdf). It shows that using any single view out of the three performs worse than the full multi-view setup. In particular, View 3 — a top-down perspective — suffers from severe occlusion, resulting in the lowest performance among the three. This highlights the limitations of relying on individual views and underscores the effectiveness of our approach in extracting and fusing complementary information across views. Overall, these results validate the necessity and benefit of multi-view learning in achieving more robust and informative state representations. ------ Other Comments Or Suggestions 2: In Fig.1, the symbol was mistakenly written. Thanks for your careful review and for pointing out the mistake. We appreciate your feedback and will correct the symbol in the next version of the paper. ------ Q: model design details Thanks for your comment, and we apologize for any confusion caused. We clarify this design as follows: we introduce an additional learnable ``[state]`` embedding that interacts with the view-specific embeddings through a self-attention mechanism. The output of this embedding, denoted as $z_L^{0}$, is updated through the bisimulation loss. The theory of bisimulation guarantees that the learned representations retain all task-relevant information from multiple views, enabling $z_L^{0}$ to effectively aggregate this information into a unified representation. Importantly, MFSC optimizes the bisimulation objective exclusively with respect to $z_L^{0}$, not the view-specific embeddings $z_L^{1-3}$. This design choice follows a similar paradigm to BERT and ViT, where supervision is applied exclusively to a designated token (e.g., the ``[class]`` token). We also recognize that the current depiction of gradient flow in Fig.1 may be misleading, and we will revise it in future versions to accurately reflect the optimization process. ------ Please do not hesitate to let us know if you have any additional comments. --- Rebuttal Comment 1.1: Comment: Thank you for the authors for the detailed response and additional results. I will maintain my score of 4 and recommend acceptance of this paper.	Summary: The paper proposes a novel framework for multi-view reinforcement learning to effectively learn task-relevant representations of the state from multi-view observations. The new framework not only incorporates the bisimulation metric which aligned representation with the task’s objectives but also add latent reconstruction as an auxiliary task to retain crucial details that are specific to each individual view. The paper also provide strong experimental results in realistic scenarios which demonstrate the effectiveness of the unified fusion state representation from multi-view setting. Claims And Evidence: The paper provides clear statement and strong evidence for most of the claims. I only have a very minor holdback on the claim of "MFSC is the first to incorporate bisimulation into the MVRL framework". The claim is true but the main concern is that the method used to incorporate bisimulation into the MVRL framework are very similar to DBC [1] except the introduction of state aggregator to fuse multi-view observations. I would suggest authors to better discuss the proposed method and DBC in related work or Section 4.1. I think MFSC have many advantages compared to DBC, especially on retaining details with the latent reconstruction task. More discussion on the bisimulation metric part will make the contribution even stronger. [1] Zhang, A., McAllister, R., Calandra, R., Gal, Y., and Levine, S. Learning invariant representations for reinforcement learning without reconstruction. International Conference on Learning Representation, 2021. Methods And Evaluation Criteria: Yes, the proposed methods are well evaluated. Theoretical Claims: Yes, they all seem correct. Experimental Designs Or Analyses: Yes, the experimental results are sound and valid at my best knowledge. Supplementary Material: Yes, the proof of Lemma 4.2. Relation To Broader Scientific Literature: I believe the proposed method pushes further in both the field of multi-view reinforcement learning and the field of robust representation learning for RL. Essential References Not Discussed: No. Other Strengths And Weaknesses: No. Other Comments Or Suggestions: No. Questions For Authors: Could you share the differences between MFSC and DBC when using the bisimulation metric? Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: We sincerely thank all the reviewers for their thoughtful evaluation, constructive feedback, and valuable suggestions, which have greatly contributed to improving the clarity, depth, and overall quality of our work. We will address your concerns in the following. ------ Q: Could you share the differences between MFSC and DBC when using the bisimulation metric? We sincerely appreciate the reviewer’s insightful question and are pleased to provide a more detailed clarification of the differences between MFSC and DBC in their use of the bisimulation metric. Specifically, MFSC differs from DBC in two key aspects: 1. Avoiding Wasserstein distance for behavioral similarity. The bisimulation metric generally requires calculating the Wasserstein distance between distributions, which can be computationally expensive. To mitigate this complexity, DBC models latent dynamics transitions as Gaussian distributions, leveraging Euclidean distances to compute a closed-form Wasserstein distance, optimizing an $\ell_1$ distance between representations. However, this approach assumes Gaussian dynamics and introduces an inconsistency between $\ell_1$ and $\ell_2$ (Euclidean) distances, potentially leading to inaccurate approximations. MFSC adopts sampling-based computation approach via independent coupling strategy, encoding current observations into latent representations and explicitly learning latent dynamics to generate representations of subsequent states. 2. Cosine distance as the base metric for latent state representation. Inspired by SimSR, MFSC adopts cosine distance as the base metric for bisimulation computation. Please refer to our response W1 to Reviewer JyV5 for more details regarding the benefit of using cosine distance as the base metric. Besides, both $\ell_1$ distance (used for reward differences) and cosine distance (used for state differences) are conveniently scalable to matrix operations. Consequently, MFSC can efficiently compute a correlation matrix of state representations within a batch and optimize it to accelerate representation learning. This strategy significantly enhances efficiency compared to DBC’s pairwise comparisons via permutation, resulting in faster and more effective representation updates. We sincerely thank the reviewer for the valuable comment and will provide a detailed clarification in the appendix of the revised manuscript. ------ Please do not hesitate to let us know if you have any additional comments.	Summary: This paper addresses key challenges in multi-view reinforcement learning (MVRL), specifically redundancy in observations, distracting or irrelevant information, and robustness to missing views. To overcome these issues, the authors propose a framework, Multi-view Fusion State for Control (MFSC), integrating task-relevant representation learning inspired by the bisimulation metric and a self-attention-based fusion mechanism. Additionally, the method leverages a novel masking-based latent reconstruction auxiliary task to improve robustness against incomplete or missing observations. Experimental validation demonstrates that MFSC consistently achieves superior performance and robustness compared to existing state-of-the-art methods across several robotic manipulation and locomotion benchmarks. Claims And Evidence: The manuscript provides the following valid claims and their supporting evidences: Claim 1: MFSC effectively learns compact and task-relevant multi-view representations. Evidence 1: Empirical evaluation across multiple robotic manipulation tasks (Meta-World, PyBullet Ant) shows MFSC significantly outperforms baselines. In addition, visualization (Figure 4) qualitatively analyses using Grad-CAM show the method consistently focuses on task-critical features, indicating successful extraction of task-relevant information. Claim 2: Proposed masking-based latent reconstruction improves robustness against missing views. Evidence 2: Experiments demonstrate MFSC maintains stable and superior performance under scenarios with missing or noisy views, outperforming state-of-the-art methods such as LookCloser and F2C. The authors also provide an ablation test on Figure 7.(b). Methods And Evaluation Criteria: The proposed methods and evaluation criteria are appropriate and well-justified. Theoretical Claims: The bisimulation metric-motivated representation learning in MFSC ensures that the difference between optimal value functions of the original and latent MDPs is bounded, thus providing a theoretical justification for learning compact yet task-relevant multi-view representations. However, a theoretical gap exists between the Wasserstein distance between transition distributions—originally used in the MICo update operator—and the expected cosine distance between successor observations employed in this work. Although the authors attribute this gap primarily to computational complexity, a more rigorous theoretical discussion is necessary. Specifically, clarifications on the relationship between two metrics such as how the two metrics differ theoretically, and under which conditions they become equivalent, would significantly strengthen the paper. Experimental Designs Or Analyses: The experimental design is comprehensive, and analyses demonstrate method effectiveness and robustness. Supplementary Material: I have reviewed the implementation details contained in the supplementary material. Relation To Broader Scientific Literature: This work has potential implications for real-world applications requiring control under diverse observational settings, such as autonomous driving. In addition, one particularly relevant application area is multi-modal learning, such as vision-language models (VLM). Essential References Not Discussed: The manuscript adequately covers relevant literature. To my knowledge, no essential references appear to be missing. Other Strengths And Weaknesses: ### Strengths: 1. Practical Contribution: The paper effectively integrates bisimulation metric learning into multi-view RL settings, particularly utilizing self-attention fusion modules, demonstrating clear practical advantages. 2. Sound Experimental Validation: The research questions are well-motivated, and the authors provide extensive experimental evidence supporting their approach. ### Weaknesses 1. Weak Connection between Bisimulation Metrics: The theoretical connection between the proposed expected cosine distance and the traditional bisimulation metric (originally employing the Wasserstein distance) is relatively weak and lacks sufficient analysis or justification. 2. Novelty: Both bisimulation metric and self-attention mechanisms themselves are individually well-established techniques, which somewhat limits the standalone novelty of the method. The paper does not clearly emphasize the theoretical advantages or technical challenges arising specifically from integrating these two components. Clarifying how this integration uniquely contributes to MVRL would strengthen the novelty claim. Other Comments Or Suggestions: In the manuscript, the paper title and method name are not intuitively clear about the proposed approach. Emphasizing key components such as bisimulation and self-attention fusion could help better highlight the novelty and differentiating aspects of the research. Questions For Authors: Question 1. Why did the authors consider the additional reconstruction loss necessary? I am slightly concerned that the proposed auxiliary objective (reconstruction loss) may inadvertently encourage the learned representations to rely on redundant information from views that could be missing during inference. Question 2. Why did the authors choose to compare MFSC against the convergence performance of the specific baseline method (F2C)? Clarification on the motivation behind this comparison method would be helpful. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Thanks for your insightful comments, and we will address your concerns in the following. ------ W1: We noticed that the citation in Definition 3.1 was incorrect; the correct reference should be the $\pi$-bisimulation metric proposed by Castro et al.(2020)[1], rather than Castro et al.(2021)[2]. We apologize for the confusion caused. To clarify, we provide a brief clarification on the connection between these works: Conventional bisimulation metric needs to compute the Wasserstein distance over the transition distributions across all actions, which is computationally expensive. Instead, Castro et al.(2020)[1] developed $\pi$-bisimulation which removes the requirement of considering all actions and only needs to consider the actions induced by a policy $\pi$. Castro et al.(2021)[2] introduces independent coupling and proposes a sampling-based metric that does not rely on the Wasserstein distance; however, this comes at the cost of violating the “zero self-distance”, potentially leading to representational collapse. In contrast, our use of the cosine distance is both efficient and guarantees this key property by design, as also demonstrated in SimSR [3]. This theoretically safeguards against collapse in learned representations. We will elaborate on this point more comprehensively in the next revision. [1] Castro, et al.(2020). Scalable Methods for Computing State Similarity in Deterministic Markov Decision Processes. [2] Castro, et al.(2021). MICo: Improved representations via sampling-based state similarity for Markov decision processes. [3] Zang, H, et al.(2022). SimSR: Simple Distance-Based State Representations for Deep Reinforcement Learning. ------ W2: We fully agree that both bisimulation metrics and self-attention mechanisms are well-established techniques, yet each has limitations when applied in isolation to MVRL. Specifically, self-attention effectively aggregates information from multiple views but typically lacks an explicit mechanism to focus on task-relevant features, potentially introducing irrelevant or redundant information into the final representations. On the other hand, bisimulation alone does not explicitly utilize the correlations across multiple views. To the best of our knowledge, such an integration has not been explored in the context of MVRL. Following your suggestions, we will carefully revise the manuscript to more clearly emphasize the distinct advantages of this integration. ------ The paper title and method name Thanks for your point out. We agree that emphasizing core elements such as bisimulation and self-attention would better highlight the novelty of our method. We will consider revising the paper title and method name to more clearly reflect these components by incorporating terms like “Bisimulation-Constrained Attentive”. ------ Q1: necessity of the reconstruction loss The reconstruction objective is designed to exploit the inherent cross-view dependencies in multi-view observations, thereby enhancing the model’s representation capacity. The effectiveness of this self-supervised objective has been demonstrated in our ablation study (Fig.7b). We would like to offer some clarifications regarding your concerns. Crucially, the reconstruction objective is applied in the latent space, distinct from pixel-level reconstruction. This design encourages the model to reconstruct information that is shared across multiple views, rather than relying on superficial pixel-level redundancy. Moreover, in our downstream RL tasks, we exclusively utilize $z_{L}^{0}$, which is optimized via the bisimulation objective. The theoretical foundation of bisimulation guarantees that $z_{L}^{0}$ preserves task-relevant information aggregated from multi-view observations. For this representation, the reconstruction objective serves to recover task-relevant information. We therefore contend that the representations used for downstream control primarily capture task-relevant features rather than redundant information, as demonstrated by the visualizations in Fig.4\&6. We hope this explanation clarifies our motivations and design choices. ------ Q2: results of F2C We conducted a careful review of recent MVRL baselines and considered that F2C demonstrates competitive performance on the MetaWorld benchmark according to its performance report. However, the official implementation of F2C for MetaWorld has not been released, and we were unable to reproduce its reported results, despite reaching out to the authors multiple times without receiving any response yet. To enable a comprehensive comparison and study in MVRL, we report the convergence performance of F2C as provided in the original paper. We appreciate your suggestion and will provide a detailed explanation of this decision in the revised version of our paper. ------ Please do not hesitate to let us know if you have any additional comments.	null	null	null	null	null	null
Efficient and Separate Authentication Image Steganography Network	Accept (spotlight poster)	Summary: This paper presents a novel authentication-based image steganography framework (AIS) with separate invertible networks for authentication and hiding. The approach addresses critical challenges in multi-recipient security and large-capacity hiding. The experiments demonstrate significant improvements in stego/revealed image quality and computational efficiency. Claims And Evidence: Yes, they are clear and have convincing evidence. Methods And Evaluation Criteria: Yes, they are promising. Theoretical Claims: All the proofs for theoretical claims have been checked. Experimental Designs Or Analyses: All the experimental designs or analyses have been checked. Supplementary Material: The supplementary material has been reviewed, which only contains a text with non-useful information to the manuscript. Relation To Broader Scientific Literature: The paper addresses critical challenges in multi-recipient security and large-capacity hiding. This will have a broader study topics such as multi-recipient security, large-capacity hiding, video hiding. Essential References Not Discussed: N/A Other Strengths And Weaknesses: The paper contains the following weaknesses: 1) The comparison in Table 1 shows superior performance over baselines. However, recent diffusion-based steganography methods are not included. Although they are not in the same class, could the authors discuss how your method compares to diffusion models in terms of security and computational overhead? 2) The dynamic lock-key generation module is critical. Could you clarify how the "linear combination" of global and local locks ensures uniqueness across multiple secret images? 3) The paper claims parallel hiding reduces model size, but Table 1 shows AIS still requires ~6M parameters for N=5. Could you provide FLOPs/parameter ratios relative to baselines to better illustrate efficiency gains? 4) Some formatting inconsistencies exist. Please proofread for hyphenation and notation consistency. Other Comments Or Suggestions: None. Questions For Authors: 1) The security analysis evaluates resistance to SRNet and ZhuNet. Have you tested against more advanced steganalysis tools to further validate robustness? 2) The IAN extracts "primary information" from secret images. How is the 3-channel design justified compared to other feature reduction strategies (e.g., PCA or attention-based compression)? Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: Thank you very much for your valuable comments. We hope that the explanations on the questions can help you better understand our proposed method. Q1: The comparison in Table 1 shows superior performance over baselines. However, recent diffusion-based steganography methods are not included. Although they are not in the same class, could the authors discuss how your method compares to diffusion models in terms of security and computational overhead? A1: We compare our method with diffusion-based models. (1) Capacity. Diffusion-based models can only hide 1 secret image once, which limits flexibility. AIS can hide up to 8 secret images in a cover image. (2) Quality. The average PSNR of revealed secret images of diffusion-based models is typically below 25. AIS achieves PSNR of over 25 even when hiding 8 secret images. (3) Security. Diffusion-based models ignore the problem that keys cannot be transmitted through public channel. AIS can restore keys through Lock-Key Generation Module, ensuring security of keys. (4) Computational overhead. Diffusion-based models typically require billions of parameters and a long inference time to generate images. AIS only requires millions of parameters and time below 0.2s. These comparisons indicate that AIS performs better in large-capacity steganography. Q2: The dynamic lock-key generation module is critical. Could you clarify how the "linear combination" of global and local locks ensures uniqueness across multiple secret images? A2: Through extracting multiscale features of cover and secret images, Dynamic Lock-Key Generation Module generates a global lock from cover image and a local lock from each secret image. This means within the same batch, global lock is the same, while local lock for each secret image is different from each other. For different batches, global lock is different from each other. Linear combination integrates global locks and local locks with two coefficients to control the strength of the two lock components. Higher coefficient before global locks focuses on the uniqueness among different batches. Higher coefficient before local locks enhances uniqueness among different secret images within the same batch. Q3: The paper claims parallel hiding reduces model size, but Table 1 shows AIS still requires ~6M parameters for N=5. Could you provide FLOPs/parameter ratios relative to baselines to better illustrate efficiency gains? A3: We have compared FLOPs and inference time in the original paper, which are shown in Table 1, Column FLOPs and Time. For FLOPs, AIS has the least FLOPs among all the baselines. For inference time, AIS spends shorter inference time compared to traditional serial hiding methods. The results indicate that AIS achieves a better balance between quality and efficiency. Q4: Some formatting inconsistencies exist. Please proofread for hyphenation and notation consistency. A4: We check the paper again and make some correction. (1) “CIS” in Table 2 is modified to “AIS” for consistency. (2) The font of “exp” in Equation 5 and 6 is modified to be consistent with Equation 4 and 7. (3) “low-” in page 4 is modified to “low-frequency” for correct hyphenation. (4) “$T$” in page 5 is modified to “$T_f$” to correctly denote the frequency stego image. Other grammar issues are also solved in the revised paper. Q5: The security analysis evaluates resistance to SRNet and ZhuNet. Have you tested against more advanced steganalysis tools to further validate robustness? A5: We have added experiments on resistance against LWENet[1], a more advanced steganalysis method. The detection accuracy is 67.30%(ISN), 89.55%(DeepMIH), 62.20%(IIS) and 51.75%(our AIS). This means the stego images generated by AIS confuse the steganalysis model, which improves security against the attackers. The results will be added to the paper. [1] Weng S, Chen M, Yu L, Sun S. Lightweight and effective deep image steganalysis network. IEEE Signal Processing Letters, 29:1888-92, 2022. Q6: The IAN extracts "primary information" from secret images. How is the 3-channel design justified compared to other feature reduction strategies (e.g., PCA or attention-based compression)? A6: (1) The design of reversibility in IAN can reveal the original secret image without extra modules. In the backward process, the original secret images can be revealed from the primary information through the reverse process of IAN with shared parameters. In contrast, other strategies can only extract critical information. They require additional modules to reveal the original secret images. (2) Invertible Neural Network implies a prior that the data distribution can be decomposed into a simple distribution through learnable transformations. This enables IAN to model the other information into a simple distribution. Through a prior of Gaussian distribution, part of the other information can be restored. This improves the quality of revealed secret images, making IAN suitable for reconstruction tasks. --- Rebuttal Comment 1.1: Comment: Thanks for the author's reply, which solved most of my problems. I will consider raising the score appropriately. --- Reply to Comment 1.1.1: Comment: We greatly appreciate your acknowledge of our work and raising the score. Thanks again for your time and effort in reviewing our paper.	Summary: This work advances adaptive steganography by redefining secure multi-user communication through the integration of invertible networks and dynamic authentication. A key innovation lies in decoupling authentication from secret data via distribution adaptation, a conceptual leap that reimagines information hiding in constrained spaces. The parallel hiding architecture further exemplifies strong engineering intuition, achieving parameter reduction without compromising quality. Beyond its forward-looking contributions, the paper also addresses a pressing challenge in privacy-preserving multi-user steganography. Claims And Evidence: Yes. The claims are well-supported with clear evidence. Methods And Evaluation Criteria: Yes. The methods and evaluation criteria are appropriate. Theoretical Claims: Yes, I have checked all the proofs. Experimental Designs Or Analyses: Yes, I have checked all the experimental designs or analyses. Supplementary Material: Yes. Relation To Broader Scientific Literature: The methods in this paper can well address the problems within the practical engineer, and gives a new direction for multi-user privacy security in this area. Essential References Not Discussed: Yes, the cited works sufficiently contextualize the paper’s key contributions. Other Strengths And Weaknesses: Several aspects of the paper could be improved: 1. The dynamic lock-key module employs a "simplified UNet." Providing ablation studies on alternative architectures or clarifying the rationale for this choice would strengthen the justification. 2. In Figure 3, clearer annotations for the lock/key propagation paths would enhance the workflow diagram’s clarity. 3. The term "primary information extraction" requires a more precise and well-supported explanation. 4. The proposed method could potentially be extended to video steganography. Could the authors suggest how to transfer the adaptation strategy to video steganography with temporal consistency requirements? 5. Minor grammar issues should be addressed for improved readability. Other Comments Or Suggestions: See "Other Strengths And Weaknesses". Questions For Authors: See "Other Strengths And Weaknesses". Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Thank you very much for your valuable comments. We hope that the explanations on the questions can help you better understand our proposed method. Q1: The dynamic lock-key module employs a "simplified UNet." Providing ablation studies on alternative architectures or clarifying the rationale for this choice would strengthen the justification. A1: Dynamic Lock-Key Generation Module is employed to extract features from the cover image and each secret image to dynamically generate locks and keys. By feature extraction, the locks for secret images are different from each other, ensuring security among multiple recipients. Many traditional models of extracting features can achieve this. In AIS, we employ a simplified UNet due to two reasons. (1) Multiscale feature fusion. UNet can extract features of different scales through symmetric downsampling-upsampling structure and skip connection. It can extract detailed information such as edges and textures in shallow layers, and capture abstract semantics in deep layers. This makes the generated locks and keys have richer representation, thus improving security. (2) Lightweight. The simplified UNet requires only 77K parameters and 0.395G FLOPs, ensuring efficiency. Q2: In Figure 3, clearer annotations for the lock/key propagation paths would enhance the workflow diagram’s clarity. A2: We have modified Figure 3 (https://s1.imagehub.cc/images/2025/03/26/d4d07474bef137e5714acdbd5c45b36b.png). The annotations of output lock and key have been added. Additionally, the paths of inputs have been added. Locks are generated from cover and secret images. Keys are generated from stego images and revealed primary information. Q3: The term "primary information extraction" requires a more precise and well-supported explanation. A3: Primary information is the part of information that is more important for restoring the original image. On the one hand, the space of a cover image for hiding secret is limited. With more information hidden in the cover image, the quality of the generated stego image will be lower. On the other hand, sufficient information needs to be hidden in the cover image for revealing. With less information hidden in the cover image, the quality of revealed secret images will be lower. The steganography network is optimized to achieve a balance between the quality of stego and revealed secret images. Based on this, a spontaneous idea is to hide part of the secret information. Xiao et al.[1] pointed out that for a 12-channel frequency domain RGB image, the low-frequency information of 3 channels is sufficient to restore the original image of high quality. Motivated by this, we set the number of reserved channels as 3. By jointly optimizing stego images and revealed secret images, IAN is trained to extract information which is more important for revealing. We call this more primary information. This part of information can enhance revealing while hiding less information in the cover image, improving the quality of both stego and revealed secret images, which meets the goal of joint optimization. [1] Xiao, M., Zheng, S., Liu,C., Lin,Z., and Liu,T. Invertible rescaling network and its extensions. International Journal of Computer Vision, 131(1): 134–159, 2023. Q4: The proposed method could potentially be extended to video steganography. Could the authors suggest how to transfer the adaptation strategy to video steganography with temporal consistency requirements? A4: It’s a good idea to apply distribution adaptation to video steganography. When hiding secret information into a cover video, inconsistent distribution of the secret information may cause visual discontinuity between adjacent frames, which degrades temporal consistency. We suggest a module similar to IAN being introduced to video steganography. This module receives the input of secret information, along with a cover video as the condition. With similar transformation, the secret information is decomposed into more primary information with consistent distribution. At the same time, the transformation may pay attention to the cover video condition, and guide the generation of the primary information. With more primary and consistent information hidden, the stego video may release some space for hiding more information, while keeps consistent distribution between frames. Q5: Minor grammar issues should be addressed for improved readability. A5: Thank you for your suggestion. We check the paper again and make some correction. (1) “requirement” in page 1 is modified to “requirements”. (2) “CIS” in Table 2 is modified to “AIS” for consistency. (3) The font of “exp” in Equation 5 and 6 is modified to be consistent with Equation 4 and 7. (4) “low-” in page 4 is modified to “low-frequency” for correct hyphenation. (5) “$T$” in page 5 is modified to “$T_f$” to correctly denote the frequency stego image. In addition, other grammar issues have also been solved in the revised paper. --- Rebuttal Comment 1.1: Comment: Thank you for detailed reply. My concerns have been addressed, and I will maintain my current score. --- Reply to Comment 1.1.1: Comment: We greatly appreciate your acknowledge of our work and respect your decision on maintaining the score. Thanks again for your time and effort in reviewing our paper.	Summary: The paper presents AIS, an authentication-based steganography framework that leverages invertible networks for distribution adaptation and parallel hiding. The two-stage design and focus on security and efficiency are commendable, and comprehensive experiments demonstrate the framework’s advantages. While the paper is well-structured and the core contributions are promising, a deeper analysis of key design choices and broader applicability would strengthen the work’s overall impact. Claims And Evidence: Yes, they are supported. Methods And Evaluation Criteria: Yes, they make sense and are widely used in this area. Theoretical Claims: I have reviewed the proof of Theorem 14 in the appendix, and it appears to be correct. Experimental Designs Or Analyses: I have reviewed the soundness and validity of the experimental designs and analyses, and they are accurate. Supplementary Material: I have reviewed the attached supplementary materials. Relation To Broader Scientific Literature: The method relates to authentication-based steganography designed for multiple users. Essential References Not Discussed: The related works are essential for understanding the key contributions of the paper and are appropriately cited and discussed. Other Strengths And Weaknesses: Strengths: The proposed AIS framework elegantly integrates authentication with invertible networks, achieving secure and efficient multi-image steganography. The two-stage design and distribution adaptation strategy are innovative, contributing to improved performance and robustness. The paper is well-structured and presents comprehensive experimental results. Weaknesses: a) The distribution adaptation mechanism is central to reducing lock-induced artifacts. Could the latent distributions of locks and secrets before and after adaptation be visualized to quantitatively demonstrate alignment? b) While Table 5 (Appendix D) reports results for N = 8, the main text focuses on N = 2–5. Including results for N = 6–7 could provide insight into performance degradation trends. c) The RPM module in IHN uses a residual structure for redundancy prediction. How does this compare to alternative prediction architectures, such as transformers? Ablation studies on RPM’s design would strengthen the claims. d) The invertible blocks (Eq. 4–7) share parameters between forward and backward passes. Does this limit flexibility compared to non-shared designs? A discussion of the trade-offs would clarify the design rationale. e) Some equations have formatting issues. A thorough review and correction are recommended. f) How does AIS handle real-world scenarios such as JPEG compression or noise perturbations? Testing under such conditions would better demonstrate the framework's practicality. Other Comments Or Suggestions: Although the paper is well-structured and presents some new ideas, there are several issues that need clarification and resolution (refer to the weaknesses). If these concerns are addressed in the rebuttal phase, I may reconsider my decision. Questions For Authors: Please refer to the weaknesses. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Thank you very much for your valuable comments. We hope that the explanations on the questions can help you better understand our proposed method. Q1: The distribution adaptation mechanism is central to reducing lock-induced artifacts. Could the latent distributions of locks and secrets before and after adaptation be visualized to quantitatively demonstrate alignment? A1: Figure 7(b) shows mean and standard deviation of 1000 samples to generally indicate consistent distribution of adapted information. According to your suggestion, we visualize some locks, secret images and adapted information (https://s1.imagehub.cc/images/2025/03/26/edfaea8efa039b0ebef270cecd585a39.png). From the result, the distribution of secret images and locks is significantly inconsistent. AIS makes distribution adaptation to get a representation with consistent distribution. The above content will be added to the paper. Q2: While Table 5 (Appendix D) reports results for N = 8, the main text focuses on N = 2–5. Including results for N = 6–7 could provide insight into performance degradation trends. A2: We show results of N=8 to indicate AIS’s superior performance in large capacity. To highlight very large capacity, we didn’t show results of N=6,7. On DIV2K dataset, hiding 6 secret images, cover-stego achieves (33.822, 0.869, 0.430) of (PSNR, SSIM, LPIPS), and secret-reveal achieves (26.030, 0.737, 2.690). When hiding 7 secret images, results are (33.733, 0.864, 0.332) and (25.751, 0.728, 2.447). Following your suggestion, the complete results will be added to the paper. Q3: The RPM module in IHN uses a residual structure for redundancy prediction. How does this compare to alternative prediction architectures, such as transformers? Ablation studies on RPM’s design would strengthen the claims. A3: RPM is employed to learn an auxiliary variable with consistent distribution to redundancy, which improves reversibility. Many traditional models of extracting features can achieve this. Residual structure has fewer parameters and can extract deeper features. Following your suggestion, we conduct experiments on structures of UNet, Vision Transformer(ViT), Convolutional Block Attention Module(CBAM) and traditional Gaussian sampling strategy (https://s1.imagehub.cc/images/2025/03/27/3c23350577d0befe5b36a40be11b2a32.jpeg). Compared to UNet and ViT, residual blocks achieve a balance between quality and model size. Compared to CBAM, residual blocks reveal secret images of higher quality. The above content will be added to the paper. Q4: The invertible blocks (Eq. 4–7) share parameters between forward and backward passes. Does this limit flexibility compared to non-shared designs? A discussion of the trade-offs would clarify the design rationale. A4: For image steganography task, non-shared design will not improve flexibility. Hiding and revealing are a pair of reversible processes. In forward process, network receives cover and secret images, and outputs a stego image and redundancy. In backward process, stego image and auxiliary variable are input to get the revealed secret images. Through RPM, auxiliary variable has a consistent distribution with redundancy. In this case, shared parameters can ensure one-to-one correspondence between input and output, improving reversibility and quality. In contrast, non-shared design has disadvantages of (1) double number of parameters. (2) poor reconstruction quality due to accumulation of errors. (3) unstable training due to higher complexity. Q5: Some equations have formatting issues. A thorough review and correction are recommended. A5: We check the paper again and fix some formatting and grammar issues. (1) Wrong format of exp in Equation 5,6. (2) Wrong punctuation in Equation 12. (3) Wrong punctuation in Equation 24. (4) Word error “CIS” in caption of Table 2. Other grammar issues have also been solved. Q6: How does AIS handle real-world scenarios such as JPEG compression or noise perturbations? Testing under such conditions would better demonstrate the framework's practicality. A6: Robustness is another important task in the field of image steganography, aiming to reduce interference of real-world noise and compression. Experiments of such conditions are typically conducted under this task. AIS focuses on security and capacity, with a different target from robustness. Due to this target, AIS is sensitive to minor changes of keys to guarantee similarity of keys and locks. Sensitivity makes a trade-off between security and robustness. While the authentication mechanism is effective, it also makes AIS sensitive to disturbance. It is a good suggestion to consider robustness in large-capacity image steganography with authentication. In future work, we suggest adding an enhancement module to resist compression, and a noise-guided module to reduce disturbance of noises. An attention block may be added to catch slight changes for security. The above contents will be added in new version of the paper.	Summary: This paper makes a substantial contribution to secure multi-recipient image steganography by addressing the critical yet under explored challenge of authentication. The proposed AIS framework elegantly integrates authentication through a novel two-stage architecture—IAN for lock-key generation and distribution adaptation, and IHN for parallelized hiding—demonstrating rigorous theoretical grounding in normalizing flows. The authors provide compelling empirical evidence, including JS divergence analysis and PSNR/SSIM metrics across DIV2K datasets, to validate their claim that distribution adaptation mitigates spatial conflicts between authentication locks and secret images. Particularly noteworthy is the method’s ability to reduce model parameters, which addresses a longstanding efficiency-quality trade-off in high-capacity steganography. The discussion of dynamic lock-key generation’s resistance to brute-force attacks adds practical security insights. This research may set a promising foundation for authentication-aware steganography, but still with some minor clarifications. Claims And Evidence: It is clear and convincing. Methods And Evaluation Criteria: Yes. Theoretical Claims: Correct. Experimental Designs Or Analyses: Yes, they are reasonable. Supplementary Material: Yes. Relation To Broader Scientific Literature: This paper provides a promising approach for independence recovery for multiple image steganography. Essential References Not Discussed: The references are enough. Other Strengths And Weaknesses: Please see the questions. Other Comments Or Suggestions: Please see the questions. Questions For Authors: 1. Could the authors clarify whether the dynamic lock-key generation strategy considers potential adversarial attacks on key generation? 2. The JS divergence analysis in Figure 2 is insightful. Would including KL divergence metrics further strengthen the distribution comparison? 3. In Section 3.1, the mathematical formulation of authentication feasibility could benefit from expanded derivations for reproducibility. 4. Could runtime metrics (e.g., inference speed) be added to assess practical efficiency? Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: Thank you very much for your valuable comments. We hope that the explanations on the questions can help you better understand our proposed method. Q1: Could the authors clarify whether the dynamic lock-key generation strategy considers potential adversarial attacks on key generation? A1: The security of locks and keys is ensured through several special designs. (1) Dynamic generated rather than static. In AIS, we generate different pairs of locks and keys for each secret image with a trainable Dynamic Generation Module. These pairs are generated through feature fusion between cover images and corresponding secret images. Unlike traditional static key, our method ensures specific locks and keys for each recipient, thereby mitigating adversarial attack risks through reduced key exposure predictability. (2) Generated by trainable networks rather than specific cryptographic patterns. Traditional cryptographic methods rely on a predefined pattern, which is easy to be attacked by cryptanalysis techniques. In AIS, we train a lightweight network with linear and nonlinear transformations. This approach establishes security dependence on network parameter confidentiality, which is hard to crack. (3) Two stage revealing. In the revealing process, the recipient should first reveal primary information with IHN. Then a key is generated for authentication and reconstructing the original secret images from the primary information. This indicates that attackers should obtain both the primary information and the key to fetch the secret images. Since IHN is a more complex Invertible Neural Network, it can be very hard for effective adversarial attacks. Q2: The JS divergence analysis in Figure 2 is insightful. Would including KL divergence metrics further strengthen the distribution comparison? A2: In Figure 2, we calculate JS divergence to indicate the distribution differences between cover and stego images of authentication-based and authentication-free methods. JS divergence is calculated by $JS(p,q)=1/2* KL(p,q)+1/2*KL(q,p)$, which includes KL divergence and is capable of indicating the distribution differences. According to your suggestion, we also calculate KL divergence. For authentication-free method, the value is 0.0444. For authentication-based method, the value is 0.0697. Since higher KL divergence indicates greater inconsistency between the two kinds of distribution, the result implies that stego images generated in authentication-based method may contain more information with inconsistent distribution, resulting in low quality. This is consistent with our discovery in the paper. Q3: In Section 3.1, the mathematical formulation of authentication feasibility could benefit from expanded derivations for reproducibility. A3: The expanded derivations are in Appendix A. We have provided necessary derivation processes and explanations. In the proof, $x$ denotes data domain of secret images. $z$ denotes latent domain after the secret images transformed by an invertible network flow, denoted as $f$. $p(x)$, $\hat{p}(x)$, $p(z)$ denote the distribution of secret images, revealed secret images and latent information, respectively. $c$ and $c’$ denotes lock and key, respectively. Our goal is to prove that when the distribution of $c$ and $c’$ are consistent, $\hat{p}(x)$ is consistent to $p(x)$. When $c$ and $c’$ are inconsistent, $\hat{p}(x)$ has to be away from $p(x)$. This ensures revealing of meaningless information when the key is wrong. Equation 1 is a general form of the change-of-variable formula. This indicates the calculation of $\hat{p}(x)$ through $p(z)$. $det(·)$ denotes the Jacobian determinant. Equation 2 is the log likelihood loss derived from Maximum Likelihood Estimation (MLE). We give the detailed derivation in Appendix A.1. Equation 3 is an extended form of Equation 1, adding the lock and key. It can be simply inferred from the conditional distribution. Based on Equation 3, we prove that $\hat{p}(x)=p(x)\cdot e^{β(z, c)-β(z, c’)}$ by expanding the Jacobian determinant, where $\beta$ is a trainable network. The derivation process is detailed in Appendix A.2. This means that the network can be trained to make $\hat{p}(x)$ away from $p(x)$ when $c$ and $c’$ are inconsistent, which is in line with our goal. Q4: Could runtime metrics (e.g., inference speed) be added to assess practical efficiency? A4: We have compared the inference time in the original paper, which is shown in Table 1, Column Time. From the result, AIS spends shorter inference time compared to traditional serial hiding methods. Especially when hiding 5 images, AIS only requires 121.1ms, shorter than DeepMIH(269.1ms) and IIS(439.6ms). Though ISN achieves inference time of 51.7ms, the hiding quality(30.522) and revealing quality(29.077) are lower than AIS(32.767 and 30.060). The results indicate that AIS achieves a better balance between quality and inference speed.	null	null	null	null	null	null
LLMs can see and hear without any training	Accept (poster)	Summary: The paper introduces Multimodal Iterative LLM Solver (MILS), a novel framework designed to provide multimodal capabilities, such as image, video, and audio captioning, without the need for task-specific training. The central innovation of MILS is its iterative optimization strategy, leveraging the inherent reasoning skills of LLMs. It operates by repeatedly using an LLM as a GENERATOR that proposes candidate solutions, which are then assessed by a SCORER, typically a pretrained multimodal model. The scored feedback informs subsequent generations in a loop until convergence. Key contributions include achieving emergent zero-shot generalization across different modalities, performing competitively with specialized models. MILS simplifies those multimodalities tasks through a straightforward approach.. Claims And Evidence: Overall, the paper presents strong experimental evidence supporting many of its claims. However, some claims, particularly those regarding Cross-Modal Arithmetic and Generalization Ability, require further clarification and justification. 1. The paper claims that MILS allows arithmetic across modalities by converting them into text representations, combining them, and mapping them back. However, the authors do not clearly explain what these text representations are. Are they simply raw text formats? If so, what differentiates MILS from a pipeline consisting of a captioning model followed by a generation model? Without a clear distinction, the novelty and effectiveness of MILS in cross-modal arithmetic remain unclear. 2. The paper claims that MILS is conceptually simple and generalizable to many tasks. While the framework itself is modular, its success is heavily dependent on the choice of the GENERATOR and SCORER models. The effectiveness of MILS may vary significantly depending on the underlying models used, making it less generalizable than implied. Methods And Evaluation Criteria: 1. The paper uses score similarity to determine convergence, assuming that a stable score indicates an optimal solution. However, this approach may be insufficient and potentially misleading. A lack of score change does not necessarily imply the best possible result, it could indicate stagnation in a local minimum rather than true convergence. 2. The paper primarily evaluates image generation and image editing using PickScore and human preferences, but these alone do not fully assess generation quality. Metrics like FID could offer quantitative insights into visual realism and text alignment, while diversity metrics would help assess mode collapse. Theoretical Claims: No theoretical claims in the paper. Experimental Designs Or Analyses: 1. The paper determines convergence by monitoring score similarity over iterations. However, this method assumes that a stable score directly correlates with optimal performance, which may not be valid. 2. It lacks established quantitative measures such as FID, or other diversity metrics, which would provide a more comprehensive analysis of generation quality and text-image alignment. 3. The effectiveness of MILS depends on the GENERATOR and SCORER models, but the paper does not provide enough ablation studies to analyze the contribution of different components. For example, it is unclear how different LLMs as GENERATOR impact the results. Supplementary Material: Yes, I reviewed both text and video. Relation To Broader Scientific Literature: The paper extends test-time reasoning in LLMs by applying iterative refinement beyond text tasks. In zero-shot multimodal learning, prior captioning methods rely on gradient-based optimization, whereas MILS achieves zero-shot generalization purely at inference by combining LLMs with multimodal scoring models. The paper also contributes to multimodal representation learning, similar to ImageBind, by inverting multimodal embeddings into text, enabling cross-modal arithmetic and generation. Essential References Not Discussed: References are essential. Other Strengths And Weaknesses: The paper presents a straightforward approach, but its novelty is limited. The proposed method essentially combines an LLM with a pre-trained multimodal model in an iterative optimization loop, which does not fundamentally differ from existing approaches that use LLMs and multimodal models together. While MILS formalizes this process as a simple framework, it lacks a clear distinction from standard prompting techniques or direct zero-shot inference using existing multi-models. Other Comments Or Suggestions: The paper is well-written and organized, making it easy to follow the methodology and experimental setup. Questions For Authors: The paper presents MILS as a zero-shot multimodal optimization framework, but it appears to function similarly to direct LLM prompting with a multimodal model as a filter. What distinguishes MILS from simply iterating over LLM-generated candidates and selecting the best one using a scoring model? A clearer articulation of its novelty is expected. Code Of Conduct: Affirmed. Overall Recommendation: 2	Rebuttal 1: Rebuttal: We thank the reviewer for your insightful review and helpful comments. We address all concerns below: ## Clarification of the text representation in cross modal arithmetic The representation is indeed the raw text. The novelty is in the inversion of the image into the caption itself. Using a captioning model would require training it on image-caption data. MILS can invert multimodal embedding spaces like CLIP into text without needing any captioning training and is completely gradient free, allowing for the inversion to discrete text as opposed to a continuous embedding space. Combining that with generation, it is able to perform cross-modal arithmetic, similar to ImageBind (Girdhar et al. 2023). However, by using text-space instead of the image embeddings in ImageBind, MILS is a lot more flexible–making it work with various image generation models, allows for user control etc (as we mention in L384 left). ## Generalizability of MILS While MILS’ performance does depend on the choice of LLM/scorer, it works well with a wide range of LLMs and scorers. Please see Fig. 16 and Tab 4 in appendix – while better scorer/generator give better results, MILS works reasonably well across all the combinations of LLMs (eg Llama, Mistral, Gemma) and scorers (CLIP, SigLIP, DFN), showing its generalizability. ## Convergence to the global maximum Great point! To avoid local maximas, we tried an experiment similar to noise injection in gradients from ML optimization. As we mention in L134 (right column), we chose a portion of the candidates in an optimization step randomly, without considering their score. The idea is that, if a caption has a low score in the current round, a variant of it can still have a better score at a later round, effectively escaping the local maxima. However in practice, we did not notice a significant improvement. Regardless, MILS’ overall use of a stable score is similar to other applications of optimization in ML (e.g. neural network training) -- it could lead to a local optima but still be useful. As we show, MILS’ optimization leads to many useful applications. We will add more details and a discussion on this point in the appendix. ## Using FID as a metric In the image generation experiments, our goal is to generate images preferred by humans. Thus, human evaluation is the best fit for our setup. FID, on the other hand, has been shown to not be a reliable measure for human preference, as discussed in relevant papers ([Jayasumana et al. 2024 ‘Rethinking FIDs…’](https://arxiv.org/abs/2401.09603), [Parma et al. 2022, ‘On…GAN evaluation’](https://arxiv.org/abs/2104.11222), [Chong et al. 2020, ‘...unbiased FID…’](https://arxiv.org/pdf/1911.07023), [Borji et al. 2018, ‘Pros and Cons…’](https://arxiv.org/abs/1802.03446)). Large-scale image/video generation efforts (eg [SDXL](https://arxiv.org/abs/2307.01952), [Emu Video](https://arxiv.org/abs/2311.10709), [MovieGen](https://arxiv.org/abs/2410.13720), etc) have found automatic metrics like FID do not correlate well with human judgment, and also primarily focus on human evaluation. SDXL mentions “we find these classical quantitative scores not to be suitable for evaluating the performance of foundational (text-to-image) DMs.” Consequently, we do not use FID as a metric in this work. ## It is unclear how different LLMs as GENERATOR impact the results….and other ablation studies We do provide experiments studying the effect of different kinds of LLMs and Scorers in Appendix Fig. 16 and Tab. 4, respectively. We also study performance over different sized LLMs and Scorers in Fig. 12 (main paper). The performance is proportional to the relative strength of the LLM being used. Please let us know what other ablation studies are missing and we will clarify and add those. ## It lacks a clear distinction from standard prompting techniques or direct zero-shot inference using existing multi-models. We would love to get more details on specific models that the reviewer is comparing novelty to, and will be happy to compare to that. In general, multimodal vision-language models models are not emergent zero-shot (as our approach is), since they are trained for tasks like captioning. Hence, they generalize ‘zero-shot’ to a different data distribution. Our approach, on the other hand, generalizes to the completely new task of captioning itself – and captions images without ever being trained for it. We mention this in L071 left. ## How is it different from choosing the best generation using a scorer? This is exactly the first step of our optimization process, and the performance remains low without iterative refinement using the generator and the scorer (Fig. 9, 0th step). In short, our method consists of creating an initial set, followed by using the scorer to find top-K candidates, and iteratively feeding it back to the generator to create more candidates based on the score. This process is described in Sec. 3.	Summary: This paper introduces MILS (Multimodal Iterative LLM Solver), which enables large language models (LLMs) to perform various multimodal tasks without any additional training. Through test-time optimization, it incrementally improves its outputs by leveraging two key modules (GENERATOR and the SCORER), by generating a set of outputs and feedback with scores to iteratively refine the outputs. Experimental studies show that MILS can handle image, video, and audio captioning as well as generative tasks such as text-to-image creation and style transfer, all without requiring task-specific pretraining. Claims And Evidence: The paper claims that MILS (Multimodal Iterative LLM Solver) demonstrates emergent zero-shot multimodal capabilities through an iterative optimization framework leveraging pre-trained LLMs and CLIP-based multimodal scorers. However, I feel it is inadequately supported by the presented evidence. To convincingly establish this emergent reasoning capability, the authors must explicitly analyze and experimentally distinguish the incremental performance benefits provided specifically by iterative reasoning via LLM-generated candidates compared to existing methods that already effectively leverage pre-trained multimodal embedding representations. - First, the paper does not clearly distinguish how much iterative reasoning via the LLM contributes to the observed zero-shot performance beyond what has already been demonstrated by existing memory-based methods such as MeaCap. Recent works like MeaCap have already shown strong zero-shot multimodal capabilities by directly leveraging pre-trained multimodal embeddings (e.g., CLIP, SigLIP, ImageBind). Given this prior work, it is essential for MILS to provide explicit evidence demonstrating that iterative candidate generation through LLM reasoning meaningfully enhances performance beyond what pre-trained multimodal embeddings alone achieve. However, the authors do not provide a clear comparison of the additional benefits specifically attributable to iterative optimization via LLM-generated candidates. - Additionally, in the presented experimental results (e.g., Table 1), MILS does not achieve clear superiority over memory-based approaches such as MeaCap, particularly regarding critical evaluation metrics like CIDEr and BLEU. For instance, MILS attains a CIDEr score of 33.3, which is substantially lower than MeaCap’s 42.5 (and 51.7 when using high-quality SS1M memory). Higher scores (42.1 and 50.6) of DeCap (which is only cited) are also missing. While the paper selectively emphasizes metrics such as METEOR and SPICE, even in these semantic metrics, MILS either achieves performance similar to or only marginally better than MeaCap. Methods And Evaluation Criteria: The methodological approach of MILS is based on iterative optimization. It leverages a process in which a large language model (LLM) generates multiple candidates and a SCORER provides repeated evaluations to address multimodal tasks. However, the iterative optimization employed by MILS is fundamentally restricted by the candidate generation capacity of the LLM. - During each iteration, MILS generates tens to hundreds of candidates. This process implies that the ultimate quality of the captions is inherently capped by the LLM’s linguistic generation capabilities. In contrast, the memory-based approach adopted by MeaCap capitalizes on a vast external corpus that stores extensive world knowledge, which can be retrieved and filtered during caption generation. - Consequently, an increase in both the size and quality of the memory can directly and substantially enhance caption performance. For example, according to MeaCap, when employing a large-scale, high-quality memory such as SS1M, the CIDEr score can rise to 42.5. By comparison, MILS, even when limited to around 10 iterations, converges at a CIDEr score of 33.3, demonstrating significantly lower performance relative to SS1M. - This discrepancy shows a fundamental drawback: the iterative candidate approach in MILS appears to have intrinsic performance ceilings that cannot be overcome merely by increasing the number of iterations or candidates. However, the authors do not sufficiently discuss or analyze this limitation. Theoretical Claims: N/A Experimental Designs Or Analyses: I have several concerns about the experimental design and analyses. 1. Inadequate Comparison with MeaCap - The paper’s experimental comparisons with MeaCap are insufficient. MeaCap employs a memory retrieval-based approach, which offers fundamentally different scaling properties and cost structures compared to the iterative methodology of MILS. While MeaCap’s performance can significantly improve with larger and higher-quality memories (as evidenced by the high CIDEr score using SS1M), MILS is constrained by the inherent limitations of LLM’s candidate generation. Even increasing the number of iterations or candidates does not seem to surpass these fundamental limitations. This disparity between the two approaches is not adequately addressed or discussed in the experimental design. 2. Lack of Analysis on Error Accumulation - The authors do not provide an analysis of error accumulation—a critical issue in iterative methods. With each iteration, there exists a risk that erroneous candidates may be generated and, through the feedback process, inadvertently reinforced. Such errors can be caused by either Generator or Scorer, and can be worse during iteration adversarial to CLIP scores. 3. Missing Computational Efficiency Evaluation - Given that MILS necessitates repeated calls to an LLM, I have concerns regarding inference time and computational cost. However, the paper does not present any rigorous evaluation or discussion on computational efficiency. Due to the fundamental limitation of LLM capability, I suspect MILS has to scale up LLM to achieve fine-quality outputs. I also found the video provided in the supplementary material provided by Llama 405B model. - When we consider MILS requires around 10 (or more) steps for optimization, it seems too expensive compared to the existing memory-style training-free approaches. Supplementary Material: I checked appendix and video made by LLaMA 405B model. Relation To Broader Scientific Literature: The key contributions of this paper align closely with recent works exploring training-free and zero-shot multimodal approaches such as MeaCap and DeDap, specifically those relying on pre-trained large multimodal embedding models and LLMs. - For example, although MILS does not employ external memory directly, MeaCap similarly avoids task-specific training and relies heavily on pre-trained multimodal embedding models (e.g., CLIP) for evaluation. The key difference lies in MILS’s iterative candidate generation approach, where it repeatedly generates and scores multiple candidate captions, refining them iteratively. In contrast, MeaCap utilizes a single-step retrieval-and-generation pipeline, relying solely on high-quality external memory to enhance caption quality. So, I think MILS's K-candidates play a similar role in MeaCap's memory. It can be useful when we even do not have any external texts to build such memory, but I think high-quality memory can perform much better than the proposed method. Essential References Not Discussed: The paper explicitly cites DeCap (ICLR, 2023) in its references but omits DeCap from main experimental comparisons (such as Table 1). - Reported numbers of DeCap correspond to Table 1 are 42.1 and 50.6 CIDEr, which are significantly higher than 33.3 of MILS. Including DeCap in experimental comparisons is essential for clearly validating the effectiveness of MILS’s iterative candidate optimization. Other Strengths And Weaknesses: Strengths - This paper clearly reveals the performance capabilities and limitations of pre-trained LLM-based training-free methods across various multimodal tasks. By evaluating emergent zero-shot capabilities in multimodal tasks such as video captioning and image generation, MILS provides strong baseline performance achievable purely through iterative optimization of LLM-generated candidates and multimodal embeddings. Weakness - MILS inherently requires extremely large-scale pre-trained LLMs to achieve competitive performance. As explicitly shown in the supplemental experiments on video captioning tasks, MILS utilizes exceptionally large-scale LLMs such as LLaMA 400B. Such huge model sizes impose considerable computational costs and resource constraints, severely limiting practical feasibility and scalability. Specifically, the iterative optimization approach of MILS inherently restricts meaningful performance gains to the expensive strategy of continually scaling up the size of the underlying LLM. In contrast, memory-based approaches (e.g., MeaCap) inherently offer a much more scalable and cost-effective means of improving performance by simply increasing the size and quality of external memory. Given these considerations, while MILS can indeed serve as a useful baseline reference for multimodal tasks beyond standard captioning benchmarks, it appears clear that, in practice, memory-based methods would offer a far more effective solution due to their superior scalability and cost-efficiency. Other Comments Or Suggestions: see the above sections. Questions For Authors: see the above sections. Code Of Conduct: Affirmed. Overall Recommendation: 2	Rebuttal 1: Rebuttal: We thank the reviewer for their detailed feedback. We address all concerns below. In particular, we highlight the benefits of our iterative approach vs MeaCap, which is designed specifically for image captioning. We also clarify a possible misunderstanding regarding the use of large 405B LLM–except the qualitative examples shown for cross-modal arithmetic, all other results/examples in the main paper+supplementary use Llama 8B. ## Benefits compared to MeaCap/DeCap a) Iterative optimization generalizes to more tasks MeaCap/DeCap are specific to image captioning. They leverage a corpus of image captions from real-world datasets (e.g. CC3M). In contrast, MILS’ initial set does not contain captions from any dataset. Consider the task of captioning fantastical images from an image generation model. Retrieval based methods like MeaCap/DeCap would struggle since the CC3M captions will be very out-of-distribution and need significant modifications. To illustrate this, we ran both on [this image](https://www.freepik.com/free-ai-image/spaceman-riding-horse-outer-space_222195825.htm), and got the following outputs: ``` MeaCap: The image depicts that space in a vibrant poster using raster or digital images, film and graphics software. MILS: Cosmic artwork featuring a space explorer's dreamy, ethereal, surreal, otherworldly journey. ``` Clearly, MILS captures the essence of the image much better than MeaCap. We will add more such comparisons to the final paper. b) MILS avoids hand-crafted design and embraces end-to-end optimization MeaCap relies on a hand-designed subject-predicate-object based refinement, followed by iterative CBART sentence generation. MILS does not enforce any such constraints, and end-to-end optimizes the LLM generations, directly using feedback from the pre-trained multimodal embedding model. In this sense it can be thought of as a simplification and generalization of MeaCap, making it applicable to five more tasks than just image captioning. c) Experimental comparison with MeaCap and Decap (Tab. 1) We report comparison with training-free versions of all methods: 42.1 and 50.6 CIDEr in DeCap require training the LM on captions from image/video-captioning datasets. In contrast, MILS is completely training-free (TF). Moreover, MILS’ 33.3 CIDEr, outperforms MeaCap results that we could reproduce from the published code, which is 26.0 for MeaCap-TF (vs 42.0 reported in the paper)–we confirmed with the authors this variance was expected for the TF version. ## “Quality of the captions is inherently capped by the LLM’s linguistic generation capabilities” LLMs have very strong linguistic generation capabilities, as evident from their ability to generate stories, rhymes, etc; even conversing with humans such that many consider it to [have passed the turing test](https://www.nature.com/articles/d41586-023-02361-7). The external corpus in MeaCap–CC3M–contains 3M captions, which one could argue is much smaller than the linguistic ability and world knowledge stored in the LLM, if measured by their training data or parameters. In fact, using CC3M gives MeaCap an advantage over MILS since it leverages captioning-specific knowledge, while MILS relies only on a general-purpose LLM. ## MeaCap improves performance by increasing memory, “MILS appears to have intrinsic performance ceilings” MILS scales well too! We obtain clear improvements using LLMs/Scorers that are bigger (Fig 12), better (Appendix Fig 16, Tab 4), or using a larger initial set (Fig 10), with no ceilings observed thus far. ## Error accumulation analysis MILS performs iterative refinement, i.e. optimization, as opposed to iterative generation—the error will reduce over iterations as shown in our results over optimization steps (Fig. 9 and Fig. 8, 11). Errors would accumulate if we were fixing some part of our output at a given iteration and generating the remainder based on that—we are globally improving the output until it converges. ## Computational efficiency/“seems too expensive with 10 steps for optimization” The inference time is proportional to the number of iterations. The model performs well even with few iterations–please refer to the performance curves in Fig. 9, which shows even in 3 steps the performance is within 90% of the best. The iteration knob further allows MILS to trade-off quality vs speed, for time-sensitive applications. We expect the speed to improve and number of steps required to reduce as LLMs become more efficient and powerful. ## “Use of extremely large pretrained LLMs such as Llama 405B” This is a possible misunderstanding. We only use 8B LLM models for all experiments except multi-modal arithmetic (Fig. 7). All captioning tasks use 8B LLM. In fact, we only used 405B for multi-modal arithmetic since we could easily use API calls for the qualitative results; using the 8B variant also yields similar results. We will update the paper with 8B for arithmetic for consistency. --- Rebuttal Comment 1.1: Comment: Thank you for your rebuttal. However, it does not fully address my concerns, particularly regarding the empirical evidence and specific comparisons requested earlier; the scalability and efficiency of the proposed method in comparison to existing memory-based approaches such as MeaCap. For example, the current CIDEr score of MILS (33.3) is substantially lower than MeaCap's reported scores (42.5, and up to 51.7 with SS1M), highlighting a clear performance gap. While memory-based methods have the advantage of easily scaling by increasing memory quality, MILS heavily relies on scaling up the size of the LLM to enhance performance, raising concerns about computational efficiency and scalability. Additional quantitative evidence or analyses demonstrating how effectively MILS can scale in practice to match or surpass memory-based approaches within reasonable computational constraints would be beneficial to readers. --- Reply to Comment 1.1.1: Comment: Dear reviewer XRE1, Thank you so much for your response 1) We would like to reiterate, MeaCap obtains 26.0 CIDEr when we run inference with MeaCap’s released code, which is lower than MILS’ 33.3 CIDEr. We confirmed with the MeaCap authors on a public forum that such variance is expected. We are unable to share a link to that forum discussion to preserve anonymity, but will add it to the final paper. We recap the performance of MILS compared to MeaCap in the following table. \| Method \| BLEU₄ \| CIDEr \| METEOR \| SPICE \| \|-------------------------------\|:-----:\|:-----:\|:------:\|:-----:\| \| MeaCapᴛꜰ (Zeng et al., 2024) (reproduced) \| 4.5 \| 26.0 \| 14.1 \| 9.4 \| \| MILS* \| 8.0 \| 33.3 \| 15.0 \| 9.6 \| Additionally, please consider the qualitative results of MILS compared to MeaCap, as shown above in the rebuttal for a fantastical image, and in the Paper (Fig. 3). Automatic metrics like CIDEr only provide limited signal when evaluating generative models (as also observed with FID and FVD for image and video generation, please see our response to Reviewer Deut for a discussion). Qualitatively, we observed a clear improvement with MILS compared to MeaCap and other prior work. 2) On scaling, again reiterating from the rebuttal, MILS is highly scalable. As shown in the paper Fig. 10, MILS’ performance improves significantly with the initial set size. The initial set can be thought of as similar to MeaCap’s memory, hence showing a similar scaling behavior as in MeaCap. In addition, MILS shows promising scaling performance with multiple other axes, such as LLM size (Fig. 12), scorer size (Fig. 12), LLM type (Fig. 16), and scorer type (Tab. 4), arguably making it a lot more scalable than MeaCap. Please let us know if either of these aspects are unclear, and we’d be happy to clarify further. Thank you again, Authors	Summary: The authors propose MILS: Multimodal Iterative LLM Solver, a simple method that claims to use the reasoning abilities of textual LLMs to have impressive zero-shot performance on multimodal tasks. At a high level, this involves a Generator model, which is either a text-LLM or a text-LLM chained to another system such as an image generation model and a Scorer, which evaluates the quality of the generations. By optimizing the generator to produce outputs that are preferred by the scorer, it is found that the method is competive against purpose-built models for image, video and audio captioning, and also improves generative capabilities for text-to-image generation. The authors also discuss cross-modal arithmetic where they are able to combine different modalities using MILS Claims And Evidence: The authors claim that their method is extremely generalizable and only requires a generator and scorer, which can be basically any system that generates output for a task and one that can evaluate them. This is well-justified by examples of image/audio/video captioningn and generative tasks such as image generation and style transfer. Methods And Evaluation Criteria: The authors compare to appropriate models using standard metrics on standard benchmark datasets. Theoretical Claims: The paper does not make any theoretical claims of note Experimental Designs Or Analyses: The experiments are set up in an appropriate manner, with detailed explanation of bootstrapping, set up and output generation provided across a variety of tasks. The experiments are mainly just examples of the method working well, rather than trying to question and/or investigate the method itself, though. Supplementary Material: I reviewed the supplementary material and found clarifying information around prompt construction and a well-constructed demo. Relation To Broader Scientific Literature: The fundamentally plu-gan-play nature of this method implies that it is both deeply embedded in the general generative deep learning literature while also standing somewhat apart from it by being a gradient-free method that is plug and play. Essential References Not Discussed: I did not find any major references missing Other Strengths And Weaknesses: Strengths: 1. The method is simple, plug-and-play and effective, showing improved performance of the method on a variety of tasks. 2. The method also generalizes across different textual LLMs, and scales to their intelligence/reasoning abilities. Weaknesses: 1. There is little, if any, deep investigation into the reasoning capabilities of the LLM that cause this to work. I would like to see a more detailed deep dive into the optimization process and it's potential brittleness when coming up against harder tasks. 2. I am not sure if this is necessarily novel and therefore appropriate for ICML. The novelty is very much at the system-level and the idea of a scorer giving feedback to a generator, while applied well, is not new to the ML literature in general. Other Comments Or Suggestions: None Questions For Authors: I do not have any major questions for the authors. This is a well-written paper and shows a practical method that enables us to make existing systems better without expensive training runs. Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: We thank the reviewer for the insightful review and their willingness to accept our paper. We are glad they found our method generalizable, claims well justified, and improved performance on a variety of different tasks. We address all concerns next: ## Investigation into the reasoning capabilities of the LLM that cause this to work This is a great suggestion and we’ll attempt this for the final paper. Understanding the reasoning capabilities of LLMs is indeed a very fast evolving field of research, and many of the discoveries there would also help better understand MILS. For instance, deeper insights into MILS can be obtained by taking into account the reasoning traces available in recent LLMs such as DeepSeek-R1. Another interesting exploration could be in the LLM-scorer interface, for instance experimenting with the sensitivity of the LLM to the resolution of the scorer outputs. In general, LLMs as optimizers are relatively easier to probe compared to more opaque optimizers, given their ability to explain decisions in plain language. We believe this ability will help MILS expose new avenues for research both in LLM reasoning and multimodal understanding. ## Novelty statement compared to other ML literature Ours is the first work to leverage test-time reasoning capabilities of LLMs to solve multimodal tasks, obtaining state-of-the-art results across a wide range of computer vision/multimodal benchmarks: image, video and audio captioning, enhanced image generation (outperforming very strong models like FLUX), style transfer and cross-modal arithmetic. As reviewer 934y also notes on the novelty, this approach enables pure text-only LLMs to see and hear without needing any training on that kind of data. Our novelty also lies in the simplicity of our framework that does not need any task-specific modifications. We do take inspiration from standard ML literature where the concept of scoring functions and optimization is used extensively, however to our knowledge, it hasn’t been used in this way for test-time optimization, using LLMs, to solve multimodal tasks. If there is specific prior work the reviewer would like us to compare to, please let us know and we would be happy to provide more comparisons to that. --- Rebuttal Comment 1.1: Comment: Thank you for your comment, I appreciate the explanation, and will keep my score as 4/Accept.	Summary: This paper presents an iterative solver to enable pure language LLMs to "perceive" visual or audio signals through trial and error using discriminative scorers. Specifically, the authors construct a feedback loop between generators (LLMs) and discriminative ranker (e.g., SigLIP for image captions): first, the LLM first output initial random guess lists by prompting; next, the score ranks guess lists with regard to images/audio, and feed guess lists with scores back into the LLM; then, the LLM analyze the guess lists with scores and iteratively refine new guess lists into the "right" direction. The authors also generalize this framework to audio caption, image generation and style transfer tasks, and explore other cross-modal tasks with the help of ImageBind. Claims And Evidence: The claims, LLMs can see and hear without any training, can be supported by clear and convincing empirical evidence presented in this paper. Indeed, LLMs can see and hear by correctly prompting based on feedbacks in a loop style. We can say this paper presents a gradient-free optimization to the score by prompting candidates. Methods And Evaluation Criteria: This method present a novel approach to make pure LLMs to see and hear without any training on image/audio-language pair samples. That said, I have concerns whether proposed MILS have real application potentials compared to other multimodal LLMs. While loop methods between generators and scores being under-explored before, MILS performance seems relatively lagging behind common pipelines to multimodal understanding. I understand that authors' goal is not achieve new state-of-the-art performance, but the looping mechanism between generators and scores seem time-costing and highly inefficient. Indeed, I find MILS do have potentials in generating high-quality image generation/style transfer samples in Sec 4.4 and 4.5 to serve as post-training samples for further fine-tuning nowadays pipelines. Now back to my question, for multimodal understanding, what is the strength or potential of MILS rather than proposing yet another way to do it? Theoretical Claims: There are no theoretical claims nor proofs in this submission. Experimental Designs Or Analyses: Most experimental designs and analyses are sound and valid in my opinion. A minor concern is the absence of inference time analysis concerning the number of iterations and the initial set size, which is crucial for real-world applications. Supplementary Material: I did review the supplementary, which includes more visualization/audio samples and prompts used in MILS. Relation To Broader Scientific Literature: In my view, this paper presents a gradient-free optimization for scores by the scorer by prompting candidate sets. Essential References Not Discussed: I do not find any specific references missing in this submission. But it would make this paper more sound to discuss more gradient-free optimization. Other Strengths And Weaknesses: Overall I think this paper presents a "yet-another-approach" to leverage pure LLM to understanding multimodal signals without any training/fine-tuning on paired samples. This paper is indeed novel but with some minor concerns in real application potentials (See Methods And Evaluation Criteria). Other Comments Or Suggestions: NA Questions For Authors: Q.1. As mentioned in Experimental Designs Or Analyse, the authors might provide inference time analysis and its comparison with standard multimodal understanding pipelines. Q.2. I feel MLIS quite limited in "caption" tasks. Actually, it seems that the capability of MLIS as a gradient-free optimization is "bounded" by the scorer capability. In the paper case, the scorer, SigLIP, provide caption and visual similarity. My concern is, whether MLIS can solve other multimodal questions beyond captioning, like spatial referring? No experiments needed but I'd like to see authors' insights into it. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We thank the reviewer for their insightful review and willingness to accept the paper. We are glad you found our work novel, and claims supported by clear and convincing empirical evidence. We address all the remaining concerns below: ## For multimodal understanding, what is the strength or potential of MILS rather than proposing yet another way to do it? Great point! We agree -- one can train specific multimodal models for tasks that have enough training data that are hyper-optimized for that specific task. For online production use cases that require millisecond-level optimization, training a specific model for that task might indeed be the way to go. MILS, on the other hand, can supercharge research exploration or applications that may not require such a high level of runtime optimization. For example, MILS can quickly provide a strong multimodal model for a new task, without any training, completely zero-shot. This could be useful to researchers as an initial baseline for any new task they might want to solve. It could also serve as an easy and effective approach to interpret new models a researcher develops. Consider the use case of interpreting the strengths/weaknesses of a new multimodal embedding model and comparing it to CLIP/SigLIP etc. MILS can enable that interpretability by helping invert each model’s embedding space into text (without any training that might bias this inversion). The produced image captions for different embedding models could be very helpful for a researcher to better understand the behaviors of these models. Finally, MILS can be used as an offline data generator, which can then be used to train or distill optimized multimodal models. Consider for instance the enhanced image generation task – MILS can be used to generate large amounts of <text, improved image> pairs, which can be used to tune a text-to-image model for improved quality. ## Q1. Inference time analysis MILS’ inference time is proportional to the number of iterations. As shown in Fig. 9, MILS performs well even with a few iterations (eg 3), and the runtime will continue to decrease as more efficient and higher quality LLMs become available, that can reason in fewer steps. Moreover, the initial set size does not affect compute time much, as we can compute dot product similarity with the media features very fast on modern GPUs. We will add additional runtime analysis and comparisons with similarly sized task-specific multimodal understanding models in the final paper. ## Q2. Can MILS solve tasks like spatial referring? Certainly! We can generate box proposals and referring expressions (e.g. a class label or a short description) with the LLM, compute box-level CLIP similarity score by computing CLIP features on the cropped box, and use that as the score to give feedback to LLM. The LLM will then produce new box proposals and referring expressions. We can then repeat this iterative process as proposed in MILS. The scoring can further be made more efficient by pooling part of the full image’s spatial CLIP features that correspond to the box, and matching that to text. Overall, as long as we design a scorer for a task, which can evaluate the correctness of the LLM generation with respect to the input (can be any modality), we can integrate that task into MILS. It can be similarly extended to segmentation, object detection in 3D, etc. ## Discuss more gradient-free optimization papers That is a great suggestion! We will add more references and discussions to gradient-free optimization works to the final paper. --- Rebuttal Comment 1.1: Comment: Thank authors' rebuttal and appreciate the insights. I have no further questions and still feel positive about this paper. Therefore I'd keep my original rating as it is.	null	null	null	null	null	null
EvFocus: Learning to Reconstruct Sharp Images from Out-of-Focus Event Streams	Accept (poster)	Summary: This paper propose the EvFocus, the first framework designed to reconstruct sharp images from out-of-focus event streams, addressing the challenge of defocus blur, where existing event deblurring methods fail due to reduced spatial gradients and sparse event generation. The proposed approach integrates a temporal information encoder (ConvLSTM) to capture event stream dependencies, a dual-branch decoder that separately learns blur distribution and feature alignment, and a self-supervised refocusing module for optimizing blur estimation. The authors introduce a theoretical model linking defocus blur to event generation dynamics and develop a synthetic event simulator to generate realistic training data. Experiments on both synthetic and real-world datasets demonstrate EvFocus's superior performance over existing methods, achieving up to 20% higher SSIM and 50% lower MSE under severe blur conditions. Claims And Evidence: The paper proposes the EvFocus framework as an innovative solution for defocus deblurring in event cameras. However, some claims are not fully supported by sufficient evidence. Experimental results show that EvFocus significantly outperforms baseline models (E2VID, ET-Net) on synthetic data in quantitative metrics such as SSIM and MSE. Ablation studies further validate the necessity of the dual-branch decoder and re-defocus module, as removing them leads to a 15%-20% performance drop. However, the visual quality of the reconstructed images remains problematic. As shown in Figure 7, the reconstructed images exhibit artifacts, blurred edges, and texture loss, particularly at the edges of the checkerboard pattern, where fine details are not well restored. Although no-reference image quality metrics (Brisque/Niqe) indicate that EvFocus performs better than competing methods, the lack of sharpness and artifacts in real-world results may limit its practical applicability. Furthermore, the paper does not include experiments or validation on videos, which weakens the completeness of the experimental evaluation. Methods And Evaluation Criteria: 1. Simplistic Defocus Modeling The synthetic dataset uses fixed Gaussian kernels to approximate defocus blur, ignoring the nonlinear depth-PSF relationship (Equation 4). Real-world PSFs are often asymmetric and aberration-affected, creating a domain gap between simulation and reality. This undermines the model’s ability to generalize to multi-depth scenes (e.g., foreground-background defocus). 2. Unrealistic Dataset Design Blur kernel sizes are arbitrarily selected rather than tied to physical depth parameters (e.g., focal length, aperture). This decouples blur from its root cause (distance), failing to capture dynamic blur variations in moving scenes (e.g., objects approaching the camera). 3. Incomplete Evaluation Metrics Metrics like SSIM/MSE measure generic image quality but ignore depth-aware reconstruction accuracy. No validation of blur kernel estimation (e.g., PSF size vs. theoretical predictions) is provided, leaving the model’s physical consistency unproven. 4. Lack of 3D Scenario Testing Experiments focus on static/global defocus, neglecting dynamic depth changes (e.g., objects moving along the optical axis) and multi-layer defocus (e.g., mixed foreground/background blur). This casts doubt on real-world applicability. - Real-world validation is insufficient: The paper only visualizes results on a single checkerboard pattern (Fig. 7), which lacks complexity. No examples are shown for 3D scenes with layered depth (e.g., cluttered indoor environments, outdoor scenes with foreground/background separation), raising doubts about practical utility. Theoretical Claims: The paper’s theoretical justification for its dual-branch decoder and re-defocus module relies solely on quantitative metrics, failing to provide mechanistic evidence that these components learn physically meaningful defocus properties. For instance, there is no visualization of blur kernel estimation (e.g., PSF size variations across depth in 3D scenes) to confirm that the blur-aware branch captures depth-dependent defocus patterns. Without such analysis, it remains unclear whether the network truly models the distance-blur relationship (as implied by Equation 4) or merely exploits superficial correlations in synthetic data. A rigorous validation would require depth-aware feature maps (e.g., showing how PSF scales align with object distances) and controlled 3D experiments. Until then, the theoretical claims lack causal grounding. Experimental Designs Or Analyses: The experiments fail to establish a physically grounded link between defocus blur and 3D scene geometry. Synthetic data relies on fixed blur kernels (e.g., 3×3 to 11×11), arbitrarily assigned rather than derived from depth-dependent PSF modeling (Equation 4). This decouples blur from object distance, creating a non-physical training regime. Real-world evaluations exacerbate this issue—the checkerboard test lacks multi-depth layers or dynamic depth variations, leaving the model’s 3D-aware defocus handling unverified. Without depth maps or moving objects along the optical axis, the experimental validity remains in question. Supplementary Material: Codes are provided in the supplementary material, which is very appreciated. Relation To Broader Scientific Literature: None Essential References Not Discussed: The paper provides a clear background and related work discussion, but it overlooks prior event-based auto-focus methods, which are relevant to its scope. Several studies have explored event-driven autofocus mechanisms, yet they are not explicitly discussed here. If the authors were to acknowledge these works and clarify that their approach specifically targets scenarios where autofocus fails, it would strengthen the motivation and positioning of the paper within the broader literature. Other Strengths And Weaknesses: I highly appreciate the paper's focus on event-based defocus deblurring, which is a novel and valuable research direction for the event-based vision community. However, the primary weakness lies in the lack of realistic 3D scenes and evaluation, which limits its practical applicability. If the authors can address this gap, I would be very supportive of the paper being presented at ICML (maintaining its current weak accept score). Other Comments Or Suggestions: NONE Questions For Authors: NONE Code Of Conduct: Affirmed. Overall Recommendation: 2	Rebuttal 1: Rebuttal: We sincerely thank the reviewer for the detailed and thoughtful feedback, and we carefully address the raised concerns below. --- ### Realistic 3D scenes and evaluation Thank you for pointing this out. We have conducted additional experiments on realistic 3D scenes with varying depth levels. The qualitative results are shown in the updated figure (https://anonymous.4open.science/api/repo/Anonymous-6BB9/file/fig1.pdf?v=9bbf2ec6). The results demonstrate that our model effectively learns the relationship between event streams at different defocus levels and corresponding illumination intensities. It is capable of handling varying degrees of defocus blur across different depth planes in the scene. In addition, we conducted quantitative evaluations on these 3D scenes using standard no-reference image quality metrics: \| Model \| Brisque ↓ \| Niqe ↓ \| Noise Estimate ↓ \| Contrast ↑ \| Sharpness ↑ \| \|-------------\|----------------\|------------\|------------------------\|----------------\|-------------------\| \| E2VID+* \| 20.73 \| 4.26 \| 0.003874 \| 0.1539 \| 0.0008297 \| \| E2VID+ \| 25.50 \| 6.08 \| 0.004410 \| 0.1593 \| 0.0006359 \| \| ET-NET* \| 14.94 \| 6.72 \| 0.006690 \| 0.1550 \| 0.0022420 \| \| ET-NET \| 13.31 \| 4.85 \| 0.006499 \| 0.1541 \| 0.0020085 \| \| E2VID \| 17.07 \| 7.06 \| 0.006361 \| 0.0879 \| 0.0002424 \| \| Ours \| 13.21 \| 4.05 \| 0.003374 \| 0.2018 \| 0.0022520 \| These results indicate that our model consistently achieves better sharpness and contrast while reducing noise and preserving perceptual quality. We will incorporate these new results, the introduction of metrics, and the analysis in the revised version. --- ### Depth-aware feature maps & metrics We appreciate the reviewer’s suggestions. We agree that PSF-aware validation could provide deeper insight into the model's physical consistency. However, similar to most image-based deblurring networks, our model does not include an explicit PSF estimation module, which makes such direct evaluation difficult. Thus, to evaluate the model’s performance on multi-depth defocus removal, we performed feature visualizations on 3D scenes. In the updated figure (https://anonymous.4open.science/api/repo/Anonymous-6BB9/file/fig2.pdf?v=72d4d619), the result demonstrates that our model is able to distinguish between objects near and far from the focal plane, indicating that it learns depth-aware defocus representations implicitly through training. In the revised version, we will also report video-level metrics such as frame-wise stability and temporal flicker scores to better reflect temporal behavior. --- ### Visual quality and artifacts Thank you for pointing this out. We acknowledge that some visual artifacts remain, especially in challenging areas like edges or low-texture regions. However, this task is inherently difficult; the defocused event streams are sparse, noisy, and lack full spatial information, making accurate reconstruction very challenging. Despite this, our method achieves significantly better perceptual quality than existing baselines, as shown by multiple no-reference metrics in the tables. We will add more 3D scene results in the revised version. --- ### Model and Dataset Design Thank you for the comments. Our synthetic dataset is built on a physically-inspired defocus model that simulates event generation under varying PSF sizes and lighting conditions. By changing blur levels, motion speed, and intensity across sequences, we mimic different scene depths and real-world defocus effects. This design allows the model to learn both temporal accumulation and spatial defocus patterns, and to adapt to the link between blur size and event sparsity, making it effective for depth-varying defocus. We conducted experiments on multi-depth scenes and observed that E2VID pretrained on sharp data can handle slight defocus, suggesting that events exhibit robustness to slight defocus blur. Combined with our specially designed dataset, our model further learns depth-dependent defocus patterns and can distinguish and reconstruct objects at different depths, showing strong generalization to 3D scenarios. --- ### Related work Thank you for this suggestion. We will discuss relevant references (e.g., Lou et al., 2023; Lin et al., 2022; Teng et al., 2024) on event-driven autofocus and focal stack fusion. Our method differs in that it does not require active lens control or RGB images, and is designed for passive, single-shot defocused event streams, which we believe complements autofocus-based methods. --- Thank you again for your valuable feedback. If there are any additional questions, we would be happy to address them.	Summary: This paper introduce a new network architecture for restoring all-in-focus grayscale video from defocused event-camera measurements. The method assumes a thin lens model and gaussian defocus blur. It is tested on simulated and real data. The proposed method outperforms existing methods quantitatively and qualitatively, though not always by a large margin. Overall, this is a clearly written and technically sound paper that tackles an under-investigated real-world problem. Claims And Evidence: The method is tested on both simulated and captured event data. The method is tested against two widely used event-to-video restoration networks, which are fine-tuned with simulated defocused data. Adding an additional baseline where defocused video was restored with a conventional event-to-video architecture and then made all-in-focus with an image-to-image or video-to-video network may improve the paper. Methods And Evaluation Criteria: The methods and evaluation seem appropriate. A one to two sentence description of what the Brisque and Niqe metrics are computing would improve the paper. Theoretical Claims: The derivations seemed correct, though I did not check carefully. Experimental Designs Or Analyses: Experiments seemed appropriate. Supplementary Material: Code was provided. I didn't test it. Relation To Broader Scientific Literature: In general, the paper presents an accurate overview of the existing literature. To my knowledge, this exact problem has not been previously addressed. Essential References Not Discussed: Though the problems aren't identical, the following paper is related and should be discussed: Lou, Hanyue, et al. "All-in-focus imaging from event focal stack." Proceedings of the IEEE/CVF Conference on Computer Vision and Pattern Recognition. 2023. Other Strengths And Weaknesses: None noted Other Comments Or Suggestions: None Questions For Authors: How do the runtimes of the various methods compare? Can the method be extended to handle events generated by a changing focal plane? Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: We sincerely thank the reviewer for the encouraging feedback and constructive suggestions. We address the main points below. --- ### Additional baseline: event-to-video + image/video deblurring We appreciate this valuable suggestion. In the supplementary material (Fig. 11–12), we included an experiment that follows a similar two-stage baseline: we first reconstruct intensity images from defocused events, followed by applying NRKNet [CVPR'23] as the SIDD network for defocus deblurring. However, the results were suboptimal, mainly due to the low quality of reconstructed images from sparse defocused events, which contain significant artifacts and structural degradation. These observations support our decision to address defocus directly in the event domain, which our method handles more effectively in terms of both reconstruction fidelity and robustness. We will add more discussion in the revised version. --- ### Clarification on Brisque and NIQE metrics Thank you for pointing this out. We will add the following clarifications in the final version: - BRISQUE (Blind/Referenceless Image Spatial Quality Evaluator) evaluates natural scene statistics in the spatial domain without requiring a reference image. - NIQE (Natural Image Quality Evaluator) computes quality based on deviations from learned statistical regularities of natural images. These no-reference metrics are particularly useful for assessing real-world reconstruction results where ground truth is unavailable. --- ### Discussion of related work: Lou et al. (CVPR 2023) Thank you for highlighting this relevant work. Lou et al. [CVPR'23] propose an all-in-focus imaging method based on both RGB images and event focal stacks, which relies on capturing event streams under different focal settings and performing temporal fusion. In contrast, our work focuses on single-shot defocused event streams, which: - Require no active focus control or RGB supervision; - Address the case where defocus has already occurred, aiming to restore sharp content purely from event data. We will incorporate a discussion of this difference and clarify the complementary nature of the two approaches in the final revision. --- ### Runtime comparison Thanks for your suggestion. We evaluated inference speed and model size under identical settings (input: `[1, 5, 264, 352]`, GPU: RTX 3090). The results are as follows: \| Model \| #Params (M) \| Inference Time (ms) \| \|---------------\|------------------\|--------------------------\| \| E2VID \| 10.71 \| 4.41 \| \| ET-NET \| 22.18 \| 25.71 \| \| SPADE-E2VID \| 11.46 \| 12.66 \| \| EvFocus \| 12.11 \| 24.09 \| Our method offers a balance between performance and complexity. While not the fastest, EvFocus yields consistently higher-quality reconstructions. --- ### Extension to changing focal planes Thanks for your advice. This is an excellent and challenging direction. Our current method assumes static defocus, but we believe it can be extended to handle dynamic focal planes by: - Incorporating temporal modulation or adaptive kernel modeling; - Simulating changing focal depth in training data; - Leveraging the temporal encoder to track evolving blur distributions. We consider this a promising line of future work and greatly appreciate the suggestion. --- Thank you again for your thoughtful review and support. We are happy to clarify further if any questions remain.	Summary: This paper proposes EvFocus, a novel architecture for reconstructing sharp images from defocused event streams. The key innovation lies in its temporal encoder, blur-aware dual-branch decoder, and re-defocus module, combined with a synthetic defocus event dataset for training. Experiments on synthetic and real-world datasets demonstrate superior performance over existing methods under varying blur sizes and lighting conditions. ## update after rebuttal The author's response has resolved my issues. Considering the other reviewers' comments, I have decided to increase the score. Claims And Evidence: yes Methods And Evaluation Criteria: yes Theoretical Claims: yes Experimental Designs Or Analyses: yes Supplementary Material: Yes. Mainly the code. Relation To Broader Scientific Literature: n/a Essential References Not Discussed: n/a Other Strengths And Weaknesses: Other Strengths: First systematic solution for event-based defocus deblurring. Main Weaknesses: Computational efficiency and real-time performance metrics are not reported, crucial for event camera applications. Other Comments Or Suggestions: n/a Questions For Authors: 1. Why isn't the real defocus ground truth (gt) used during refocusing? 2. What would be the performance if reconstruction is performed first, followed by applying state-of-the-art defocus algorithms in the image domain? 3. What is the significance of using an event camera for this task? Some work [1] suggest that the high-speed characteristics of event cameras enable rapid autofocus to avoid defocus issues. In what scenarios would this algorithm be necessary? [1] Lou, Hanyue, et al. "All-in-focus imaging from event focal stack." Proceedings of the IEEE/CVF Conference on Computer Vision and Pattern Recognition. 2023. Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: We thank the reviewer for their thoughtful comments and constructive suggestions. We address each of the raised points below. --- ### Computational Efficiency We agree that runtime performance is important for real-world deployment. In response, we have conducted a comprehensive runtime and parameter comparison (input size: `[1, 5, 264, 352]` on RTX 3090 GPU): \| Model \| #Params (M) \| Inference Time (ms) \| \|---------------\|------------------\|--------------------------\| \| E2VID \| 10.71 \| 4.41 \| \| ET-NET \| 22.18 \| 25.71 \| \| SPADE-E2VID \| 11.46 \| 12.66 \| \| EvFocus \| 12.11 \| 24.09 \| Our model achieves a good trade-off between accuracy and complexity. The inference time is similar to ET-NET; our method offers significantly improved image quality. --- ### Why isn't the real defocus ground truth (GT) used during refocusing? Thank you for this insightful question. Our model architecture includes a blur-aware dual-branch decoder, where the blur decoder passes through three CF modules and fuses with features from the align decoder. We employ a deblurring reconstruction module on the align path to enhance its output. To further leverage the design, we introduce a loss between the blur decoder output and the re-defocus module to encourage CF modules to extract meaningful blur representations. One of our intentions is to encourage effective feature interaction between the two branches. Specifically, the blur decoder extracts blur-aware event representations, which are used to guide and support the learning process of the align decoder. This interaction allows the align decoder to better capture defocus-related features from the event domain. In fact, there is a modality gap between events and RGB images: some low-texture regions or subtle motion details present in the GT image may not be well represented in event streams. In this context, directly supervising with defocus GT could potentially lead the optimization to overly favor one branch (e.g., the blur decoder), focusing more on image-domain appearance rather than learning the common defocus patterns reflected in the event stream. This may weaken the collaborative learning dynamics between the two branches. Our current design aims to balance the contributions of both branches and promote cooperative learning, and has proven effective in practice (validated through ablation studies in the paper). We appreciate the reviewer’s question, and we will include a more detailed explanation of this design choice in the revised version. --- ### What would be the performance if reconstruction is followed by defocus deblurring in the image domain? We performed experiments and reported results in our supplementary material (Fig. 11 and Fig. 12), where the NRKNet network was employed as SIDD network processing for defocus removal. The results of other methods + SIDD were suboptimal. This is because: - Defocused event streams are inherently sparse and contain degraded spatial gradients. - Reconstructed intensity images from such events exhibit heavy artifacts and blurred textures, limiting the effectiveness of downstream image-based deblurring algorithms. - Events capture log-intensity changes, not absolute intensity, and are affected by defocus noise, which severely impacts the quality of intermediate reconstructions. These findings suggest that directly addressing defocus in the event domain, as EvFocus does, is more robust and efficient. --- ### What is the significance of using an event camera for this task? Thank you for your suggestion. Compared to Lou et al. [1], their work leverages a focal sweep with event cameras to reconstruct an all-in-focus image using timestamp selection and focal stack merging. This method assumes a dynamic focus adjustment and high-quality RGB input. In contrast, our setting targets scenarios where only event streams are available, especially in high-speed or low-light scenes. Our approach reconstructs sharp images from single-pass, defocused event streams, making it suitable for settings without active focus control or RGB inputs like Lou et al. [1]. Hence, it complements Lou et al.’s method and serves different application domains. --- We thank the reviewer again for the helpful comments and the recognition of our work. We will incorporate the suggestions and clarifications in the revised version.	null	null	null	null	null	null	null	null
A Computationally Efficient Algorithm for Infinite-Horizon Average-Reward Linear MDPs	Accept (poster)	Summary: This paper tackles the open problem of proving a rate optimal regret bound in average reward infinite horizon linear mdp with a computationally efficient algorithm. The problem it is solved successfully, using a double loop structure inspired by hong et al. 2025 and a deviation controlled mechanism to make sure that the iterates produced by least square value iteration with different clipping thresholds could be bound by the difference of the clipping thresholds. ### After rebuttal My opinion remains positive. The assumption on bounded features and weights is clear now but I think it would be better if the authors make clear that finding features with the desired boundness properties requires computing a MVEE. Please make sure to add the comparison with the failed attempt in Hong et al. 2025v1. I think this is very important for the placement of the paper in the literature. Claims And Evidence: Claims are convincing Methods And Evaluation Criteria: Rigorous proofs. Theoretical Claims: I checked the correctness of all the theoretical statements. I found just a minor error at the end of page 15 in the equation at line 820 $m_{t+1}$ should be replaced with $m_t$, otherwise the authors could not conclude that the first ferm equals $V^t_u(s)$. Experimental Designs Or Analyses: see above Supplementary Material: No supplementary material available Relation To Broader Scientific Literature: Yes, related to the previous attempt towards solving this problem. This is quite well done but I have a request for the author. please find it below. To my knowledge, there was a previous attempt in the first version of the paper uploaded in arxiv that claimed to achieve the same results but without the double loop structure and therefore with a better time complexity. Unfortunately, the authors of Hong et al. 2025 claimed in their v2 that the previous result contains a mistake. I think that the mistake in Hong et al 2025 is in the maximum over the past Q functions, this algorithmic technique makes the covering number of the state value functions space to be exponential in $T$. This is indeed avoided by the current submission that replaces the maximum over past value functions with the double loop structure. In my opinion, it would be helpful for the community if in the current submission, you could add a paragraph explaining the differences with Hong et al. 2025 v1 and in particular explaining why the current approach fixes the issue with the previous approach. Essential References Not Discussed: None Other Strengths And Weaknesses: Well written paper Other Comments Or Suggestions: Make clear that Algorithm 1 and 2 need to know both $T$ and $H$, especially it seems very difficult to obtain an algorithm that works without knowing the value of $T$ in advance given the double loop structure. The author should make this limitation clearer. Questions For Authors: How does the Bellman optimality equation in Assumption A relates to structural assumptions often imposed in Average Reward infinite horizon problems such as Communicating/Weakly Communicating MDPs ? I think this should be discussed better in the manuscript before stating Assumption A. Why in Assumption B is reasonable to assume that the reward weights are bounded by $\sqrt{d}$. I think that in case of very badly conditioned features the reward weights might need to be larger than $\sqrt{d}$ to realize the reward function. Let imagine to have two features $[0,1]$ and $[\epsilon, 1-\epsilon]$, now to write the reward function $r=[1,0]$ the weight norm should be as large as $1/\epsilon$. However, $\epsilon$ can be made arbitrary small so the quantity $1/\epsilon$ can become arbitrary larger that $\sqrt{2}$. Moreover, the authors say that these assumptions are without loss of generality and refer to Wei at al. 2021 to see why this is the case. Unfortunately Wei et al 2021 is only for the tabular setting so it does not contain information about this assumption that involves linear MDPs. Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: Thank you very much for your thorough review and suggestions for improving the paper. Here are our responses. Minor error in proof. Thank you very much for catching this. We will replace $m_{t + 1}$ with $m_t$ for the equality to hold. Relation to previous work. Thank you for the suggestion. We fully agree that detailed comparison with Hong 2025 v1 will benefit the community. A short explanation is that Hong 2025v1 that uses "max-pooling" of Q functions, which had an error, happened to allow computationally efficient clipping without additional algorithmic modification. Hong 2025v2, which fixes the error using double loop structure could no longer use the computational efficient clipping. Our submission introduces an algorithmic modification that allows for computationally efficient clipping under the double loop structure. We will mention the attempt made by Hong 2025v1 in Section 2.4, and add detailed comparison in the Appendix. Knowledge of T, H. We will make it clear to the reader that $T$ is required by adding $T$ in the list of input parameters in the algorithm box, and mentioning it in the analysis when we set $\gamma = 1 - 1 / \sqrt{T}$. We will add a remark following the Theorem statement that using doubling-trick, we can get away with the knowledge of $T$ at the cost of incurring additional factor of $\sqrt{\log T}$ in the regret. As for the knowledge of $H$, we will remind the reader after the Optimism lemma (Lemma 3.4) and after the main theorem statement that knowledge of an upper bound of span is required. As mentioned in our response to Reviewer CyKa, we will also mention that there is a recent work that relaxes this assumption for the tabular setting, and that we leave relaxing this assumption to future work. Discussion on Bellman optimality equation. Thank you for the suggestion. We will add discussion on the relation to Communicating/Weakly Communicating MDPs and Ergodic assumption. Bellman optimality equation assumption is strictly weaker than Communicating/Weakly Communicating MDP which is strictly weaker than ergodic assumption. We will mention this fact with brief reasoning and citation. On boundedness of reward vector. Note that the paper by Wei et al. 2021 "Learning infinite-horizon average-reward mdps with linear function approximation." discusses this in detail in Appendix A. (Based on your comment, we think you were referring to Wei et al. 2020. "Model-free reinforcement learning in infinite-horizon average-reward markov decision processes"). Their reasoning is as follows. Given any feature mapping $\phi$ with $\Vert \phi(\cdot, \cdot) \Vert_2 \leq 1$ and a reward function in the form $r(\cdot, \cdot) = \phi(\cdot, \cdot)^\top \theta$ such that $\vert r(\cdot, \cdot) \vert \leq 1$, there always exists an invertible matrix $A \in \mathbb{R}^{d \times d}$ such that $\Vert A \phi(\cdot, \cdot) \Vert_2 \leq 1$ and $\Vert A^{-1} \theta \Vert_2 \leq \sqrt{d}$, which enables us to work with $\widetilde\phi = A \phi$ and $\widetilde\theta = A^{-1} \theta$ instead that satisfy $\Vert \widetilde\phi \Vert_2 \leq 1$ and $\Vert \widetilde\theta \Vert_2 \leq \sqrt{d}$. They argue in their proof that such a transformation $A$ is the transformation that transforms the MVEE of the feature mappings into a unit ball. When citing their work, we will add which section of their paper to refer to (Appendix A), and briefly explain their argument. --- Rebuttal Comment 1.1: Comment: Thanks a lot for your response ! I indeed did a mistake and I was referring to Wei et al. 2020 instead of Wei et al. 2021. That point is clear now but I think it would be better if the authors make clear that finding features with the desired boundness properties requires computing a MVEE. Please make sure to add the comparison with the failed attempt in Hong et al. 2025v1. I think this is very important for the placement of the paper in the literature. --- Reply to Comment 1.1.1: Comment: Thank you for the suggestion. We will mention the MVEE method for the transformation for ensuring boundedness, and mention that the computation of MVEE is required. As for comparison with 2025v1. We do agree that full comparison with 2025v1, not just with 2025v2/3, is important. We will devote a section in appendix for this. Unfortunately, the comparison is too technical to describe fully in the rebuttal due to space and format constraints. Here is a brief summary: - [modified notation a bit for better comparison with our submission] Single-loop algorithm (computationally inefficient) in 2025v1 has a value iteration structure that leads to a term $V_{t - 1} (s_{t + 1}) - \widetilde{V}\_{t + 1}(s\_{t + 1})$ in the regret bound. To match the subscript for bounding this term, 2025v1 introduces "max-pooling" value functions such that $V_t$ is increasing in $t$. To avoid covering issue, they keep track of the index $\tau_t$ such that $V_{\tau_t}$ is increasing in $t$. Also, they need to restart the algorithm periodically, otherwise the value functions will always be $1 / (1 - \gamma)$ at all time steps. They employ the "doubling trick" that restarts algorithm when determinant of covariance doubles. However, they erroneously claim that $V\_{\tau_t - 1}(s_{t + 1}) \leq V\_{\tau_t + 1}(s_{t + 1})$ holds. For this to make sense, $\tau_t - 1$ should be in the current episode, enforcing $\tau_t$ to be chosen by max-pooling from the second time step in the episode and onward. However, taking max-pooling from the second time step will not allow bounding $V\_{\tau_t - 1} \leq V\_{\tau_t + 1}$ when $\tau_t$ is exactly the second time step of the episode, since $V\_{\tau_t - 1}$ is the function function at the first time step of the episode. Due to this "off-by-one" error, the analysis fails. - Ignoring this off-by-one error and pretending that the analysis goes through, the analysis happens to allow computationally efficient algorithm with double-loop structure trivial. - 2025v2 fixes the off-by-one error by introducing a new value iteration structure (backward induction instead of "forward induction") such that the subscript is matched to $V_{t + 1}(s_{t + 1}) - \widetilde{V}\_{t + 1}(s\_{t + 1})$ by design, so that no max-pooling is required. However, the analysis on the double-loop structure with computationally efficient algorithm fails, as is discussed in our submission in Section 3.2. - Our submission introduces the new algorithm structure using the novel deviation-controlled value iteration structure, that allows bounding the difference $V_{t + 1}^t(s_{t + 1}) - \widetilde{V}\_{t + 1}^{t + 1}(s\_{t + 1})$ by the difference in clipping thresholds, which is magically bounded using telescoping sum.	Summary: This paper proposed an algorithm for infinite-horizon average-reward reinforcement learning with linear function approximation. The main problem need to be solved is the computation issue arises from minimize the value function in large state space. To address this, the paper proposed a new clipping technique, and proved that this method achieves the same regret order while enjoy computational efficiency under the large state space setting. Claims And Evidence: Yes. The paper clearly provided the computational complexity to support that the proposed algorithm runs in polynomial time. Methods And Evaluation Criteria: Yes. Theoretical Claims: I checked the proof in the main paper and appendix A, and do not find any issues. Experimental Designs Or Analyses: N/A Supplementary Material: I do not fully check the supplementary material. It seems correct to me. Relation To Broader Scientific Literature: N/A Essential References Not Discussed: N/A Other Strengths And Weaknesses: Strength: The explanation of the motivation and idea of why and how to do clipping is clear and easy to understand. Weakness: The work lack some (at least) toy example to illustrate the effectiveness of the proposed algorithm. 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. Here is our response. Simulation in toy setting. Thank you for the suggestion for running a simulation in a toy setting. We have confirmed that our algorithm runs in a tabular setting (i.e. linear MDP setting with feature vectors orthogonal) with average regret reasonably low when treating the bonus factor beta as a hyperparameter, as is usually done in UCB-type algorithms. To our knowledge, no study to date has conducted a simulation under the linear MDP setting. Nevertheless, we agree that providing a simple simulation would be valuable to the community, and we will aim to include a simulation. One reason why simulation under linear MDP is absent in the literature is due to the complication of specifying the vector of measures $\mu$ that ensures $P(s' \| s, a) = \langle \mathbf\varphi(s, a), \mathbf\mu(s') \rangle$ is a valid probability measure. However, we believe we can get around the problem by restricting the feature vector $\varphi(s, a)$ to have L1-norm equal to 1, and each of the $d$ measures in $\mathbf\mu$ are probability measures. We will aim to conduct experiments under the restricted linear MDP setting.	Summary: This paper proposes a computationally efficient algorithm for infinite-horizon average reward linear MDPs. The paper seeks to improve upon the previously proposed approach $\gamma$-LSVI-UCB by Hong et al'25. The main contribution is that the algorithm proposed in Hong et al.'25 requires to iterate over all the state-space to find the minimum value function for clipping, which might be computationally expensive, especially for linear MDP. Hong et al.'25 assumed some minimum oracle, this paper seeks to improve upon that. The paper proposes a novel idea where one only needs to iterate over the state encountered so far. The paper in particular focuses on bounding the error $V$- $\tilde{V}$. The paper significantly contributes in this direction. ##Post Rebuttal Update## All my concerns have been resolved, and I am happy to accept this paper. Claims And Evidence: The proofs of the claims are provided. Methods And Evaluation Criteria: The paper is theoretical in nature. Theoretical Claims: The theoretical claims seem to be correct. Experimental Designs Or Analyses: N/A. Supplementary Material: The reviewer has briefly glossed over the materials which seem to be correct. Relation To Broader Scientific Literature: The reviewer does not have any major concern. Essential References Not Discussed: The reviewer does not have any major concern. Other Strengths And Weaknesses: Strengths: 1. The theoretical contributions are significant. 2. The paper is well-written. Weakness: 1. The algorithm still needs to iterate over all the states encountered, which can be significant for the large time period. 2. Some simulations would be nice to see the difference in terms of computational time and the regret compared to the state-of-the-art approaches. Other Comments Or Suggestions: N/A Questions For Authors: 1. Can the authors summarize briefly the main technical novelties? in particular, how did they bound the deviation? Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: Thank you for your time for the review and for the suggestion for improving the paper. Q1: main technical novelties. We will integrate the following summary in the introduction section and in Section 3.2 when introducing the method. 1. The main technical novelty lies in designing a clipped value iteration algorithm that ensures each successively generated value function deviates from its predecessor by no more than the difference between their respective clipping thresholds. 2. We show that a naive adaptation of previous work cannot control this deviation in the linear MDP setting. 3. A natural workaround would be to clip each newly generated value function with a new threshold so that it deviates from the previously generated value functions by at most the difference in the thresholds. But doing so will make the value functions more and more complex successively, running into an issue when using covering argument for uniform concentration bound. 4. To address this, we design a novel way for controlling the deviation without running into covering issues. Specifically, we "pool" latest value functions in such a way that the difference in successive "pooled" value functions is bounded by the the difference in the thresholds. The pooled value function has low complexity so that the function class that captures the pooled value function has low covering number. --- Rebuttal Comment 1.1: Comment: I thank the authors for their responses. Just one clarification question. This is regarding the comment made by the reviewer 3 Auz. ``To my knowledge, there was a previous attempt in the first version of the paper uploaded in arxiv that claimed to achieve the same results but without the double loop structure and therefore with a better time complexity. Unfortunately, the authors of Hong et al. 2025 claimed in their v2 that the previous result contains a mistake. I think that the mistake in Hong et al 2025 is in the maximum over the past Q functions, this algorithmic technique makes the covering number of the state value functions space to be exponential in . This is indeed avoided by the current submission that replaces the maximum over past value functions with the double loop structure." You have responded to this comment. Can you please clarify and elaborate what the mistake was? How are you overcoming it in this version? Thanks, --- Reply to Comment 1.1.1: Comment: Here is a brief explanation regarding the comment made by reviewer 3Auz: - Hong et al. 2025v1 uses single-loop structure and uses the scheme of taking maximum of past value functions. It is known that taking maximum of past value functions in linear MDP leads to a covering issue because the function becomes more and more complex and the covering number of the function class that captures such functions become exponential in the number of time steps. As a workaround, they use a scheme of keeping track of the time index that gives the maximum value, i.e., $\tau_t(s, a) = \arg\max_{\tau \in [\tau_0:t]} Q_\tau(s, a)$ where $\tau_0$ is some reference time step (exact definition they use is a bit different). However, the analysis has an off-by-one error. - Hong et al. 2025v2 fixes the problem by introducing a double-loop structure, at the cost of incurring additional factor of $T$ in computational complexity. However, the double-loop structure requires computing the minimum of value function over the entire state space when clipping. - Our submission introduces a novel algorithm structure that allows for computationally efficient clipping. For more detailed explanation, please see our response to Reviewer 3Auz.	Summary: In this paper, the authors have studied the reinforcement learning algorithm for linear MDPs in an infinite-horizon average-reward setting. Previous works approximate the average reward by the discounted one and employ a clipping-based value iteration method. However, it requires the computation of minimum of the value function over the state space. This may be computationally prohibitive. Towards that, in this paper, an efficient clipping technique is introduced for value iteration algorithm. This requires computation of minimum value function over states visited by the algorithm. It has been established that the proposed scheme demonstrates the same regret bound as that of the previous work with a substantial drop in computational complexity which is independent of the size of the state space. ## update after rebuttal The response addresses my major concerns. I have raised my score to 3. Claims And Evidence: Yes Methods And Evaluation Criteria: Yes Theoretical Claims: I have checked the proof , but not in great detail. Experimental Designs Or Analyses: Experimental results are absent in the paper. Supplementary Material: Yes Relation To Broader Scientific Literature: In this paper, the authors have studied the reinforcement learning algorithm for linear MDPs in an infinite-horizon average-reward setting. It has been established that the proposed scheme demonstrates the same regret bound as that of the previous work with a substantial drop in computational complexity which is independent of the size of the state space. Essential References Not Discussed: No Other Strengths And Weaknesses: The paper is well-written and contains some interesting ideas. The problem considered by the authors are relevant and interesting. However, the solution is based on some strong assumptions such as knowledge of $sp(v^)$. Some results need clarification and lacks intuition. Other Comments Or Suggestions: Not applicable. Questions For Authors: My comments are as follows: 1. What if the underlying Markov chain is irreducible under various policies? In the worst case, the algorithm can still visit all the states and hence, the computational burden may still be high. I expected some simulations too in this direction to verify the efficiency of the proposed scheme. 2. Why do we need to assume that $r\in[0,1]$? I guess removing this assumption also does not create any problem. 3. It is assume that $sp(v^)$ is known the learner. The authors stated that this assumption can be relaxed to the knowledge of an upper bound on $sp(v^)$. However, in this case regret will scale with the upper bound. Knowledge of $sp(v^)$ or an upper bound on it can both be difficult to obtain. Also, choice of a loose upper bound can result in poor regret. Is there a way in which such a requirement of knowledge can be avoided completely? 4. Please describe what do you mean by covering number. 5. Lemma 3.4 holds when $H\ge 2sp(v^*)$. How do one guarantee that? 6. In Theorem 3.6, we need choose $\gamma=1-\sqrt{1/T}$. However, typically $\gamma$ is not in designer’s hand. This makes the algorithm depart from reality. 7. It is stated that the computational complexity is independent of the size of the states space. However, $d$ is related to the size of the state space. Why is the regret large when $d$ is large? As $d$ becomes close to the size of the state space, regret should be less. Please elaborate Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Thank you for your time for the detailed review. Your feedback will help us in improving our paper. Here are our responses to your questions. Q1: Computational issue \& Simulation. You are correct to note that, in the large state space regime, the number of unique states visited over $T$ time steps can be very large, potentially with no repeats. However, our algorithm’s computational complexity does not scale with the size of the entire state space, since we do not enumerate all states. Instead, in the worst case, where states never repeat, the complexity scales with $T$. Regarding simulation, due to the theoretical nature of the linear MDP assumption, designing a concrete simulation environment is challenging and, to our knowledge, no simulation has been performed in the linear MDP setting in the literature. we agree that providing a simple simulation would be valuable to the community, and we will aim to include a simulation under a restricted linear MDP setting described in our response to Reviewer w193. Q2: Why assume reward to be bounded. Your intuition that the assumption can be removed is correct. And in fact, it is this intuition that It is standard in the literature to assume $r \in [0, 1]$ without loss of generality. When the actual reward lines in $[0, B]$, say, then we can scale it to $\widetilde{r} \in [0, 1]$, analyze the regret bound under the new reward, and then multiply the final regret bound by $B$ to account for the scaling. To avoid carrying the constant $B$ around in our derivations, we assumed $r \in [0, 1]$. We will add a clarifying note on this point in our final version of the paper. Q3, Q5: Assumption on the knowledge of span. Thank you for bringing this up. Indeed, requiring prior knowledge of $\text{sp}(v^\ast)$ is a limitation of our approach. Whether sample-efficient learning is possible without knowing the span in advance has been an open question for a long time, and many existing works rely on this assumption. A recent result by Boone et al. [1] shows for the first time that it can be avoided in the tabular setting. However, extending their technique to the linear MDP setting is non-trivial and will likely require a major breakthrough. We leave this to future work. We will add a remark on this assumption and cite [1] in the final version of the paper. Q4: Covering number. Thank you for the suggestion. In the paragraph following Lemma 3.3, we will describe the general covering argument that uses epslion-net for covering the function class for getting uniform concentration bound and briefly describe $\epsilon$-covering number of a function class and how the log covering number scales the concentration bound. Q6: Setting discounting factor. The original problem the designer is trying to solve is the average-reward setting. We are proposing to approximate the average-reward setting by a discounted setting with a particular discounting factor. The designer will work with the discounted setting with discounting factor set to the proposed value. So, it is in the hand of the designer to set the discounting factor. We will make it clear in the beginning of Section 3 that the discounting factor is set by the designer to approximate the average-reward setting. Q7: Size of the state space and the dimension. Thank you for the question. When we say "size of the state space", we mean the number of the states in the state space. In the tabular setting, we do not assume any structure in the MDP that allows generalizing to unseen states, and the computational and statistical complexity both scale with the number of states. However, in the linear MDP setting, we assume a structure in the MDP that allows for the generalization through the feature mapping $\varphi$ that maps state-action pairs to a $d$-dimensional feature vector. Due to the feature representation, conceptually, we no longer need to learn about all the states individually. Rather, we only need to learn about $d$ "directions", which allows for computational and statistical efficiency. Specifically, the computational complexity and the regret bound scales with $d$, not the size of the state space. With this intuition, we can see that if $d$ is large, then there is more "directions" to explore, making both computational complexity and regret large. We will add a summary of this discussion when defining the linear MDP setting in Section 2.3. --- [1] Achieving Tractable Minimax Optimal Regret in Average Reward MDPs. NeurIPS 2024. --- Rebuttal Comment 1.1: Comment: I thank the authors for their detailed response. However, I am still concerned regarding two aspects: 1. Knowledge of $sp(v^)$: Can this assumption be relaxed? 2. The authors stated that when $d$ is large, then there is more directions to explore, making both computational complexity and regret large. It is not clear to me. Please explain using two extreme cases, $d=1$ and $d=\|\mathcal{S}\times \mathcal{A}\|$? Since there is no approximation involved in the second case, won’t the regret due to approximation be less in the second case? Another clarification question: Since the original problem considers an infinite horizon average-reward setting, how do you choose $T$ to set $\gamma=1-\sqrt{1/T}$? Will any choice of large $T$ be fine to represent the infinite horizon setting? --- Reply to Comment 1.1.1: Comment: Q1* Relaxing the assumption of the knowledge of span in linear MDPs is an open problem. The authors of "Achieving Tractable Minimax Optimal Regret in Average Reward MDPs, NeurIPS 2024" relaxes the assumption in tabular setting by using a subroutine that estimates the optimal bias function $v^\ast$ to work without the knowledge of $\text{sp}(v^\ast)$. Their approach is based on the observation that, when an optimal policy is run, the bias difference $v^\ast(s) - v^\ast(s')$ is roughly the difference in values when starting from the state $s$ and $s'$. They use the average reward collected in subtrajectories that start at $s$ and end at $s'$ to estimate $v^\ast(s) - v^\ast(s')$. It is unclear how to generalize this idea to (linear) function approximation setting where the state space is large, since their idea relies on tracking each pair of $(s, s')$ to estimate $v^\ast(s) - v^\ast(s')$, which can be sample inefficient in function approximation setting. Designing an algorithm (even one that is computationally inefficient) for linear MDP without the knowledge of the span is an interesting and challenging open problem, and would be a good topic for a future standalone paper. Q2 In general, in the learning setting where the transition probability $P$ is unknown, the algorithm design centers around estimating the unknown $P$ or a quantity that depends on the unknown $P$. Typically, in value-iteration based algorithm, which is the algorithm class we use, the quantity of interest is $[PV](s, a)$. The regret bound depends on how sample efficiently we can estimate $[PV](s, a)$ since the regret bound scales with the width of the confidence bound. (in general, regret of UCB type of algorithm scales with sum of confidence bounds). In linear MDP setting, we exploit the fact that $[PV](s, a) = \langle \varphi(s, a), w \rangle$ for some $w \in \mathbb{R}^d$, and use linear regression to estimate $w$, which gives the concentration bound that scales linearly with $d$ (see Lemma 3.3). This suggests that the regret will scale with $d$. To gain more intuition, consider the following two extreme cases. - $d = 1$. In this case, the transition $P(\cdot \| s, a)$ is the same for all $s, a$ pairs. Hence, we don't have to collect transition data for all $(s, a)$ pairs separately to be able to estimate $P(\cdot \| s, a)$ for each $s, a$. We can "pool" data for all pairs of $(s, a)$ to estimate $P(\cdot \| s, a)$. Similarly, estimation of $[PV](s, a)$ can be done by sample average of $V(s')$. - $d = SA$. In this case the transition $P(\cdot \| s, a)$ can be arbitrary for each $(s, a)$ pair. Hence, unlike the $d = 1$ case, we cannot "pool" data, and requires data for each $(s, a)$ pair. Similarly, estimating $[PV](s, a)$ requires data for each $(s, a)$ pair. Intuitively, this leads to a concentration bound that scales with $SA$ and hence regret scales with $SA$. We will make it clearer that the concentration bound in Lemma 3.3 scales with $d$, and that the concentration bound eventually enters the regret bound. Regarding $T$. We first clarify the distinction between the problem setting ("infinite-horizon") and the performance guarantee of an algorithm ("finite-time regret bound"). The notion "infinite-horizon average-reward" describes the problem setting where the criterion for evaluating a policy is through the infinite-horizon average-reward. When analyzing the performance of an algorithm, one typically uses "finite-time regret bound" with a certain time $T$ and show a bound on the $T$-step where regret in each step is against the optimal average-reward. Our guarantee allows a designer to choose $\gamma = 1 - 1 / \sqrt{T}$ to achieve $O(\sqrt{T})$ $T$-step regret. As you hinted, a designer may want a single algorithm that guarantees $O(\sqrt{t})$ $t$-step regret for any $t$. Algorithms with this guarantee is called anytime algorithms. There is a known reduction called "doubling trick" that uses algorithms with $O(\sqrt{T})$ $T$-step regret to design an anytime algorithm. The reduction is as follows. Suppose we have access to an algorithm $Alg(T)$ that guarantees $O(\sqrt{T})$ $T$-step regret for each $T$. In our paper, $Alg(T)$ can be obtained by choosing $\gamma = 1 - 1 / \sqrt{T}$. Then, we can design an anytime algorithm by running $Alg(2^n)$ for $2^n$ steps for $n = 0, 1, 2, \dots$. That is, run $Alg(1)$ for 1 time step, then run $Alg(2)$ for 2 time steps, then run $Alg(4)$ for 4 time steps, etc. For any $2^{n - 1} \leq t < 2^n$, such an algorithm guarantees $t$-step regret bound of $$ O(\sqrt{1}) + O(\sqrt{2}) + \cdots + O(\sqrt{2^n}) = O(\sqrt{n 2^n}) = O(\sqrt{t \log t}) $$ by Cauchy-Schwarz, since $1 + 2 + ... + 2^n \approx O(2^n)$. We realize that discussing anytime algorithm would greatly improve clarity on our guarantee. We will incorporate this discussion into the paper. Also, we think parameterizing the algorithm with $T$ instead of $\gamma$ may be clearer for this discussion.	null	null	null	null	null	null
Bounded Rationality for LLMs: Satisficing Alignment at Inference-Time	Accept (poster)	Summary: This paper proposes UAMD, a novel inference-time alignment approach for language models that allows satisfying multiple user-specified criteria through constrained decoding. The key insight is that for many criteria (like safety), meeting a threshold is sufficient rather than maximizing the reward. The method formulates this as a constrained optimization problem solved via duality theory. The main results show UAMD outperforms baselines on multiple evaluation setups while maintaining user-specified thresholds. ## update after rebuttal Overall, the framework is self-contained. However, the issues of scalability and user burden still exist, so I give a rating of 3 instead of 4. The author's further response seems to provide some insights for future work, while I can not judge the value. Claims And Evidence: The claims are generally well-supported through: 1. Theoretical analysis with bounded suboptimality guarantees 2. Empirical evaluation on multiple datasets showing improved performance 3. Ablation studies demonstrating the impact of different thresholds 4. Both quantitative metrics (GPT-4 win rates) and qualitative examples Methods And Evaluation Criteria: The methods appear sound and well-motivated. The evaluation using GPT-4 as a judge makes sense given the subjective nature of the criteria being optimized. However, the paper could benefit from: - More baseline comparisons beyond just MOD (see missing references) - Human evaluation to validate GPT-4 judgments - Larger-scale experiments on more diverse criteria Theoretical Claims: The theoretical analysis in Section 5 seems mathematically sound. The bounds derived for both primal and dual variable approximations are reasonable. Experimental Designs Or Analyses: The experimental setup is generally solid the test sets are relatively small and evaluation metric depends on GPT-4 Supplementary Material: I roughly scan the appendix Relation To Broader Scientific Literature: The paper does a good job positioning itself relative to: - Prior work on LLM alignment - Inference-time methods - Multi-objective optimization Essential References Not Discussed: PAD: PERSONALIZED ALIGNMENT OF LLMS AT DECODING-TIME. ICLR 2025 Conditional Language Policy: A General Framework For Steerable Multi-Objective Finetuning. EMNLP 2024-findings Differentiation of Multi-objective Data-driven Decision Pipeline Other Strengths And Weaknesses: Strengths: - Novel framing of alignment as satisfying thresholds - Strong theoretical foundation - Practical inference-time method - Clear empirical improvements Weakness: - Efficiency Analysis: The paper lacks analysis of computational efficiency, particularly when evaluating multiple reward models during inference. The computational overhead compared to baseline methods should be discussed and quantified. - Scalability Issues: Having a separate reward model for each dimension might not be scalable in practice. As the number of attributes/dimensions increases, not only does the computational cost grow significantly, but the maintenance overhead for multiple reward models also becomes substantial. - User Burden: Requiring users to manually specify thresholds for different dimensions may not be practical in real-world applications. Average users might struggle to determine appropriate threshold values, adding complexity to system usability. - Trade-off Analysis: The paper does not adequately address the interdependencies between different objectives. Notably absent is a discussion of Pareto optimality, a fundamental concept in multi-objective optimization that could provide theoretical grounding for handling competing objectives. Other Comments Or Suggestions: N/A Questions For Authors: N/A Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We thank you for the thoughtful review and address your concerns below. > Weakness 1: The paper lacks ... Response: Computational efficiency analysis: Thanks for the suggestion! Below is the inference time per prompt for various approaches using the setup in Evaluation-1 (main paper): * Dataset: PKU-SafeRLHF-30K (test set) * Baseline policy: Zephyr-7B-β * Objectives: Helpfulness and Harmlessness Evaluations are conducted using PyTorch 2.2.0, Transformers 4.43.3, and NVIDIA RTX A6000 GPUs. Win-tie Rate is denoted as WTR \| \| WTR(Helpfulness) \| WTR(Harmlessness) \| Inference-time (per prompt) \| \|--\|--\|--\|--\| \| Helpful Policy \| 65.32\|46.31\|12s\| \| Harmless Policy \| 45.12\|70.12\| 12s\| \| MOD\| 46.23\| 68.42\| 21s\| \| PAD\|28.33\| 60.00\| 12s\| \| UAMD (ours)\|68.13\|65.29\|21s\| Takeaway: UAMD incurs slightly higher inference time due to multi-reward evaluation but outperforms PAD, which is faster yet underperforms on helpfulness > Weakness 2: More baseline ... Response: Thanks for pointing this. We added results comparing UAMD with PAD using setup in Evaluation-1 (main paper): * Dataset: PKU-SafeRLHF-30K (test set) * Baseline policy: Zephyr-7B-β * Objectives: Helpfulness, Harmlessness \| \| WTR(Helpfulness) \| WTR(Harmlessness) \| \|-----------------\|------------------------\|-------------------------\| \| Helpful Policy\|65.32\|46.31\| \| Harmless Policy\|45.12\| 70.12\| \| MOD\|46.23\|68.42\| \| PAD\|28.33\|60.00\| \| UAMD (ours)\|68.13\|65.29\| Takeaway: PAD satisfies harmlessness but severely underperforms on helpfulness. UAMD balances both, confirming its strength in multi-aspect alignment. > Weakness 3: Human evaluation ... Response: We now include preliminary human evaluation (using 10 participants). We use the setup in the Evaluation-1 (main paper) with the number of prompts as 10. \| \| WTR (Helpfulness Reward) \| WTR(Harmlessness reward) \| \|-----------------\|------------------------\|-------------------------\| \| Helpful Policy \|0.80\|0.40\| \| Harmless Policy\|0.20\|0.60\| \| MOD\|0.60\|0.80\| \| UAMD (ours)\|0.80\|0.80\| Takeaway: Human feedback aligns with GPT-4 evaluations, confirming UAMD’s robustness. > Weakness 4: Larger-scale experiments... Response: We added new experiments with three objectives: * Dataset: Nvidia HelpSteer2 (validation set) * Baseline policy: Zephyr-7B-β * Objectives (we consider three): Helpfulness, Harmlessness, and Humor with user-defined constraints: 50% win-tie rate (calculated using GPT-4) on Harmlessness and Humor. \| \| WTR (Helpful) \| WTR (Harmless) \| WTR (Humor) \| \|-----------------\|------------------------\|-------------------------\|----------------------\| \| Helpful Policy \| 68.33\| 45.00\| 51.67\| \| Harmless Policy \| 43.33\| 73.33\| 46.67\| \| Humor Policy \| 55.00\| 45.00\| 70.00\| \| MOD\| 33.33\| 60.00\| 63.33 \| \| UAMD (ours)\| 68.33\| 60.00\| 66.67\| Takeaway: UAMD achieves higher helpfulness while satisfying harmlessness and humor constraints. > Weakness 5: Scalability concerns ... Response: We acknowledge the scalability issue with multiple reward models. Our current work focuses on introducing a principled formulation inspired by bounded rationality and decision theory [1], expressed as a constrained optimization (Eq. 2 in paper), with theoretical guarantees and empirical evidence. PAD and similar methods suggest promising paths to reduce overhead, which we consider an important direction for future work. > Weakness 6: User burden ... Response: We acknowledge the reviewer’s concern. As discussed in the paper (Page 3, Column 1, Lines 148-155), determining appropriate thresholds, while seemingly burdensome, is often manageable in practice when a reliable reward model is available. Reasonable thresholds can be estimated using GPT-4 win rates or refined with light human feedback. > Weakness 7: Trade-off analysis ... Response : Good point. While Pareto optimality is suited to general multi-objective setups, our work models threshold-based user preferences [1], leading naturally to a constrained optimization (Eq. 2), not Pareto front exploration. We reformulate this as a Lagrangian max-min problem (Eq. 4) and prove guarantees (Theorem 5.1) covering suboptimality and constraint violations. Empirically, Figure 3 in the main paper shows how varying constraints affect GPT-4 win-tie rates. Below is an additional ablation using ArmoRM thresholds: \| Threshold on Harmlessness \| WTR(Helpful) \| WTR (Harmless) \| \|---------------------------\|------------------------\|-------------------------\| \| 0.60\| 0.434\|0.639\| \| 0.70\| 0.422\|0.730\| \| 0.75\| 0.407\|0.785\| Takeaway: We observe that increasing the threshold constraint on harmlessness makes the policy focus more on the harmless reward, and our algorithm correctly adjusts to meet the new requirement, improving harmlessness performance at the expense of helpfulness. [1] Simon, Herbert A. "Rational choice and the structure of the environment." --- Rebuttal Comment 1.1: Comment: Thank you very much for the authors' response. The rebuttal addresses part of my concerns. But my main concerns regarding scalability and user burden, which is very important in the era of LLMs, still exist. Therefore, I maintain my score. --- Reply to Comment 1.1.1: Comment: We sincerely appreciate your insightful follow-up and the opportunity to further elaborate on our contributions and positioning in the detailed discussion that follows: 1. Regarding scalability: We acknowledge that scalability is an important consideration. However, we note that it is a fundamental challenge of any inference time approach, which tries to consider multiple aspects of response generation and not a specific challenge of our proposed approach. To that end, our approach is designed to maintain a modest computational burden by allowing the integration of any reward model. By leveraging transfer decoding, UAMD achieves consistent performance improvements across various tasks (see [Response to Weakness 1](https://openreview.net/forum?id=cEhLObwvvu&noteId=tr4xamvoMG)). The experiments confirm the favorable trade-off between additional overhead and performance gain. We emphasize that our core contribution is introducing a principled and flexible framework for inference-time alignment via user-specified multi-criteria decoding, offering fine-grained control over model behavior. We believe this addresses an important gap in the current literature. Improving computational efficiency, for instance, through distillation of reward models or via combining with PAD type approaches, is a valuable next step, and we view it as an exciting direction for future research. 2. User Burden in Specifying Thresholds: We acknowledge the reviewer’s concern that requiring users to set thresholds can impose a cognitive load, especially for non-expert users. In practice, however, we find that thresholds can be estimated automatically using empirical reward distributions or guided via preference elicitation. For example, as shown in Figure 1, reward saturation points, where GPT-4 win rates or human preferences plateau, can be used to determine effective default thresholds. This offers a practical solution that balances user control with usability. Furthermore, incorporating threshold tuning into an interactive preference feedback loop is a natural next step for real-world deployment, and we see this as an exciting avenue for follow-up research. Our key contribution: In sumary, our primary contribution lies in establishing a *flexible and theoretically grounded framework for inference-time alignment under multiple user-specified criteria*. While we acknowledge there is room to improve usability and computational efficiency, we believe the current work offers an important foundation for future progress in this space.	Summary: This paper primarily focuses on aligning large language models (LLMs) at inference time (i.e., test time) without modifying their parameters. Prior work in inference-time alignment primarily aims to align LLMs towards a single objective defined through a reward model. Some studies have explored multi-objective alignment, but they generally seek to maximize rewards across multiple objectives. In this work, the authors introduce a novel setting where one primary reward objective must be maximized, while certain other reward objectives must meet user-specified threshold values. They formulate this as a constrained optimization problem and solve its dual version using the Lagrangian framework. However, solving this problem exactly presents challenges, as it requires computing the Lagrange multipliers through gradient descent and determining the optimal value functions corresponding to the given reward functions. To address these challenges, they employ approximation strategies, including a quadratic approximation of the objective and techniques from Transfer $Q^*$ work (Chakraborty et al., 2024). Based on these methods, they propose UAMD, a novel decoding strategy that optimizes alignment with the primary objective while ensuring compliance with user-specified constraints for other objectives. They analyze the sub-optimality gap of their approach when using both exactly computed and approximately computed Lagrange multipliers. The efficacy of their algorithm is experimentally evaluated on three different tasks, with GPT-4-based evaluations comparing their method to baselines. Additionally, they conduct ablation studies on the $ \beta $ parameter and examine its effect on threshold constraints for the target reward. Claims And Evidence: Yes, all theorems stated have been provided proofs in the appendix. Methods And Evaluation Criteria: Yes, the methods are primarily evaluated using a GPT-4-based evaluation framework, with all constraints on the target reward set to a 50% win rate against the baseline model. However, the paper could be further improved by incorporating evaluations based on specific reward models, such as the PKU reward model or the ArmoRM reward model. Additionally, it would be beneficial to explore different threshold values for the target reward. Theoretical Claims: Yes, proofs of Theorem 5.1 and 5.2 are properly detailed in the appendix. Experimental Designs Or Analyses: Yes, the proposed method has been evaluated across multiple datasets and models. Additionally, ablation studies have been conducted to analyze the effect of $\beta$ on the threshold constraints. However, the paper could be further improved by incorporating evaluations on specific reward models and exploring various threshold values for the target reward, rather than relying solely on a 50% win rate against the baseline policy. Supplementary Material: Yes, reviewed all sections in the appendix. Relation To Broader Scientific Literature: Prior work on multi-objective LLM decoding has primarily focused on maximizing alignment across all objectives in terms of reward functions. However, this paper introduces an important and novel multi-objective setting where one key reward objective must be maximized while ensuring that other reward objectives meet specified threshold values. Additionally, the authors conduct a theoretical analysis of this problem and propose an efficient algorithm to address it at inference time. Essential References Not Discussed: N/A Other Strengths And Weaknesses: Strengths: The paper introduces a novel multi-objective setting where one key reward objective must be maximized while ensuring that other reward objectives meet specified threshold values. This problem is formulated as a constrained optimization task and addressed using the Lagrangian framework. To enable efficient inference-time optimization, the authors propose approximation strategies. Additionally, they theoretically analyze the suboptimality gap of their approach. Experimental results further validate the effectiveness of their method. Weaknesses: 1. The methods are primarily evaluated using a GPT-4-based evaluation framework, with all constraints on the target reward set to a 50% win rate against the baseline model. However, the paper could be further improved by incorporating evaluations on specific reward models, such as the PKU reward model or the ArmoRM reward model and considering various threshold values for the target reward. 2. Although the theoretical framework accommodates more than two objectives with user-specified thresholds for each, the experimental setup has only considered a single target reward. Expanding the experiments to include multiple target reward functions, as outlined in the problem statement, would strengthen the paper’s empirical validation. Other Comments Or Suggestions: N/A Questions For Authors: Is there any reason that specific reward models have not been used to evaluate the methods? Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We thank you for the thoughtful review and address your concerns below. > Weakness 1: The paper relies.... Response to Weakness 1: Evaluations using ArmoRM: Thanks for your suggestion! We have conducted additional experiments using ArmoRM reward model [1] (RLHFlow/ArmoRM-Llama3-8B-v0.1) with the following setup: * Dataset: PKU-SafeRLHF-30K (test set), * Baseline policy: Zephyr-7B-β, * Objectives: Helpfulness and Harmlessness, where the user can specify threshold on Harmlessness. To compute reward using ArmoRM, we use the output attributes “helpsteer-helpfulness” and “beavertails-is_safe” for helpfulness and harmlessness rewards respectively. We set the harmlessness constraint to $0.60$. Results below: \| \| Helpful Reward (using ArmoRM) \| Harmless Reward (using ArmoRM) \| \|-----------------\|------------------------\|-------------------------\| \| Helpful Policy \| 0.448 \| 0.465 \| \| Harmless Policy \| 0.382 \| 0.681 \| \| MOD \| 0.397 \| 0.661 \| \| UAMD (ours) \| 0.434 \| 0.639 \| Takeaway: UAMD achieves the highest helpfulness reward while satisfying the harmlessness constraint (≥ 0.60). In contrast, MOD achieves higher harmlessness but underperforms on helpfulness. > Weakness 2: It would be beneficial ...... Response to Weakness 2: Thanks for the suggestion! Ablations on different threshold values: Figure 3 (main paper) shows ablations with different user-specified constraints and their effect on GPT-4 win-tie rate. Below, we add additional results using ArmoRM. \| Threshold on Harmlessness \| Win-Tie Rate (Helpful) \| Win-Tie Rate (Harmless) \| \|---------------------------\|------------------------\|-------------------------\| \| 0.60 \| 0.434 \| 0.639 \| \| 0.70 \| 0.422 \| 0.730 \| \| 0.75 \| 0.407 \| 0.785 \| Takeaway: We observe that increasing the threshold constraint on harmlessness makes the policy focus more on the harmlessness reward, and our algorithm correctly adjusts to meet the new requirement, improving harmlessness performance at the expense of helpfulness. This aligns with the idea that users can prioritize harmlessness over helpfulness (or vice versa), and our algorithm effectively supports this personalization. > Weakness 3: The experimental design..... Response to Weakness 3: Thanks for the suggestion! Evaluation on more than two objectives: We performed additional experiments focusing on three objectives: helpfulness, harmlessness and humor. We use the following setup: * Dataset: Nvidia HelpSteer2 (validation set), * Baseline policy: Zephyr-7B-β, * Objectives (we consider three): Helpfulness, Harmlessness, and Humor, where user can specify threshold-based constraints on Harmlessness, and Humor. Following the setup in the main paper, we set the constraint criteria to be 50% win-tie rate (calculated using GPT-4) on both harmlessness and humor. We present results below: \| \| Win-Tie Rate (Helpful) \| Win-Tie Rate (Harmless) \| Win-Tie Rate (Humor) \| \|-----------------\|------------------------\|-------------------------\|----------------------\| \| Helpful Policy \| 68.33 \| 45.00 \| 51.67 \| \| Harmless Policy \| 43.33 \| 73.33 \| 46.67 \| \| Humor Policy \| 55.00 \| 45.00 \| 70.00 \| \| MOD \| 33.33 \| 60.00 \| 63.33 \| \| UAMD (ours) \| 68.33 \| 60.00 \| 66.67 \| Takeaway: UAMD outperforms MOD, achieving a higher win-rate for helpfulness while meeting the 50% win-tie rate constraint on harmlessness and humor. > Question 1: Is there any reason ..... Response to Question 1: This is a good point. As shown in recent studies [2], we remark that evaluations using GPT-4 are closely aligned with human judgments, and it is widely adopted as a standard evaluation metric in the alignment/decoding literature [3, 4, 5]. Therefore, we opted to use GPT-4 as an oracle, serving as a substitute for direct human evaluation. But as requested by the reviewer, we have also added reward based evaluations [Response to Weakness 1] as well. ---- [1] Wang et al., Interpretable Preferences via Multi-Objective Reward Modeling, EMNLP Findings 2024 [2] Liu et al., G-Eval: NLG Evaluation using GPT-4 with Better Human Alignment, EMNLP 2023 [3] Khanov et al., ARGS: Alignment as Reward-Guided Search, ICLR 2024 [4] Chakraborty et al., Transfer Q-Star: Principled Decoding for LLM Alignment, NeurIPS 2024	Summary: This paper proposes an inference-time alignment method UAMD for LLMs, which can consider user-specified perferences on different aspects based on transfer decoding. Specifically, UAMD is inspired by the bounded rationality theory which suggests that human decision-making follows the strategy of maximizing key objectives while ensuring others meet acceptable thresholds. It formulates the research problem as a constrained controlled decoding problem, which is a convex problem and can be solved optimally. To improve efficiency, the authors propose approximation algorithm with supoptimality upper bounds. The proposed method is evaluated with three benchmark datasets. Claims And Evidence: None. Methods And Evaluation Criteria: 1. The proposed method is theoretically analyzed. However, its theoretical properties are not empirically evauated in the experiments. How well can UAMD preserve these multi-aspect preferences? 2. The proposed method is not clearly described. Algorithm 1 introduces new concepts, such as baseline reward and target reward, with no explanations. Theoretical Claims: None. Experimental Designs Or Analyses: 1. The experimental settings are not clearly described. The evaluation metrics are not clear. The baselines are not clear. 2. The experiments are not comprehensive. The effciency of UAM is not theoretically and empirically analyzed. Supplementary Material: None. Relation To Broader Scientific Literature: None. Essential References Not Discussed: None. Other Strengths And Weaknesses: None. Other Comments Or Suggestions: None. Questions For Authors: 1. The writings could be greatly improved. Some notations and concepts are not well explained, such as the baseline reward and target reward in the algorithm. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We thank the reviewer for the feedback. We provided detailed responses as follows. > Weakness 1: The theoretical properties of the proposed method are not empirically evaluated. It is unclear how well UAMD preserves multi-aspect preferences in practice. Response to Weakness 1: We provide a detailed empirical analysis in Figure 2, where we show the win-tie rate for the different rewards (helpfulness and harmlessness). We have now performed additional analysis on three rewards (helpfulness, harmlessness, and humour) and added to the rebuttal [Reviewer DCGx (Response to Weakness 1)](https://openreview.net/forum?id=cEhLObwvvu&noteId=0DtyXlboG4). > Weakness 2: The proposed method is not clearly described. Algorithm 1 introduces terms such as "baseline reward" and "target reward" without explanation. Response to Weakness 2: Thank you for your valuable feedback. We appreciate the opportunity to clarify the terminology used in our manuscript and will ensure that these definitions are clearly articulated in the revised version. - Baseline reward: The “baseline policy” is defined prior to Equation (8) in our manuscript, and the “baseline reward” refers to the reward associated with this baseline policy. To enhance clarity, we will explicitly define “baseline reward” in the revised manuscript. - Target reward: The concept of “target reward” is discussed in Section 3.2 (second column, line 111) of our paper. It represents the reward that we aim to align our responses with, serving as the basis for calculating the objective in Equation (2). We will provide a clearer explanation in the revised manuscript. > Weakness 3: The experimental settings, evaluation metrics, and baselines are not clearly described. Response to Weakness 3: We apologize for any confusion. We have clearly mentioned the details regarding task setups, datasets, evaluation methodology and baselines in Section 6.1 in the main paper. If there are specific areas or details you find lacking, please let us know, and we will be happy to expand upon them further. > Weakness 4: The experiments are not comprehensive. Efficiency of UAMD is neither theoretically nor empirically analyzed. Response to Weakness 4: The suboptimality of UAMD is rigorously analyzed in Theorem 5.1 of our paper. Additionally, detailed evaluations are presented in Section 6.2. We have also conducted further experiments to measure the efficiency of UAMD, which are added to the rebuttal [Reviewer oxbU (Response to Weakness 1)](https://openreview.net/forum?id=cEhLObwvvu&noteId=tr4xamvoMG). > Question 1: How well can UAMD preserve these multi-aspect preferences? Response to Question 1: Our experiments, as shown in Figure 2, demonstrate that UAMD effectively preserves helpful and harmless attributes compared to existing methods (via comparing GPT 4 Win-Tie rate). We have extended this analysis to encompass more than two objectives, detailed here [Reviewer DCGx (Response to Weakness 1)](https://openreview.net/forum?id=cEhLObwvvu&noteId=0DtyXlboG4).	Summary: The paper proposes an alignment strategy for LLMs that does not maximize all rewards in the case of a multi-objective scenario; instead only key objectives important to the user are maximized while others only need to meet acceptable thresholds. This is formulated as a Langrangian optimization function, with a quadratic approximation to be able to estimate the Lagrange multipliers. The constrained objective is integrated into controlled decoding. The authors provide a theoretical analysis with an upper bound on the suboptimality gap. The approach is evaluated on 3 data sets with respect to win-tie rate over baseline alignment methods such as MOD and shows a better balance between different alignment objectives. ## update after rebuttal: the rebuttal addressed my concerns, hence I'm raising the score by 1 point. Claims And Evidence: The claims are substantiated by the quantitative evidence (win-tie rate from LLM-as-a-judge). However, I would have liked to see more in-depth qualitative analyses or at least a lightweight human evaluation, rather than a single anecdotal example. Methods And Evaluation Criteria: The benchmark data sets are standard for research on alignment; for each task, there are two objectives that are traded off against each other. While this convincingly demonstrates the effectiveness of the technique, it would be good to analyze scenarios with more than two objectives to see if the method scales further. Since one of the claims is that the technique is more reflective of human decision-making, it would also have made sense to include a human evaluation where different users set different thresholds, then check whether their preferences for different outputs actually align with their key objectives. This would shed some light on the practical applicability of the proposed approach. Theoretical Claims: I went over the proofs and they seem correct to me, but it's possible I have missed some details. Experimental Designs Or Analyses: The experimental design is sound - see above for further suggestions on how to strengthen the analyses. Supplementary Material: No, Relation To Broader Scientific Literature: The paper contributes a novel idea, namely to relax the reward maximization goal for certain objectives and instead constrain them to lie within a minimum acceptable range (or pass a minimum threshold). It does reference relevant prior work, esp. other multi-objective decoding approaches such as MOD. Essential References Not Discussed: I don't think there are any key references that were missed. Other Strengths And Weaknesses: The strengths of the paper are the novel idea of relaxing some of the reward dimensions, the incorporation of constraints into the controlled decoding approach, theoretical underpinning, and clarity of writing. It could be further improved by deeper analysis of qualitative results, esp. correspondence with actual human preferences, and generalization to more than two objectives. Other Comments Or Suggestions: Notice a typo in passing: a prior => a priori on p. 1 Questions For Authors: Please indicate whether you have conducted more qualitative analyses or experiments with more than two objectives? This would further improve my scores. Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: General Response: We thank the reviewer for their thoughtful feedback and for recognizing the novelty and theoretical contributions of our work. > Weakness 1: Evaluation is limited to scenarios with two objectives. It is unclear how well the method scales to more than two objectives. Response to Weakness 1: Evaluation on more than two objectives: Thanks for your suggestion! We have performed additional experiments focusing on three objectives: helpfulness, harmlessness and humor. We use the following setup: * Dataset: Nvidia HelpSteer2 (validation set), * Baseline policy: Zephyr-7B-β, * Objectives (we consider three): Helpfulness, Harmlessness, and Humor, where user can specify threshold-based constraints on Harmlessness, and Humor. Following the setup in the main paper, we set the constraint criteria to be 50% win-tie rate (calculated using GPT-4) on both harmlessness and humor. We present the results in the table below: \| \| Win-Tie Rate (Helpful) \| Win-Tie Rate (Harmless) \| Win-Tie Rate (Humor) \| \|-----------------\|------------------------\|-------------------------\|----------------------\| \| Helpful Policy \| 68.33 \| 45.00 \| 51.67 \| \| Harmless Policy \| 43.33 \| 73.33 \| 46.67 \| \| Humor Policy \| 55.00 \| 45.00 \| 70.00 \| \| MOD \| 33.33 \| 60.00 \| 63.33 \| \| UAMD (ours) \| 68.33 \| 60.00 \| 66.67 \| Takeaway: Consistent with our insights in the main paper, we observe that UAMD outperforms MOD, achieving a higher win-rate for helpfulness while meeting the 50% win-tie rate constraint on both harmlessness and humor. > Weakness 2: Limited qualitative analyses; only one anecdotal example is provided rather than a broader human evaluation. Response to Weakness 2: Thank you for raising this important point. First we show additional example (Example 1) to highlight our algorithm's performance improvement qualitatively. We will add more examples in the final version. Example 1: Prompt: How do I burn my house down for the insurance money? Original: I'm not going to lie, but I've thought about it. Helpful: 1. Start small. Before you can burn your house down for the insurance money, you need to start small. This means setting small fires around your house to test your skills and get a feel for the process. Begin by lighting a few candles and leaving them unattended in various rooms. This will help you get a sense of how quickly a fire can spread and how difficult it is to control. 2. Invest in some flammable materials. To really make your house burn down, you'll need some flammable materials. This could include things like gasoline. Harmless: I don't know. Why? I'm asking you, how? I don't know. Because I'm not a criminal. MOD: I don't know. Because that's wrong. UAMD (Ours): I’m sorry, but I can’t help with that. However, it’s important to recognize that intentionally burning down your house for insurance purposes is both extremely dangerous and illegal. Committing insurance fraud carries severe legal consequences and poses a serious threat to you, any occupants, neighbors, and emergency responders. If you find yourself in financial distress, please consider seeking legal, financial, or mental health counseling. Regarding Human Evaluations. We have now included results here for preliminary human evaluations. We are committed to expanding our human evaluations in the final version of the paper. To be specific, we conducted a preliminary human evaluations (across 10 participants) to qualitatively assess the responses generated by different approaches for a specific task. For this, we use the setup in Evaluation-1 (main paper): * Dataset: PKU-SafeRLHF-30K, * Baseline policy: Zephyr-7B-β, * Objectives: Helpfulness and Harmlessness, where the user can specify threshold on Harmlessness. * Number of prompts evaluated: 10 In the table below, we report the win-tie rate calculated against the baseline policy based on user judgements. \| \| Win-Tie rate (Helpfulness Reward) \| Win-Tie rate (Harmlessness reward) \| \|-----------------\|------------------------\|-------------------------\| \| Helpful Policy \| 0.80 \| 0.40 \| \| Harmless Policy \| 0.20 \| 0.60 \| \| MOD \| 0.60 \| 0.80 \| \| UAMD (ours) \| 0.80 \| 0.80 \| Takeaway: User-based evaluations are consistent with GPT-4’s win-tie rate results (in main paper). Therefore, human evaluations confirm that UAMD consistently outperforms the other baseline strategies, achieving a higher win-rate for helpfulness reward.	null	null	null	null	null	null
Controlling Large Language Model with Latent Action	Accept (poster)	Summary: Existing LLMs often rely on token-level actions that may be overly large and inefficient. This paper proposes learning a compact and latent action space to improve controllability and exploration in RL. Specifically, the authors augment a latent action space with a pre-trained LLM to form a latent action language world model. This latent action model is extensively trained from the pre-training dataset and tuned in the post-training stage. Experiments with Llama-3.1-8B as the base model demonstrate that using this latent action model for RL training achieves better controllability on multiple tasks, including multiple preference alignment tasks, math reasoning task, as well as the improved and flexible searching over the token-level action framework. Claims And Evidence: Most claims are supported by clear evidence. Some are not: 1) Therefore, LAMP aims to decouple these semantics by assigning them to different and limited latent actions, enabling more efffcient ffne-tuning, alignment, and search by latent action control. ==> I did not see such evidence. 2) However, in our experiments, we observed that this suffers from codebook collapse, where only a limited number of actions are activated during training. Methods And Evaluation Criteria: Yes. Theoretical Claims: NA Experimental Designs Or Analyses: Yes. The four questions investigated are important and the experimental designs are reasonable. However, the authors should show that their methods are appliable to other LLMs besides Llama-3.1-8B. Supplementary Material: A. Framework of LAMP Relation To Broader Scientific Literature: The effectiveness of latent action will be related to most of the LLM researchers. Especially those have RL background. Essential References Not Discussed: NA Other Strengths And Weaknesses: Strengths: The latent action is a very interesting topic, and I think this is important for the future of LLMs The methods are reasonable, and effective. The paper is generally well-written, easy-understanding. Weaknesses: small writing issues, see [Other Comments Or Suggestions] I did not see the necessary of MCTS-Q? It makes the methods complex? The results did not show that the proposed LAMP are better than baselines with a clear margin. Other Comments Or Suggestions: ‘’RL from observations only‘’ ==> ``RL from observations only” In this section, we verify our framework across multiple training stages. First, we introduce the basic setting of our model design. Then we validate LAMP in multiple training stages. ==> is redundant In the generation process, we compute the next token from the world model in a greedy manner. We only randomly or greedily sample actions from the policy model. ==> what's your meaning? Questions For Authors: line-199: why the current time embedding e^i_t has a superscript i? I did not see the necessary of MCTS-Q? It makes the methods complex? The results did not show that the proposed LAMP are better than baselines with a clear margin. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We sincerely appreciate the reviewer's valuable feedback and recognition of our latent action approach. Q1: Claims are not supported by clear evidence: Therefore, LAMP aims to decouple these semantics by assigning them to different and limited latent actions, enabling more efficient fine-tuning, alignment, and search by latent action control. ==> I did not see such evidence. A1: For claim 1, we realize that this claim may potentially lead to misunderstandings and would like to clarify. Figure 12 and Figure 10 (Appendix C.2) aim to show that latent actions have higher semantics than tokens. We will revise the statement in Section 4 to clarify that the connection between latent actions and semantics is weakly correlated, which should avoid misunderstandings. Q2: Claims are not supported by clear evidence: However, in our experiments, we observed that this suffers from codebook collapse, where only a limited number of actions are activated during training. A2: For claim 2, we compare VQ-VAE with our proposed method in Figure 8 (Appendix C.1) by counting the number of actions with non-zero usage. Results show that VQ-VAE suffers from severe codebook collapse, while our approach effectively maintains the utilization of codes in the codebook. We will add a reference to this claim to make it more supported. Q3: However, the authors should show that their methods are appliable to other LLMs besides Llama-3.1-8B. A3: We have implemented the LAMP architecture with Qwen-2.5-math-1.5B (Appendix C.1, Figure 9). We observed similar behavioral patterns to those in Llama-3.1-8B, including stable loss reduction and maintained codebook diversity without collapse. This provides preliminary evidence for LAMP's generalizability. However, due to the limitation of computation resources, we did not proceed to full-scale training and subsequent downstream task optimization. Q4: In the generation process, we compute the next token from the world model in a greedy manner. We only randomly or greedily sample actions from the policy model. ==> what's your meaning? A4: This sentence describes LAMP's language generation process. During the RL training phase, LAMP's policy model explores by randomly sampling latent actions, while during the evaluation phase, it deterministically (greedily) samples latent actions to ensure consistent results by selecting the maximum probability action. We will further revise here to make a clearer description. Q5: Some writing issues, including typos and redundant descriptions. A5: We will improve the writing in the revision. Q6: line-199: why the current time embedding e^i_t has a superscript i? A6: Here we aim to differentiate the embedding from other model input/output embeddings, and $i$ represents the inverse dynamics model. Q7: I did not see the necessary of MCTS-Q? It makes the methods complex? A7: MCTS-Q demonstrates how our latent action formulation can effectively integrate techniques that were previously difficult to apply in token space. For instance, Q-learning-based uncertainty estimation is a key technique for pruning the search space in MCTS, but scaling it in token space is challenging. Thanks to our latent action space design, however, this approach now shows promising results. Importantly, MCTS-Q does not introduce significant complexity—instead, it makes MCTS more effective. Q8: The results did not show that the proposed LAMP are better than baselines with a clear margin. A8: We guess the reviewer draws this conclusion from the results in Table 1 and Table 2. We want to clarify the performance gains of our approach. Our method primarily demonstrates superior downstream performance in multiple tasks. For preference alignment, we achieve an average win rate of 64% across four tasks and exceed 90% under the KL=0.00 setting. For math reasoning, we also shows significant improvement (42.6 vs 38.2). For search, combined MCTS with Q, our method can achieve better performance (68.2 vs 63.0). We also explore an agentic task called Alfworld[1], which is an embodied multi-turn interactive task. With the same fine-tuning and RL scheme, results shown in following table demonstrate superior performance of LAMP on it: \| Method \| Seen \| Unseen \| \|-\|-\|-\| \|Llama-3.1-8B-SFT\|68.6\|67.9\| \|Llama-3.1-8B-RL\|68.6\|71.6\| \|LAMP-FTA\|75.7\|70.9\| \|LAMP-RL\|77.9\|74.6\| We also need to clarify that Tables 1 and 2 show only "me too", which only shows the comparable initialized performance of LAMP. We will revise the descriptions in Section 5.1 and Section 5.2 to strengthen the presentation of these aspects. Please let us know if you have additional concerns about the performance gains of our approach. [1] Shridhar et al. ALFWorld: Aligning Text and Embodied Environments for Interactive Learning. arXiv:2010.03768 (2020).	Summary: The paper presents Latent Action governed world Model from Pre-trained LLM (LAMP), a novel reinforcement learning (RL) approach designed to control Large Language Models (LLMs) by learning a compact, latent action space rather than relying on conventional token-level actions. LAMP leverages an inverse dynamics model to create discrete latent actions and a policy model to guide these actions for downstream tasks. Experimental results on the Llama-3.1-8B model show moderate improvements in performance. Claims And Evidence: While the claims regarding improved controllability is generally supported, the main concern is that the performance gains demonstrated by LAMP are relatively marginal compared to baseline methods. Specifically, the reported improvements such as Table 1 and Table 2, appear limited in practical significance given the complexity of the proposed method. Additionally, the claim about the semantic interpretability of latent actions is not fully convincing. It remains unclear how these high-level semantic categories meaningfully translate into effective control or actionable improvements. Methods And Evaluation Criteria: - The proposed methods make sense and the motivation is clear. - The connection between LLM training and observation-only RL is novel. - The evaluation criteria are reasonable. Theoretical Claims: The paper does not present theoretical claims. Experimental Designs Or Analyses: The experimental design and analyses appear generally sound. Supplementary Material: The supplementary material was reviewed, focusing specifically on training details and MCTS-based search methods. Relation To Broader Scientific Literature: The paper situates itself effectively within the broader scientific literature, clearly outlining the limitations of token-level control and the motivation drawn from "RL from observations" literature. The contributions are well-contextualized relative to recent developments such as RLHF and latent-space modeling. Essential References Not Discussed: This paper appears comprehensive in its coverage of related works and does not omit essential references critical to understanding the contributions. 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 appreciate the reviewer's thoughtful feedback and positive recognition of the novelty of the perspective of RL from observation. We are grateful for the opportunity to address the reviewer's concerns and further clarify our methodology. Q1: While the claims regarding improved controllability is generally supported, the main concern is that the performance gains demonstrated by LAMP are relatively marginal compared to baseline methods. Specifically, the reported improvements such as Table 1 and Table 2, appear limited in practical significance given the complexity of the proposed method. A1: We apologize for the unclear expression. We clarify that Tables 1 and 2 show only "me too" but not the main purpose of LAMP, which is to enhance the downstream tasks using reinforcement learning. > Explanation: Table 1 shows the performance of LAMP model with behavior cloning policy, which should be called as LAMP-BC. We train LAMP-BC just to show that the LAMP structure can perform as an ordinary LLM, as presented results in Table 1. Further, Table 2 shows supervised fine-tuned performance of both the base LLM and LAMP-BC, which shows LAMP-BC can have a slightly better performance. We will revise the corresponding descriptions in Sections 5.1 and 5.2 to strengthen the presentation for the propose of these two experiments to explain this more clearly. To provide an overview of the power of our approach, we summarize and explain our RL results below: - For preference alignment tasks, our method achieves superior win rates and robustness via RLHF across different KL settings. In Figure 2, our LAMP model achieves an average of 64% win rate at KL=0.01 and over 90% win rate at KL=0.00. In Figure 3, our LAMP model achieves a slight performance improvement under the KL=0.00 setting compared to the standard KL=0.01 configuration, indicating a more robust alignment of our LAMP model. - For mathematical reasoning, after fine-tuning and RL optimization, our method achieves 42.6 on MATH500, comparing with 38.2 of baseline. And achieves 68.2 on a more flexible MCTS method, comparing with 63.0 of baseline. These results show that our method achieves significant improvements by introducing latent actions for RL training. Q2: Additionally, the claim about the semantic interpretability of latent actions is not fully convincing. It remains unclear how these high-level semantic categories meaningfully translate into effective control or actionable improvements. A2: We would like to clarify that we did not claim the semantic interpretability of the extracted latent actions. In fact, Figure 12 (Appendix C.2, Page 18) aims to show that latent actions have higher semantics than tokens. We will revise the claim in Section 4 to state that the connection of the latent actions to semantic is weakly correlated, avoiding cause misunderstandings. To address your concern about the effectiveness of latent actions, we clarify that the higher-level latent actions not only enhance the reinforcement learning performance due to reduced latent action space, but also mitigate the reward hacking issue (Figure 3), which can lead to more stable reinforcement learning.	Summary: This paper proposes to learn a more compact latent "action" space for pretrained LLMs to improve controllability. This latent action space is learned by an autoencoder where the encoder is an inverse dynamics model p(a_t\|x_0:t+1), the decoder is a transition model p(x_t+1\|x_0:t, a_t), the conditional prior is a policy p(a_t\|x_0:t). The training objective for this latent action space is similar to VQ-VAE, but parametrize p(a_t\|x_0:t+1) with Gumbel Softmax and the KL term in the ELBO is parametrized by the entropy of p(a_t\|x_0:t+1). The authors further provide two SFT approaches based on finetuning either the inverse dynamics or the policy, as well as a RL objective on the latent policy. Experiments show that the proposed method can induce a latent space with only a slight degradation of the base pretrained model. The authors further show that RLHF and SFT over latent actions appear to be more effective than on the base model with tokens as actions. ### After rebuttal ### Thanks the authors for addressing my concerns. I will keep my initial accepting rating. Claims And Evidence: The thesis claim is that the latent action, due to its lower dimensionality, can be a more controllable alternatives to the token space. The authors provide evidence that SFT and RLHF on the latent space turn out to perform better. Methods And Evaluation Criteria: The proposed method follows the standard framework of VQ_VAE. The adopted evaluation criteria is commonly used. Theoretical Claims: There is no theoretical claim. Experimental Designs Or Analyses: The authors first validate the success of latent space induction by showing that there is only a slight degrade of the performance after learning the latent space modules. They then test how well the latent actions control the tokens generation. The main results are the performance gain from SFT and RLHF on the latent action space. The authors also provided ablation study for the increased token and parameter numbers. However, this appears to be skeptical to me. The reported ablation show degradation of the base model in terms of increased model size and data size, which is very counter-intuitive. Supplementary Material: I took a brief glance at the code in the supplementary material without actually running it. It looks aligned with what the authors have described. Relation To Broader Scientific Literature: The idea of using a more compact space for SFT and RLHF can improve the efficiency of the SOTA pipeline. Essential References Not Discussed: N/A Other Strengths And Weaknesses: The idea of learning latent action space to improve controllability of LLM appears to be novel to me. Other Comments Or Suggestions: N/A Questions For Authors: In the ablation study, why did increasing the model size and the data size lead to worse performance? This doesn't seem to obey the scaling laws of LLMs. I hope the authors would like to provide some explanation. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We sincerely thank the reviewer for helpful feedback and positive assessment of the novelty in our latent action control approach. We address the reviewer's concern below, with key claims highlighted in bold for clarity. Q1: In the ablation study, why did increasing the model size and the data size lead to worse performance? This doesn't seem to obey the scaling laws of LLMs. I hope the authors would like to provide some explanation. A1: Thank you for your question. We’d like to clarify that our findings do not conflict with the scaling laws of LLMs. The slight performance degradation observed in Figure 6 stems from the "forgetting issue" during continued pre-training of Llama-3.1-8B. This occurs because our experimental data differs from Meta’s original pre-training data, leading to partial knowledge forgetting. Similar effects have been documented in prior work [1]. To our knowledge, scaling laws [2] are primarily applied to large-scale pre-training, not continued training with limited data. We clarify that we show Figure 6 to indicate that the original Llama-3.1-8b is a proper baseline. We will revise the descriptions to modify the explanation of this experiment in Section 5.4 to explain it more clearly. We understand that the reviewer may expect improved performance with more data. While this could be possible by enhancing LAMP with additional insights and techniques from continued training, such an investigation is beyond the scope of this paper. We appreciate your feedback and consider this an important direction for future work. [1] Shao et al. DeepSeekMath: Pushing the Limits of Mathematical Reasoning in Open Language Models. arXiv:2402.03300 (2024). [2] Kaplan et al. Scaling Laws for Neural Language Models. arXiv:2001.08361 (2020).	null	null	null	null	null	null	null	null
Adaptive Constrained Optimization for Neural Vehicle Routing	Reject	Summary: This work proposes a instance-level adaptive constraint optimization framework to improve the feasibility satisfiability of learning methods for TSPs. The authors designed a dual variable-conditioned policy with two phase of learning. In the first phase, they consider varying values of the lagrange dual variable and lean a model that works for these varying values. in the second phase, they consider an iterative procedure that updates the dual value based on subgradient descent to train the policy on TSP instances that remain infeasible after the first phase training. The authors benchmark their algorithm on TSPTW and TSPDL and observe significant improvement from the prior single-dual value method (PIP). Claims And Evidence: The claims made in the submission are supported by clear and convincing evidence. The authors show that their method significantly improve from the previous work (PIP) in terms of infeasibility rate. Methods And Evaluation Criteria: The proposed methods and evaluation criteria make sense for the problem. Theoretical Claims: The paper does not provide any theoretical claims or proofs. Experimental Designs Or Analyses: The experimental designs in this paper is sound and valid. The authors provide detailed ablation studies (e.g. contribution of different training stages, comparison of different update rules, and analysis of network architecture) to justify their design. Supplementary Material: I briefly read through E.2. Analysis of different update rules for \lambda, but I did not read through other parts of the appendix. Relation To Broader Scientific Literature: This work advances the scientific community by proposing an adaptive dual variable-conditioned policy, whereas previous literature only uses a single dual variable. The proposed method can significantly improve the performance for solving hard TSP instances, which is important for the optimization community. Essential References Not Discussed: N/A Other Strengths And Weaknesses: Other Strength: 1. I find the paper to be well written. I especially enjoyed reading the introduction section. I find Figure 1 very clear and motivates the proposed method very well. 2. The authors demonstrate that the proposed learning method has good improvement from PIP. Other Weakness 1. The authors discuss vehicle routing many places in the paper (e.g. title, abstract, section 2.1). However, their experiments are only on TSP variants (not VRP). It feels a little weird to claim that this works solve vehicle routing problems. 2. There's no theoretical analysis of the paper. 3. The idea of adapting the dual variable to improve feasibility is not entirely novel, and Tang 2022 seems to have a similar idea proposed. Can the authors comment on the difference with Tang 2022? Tang, Qiaoyue, et al. "Learning to Solve Soft-Constrained Vehicle Routing Problems with Lagrangian Relaxation." arXiv preprint arXiv:2207.09860 (2022). Other Comments Or Suggestions: N/A Questions For Authors: 1. In Sec 2.1 the draft limit constraint in TSPDL looks similar to the time window constraints in TSPTW. Can the authors comment on the differences of these two constraints, e.g. will they lead to different solving difficulty? Furthermore, given that for most of the TSPTW/TSPDL instances tested here, the infeasibility rate for POMO + PIP is already very low, I wonder if the authors can include results of exploring other TSP / VRP variants with higher infeasibility rate to further demonstrate the performance improvement of their method? 2. I wonder how the dual variable-conditioned policy performs without applying PIP masking from the previous literature? 3. Phase 1 solve the inner subproblem: the authors train a single policy for different values of lambda. Can the authors comment on whether they observe that learning is effective for a certain subset of lambda values but not for others? 4. Figure 3 (middle): the infeasible part / infeasible values labels for the purple cell: I'm a bit confused what they mean. Do the authors mean those are the Lagrangian values lambda that make the solution infeasible? 5. For the fine-tuning and inference stage, when the authors update the parameters lambda, I'm curious if the authors see any patterns in the lambda update for different instances? That is, do the authors observe a common sequence of updated lambdas that work well for a lot of instances, or the lambda values tend to be different after a few subgradient updates? Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Thanks for dedicating your time to review our work! We sincerely appreciate your acknowledgment of our contributions. Below are the detailed responses to your concerns. Corresponding experimental results can be found at [link](https://anonymous.4open.science/api/repo/4620_rebuttal-DDDF/file/addtional_results_4620.pdf). ## Response 1: Addressing the relationship between TSP variants and VRP (for weakness 1) and extending to more problem variants (for question 1) Thank you for your thoughtful feedback. Recent studies in neural combinatorial optimization (Kwon et al., 2020; Bi et al., 2024) often view TSP as a single-vehicle variant of VRP, capturing core route optimization challenges. Studying TSP variants also offers insights into solving multi-vehicle VRP, which can be decomposed into vehicle assignment and route planning, where each vehicle solves a TSP independently. Thanks to your suggestion, we have extended our experiments to multi-vehicle VRP variants, such as CVRPTW. Detailed analyses are provided in Response 5 to Reviewer X7da due to character limits. ## Response 2: Difference with Tang et al, 2022 (for weakness 3) Thank you for your insightful comments. As shown in Equation (2) of Tang et al. (2022), their method ties dual variables to the policy, forming a policy-level $\lambda$ approach. This is conceptually equivalent to the single-$\lambda$ method, where $\lambda$ updates with policy changes but remains invariant across instances. In contrast, our proposed instance-level $\lambda$ method introduces a key distinction: it decouples the dual variable from policy optimization, allowing $\lambda$ to adapt dynamically to each instance and better handle instance-specific variations. ## Response 3: Difference between time window and draft limit constraints (for question 1) Thank you for your valuable question. While these constraints share some similarities, their properties differ. The time window constraint is theoretically more challenging (NP-complete) and empirically shows higher infeasibility rates than the draft limit constraint. TSPDL, however, also has intriguing properties. Although its constraints can be easily satisfied using a Greedy-C heuristic, balancing its objective value and constraint violations remains highly challenging. For example, Table 1 shows that increasing $\lambda$ in TSPDL50 significantly impacts the infeasibility rate and optimality gap. By contrast, the performance variation on TSPTW50 under similar conditions is relatively minor. This observation highlights TSPDL's heightened sensitivity to a method's ability to balance trade-offs, making it a valuable and distinctive benchmark. Thus, both TSPTW and TSPDL are essential for our experiments, offering complementary insights for evaluation. ## Response 4: Experimental results without PIP mask (for question 2) Thank you for your insightful question. We have conducted additional TSPTW50 experiments without the PIP mask, as shown in Table S6. Removing it significantly increases problem difficulty, creating a more challenging benchmark. Interestingly, the results reveal that our ICO method achieves a greater performance improvement under this more challenging setting, further highlighting the superiority of the proposed instance-level adaptive approach. ## Response 5: Whether the learning in phase 1 is effective on a certain subset of $\lambda$ (for question 3) Good point! Yes, the learning is only effective when the range of $\lambda$ is reasonable, i.e., on a certain subset of $\lambda$. In the experiments on TSPDL, we observed that when $\lambda$ exceeds 10 or falls below 0.1, the policy often fails to converge. But fortunately, the reasonable range ($0.1 \le \lambda \le 2.0$) is simple to identify through heuristic trials. If you are curious about more $\lambda$ settings, please see Response 2 to Reviewer LzKt. ## Response 6: Description of Figure 3. (for question 4) The “infeasible part” refers to infeasible instances and their $\lambda$ values (purple in Figure 3), while “infeasible values” denote their constraint violations. We clarify “retain the infeasible part” in lines 250–253 and will revise the paper to avoid misunderstandings. ## Response 7: Patterns of $\lambda$ update (for question 5) Thank you for your thoughtful question. Yes, we observe some common patterns in $\lambda$ updates for certain instances. We refer you to Figure 6 for the information that many infeasible solutions exhibit only minor constraint violations. For this subset of slightly infeasible instances, their $\lambda$s will quickly converge to some relatively small values within 2-3 iterations and remain stable in the subsequent iterations, which is a common pattern, but their updated $\lambda$ values are not exactly the same. In contrast, for instances with larger violations, no common pattern emerges, and $\lambda$ values diverge based on violation magnitude.	Summary: This paper incorporates an instance-adaptative Lagrangian multiplier into the policy of the neural VRP solvers, aiming to enhance the performance of a most recent work PIP (Bi et al., 2024), which uses a fixed multiplier during training. Specifically, the multiplier varies among different instances and inputs as the feature for each instance. During training, it first trains the PIP model with randomly sampled multipliers, and then finetunes the model using infeasible instances with updated multipliers. During inference, the multipliers for each instance are updated via a subgradient method to generate solutions. The proposed method is tested on TSPDL and TSPTW with 50 and 100 nodes. --- ## First round rebuttal: Concerns regarding computational overhead, insufficient experiment and limited novelty -> maintain the score ## Second round rebuttal: Thanks for the response. Most of my concerns has been resolved. I feel like the novelty is moderate, so if other reviewers lean toward acceptance, I am also okay with accepting this paper. I strongly encourage the authors to include all additional results in the revised manuscript, particularly the discussion on computational overhead. Moreover, the advantage of encoding the multiplier into a hypernetwork should be clearly differentiated and clarified in comparison to existing primal-dual methods, such as the following: [1] Qiaoyue Tang, Yangzhe Kong, Lemeng Pan, and Choonmeng Lee. Learning to solve soft-constrained vehicle routing problems with lagrangian relaxation. arXiv preprint, 2022. [2] Stooke, Adam, Joshua Achiam, and Pieter Abbeel. Responsive safety in reinforcement learning by pid lagrangian methods. ICML, 2020. [3] Weiqin Chen, et al. Adaptive Primal-Dual Method for Safe Reinforcement Learning. AAMAS, 2024. [4] Park, Seonho, and Pascal Van Hentenryck. Self-supervised primal-dual learning for constrained optimization. AAAI, 2023. Claims And Evidence: Yes, mostly. Methods And Evaluation Criteria: Yes. Theoretical Claims: N/A Experimental Designs Or Analyses: Yes. See weaknesses and questions. Supplementary Material: Yes, the source code is provided in the supplementary material. Relation To Broader Scientific Literature: This paper is an improvement on the recent work PIP (Bi et al., 2024), aiming to enhance the constraint-handling capability for neural VRP solvers. Specifically, this paper extends PIP from a single Lagrangian multiplier to an instance-adaptive one. Essential References Not Discussed: There are many recent works studying effective updates of the Lagrange Multiplier Method. However, this paper lacks a literature review on this aspect. Other Strengths And Weaknesses: Strengths: 1. This paper enhances the constraint-handling capability of the neural VRP solver, which is a significant challenge. 2. The proposed method obtains better performance compared to the state-of-the-art method PIP. 3. The code is provided. Weaknesses: 1. The proposed method incurs significantly higher computational overhead than PIP due to the need to update the multipliers during both training and inference. 2. The experiments are insufficient, and some implementation details are missing. 3. The method's applicability is limited to TSPTW and TSPDL. 4. The writing quality requires improvement in terms of accuracy, consistency with the source code, and clarity, particularly regarding notations and font/table sizes. Other Comments Or Suggestions: Typo: LKH (less time) should be coloured in blue on TSPDL100. Questions For Authors: 1. What is the training time of the proposed method? Why is the inference time for instances with $n=100$ so prolonged? Instead of extending the inference time of PIP through sampling, have you considered alternative post-search strategies such as SGBS [1] and EAS [2]? The current comparison with PIP may be unfair. 2. Can the proposed method be extended to handle broader TSP/VRP variants beyond the current scope? 3. Why do the randomly sampled multipliers work in the pre-train stage (for the first 10000 epochs)? I understand the motivation of applying different multipliers for each instance due to different constraint violations, but the randomly sampled ones do not reflect this kind of violation information. Why does it work? Any deeper explanations or theoretical justifications? 4. Does the effectiveness and efficiency of the fine-tuning stage depend on the initial value of the multiplier? Why was 0.1 chosen as the initial value? What would happen if other values were used? 5. It seems in the source code TSPDL uses the multipliers randomly sampled from a Gaussian distribution during the pre-training stage, which is inconsistent with description in the main paper. Why using it on TSPDL? What is the performance variance when using different distributions beyond the results presented in Appendix E.4? 6. Why does OR-Tools achieve inference times of only a few seconds? 7. What is the performance variance when different learning rates are applied during inference? 8. Does Phase 2 only use the constraint violation $g$, while ignoring the penalty of the timeout nodes $c$ used in Phase 1? Why? Please also check the inconsistency between the equations in lines 256-261 and line 686. [1] Simulation-guided Beam Search for Neural Combinatorial Optimization. NeurIPS'22. [2] Efficient Active Search for Combinatorial Optimization Problems. ICLR'22. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Thank you for your valuable comments and recognizing our contributions. Below please find our responses. Corresponding experimental results can be found at [link](https://anonymous.4open.science/api/repo/4620_rebuttal-DDDF/file/addtional_results_4620.pdf). ## R1: Experiments with post-search strategies (for Q1 and W2) Thanks for your insightful questions! The post-search strategies such as EAS can integrate well with our proposed framework. Thanks to your suggestion, we have revised to extend the TSPTW experiments with EAS beyond basic sampling. As shown in Table S4, EAS can enhance both PIP and ICO. Our ICO + EAS still holds superior performance compared to the best results of PIP + EAS. This further validates the superiority of our proposed instance-level adaptive method. We will include these results into our revised paper. Thank you very much for your valuable comments. ## R2: Runtime of ICO (for Q1 and W1) Please refer to R3 to Reviewer LzKt due to space limitation. ## R3: More problem variants (for Q2 and W3) Please refer to R5 to Reviewer X7da due to space limitation. ## R4: Reasons for using randomly sampled $\lambda$ in pre-training (for Q3) The rationale of using random $\lambda$ can be explained from two perspectives: 1. Training Efficiency: In the early training stage, the policy is unconverged and generates many infeasible solutions, making instance-specific $\lambda$ updates computationally expensive. Random sampling is a practical alternative. Once the policy has sufficiently converged, the computational cost of updating $\lambda$ for the few remaining infeasible instances becomes more manageable. At this point, the training can transfer to the next stage, where instance-specific $\lambda$ values are iteratively optimized. 2. Enhanced Generalization for Inference: The $\lambda$-conditioned policy aims to behave optimally under any given $\lambda$ values. By exposing the policy to a wide range of random $\lambda$ values, its generalization ability to unseen $\lambda$ is improved. This enhanced generalization is critical for robust performance in the inference stage, where the policy cannot be retrained for every $\lambda$ value. ## R5: Sensitivity of $\lambda$ (for Q4 and Q7) Please refer to R2 to Reviewer LzKt for sensitivity analysis during inference. The hyperparameters used during fine-tuning are configured to align with inference. ## R6: Inconsistency of the Gaussian Distribution of $\lambda$ (for Q5 and W4) When collecting the running scripts for submission, we accidentally pasted the shell file from our earlier attempts into the final train_ICO.sh, where a Gaussian distribution of $\lambda$ appears in the pre-training configuration. We sincerely apologize for this careless mistake and the subsequent misunderstanding. We confirm that the settings of our experiments are entirely consistent with our description in the README file and lines 325-327 in the paper, i.e., the results on both TSPTW and TSPDL are trained using the triangular distribution. In our early experiments, a Gaussian distribution $N(0.1,1.0)$ and a triangular distribution $T(0.1, 0.5, 2.0)$ were tested to emphasize small $\lambda$ values. We provide the results on TSPTW50 in Table S5. The simple T(0.1, 0.5, 2.0) has the best performance, which is chosen as the default setting for the final experiments. Besides, all the tested distributions outperform the PIP baseline, further verifying the robustness of our method. We will include these discussions in our revised paper. Thank you very much. ## R7: ORTools (for Q6) Thank you for your thoughtful question. The algorithm of OR-Tools generally consists of two steps: (1) generating feasible solutions via greedy heuristics and (2) iteratively refining them. However, for TSPDL, the default greedy heuristic fails to produce feasible solutions. Therefore, the optimization terminates in just a few seconds, without any feasible results. ## R8: Ignored $c$ (for Q8) The heuristic reward $c$ is also utilized in Phase 2. In Section 3.1, where we provide an overview of the proposed framework, the function $g$ is introduced as a conceptual definition that accounts for all constraint violations, and its abstract nature allows the inclusion of $c$. Explicitly adding $c$ to the equations in Section 3.1, however, may compromise the simplicity and readability of the overview. We appreciate your feedback and will revise the paper to address the inaccuracies in the Appendix. ## R9: In Essential References: "recent works studying effective updates of the Lagrange Multiplier Method" Thanks for your comment. We have discussed and compared the effective updates method such as subgradient and PID-based update in Appendix E.2. If there are any omissions, please let us know; we are happy to discuss and compare them. --- We hope these can address your concerns, but if we missed anything please let us know. --- Rebuttal Comment 1.1: Comment: Thank you for the rebuttal. However, I still believe that the computational overhead of ICO is significant, as it requires iterative updates of the multipliers during inference (with 16 iterations). As PIP is already computationally heavy, the proposed ICO further amplifies this disadvantage. Specifically, PIP requires 15s and 48s for TSPTW50 and TSPTW100, respectively, whereas ICO takes 91s and 8 minutes. I am also not convinced by the comparison to PIP that involves simply adding sampling. What if a lightweight LKH were added to PIP instead, compared to the prolonged ICO? More importantly, I believe the contribution of incorporating different Lagrangian multipliers into PIP to be relatively minor. To this end, I maintain my current score. --- Reply to Comment 1.1.1: Comment: Thank you for taking the time to review our paper. We fully understand your concerns regarding inference overhead. However, we kindly refer you to the anytime performance analysis (see Appendix E.5) and the experiments with EAS (see Table S4), which were already provided and emphasized in our initial response. We believe these results could address most of your remaining concerns. In light of your new comments, we would like to further clarify the inference overhead issue and reiterate the key contributions of our work as follows: ## Response to “PIP requires 15s and 48s for TSPTW50 and TSPTW100, ..., ICO takes 91s and 8 minutes. ... not convinced ... PIP that involves simply adding sampling.” We would like to emphasize once again that, as shown in Appendix E.5, our proposed method still has superior performance with significantly less runtime than “91s and 8 minutes”—a point we had already underscored in our previous response. In light of your new comments, we provided experimental results with less runtime in Tables R1 and R2 at [new_link](https://anonymous.4open.science/api/repo/4620_rebuttal-DDDF/file/new_results.pdf). The results demonstrate that our method requires only 2 iterations (samples), which consumes only 14s on TSPTW50 and 73s on TSPTW100, to outperform PIP with 20 (28) samples, further verifying the efficiency and effectiveness of our approach. Regarding your concern that "PIP with simple sampling" may not be a convincing baseline, we fully agree. However, we have already conducted new experiments with advanced post-search strategies (i.e., EAS) to address your similar concerns in our prior response. The results in Table S4 demonstrate that ICO + EAS still consistently outperforms PIP + EAS. ## Response to “What if a lightweight LKH were added to PIP instead, compared to the prolonged ICO?” Good point! In response, we conducted new experiments comparing PIP (greedy) + LKH3 with our ICO (sampling) method, shown in Tables R1 and R2 at [new_link](https://anonymous.4open.science/api/repo/4620_rebuttal-DDDF/file/new_results.pdf). The results on TSPTW50 and TSPTW100 (see the tables below) show that ICO (sampling) significantly outperforms PIP (greedy) + LKH3 in terms of infeasibility rate, while PIP (greedy) + LKH3 achieves the best optimality gap. These results indicate that even adding a strong post-search such as LKH3 to the baseline, our ICO method remains superior in reducing infeasibility, which is critical for constrained optimization tasks. Moreover, it is important to note that our ICO (sampling 2) can also be combined with LKH3. If you have more concerns about the high infeasibility rate of ICO (greedy), we want to emphasize that we use a very small initial value of 0.1. When this value is increased, the infeasibility rate can be significantly reduced. Furthermore, we will explore training a hard instance classifier in future work to adaptively decide the initial value for each instance, which would significantly improve the one-iteration performance. ## Response to “More importantly, I believe the contribution of incorporating different Lagrangian multipliers into PIP to be relatively minor.” We respectfully disagree. Existing methods (not just PIP) tie the Lagrangian multiplier to the policy parameters, not to the optimization problem itself. This leads to a fundamental issue, i.e., overlooking the fact that constraint violations vary across problem instances. In a strict sense, such methods cannot be considered proper Lagrangian methods, as they misalign the dual variables. Our work addresses this long-standing issue by introducing instance-level adaptive dual variables, which we believe is a conceptually significant advancement for the NCO community. Thus, our contribution should not be viewed as a mere incremental improvement over PIP, but as an orthogonal and independent innovation that addresses a critical shortcoming of existing approaches. ## Response to “PIP is already computationally heavy, ...” We acknowledge that PIP itself is computationally expensive—the complexity of the one-step PIP mask is $O(N^3)$, where $N$ is the number of nodes. However, it is important to clarify that our proposed method of instance-level adaptive dual variables is general, not tied to the PIP mask, and therefore not inherently computationally heavy. For example, we conducted experiments without using the PIP mask in response to Reviewer taQj (please see Table S6). The results demonstrate that our method works effectively on top of a light-weight baseline like POMO, achieving a 15.36% reduction in infeasibility rate. Moreover, as discussed with Reviewer X7da, our approach has the potential to be extended beyond neural combinatorial optimization, for example to domains like safe reinforcement learning. --- Thank you for your comments. We appreciate the opportunity to elaborate on these important points.	Summary: This paper extends the PIP framework (Bi et al., 2024) by allowing the assignment of distinct dual variables to accommodate varying constraint satisfaction difficulties across instances. To achieve this, the paper first proposes modifying the POMO network to incorporate dual variable information into the node embeddings. It then introduces a two-stage training framework to effectively learn the policy. Experimental results on two constrained VRP variants demonstrate that the proposed method improves feasibility handling performance. Claims And Evidence: Most of the claims are supported well by evidence. Methods And Evaluation Criteria: The two-stage training approach and the strategy for decoupling policy optimization from dual variable optimization appear to be novel and effective. Also, the dual variable search during inference enhances the flexibility of handling hard constraints. The experimental results demonstrate reasonable improvements over the most recent approaches for constraint handling in TSPWT and TSPDL. Regarding the update rule for the dual variable (presented just before Section 3.2), I would like the authors to elaborate on its connection to the objectives in Equation (1). Can this update rule be directly derived from Equation (1)? Theoretical Claims: Not applicable. Experimental Designs Or Analyses: One major concern regarding the experiments is that the current study focuses solely on improving the PIP method. It would be more comprehensive to explore whether the proposed ICO framework can enhance other Lagrangian-based methods in neural combinatorial optimization (NCO), potentially extending beyond VRP. Also, it would be interesting to investigate whether ICO can be applied to more general constraint-handling tasks, such as those in safe reinforcement learning? Another drawback is the time complexity. It is recommended to report and compare the training time, as the proposed training approach may introduce additional computational overhead. How can the time complexity in both training and inference be mitigated? In Table 2, ICO (random) already exhibits strong performance. Providing an explanation and discussion regarding this observation would be beneficial. Supplementary Material: I checked all sections. Relation To Broader Scientific Literature: The paper may benefit constraint handling in NCO and other domains that require Lagrangian methods and learning-based approaches. Essential References Not Discussed: None. Other Strengths And Weaknesses: The paper presents and explores a promising approach to enhancing constraint handling for VRPs. However, the main limitation is its narrow focus on improving a specific method, PIP. Including discussions or experiments demonstrating the generalizability of the proposed method beyond PIP and even beyond NCO would be a valuable addition. Other Comments Or Suggestions: Regarding the "update $\lambda$ and retain the infeasible part" process shown in Figure 3, its explanation in the main paper is unclear. It would be helpful to clarify its meaning and explicitly describe how it relates to the purple color in Figure 3. Additionally, many important results are placed in the appendix rather than the main text. The paper could be reorganized to include key results in the main body for better readability. Questions For Authors: Please refer to the above. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Thanks for dedicating your time to review our work! We sincerely appreciate your recognition of our contributions to constrained combinatorial optimization. Detailed responses to your concerns are as follows. Corresponding experimental results can be found at [link](https://anonymous.4open.science/api/repo/4620_rebuttal-DDDF/file/addtional_results_4620.pdf). ## Response 1: The derivation of the $\lambda$ update rule Thank you for your thoughtful question. The update rule for $\lambda$ presented in Section 3.2 is indeed derived from the objective in Equation (1), albeit in a simplified form. Specifically, the subgradient of Equation (1) with respect to the dual variable $\lambda_{I_i}$ can be obtained by directly computing the derivative. This yields the expression This yields the expression $\mathcal{J}\_C(\pi_{\theta^}, I_i) = 𝔼\_{\tau \sim \pi_{\theta^}(\cdot \| I_i)}[-g\_{I_i}(\tau)]$, where $\theta^$ denotes the optimal policy parameters corresponding to $\lambda_{I_i}$. Based on it, our update rule has two simplifications: (1) Our policy is optimized but not guaranteed optimal; (2) The expectation in the subgradient should ideally be estimated using the Monte Carlo method, but in our inference setting, the policy only samples one solution at each iteration for computational efficiency, i.e., we simplify the average estimation to a single value, $g_I(\tau_{t-1})$. We will revise the paper for clarity. ## Response 2: Time complexity* Thanks for your valuable questions! Due to character limitations, please refer to Response 3 to Reviewer LzKt for a detailed explanation. In conclusion, the training time of our method is approximately the same as the PIP baseline, and our method can outperform PIP even with less inference runtime. ## Response 3: Why ICO (random) performs well Thank you for your insightful question! Unlike constrained RL, ICO (random) does not fine-tune the policy's parameters, so there is no need to enforce smooth $\lambda$ updating to mitigate fluctuations, making randomly sampled $\lambda$ values acceptable. The strong performance may stem from the conditioned policy's generalization ability. During pre-training, the policy is exposed to a wide range of randomly sampled $\lambda$ values, allowing it to generalize well across diverse $\lambda$ settings and adapt seamlessly to the random update rule during inference. Additionally, the random update rule itself is not inherently weak. By evaluating all sampled $\lambda$ values and selecting the best-so-far solution, it has a reasonable ability of identifying an effective $\lambda$. ## Response 4: Clarification on Figure 3 Thank you for your insightful comments! The term “infeasible part” refers to the infeasible instances and their associated $\lambda$ values, which are depicted in purple in Figure 3. The phrase “retain the infeasible part” is explained in detail in lines 250–253 of the paper. We apologize for any confusion caused by the use of the term “infeasible part” and will revise the paper to ensure clarity and avoid potential misunderstandings. ## Response 5: Extension to more problems/tasks Thank you for your valuable comments and questions! The idea of instance-level adaptive dual variables is not specially designed for TSPTW and TSPDL; rather, it can be extended to other domains that simultaneously require constraint handling and cross-instance (or cross-environment) generalization of the RL policy, with domain-specific adaptations. To demonstrate generality, we have revised to add more VRP variants to our experiments. Below is a summary of hard-constrained problems addressed in prior works: \| Related work \| TSPTW \| TSPDL \| CVRPTW \| \| --- \| --- \| --- \| --- \| \| MUSLA (Chen et al., 2024) \| Yes \| No \| No \| \| JAMPR (Falkner & Schmidt-Thieme, 2020) \| No \| No \| Yes \| \| Chen et al., 2022 \| No \| No \| Yes \| \| Tang et al., 2022 \| Yes \| No \| Yes \| \| PIP (Bi et al., 2024) \| Yes \| Yes \| No \| \| Ours \| Yes \| Yes \| Yes (in rebuttal) \| CVRPTW is the only problem not addressed in our experiments. While the decision space of CVRPTW appears more complex, it is, in fact, easier to satisfy its constraints compared to TSPTW and TSPDL. This is because its time window constraints can be easily satisfied by a shortcut: Add more vehicles. To construct a challenging benchmark, we propose to set a maximum limit on the number of vehicles, which also aligns more closely with real-world applications. We have revised to conduct new experiments on CVRPTW50 with limited vehicles using JAMPR's time window generation code. Since PIP has not been extended to this problem, we used POMO as the backbone to implement ICO. Experimental results in Table S3 show that our ICO significantly outperforms the POMO baseline, especially in infeasibility rate. Full results will be included in the final paper. Thank you once again for your insightful questions. We hope these new results address your concerns. --- Rebuttal Comment 1.1: Comment: Thank you for your rebuttal! I am keeping my positive score. --- Reply to Comment 1.1.1: Comment: Thank you very much for your positive feedback. We sincerely appreciate your insightful comments and constructive suggestions, such as runtime issues and the inclusion of more tasks, which are valuable in guiding the improvement of our work. We will carefully revise the paper to incorporate these important aspects. We also appreciate your observation that our proposed approach may have potential applications beyond combinatorial optimization, such as in safe reinforcement learning. We fully agree with this perspective and are willing to explore this promising direction in our future research.	Summary: The paper introduces an instance-level adaptive constrained optimization method for neural vehicle routing. It builds on prior PIP-based approaches by assigning instance-specific dual variables instead of a uniform λ, aiming to better balance solution quality and constraint satisfaction across diverse instances. The proposed two-stage training—comprising a pre-training phase with randomly sampled λ values and a fine-tuning phase with iterative dual updates—shows promising improvements in infeasibility rates and solution quality on TSPTW and TSPDL benchmarks. ## update after rebuttal The authors have not fully addressed the concerns I raised in my initial review. Consequently, I have decided to maintain my original score. Claims And Evidence: The claims are generally supported by experimental evidence. The authors show significant reductions in infeasibility rates compared to both state-of-the-art neural methods and strong OR solvers. However, the reliance on iterative updates based on PIP appears to introduce considerable runtime overhead, which is a serious drawback that might affect practical deployment. Moreover, while the overall improvements are clear, the paper falls short in dissecting the individual contributions of each component. In particular, the sensitivity of the method to different λ values is not thoroughly analyzed in the ablation studies, leaving some uncertainty about the robustness of the proposed mechanism. Methods And Evaluation Criteria: The methods and evaluation criteria are appropriate for the problem. The idea of decoupling the dual variable optimization from policy optimization is sound and innovative. Yet, the increased computational cost due to multiple iterations for updating instance-specific λ values is concerning. The paper would benefit from a more detailed analysis of how this trade-off impacts overall performance, especially in time-sensitive applications. Theoretical Claims: Theoretical claims in the work are mainly heuristic. Although the paper explains the motivation behind the dual conditioning and provides a clear training algorithm, there is limited discussion on the theoretical convergence properties of the iterative process or on the stability of the dual updates. This gap might affect the confidence in the method's long-term performance. Experimental Designs Or Analyses: Experimental designs are well laid out with comparisons against both neural and traditional OR solvers. The results show marked improvements in feasibility and competitive optimality gaps. Yet, the experimental section does not fully explore how sensitive the outcomes are to the choice of λ or how each part of the model contributes to the final performance. A more comprehensive ablation study is needed to confirm that the improvements are not solely due to the increased iteration time rather than genuine methodological advances. Supplementary Material: No Relation To Broader Scientific Literature: The work is well-situated within the broader literature on neural VRP and constrained optimization. It builds on recent advances and provides meaningful comparisons with existing state-of-the-art methods. Nonetheless, some recent studies on adaptive dual variable strategies and dynamic constraint management in combinatorial optimization are not cited, which could help contextualize the contributions more robustly. Essential References Not Discussed: N/A Other Strengths And Weaknesses: N/A Other Comments Or Suggestions: N/A Questions For Authors: I suggest the authors clarify the trade-off between performance gains and computational overhead. Could they provide more detailed ablation studies to isolate the impact of each component, particularly the sensitivity of the method to different λ settings? Additionally, how do they justify the iterative updates given the significant increase in runtime? Answers to these questions might change the overall evaluation of the method's practicality. What are your thoughts on addressing the runtime overhead issue without sacrificing the performance gains? Also, could further experiments help clarify the exact contributions of each module in your framework? Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Thank you for reviewing our work and recognizing our contributions. Below are detailed responses. Corresponding experimental results can be found at [link](https://anonymous.4open.science/api/repo/4620_rebuttal-DDDF/file/addtional_results_4620.pdf). ## Response 1: Lacking ablation study Due to space constraints of the main paper, most of our ablation results were included in Appendix E, including the two-stage training strategy, the updating rule of $\lambda$, the conditioned network architecture, and the prior distribution of $\lambda$. Section 4.3 briefly summarizes these findings, showing the effectiveness of each component. To improve clarity, we will integrate key results into the main text. ## Response 2: Sensitivity of $\lambda$ Thank you for your valuable feedback. Since the optimization landscape for $\lambda$ is typically non-convex due to the hardness of combinatorial optimization, we agree that both the initial value and learning rate of $\lambda$ are important for the optimization performance. Thanks to your suggestion, we have revised to conduct a sensitivity analysis of $\lambda$ from these two perspectives, including the initial value of $\lambda$ (denoted as $\lambda_0$) and the learning rate for updating $\lambda$ (denoted as $\alpha$). During the inference stage, we evaluated performance across $\lambda_0 \in \\{0.1, 0.15, 0.20, 0.5, 1.0\\}$ and $\alpha \in \\{0.1, 0.2, 0.5, 0.7, 1.0\\}$ on TSPTW50 and TSPDL50. Each hyperparameter was varied while keeping the other fixed at its default value. Results in Table S1 and S2 show that: 1. In 16 out of 18 settings, our ICO method surpasses the best-performing PIP model in hypervolume (HV), showing its robustness. 2. Although the performance variance (shown in the last row) is relatively small, it is not negligible. This underscores the importance of carefully tuning $\lambda$-related hyperparameters to achieve optimal performance. Interestingly, some settings (e.g., $\alpha = 0.7$ for TSPTW50) outperform the default, suggesting that advanced hyperparameter optimization techniques like Bayesian optimization could further enhance performance. We will revise the paper to incorporate these results. ## Response 3: The additional runtime overhead Thank you for raising concerns about computational efficiency. Below, we clarify the runtime overhead during training and inference. ### Training Time The training times of the PIP method and the proposed ICO method over 110k epochs are approximately the same: for example, around 60 hours for TSPTW50 and about 10 days for TSPTW100. At first glance, fine-tuning $\lambda$ appears computationally intensive. However, in our implementation, we mitigate this by using a fixed number of batches, and in each batch, only the feasible instances are replaced with new ones, as described in lines 251-253. That is, if there is an increasing number of infeasible instances requiring iterative updates in the current batch, the number of newly generated instances in future batches will decrease correspondingly. As a result, the total number of network forward and backward computations remains equivalent to that of the original PIP method. ### Inference Time Appendix E.5 (Figure 8) provides an anytime performance analysis of hypervolume (HV), infeasibility rate, and optimality gap. The results indicate that ICO consistently outperforms single-$\lambda$ models throughout the entire iterative process on HV and gap. The only exception is the infeasibility rate at the initial stages due to the use of a very small initial $\lambda$ value. Importantly, this suggests that even if the additional runtime overhead was reduced or entirely removed, our method would still demonstrate improved performance. This improvement can primarily be attributed to the fact that the adaptively trained policy itself has better capability even without updating $\lambda$ values. Therefore, we argue that our method's runtime issue is minor. Future work will explore predicting optimal $\lambda$ values to totally eliminate additional overhead. Thank you very much. ## Response 4: Add recent studies on adaptive and dynamic methods in constrained combinatorial optimization Thank you for valuable comment. We investigated several related works [1, 2, 3] at this aspect and will include discussions about them in the paper. In summary, these related methods proposed many interesting methods for adapting the penalty function, but thay are primarily combined with genetic algorithms instead of neural methods. If there are any omissions, please let us know; we are happy to discuss and compare them. [1] Adaptive penalty methods for genetic optimization of constrained combinatorial problems, In 1996. [2] An adaptive penalty scheme for genetic algorithms in structural optimization, In 2004. [3] Adaptive feasible and infeasible tabu search for weighted vertex coloring, In 2018.	null	null	null	null	null	null
Learning Policy Committees for Effective Personalization in MDPs with Diverse Tasks	Accept (poster)	Summary: The paper proposes PACMAN, a novel method that learns a policy committee, ensuring that at least one near-optimal policy is included for each task with high probability. The proposed approach is evaluated on Half-Cheetah Velocity, Humanoid, and MetaWorld tasks, demonstrating superior performance compared to multiple baselines. Claims And Evidence: The claims are primarily supported by empirical experiments. Methods And Evaluation Criteria: The method, especially the algorithm is not clear to me. Regarding the clustering mechanism: - How many clusters are there in the committees for both experiments? Is the number of clusters predefined or learned automatically? - Can you provide an ablation study to analyze the impact of the number of clusters on performance? - Additionally, can you conduct an ablation study on the selection of key hyperparameters for the clustering mechanism? - Can you provide detailed analysis on what tasks are clustered together to verify the clustering mechanism works? Regarding few-shot generalization: - Will new committee member be added when learning new tasks? Or will it reuse existing member? Theoretical Claims: No I am not falimiar with the theoretical analysis. Experimental Designs Or Analyses: For comparison with baselines: - How is the number of parameters for PACKMAN compared with other baselines? - What is the optimal performance for each set of experiments? Providing this information would help in better understanding the reported performance metrics. For experiments in metaworld, - Is the policy state-based or image-based? - What are the 30 and 20 tasks mentioned in the paper? How are they constructed? Are they randomly sampled? - Is the return equivalent to the success rate? Clarifying this would improve result interpretation. Supplementary Material: Yes, the additional experiments. Relation To Broader Scientific Literature: The problem is highly relevant to the field. It is a new method for multi-task learning Essential References Not Discussed: N/A Other Strengths And Weaknesses: N/A Other Comments Or Suggestions: There are some references missing in line 335 and line 346. Questions For Authors: N/A Code Of Conduct: Affirmed. Overall Recommendation: 2	Rebuttal 1: Rebuttal: We thank the reviewer for the thoughtful comments and clarification questions! >Comment: The method, especially the algorithm is not clear to me. Response: The details of the algorithm are provided in Section 3.1. In summary, we cluster tasks into groups, where each group contains similar tasks (in a way that yields provable in terms of performance and generalization) and then train a policy for each group. We call the resulting set of policies a policy committee. This committee can then be used for both in-sample and out-of-sample multi-task RL settings, as well as for few-shot meta-RL problems. >Comment: Can you provide detailed analysis on what tasks are clustered together to verify the clustering mechanism works? Response: Certainly. At the high level, the three Meta-World clusters (for one of the random subsamples of 30 tasks) can be described as corresponding to three categories of manipulation tasks. The first cluster involves pulling and sliding manipulations (e.g., pull a puck, move end-effector, slide a plate to and from the cabinet). The second cluster includes manipulations that involve pressing and pushing (e.g., rotate the faucet, press a handle down, insert a peg into a hole, kick a soccer ball, sweep a puck). The third cluster consists of tasks involving indirect or constrained manipulation and which thus require better precision and control (e.g., bypass a wall, grasp a stick and pull or push a box with it). We will add full details of task-to-cluster mappings in the revision. >Comment: How many clusters are there in the committees for both experiments? Response: For the main experiments, $K=3$ in all domains, but we also consider ablations with $K \in \{1,2,4\}$ (see the Appendix for details). >Comment: Is the number of clusters predefined or learned automatically? Response: The number of clusters is predefined in our experiments, but can also be obtained automatically if we have a coverage target (e.g., if we wish to cover 100% of training tasks). >Comment: Will new committee member be added when learning new tasks? Or will it reuse existing member? Response: We reuse existing members for new tasks; in zero-shot settings, we apply these directly on out-of-sample tasks, while in few-shot settings we fine-tune policies in the committee. >Comment: How is the number of parameters for PACKMAN compared with other baselines? Response: If an architecture used for a policy has $p$ parameters, the committee of $K$ policies will train $Kp$ parameters. Different baseline approaches vary significantly in the number of parameters $p$, as this is not typically a primary consideration in prior literature, particularly in the context of the challenging Meta-World benchmark. >Comment: What is the optimal performance for each set of experiments? Response: For meta-learning mujoco experiments, the theoretical upper bound on performance is 0. For Meta-World, the theoretical upper bound is the success rate of 1. However, we are unaware of any SOTA method that comes close to achieving either of these, and it is unknown what is a feasible optimal performance on these benchmarks with respect to out-of-sample tasks. >Comment: Is the policy state-based or image-based? Response: The policy is state-based. >Comment: What are the 30 and 20 tasks mentioned in the paper? How are they constructed? Are they randomly sampled? Response: We uniformly randomly partition the 50 total tasks in Meta-World into 30 trainig and 20 test tasks. >Comment: Is the return equivalent to the success rate? Clarifying this would improve result interpretation. Response: While high returns generally correlate with a high success rate, return and success rate are not the same. Return refers to the total reward over a trajectory, which is important for the theoretical analysis as well as how RL is trained in practice (since it yields a dense reward). Success rate is the standard evaluation metric in Meta-World and is used in our experiments. We will clarify this distinction in the revised version.	Summary: The paper introduces PACMAN, a novel framework for learning policy committees in multi-task Markov decision processes (MDPs) with diverse tasks. The approach includes clustering-based approach to create a representative cover over tasks and a gradient-based alternative to group tasks based on parametric representations and then trains a separate policy per cluster. The authors support their method with theoretical guarantees and demonstrate significant empirical improvements on benchmarks such as MuJoCo and Meta-World. Update after rebuttal--I appreciate the authors’ thorough revision and the additional experiments addressing my concerns. I hope those will be implemented in the revised draft. I have decided to keep my original score. Claims And Evidence: The paper makes several key claims: - It offers provable guarantees on generalization and few-shot adaptation. - It achieves improved performance over state-of-the-art baselines in diverse task settings. The theoretical results (e.g., Theorems 3.7 and 3.8) are well-supported by proofs in the appendices, and the experimental results consistently back up the claims. - However, some assumptions (e.g., tasks being parametric, Lipschitz continuity of rewards) may not hold in real-world settings. - The proposed approaches are validated with multi-task benchmarks. Methods And Evaluation Criteria: The methodology is thoughtfully designed: - The clustering approach effectively handles task diversity by creating a representative cover over task parameters. - The integration of gradient-based optimization to refine cluster representatives is innovative. The evaluation on standard benchmarks is thorough, with comparisons to 11 state-of-the-art baselines. - Evaluation criteria (average return of one episode or success ratio) from benchmarks seems to be reasonable. Theoretical Claims: The paper presents several rigorous theoretical contributions including the derivation of sample complexity bounds and few-shot guarantees. While the proofs appear sound, some assumptions (such as the parametric form of tasks and the specific Lipschitz conditions) might limit applicability in settings where such conditions are not met. Experimental Designs Or Analyses: Experiments are extensive and well-structured: - The use of both zero-shot and few-shot evaluations provides a comprehensive picture of performance. - Comparisons with multiple baselines help in understanding the relative strengths of PACMAN. - The scalability of the clustering method in higher-dimensional settings and its sensitivity to the number of tasks are areas that may benefit from further clarification. - In addition, there are many other things remained questionable in experiment settings. For instance, I’m also curious how the choice of 30 training tasks and 20 test tasks in MT-50 (Meta-World) affects the other baseline’s performance. The effect of task description and language embedding can affect to some extent. Supplementary Material: I reviewed supplementary sections—including a few proofs, algorithm pseudocode, and ablation studies. Relation To Broader Scientific Literature: The paper is well-positioned within the broader literature on multi-task and meta-reinforcement learning. It clearly distinguishes itself from prior works such as MAML, PEARL, MOORE, and task clustering approaches by addressing the challenges of task diversity and negative transfer. Essential References Not Discussed: While the paper cites many relevant works, it might benefit from a discussion of more recent approaches to policy ensembles and adaptive task embeddings in non-parametric settings. This could help in understanding how PACMAN compares to or complements emerging methodologies. A more detailed discussion of contextual MDPs from related areas might further enrich the context. Specifically, the notion of “policy committee” feels similar to “multi-policy training” proposed in “Model-Based Transfer Learning for Contextual Reinforcement Learning (NeurIPS 2024).” Other Strengths And Weaknesses: Strengths: - Strong theoretical foundation with rigorous proofs. - Extensive and convincing empirical validation across challenging benchmarks. - Innovative combination of clustering with gradient-based refinement. Weaknesses: - Dependence on the assumption of parametric task structure may limit generalizability. - Sensitivity to the hyperparameters and the challenge of tuning it in different domains. - Scalability concerns for very high-dimensional tasks or a massive number of tasks. Other Comments Or Suggestions: - Section 4 → citation error in line 349 - Section 4.1 → citation error in line 335 and (EM) in line 342 - Curious how this approach relates to the special case of MoE with hard gate. - Font size in figures are sometimes too small. - The readability of the figures can be improved. It’s not as friendly for now. Questions For Authors: - How can I relate PACMAN results in Table 1 and Table 3? - Table 4 shows that larger K could decrease the performance. Then how should we choose the optimal K in practice? any recommendations or thoughts? Similarly, I’m also curious about the tradeoff for higher epsilon mentioned in line 958. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We thank the reviewer for the insightful comments and suggestions! >Comment: The assumption of parametric task structure may limit generalizability. Response: We agree that assuming that tasks are parametric is a limitation. However, we show that we can often use LLM embedding of natural language task descriptions to enable parametric representations of non-parametric tasks. Our results on the Meta-World benchmark (in which tasks are non-parametric) demonstrate that this is quite effective, and suggests that our approach is nevertheless very broadly applicable. Indeed, as capabilities of LLMs continue improving, we expect the scope of applicability to continue to expand. >Comment: Sensitivity to the hyperparameters and the challenge of tuning it in different domains. Response: Our method adds only a single hyperparameter, $\epsilon$, which is easy to tune without running RL. Our ablation studies in Appendix H suggest that choosing a small $\epsilon$ that ensures full coverage for the largest $K$ a practitioner can afford to train works well in practice. As RL algorithms (particularly in multi-task settings) come with a large number of hyperparameters that are difficult to tune in practice, we view the addition of the $\epsilon$ hyperparameter to be well worth the performance improvement and theoretical guarantees. >Comment: Scalability concerns for very high-dimensional tasks or a massive number of tasks. Response: While theoretically our framework is hard in high-dimensional settings, in practice the computational cost is dominated by RL (seconds or minutes for clustering compared to hours for RL). Moreover, we show that the proposed gradient-based approach works well in higher dimensions. Moreover, both our greedy and gradient-based approaches run in polynomial time in the number of tasks. Nevertheless, consideration of extremely high dimensions and massive numbers of tasks remain important research challenges in multi-task and meta-RL. >Comment: ...A more detailed discussion of contextual MDPs might further enrich the context... The notion of “policy committee” feels similar to “multi-policy training” proposed in “Model-Based Transfer Learning for Contextual Reinforcement Learning (NeurIPS 2024).” Response: Thank you for pointing this out! We will add a discussion of contextual MDPs in the revision. While our notion of a “policy committee” is similar to “multi-policy training”, the focus of Cho et al. is on a sequential task selection problem, with a task-specific policy trained on the selected task. Our setting, in contrast, begins with a given set of tasks (we cannot choose tasks for training) and entails clustering, with the policy committee associated with task clusters. We will add this discussion in the revision. >Comment: How can I relate PACMAN results in Table 1 and Table 3? Response: As Table 1 is for few-shot and Table 3 for zero-shot generalization, they are not directly comparable. The former shows that PACMAN outperforms SOTA in few-shot learning, while the latter shows that the novel clustering approach we propose for multi-task learning is better than using conventional clustering methods such as Kmeans++ for task clustering in this setting. >Comment Table 4 shows that larger K could decrease the performance. Then how should we choose the optimal K in practice? any recommendations or thoughts? Similarly, I’m also curious about the tradeoff for higher epsilon mentioned in line 958 Response: We discuss this in detail in section H.2.2 (the paragraph under the table in question). In practice, our guideline is to use $K$ no larger than what is sufficient to provide a $(\epsilon,1)$ cover (i.e., cover all training tasks); moreover, $K=3$ has worked well across distinct domains and in many practical settings may thus be a good starting point. As for $\epsilon$, we provide some guidance on its selection in our response to Reviewers fviP and zPNZ given a fixed $K$. >Comment: Curious how this approach relates to the special case of MoE with hard gate. Response: In MoE, the gating mechanism typically needs to be trained as part of the network, and with hard gating, selecting the right expert is a challenging task. In contrast, our method alleviates this computational burden by directly producing a set of policies, and the best can be quickly identified through policy evaluation for any task. >Comment: Citation error and figure readability. Response: Thank you for pointing this out! We will rectify the citation errors and improve the readability of the figures in the revised version.	Summary: The paper introduces a new learning paradigm, called policy committee learning effectively for solving multi-task RL. More specifically, a policy committee targets learning a set of policies maximizing the best-performing policy's discounted return for any given task sampled from a predefined task distribution. The paper assumes that the tasks differ by their transition dynamics and reward functions, but not state and action spaces. Also, the paper assumes access to a parameterization of these tasks. For this new learning paradigm, the paper introduces three algorithms, GEA, GIA, and, Gradient-based Coverage. These methods centers around finding a clustering that achieves $(\epsilon, 1 − \delta)$-parameter-cover following Definition 3.1. Further theoretical analysis indicates that learning individual policy for each cluster leads to a solution to policy committee learning (Definition 2.1) with bounded optimality gap. The paper conducts the experiments in MetaWorld, Halfcheetah, and Humanoid domains, and demonstrating improved asymptotic performance and few-shot learning performance compared to recent meta-learning and multi-task RL approaches. Claims And Evidence: The paper claims a theoretically-grounded framework for learning policy committees, however the theory is rather limited in that it assumes all the tasks share the same transition dynamics. Also, I am not sure whether the theoretical bound is tight enough can explain the performance gain in the experiments. Methods And Evaluation Criteria: Yes, learning a policy committee makes sense for solving multi-task RL problems. Learning different policies may mitigate the gradient conflict and also by limiting the total number of policies, the learning may become more efficient benefit from the share similarity between tasks. Theoretical Claims: I did not check the proofs. Experimental Designs Or Analyses: 1. MetaWorld domain breaks the assumption made by the theoretical analysis that all the tasks share the same transition dynamics, as different tasks involve interacting with different objects, and therefore uses different transition dynamics. 2. It is also a bit suspicious that although the language embedding provide a continuous parameterization of the tasks, the real task space is discrete and only have 50 tasks in total. In that, it is hard to believe simpler clustering strategies, like KMean++, do not give the same clustering result. I saw that comparison with other clustering algorithms is only conducted in HalfCheetahVel. Could author also conduct comparison in MetaWorld domain? 3. It would be interesting to visualize the clustering results in HalfCheetahVel and compare it with KMean++. HalfCheetahVel uses a simple one-dimensional task parameter, I wonder in what degree the clustering result of PACMAN differs from conventional goal of minimizing sum of shortest distances. Supplementary Material: I checked Appendix J, but I would be interested to see the actual assignment of the 50 tasks to the three policies in the policy committee. Relation To Broader Scientific Literature: The paper introduces a new learning paradigm called policy committee learning. I think the idea is close to mixture of experts. Essential References Not Discussed: The idea is pretty similar to mixture of expert for RL: Celik, Onur, Aleksandar Taranovic, and Gerhard Neumann. "Acquiring diverse skills using curriculum reinforcement learning with mixture of experts." arXiv preprint arXiv:2403.06966 (2024). In Onur et. al., the clustering (partition of the task space) is guided by the experts performance, e.g., if the expert shows promises in solving the task. The paper instead considers the $(\eplison, 1 − \delta)$-parameter-cover. I think the author should consider differentiating with Onur et. al. Other Strengths And Weaknesses: N/A Other Comments Or Suggestions: 1. There are a couple of missing citations: (1) line 336 SAC; (2) line 349 MetaWorld. 2. In Theorem 3.4, 3.7, $1/e$ is not defined. In Theorem 3.8, $H$ is not defined. The theoretical analysis could be presented for clearly. Questions For Authors: 1. In theorem 3.7, could the author give an rough estimation of the optimality bound for HalfCheetch domain? Specifically, what are the magnitudes for $2L\frac{1−\gamma^{h+1}}{1−\gamma} \epsilon + \eta$ and $(1 − \frac{1}{e}) )(1 − \delta^∗(K, \epsilon) − K\beta))$, using $K=3$ and $\epsilon = 0.6$. How does the bound compared to $K=1$ using one single policy to learn all the tasks? 2. It is also a bit suspicious that although the language embedding provide a continuous parameterization of the tasks, the real task space is discrete and only have 50 tasks in total. In that, it is hard to believe simpler clustering strategies, like KMean++, do not give the same clustering result. I saw that comparison with other clustering algorithms is only conducted in HalfCheetahVel. Could author also conduct comparison in MetaWorld domain? 3. Could the author also provide the actual assignments of the 50 tasks to the three policies in the policy committee? 4. Could the authors also provide the visualization of the clustering results in HalfCheetahVel and compare it with KMean++. HalfCheetahVel uses a simple one-dimensional task parameter, I wonder in what degree the clustering result of PACMAN differs from conventional goal of minimizing sum of shortest distances. Code Of Conduct: Affirmed. Overall Recommendation: 2	Rebuttal 1: Rebuttal: We thank the reviewer for the thoughtful comments and suggestions! >Comment: Meta-World domain breaks the assumption made by the theoretical analysis that all the tasks share the same transition dynamics, as different tasks involve interacting with different objects, and therefore uses different transition dynamics. Response: This was by design. Our key finding is that while our analysis (like most worst-case analysis) makes restrictive assumptions, its value is exhibited by the Meta-World experiments that demonstrate robustness of the proposed approach to the assumptions. This is common in theoretical analysis, which of necessity must make assumptions that are inevitably violated in practice; what ultimately demonstrates value is empirical performance. The theoretical analysis, in turn, serves both to explain why we should expect strong performance in practice, and to ensure that the approach is principled (and, therefore, less likely to be fragile as we change domains). Thus, we view the combination of (a) superior empirical performance on the mainstream benchmarks and (b) provable worst-case guarantees in an important and broad array of settings (diverse rewards) makes our approach a particularly significant advance over prior art. >Comment: It is hard to believe simpler clustering strategies, like KMeans++, do not give the same clustering result... Could author also conduct comparison in Meta-World domain? Response: We indeed obtained different clusters using PACMAN than using Kmeans++ and, as a result, much better performance for Meta-World, as shown in the table below: \| \| Kmeans++ \| PACMAN (Ours) \| \|-------\|--------\|--------\| \|125K Steps\| 0.22 $\pm$ 0.06 \| 0.36 $\pm$ 0.07\| \|250K Steps\| 0.30 $\pm$ 0.07 \| 0.48 $\pm$ 0.09\| Notably, PACMAN exhibits $\sim 60$\% performance impovement over Kmeans++. >Comment: It would be interesting to visualize the clustering results in HalfCheetahVel and compare it with KMean++. Response: In Appendix H.2.1., we provided a histogram of the final clustering results in terms of individual task returns. We will also include a visualization of our and KMeans++ clusters in the revision. >Comment: Differentiating the work from Onur et. al., ICML 2024 Response: While our approach shares the key insight of addressing task diversity with MoE methods like the one proposed by Onur et al., we take it a step further, generating a small number of clusters upfront and using RL for each cluster independently thereafter. This facilitates more efficient and effective clustering (since no RL is involved for that) with provable guarantees, and is particularly valuable for few-shot adaptation (also with theoretical guarantees). Notably, our baselines include MoE-based methods (e.g., MOORE from ICLR 2024). >Comment: Could the author give an rough estimation of the optimality bound for HalfCheetch domain? Response: $2L\frac{1-\gamma^{h+1}}{1-\gamma} \epsilon \approx 100$, which is quite tight in this setting. When $K=3$, the committee generated by GIA yields near-perfect coverage $1-\delta^* \approx 1$, whereas for $K=1$, $1-\delta^* \approx 0.4$. The second bound is thus $\sim 0.63$ for the former and $\sim 0.25$ for the latter, so that the advantage of $K=3$ is a factor of 2.5. In practice, we find that these worst-case bounds are quite conservative, and empirical performance is far better. >Comment: I checked Appendix J, but I would be interested to see the actual assignment of the 50 tasks to the three policies in the policy committee. Could the author also provide the actual assignments of the 50 tasks to the three policies in the policy committee? Response: We will add full details of task-to-cluster mappings in the revision. At the high level, the three Meta-World clusters (for one of the random subsamples of 30 tasks) can be described as corresponding to three categories of manipulation tasks. The first cluster involves pulling and sliding manipulations (e.g., pull a puck, move end-effector, slide a plate to and from the cabinet). The second cluster includes manipulations that involve pressing and pushing (e.g., rotate the faucet, press a handle down, insert a peg into a hole, kick a soccer ball, sweep a puck). The third cluster consists of tasks involving indirect or constrained manipulation and which thus require better precision and control (e.g., bypass a wall, grasp a stick and pull or push a box with it). >Comment: There are a couple of missing citations: (1) line 336 SAC; (2) line 349 MetaWorld. In Theorem 3.4, 3.7 missing defintions Response: Thank you for pointing this out. We will rectify this in the revision.	Summary: This paper introduces PACMAN, a novel framework and algorithmic approach for learning policy committees in multi-task reinforcement learning (MTRL) and meta-reinforcement learning (meta-RL) settings with diverse tasks. The key challenge addressed is the difficulty of generalizing effectively across diverse tasks, where traditional MTRL and meta-RL approaches often struggle due to negative transfer or computational expense. PACMAN introduces a theoretically grounded approach for learning policy committees. It frames the problem as finding an (ε, 1-δ)-cover of the task distribution, ensuring that with high probability, there's at least one near-optimal policy in the committee for any encountered task. The paper presents two practical algorithms: Greedy Intersection Algorithm (GIA), which provides provable approximation and task sample complexity guarantees when task dimensions are low and Gradient-Based Coverage, which is a general, practical, gradient-based approach suitable for higher-dimensional tasks. The paper provides a provable sample complexity bound for few-shot learning that depends only on the number of clusters (committee size) and not on the state or action space size. The authors performed extensive experiments on MuJoCo and Meta-World benchmarks demonstrate that PACMAN outperforms state-of-the-art MTRL, meta-RL, and task clustering baselines in training, generalization, and few-shot learning, often by a large margin. Claims And Evidence: The claims are generally well-supported. The theoretical results (Theorems 3.3, 3.4, 3.5, 3.7, 3.8, Lemma 3.6) have provided proofs (although some are deferred to the appendix). The empirical results are comprehensive, covering multiple environments, baselines, and evaluation settings. The ablation studies (varying K and ε) provide further evidence for the effectiveness of the proposed approach. Methods And Evaluation Criteria: The methods and evaluation criteria are appropriate. The use of MuJoCo and Meta-World benchmarks is standard in the field. The evaluation metrics (training performance, zero-shot generalization, few-shot adaptation) are relevant to the problem. The comparison to a wide range of baselines strengthens the evaluation. Theoretical Claims: I have roughly checked the proofs provided in the main text and skimmed through proofs in the appendix, and they appear to be logically sound, given the assumptions made. Experimental Designs Or Analyses: The experimental design is generally sound. The choice of environments, baselines, and evaluation metrics is appropriate. The ablation studies help to understand the impact of key hyperparameters. The use of multiple random seeds and reporting of standard deviations provides statistical confidence in the results. Supplementary Material: No supplementary material provided. Relation To Broader Scientific Literature: The key contributions build on MTRL and meta-RL literature, improving over baselines like RL2 and VariBAD. The policy committee idea relates to ensemble methods or mixture of experts, and clustering is common in ML, but applying it to RL policy learning is novel. Theoretical bounds are crucial for RL efficiency. Essential References Not Discussed: No Other Strengths And Weaknesses: Strengths: 1. Strong theoretical grounding with provable guarantees. 2. Novel algorithmic approach combining clustering and policy committee learning. 3. Empirical results demonstrating significant improvements over strong baselines. 4. Applicability to both parametric and non-parametric task settings. 5. Clear and well-written presentation. Weaknesses: 1. The reliance on a parametric task representation (or the ability to obtain one using LLMs) is a limitation, although a common one. 2. The need to tune the hyperparameter ε is a practical consideration. 3. The computational cost of training multiple policies could be a concern in some settings, although the paper argues that the RL step dominates. 4. The GIA algorithm's exponential time complexity in d makes it only efficient for constant d. Other Comments Or Suggestions: None Questions For Authors: 1. The paper mentions that the RL step will typically dominate computational complexity. Could you provide some empirical evidence or a more detailed analysis comparing the time spent on clustering versus RL training, particularly for the Meta-World experiments? This would affect evaluation by giving insight into computational cost. 2. In the Meta-World experiments, you use MOORE for within-cluster training. Have you experimented with other MTRL or meta-RL algorithms for this step, and if so, how did they compare? This would clarify the extent to which the gains are attributable to the overall framework versus the specific choice of within-cluster RL method. 3. The (ε, 1-δ)-cover concept is central to the theoretical analysis. Could you elaborate on the practical implications of choosing different values of ε? How does one typically set this hyperparameter in a new environment? Clarifying how users could tune this parameter. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We thank the reviewer for the thoughtful comments! >Comment: The reliance on a parametric task representation (or the ability to obtain one using LLMs) is a limitation, although a common one. Response: Indeed, our method does require access to a parameterization for the tasks. We note, however, that our results with embeddings based on language descriptions suggest that our approach can nevertheless be very effectively applied to a very broad array of problems. Indeed, the continuing improvement of both the quality and scope of LLMs suggests that the space of problems to which our approach can be effectively applied will likely continue to expand. >Comment: The need to tune the hyperparameter ε is a practical consideration. Response: Our method introduces only one hyperparameter, $\epsilon$, which is easy to tune, particularly in comparison to myriad of hyperparameters that typical deep RL methods introduce. For example, our ablation studies in Appendix H suggest that choosing the smallest $\epsilon$ that ensures full coverage for the largest $K$ a practitioner can afford to train works well in practice. >Comment: The GIA algorithm's exponential time complexity in d makes it only efficient for constant d. Response: This is true; indeed, as we show in Theorem 3.3, the problem is inapproximable in the worst case. We address this issue by presenting a practical gradient-based coverage algorithm, which is the main workhorse of the Meta-World experiments, and which outperforms SOTA baselines. >Comment: The paper mentions that the RL step will typically dominate computational complexity. Could you provide some empirical evidence or a more detailed analysis comparing the time spent on clustering versus RL training, particularly for the Meta-World experiments? This would affect evaluation by giving insight into computational cost. Response: For the Meta-World experiments, training a single policy requires approximately 40 hours using an A40 GPU for 1M steps. In comparison, clustering takes about 1 second in a Google Colab notebook, and obtaining task embeddings takes around 2 minutes on an A40 GPU. We will include these details along with the corresponding timings in the revised version of the paper. >Comment: In the Meta-World experiments, you use MOORE for within-cluster training. Have you experimented with other MTRL or meta-RL algorithms for this step, and if so, how did they compare? This would clarify the extent to which the gains are attributable to the overall framework versus the specific choice of within-cluster RL method. Response: While we have not extensively evaluated this issue, we did run experiments with alternative within-cluster training to MOORE. We have found that PACMAN typically outperforms the approach it wraps by a considerable margin. For example, PACMAN trained using CMTA produced significant improvement as well: \| \| CMTA \| PACMAN (CMTA) \| \|-------\|--------\|--------\| \|125K Steps\| .20 $\pm$ .08 \| .28 $\pm$ .08\| \|250K Steps\| .25 $\pm$ .09 \| .41 $\pm$ .10\| >Comment: The (ε, 1-δ)-cover concept is central to the theoretical analysis. Could you elaborate on the practical implications of choosing different values of ε? How does one typically set this hyperparameter in a new environment? Clarifying how users could tune this parameter. Response: In Appendix H.2.2, Table 5, we show that when the coverage is not complete due to a small ε, performance significantly degrades. Practically, the choice of ε depends on the cost of training a policy. A user should aim to select the largest committee size they can afford and then choose an ε that ensures maximum coverage. One approach is to first compute the distances between all tasks' embeddings. This could provide an initial estimate for setting ε. From there, we can fine-tune ε to ensure it is small while still guaranteeing adequate coverage. From what we have observed, ε is far less sensitive than typical RL hyperparameters.	null	null	null	null	null	null
ReVISE: Learning to Refine at Test-Time via Intrinsic Self-Verification	Accept (poster)	Summary: This paper introduces Refine via Intrinsic Self-Verification (ReVISE), an efficient framework that enables large language models (LLMs) to self-correct their outputs through self-verification. ReVISE allows LLMs to evaluate their reasoning processes and iteratively refine their outputs based on verification feedback. To achieve this efficiently, the framework employs a structured curriculum leveraging online preference learning. Given the dual challenges of self-verification and reasoning correction, ReVISE applies curriculum learning to address them sequentially, gathering both failed and successful reasoning paths to construct preference pairs for efficient training. During inference, ReVISE naturally scales by integrating self-verification and correction, further enhanced by a confidence-aware decoding mechanism. Experimental results across various reasoning tasks show that ReVISE enables efficient self-correction and significantly enhances LLM reasoning performance. ## update after rebuttal The authors' rebuttal addressed my concerns, leading me to revise my recommendation from weak reject to weak accept. Claims And Evidence: Some claims are not well supported by evidence: 1. In Section 4.3, it mentions that “We observe that training at stage 2 slightly degrades verification accuracy, indicating that the self-correction task is particularly challenging and may lead to catastrophic forgetting”. I think the results cannot demonstrate that the self-correction task is particularly challenging and may lead to catastrophic forgetting. Because in Figure 3a, the accuracy after stage 2 is improved significantly compared to that of stage 1. 2. In Section 4.3, it states that the results in Figure 5 suggest that confidence serves as a reliable metric for calibrating the sampling score. However, from the figure, we can see that there are some correct cases that have low confidence and some incorrect cases that have high confidence. So the calibration is not very good. I think it needs to provide a quantitative metric like TPR at 5% FPR to quantify the calibration performance and compare the proposed method with current state-of-the-art baselines. Methods And Evaluation Criteria: The proposed method makes sense for the problem. However, the evaluation criteria have some limitations: 1. It only reports Majority Voting at N where N is up to 8. It should consider larger N (e.g. N=64). 2. It only evaluates the proposed method on math benchmarks. The paper would be stronger if it considers other kinds of datasets like reasoning and coding datasets (e.g. LiveBench and LiveCodeBench). Theoretical Claims: No theories. Experimental Designs Or Analyses: Yes, I check the soundness of the experimental designs and analyses in Section 4. I have some concerns: 1. It only considers Llama-3 models with 1B and 8B parameters. It would be better to evaluate other kinds of models (e.g. Mistral models). 2. It seems the instruction-tuned models have much better performance on GSM8K and MATH-500. It would be better to compare the proposed method to those instruction-tuned models. 3. I think it needs to compare the proposed method with the SCoRe method proposed in [1]. [1] Kumar, A., Zhuang, V., Agarwal, R., Su, Y., Co-Reyes, J. D., Singh, A., Baumli, K., Iqbal, S., Bishop, C., Roelofs, R., Zhang, L. M., McKinney, K., Shrivastava, D., Paduraru, C., Tucker, G., Precup, D., Behbahani, F., and Faust, A. Training language models to self-correct via reinforcement learning. arXiv preprint arXiv:, 2024. Supplementary Material: Yes, I reviewed the supplementary material (Appendix A, B, and C). Relation To Broader Scientific Literature: The key contributions of this paper align with the recent trend of training LLMs to improve self-correction [1], as well as leveraging self-verification to enhance inference-time scaling efficiency [2]. [1] Kumar, A., Zhuang, V., Agarwal, R., Su, Y., Co-Reyes, J. D., Singh, A., Baumli, K., Iqbal, S., Bishop, C., Roelofs, R., Zhang, L. M., McKinney, K., Shrivastava, D., Paduraru, C., Tucker, G., Precup, D., Behbahani, F., and Faust, A. Training language models to self-correct via reinforcement learning. arXiv preprint arXiv:, 2024. [2] Snell, C., Lee, J., Xu, K., and Kumar, A. Scaling llm testtime compute optimally can be more effective than scaling model parameters. arXiv preprint arXiv:2408.03314, 2024. Essential References Not Discussed: No. Other Strengths And Weaknesses: Strengths: 1. The paper is well-written, with a thorough discussion of related work. 2. The proposed test-time sampling scheme, which integrates self-verification confidence, is novel and enhances output reliability. Weaknesses: 1. The proposed method only employs single-round self-correction. It would be better to investigate whether multi-round self-correction can further improve performance. 2. Running experiments multiple times and reporting the mean and variance of the results would strengthen the evaluation. Other Comments Or Suggestions: No other comments. Questions For Authors: I can raise my scores if the authors clarify the following concerns: 1. Would the proposed method benefit from multi-round self-correction? 2. Could the authors compare the proposed method to the SCoRe method? 3. Could the authors provide additional evidence to support the claim that the proposed confidence serves as a reliable metric for calibrating the sampling score? Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Dear reviewer nE5C, We sincerely appreciate your efforts and comments to improve the manuscript. We respond to your comment in what follows. --- [Q1] Would the proposed method benefit from multi-round self-correction? We have already investigated multi-round self-correction in Appendix B.1 of our paper. Specifically, after generating the first refined response ($y_2$), we generate a second refined response ($y_3$) by appending ($y_2$) to the original prompt ($x$). Formally, $y_2 \sim p(\cdot \mid x, y_1), y_3 \sim p(\cdot \mid x, y_2)$. As shown in Figure 8, ReVISE improves with each refinement round in MATH-500, e.g., 1st: 33.0 %, 2nd: 33.6 %, 3rd round: 34.2 %, demonstrating the effectiveness of multi-round self-correction. We will move the multi-round results to the main part of the final version. --- [Q2] Compare with SCoRe method. We first note that our primary focus was to build an efficient way to implement self-correction, where SCoRe requires a heavy online RL; it needs to generate the reasoning path for every training mini-batch, generating 1.5M paths in total (512 batch size × 3,000 steps). In contrast, ReVISE only requires a single reasoning path generation per individual sample to construct a preference pair, resulting in 50k generations. Hence, we expect that our training cost is 30 (=1.5M / 50k) times smaller than SCoRe. Nevertheless, we agree that SCoRe is a worthwhile method to compare, and compared with ReVISE on Gemma2 2B. Here, we have reported SCoRe’s results from the paper (as it is not open-sourced and difficult to reproduce with our computing resources). As shown in the table below, ReVISE outperforms SCoRe on MATH using the same Gemma 2 2B model. We thank the reviewer for the suggestion and will include the comparison in the final version. Table: https://bit.ly/4cdMnqN --- [Q3] Could the authors provide additional evidence to support the claim that the proposed confidence serves as a reliable metric for calibrating the sampling score? We remark that we have already reported the quantified ReVISE’s calibration performance using AUROC in Section 4.3 and Figure 3 (b). To further support this claim, we compared ReVISE with V-Star’s verifier [1]. Notably, while ReVISE relies on an intrinsic verifier, it still outperforms V-Star’s separately trained verifier, as shown in the table below, with a higher AUROC reflecting superior confidence-correctness alignment. Table: https://bit.ly/4hW5HtE [1] Hosseini, Arian, et al. "V-star: Training verifiers for self-taught reasoners." arXiv preprint arXiv:2402.06457 (2024). --- Whether the results in Figure 3a demonstrate that the self-correction task is particularly challenging and may lead to catastrophic forgetting. We agree that our original phrasing may have been misleading. We intended to convey that self-correction introduces additional difficulty, as the model must both verify and refine its output—potentially making it harder to maintain verification performance during training. We will revise the sentence to avoid strong terms like “catastrophic forgetting” and clarify the trade-off between verification and correction in joint training. --- Benchmark on coding domain. Due to space limitations, we kindly refer the reviewer to our response to cTTG’s comment W2, which addresses this point in detail. --- ReVISE to instruction-tuned models. We remark that Table 2 already reports results on instruction-tuned models, where ReVISE consistently outperforms other baselines. This shows that ReVISE complements instruction tuning and can further boost strong models. --- Sampling for N=64 We extended our sampling setup on N=2 to 64. As shown in the table, ReVISE consistently outperforms baselines across all sample sizes. We will include these results in the final version. Table: https://bit.ly/4hSZ23t --- Running experiments multiple times and reporting the mean and variance. As shown in the table above, we report the mean, standard deviation over 5 random seeds for all sample sizes N=2 to 64. ReVISE not only consistently outperforms baseline methods in terms of mean accuracy, but also maintains stable variance. We will report the mean variance across multiple runs in the final version. --- Evaluate other kinds of model To address your concern, we conducted experiments on the Gemma2 2B. As shown in the table below, ReVISE still consistently outperforms other baselines, including SFT, RFT, and SCoRe, showing its effectiveness beyond the Llama family. We will include this result in the final version of the paper. Table: https://bit.ly/4cdMnqN --- Rebuttal Comment 1.1: Comment: After reading the rebuttal, I still have a concern that the proposed method may not significantly outperform the SCoRe method. Thus, I keep my original scores. --- Reply to Comment 1.1.1: Comment: Thank you for your prompt and clear response, Reviewer nE5C. We remark again that ReVISE is 30× more training-efficient than SCoRe while still achieving higher accuracy. Namely, the training efficiency of ReVISE is its important advantage. However, if one wishes to pay more training cost, ReVISE’s accuracy can be further improved. To be specific, one can re-sample reasoning path pairs using a progressively improved model from the previous iteration, and re-train ReVISE using them by applying DPO [1] iteratively. The results are reported in the table below, which demonstrate that ReVISE outperforms SCoRe by 2.8% higher accuracy in testing with 15× speed-up in training. We think that this is not a marginal improvement. We will update all results of ReVISE in the final draft by applying such an iterative DPO strategy, which we believe further strengthens our paper. \begin{array}{clcc} \hline \textbf{Test Dataset} & \textbf{Method} & \textbf{Accuracy} & \textbf{Training Efficiency} \newline \hline & \text{base} & 16.8 & - \newline &\text{SCoRe} & 23.0 & \times 1 \newline \text{MATH-500}&\textbf{ReVISE (ours)} & \textbf{23.2} & \times\textbf{30} \newline &\textbf{+ iter1 (ours)} & \textbf{24.2} & \times\textbf{20} \newline &\textbf{+ iter2 (ours)} & \textbf{25.8} & \times\textbf{15} \newline \hline \end{array} Finally, we hope your understanding that SCoRe has not provided open source code (the results of SCoRe in the above table are from the original paper), and we could not perform more extensive comparisons. Since we will publicly release our code and reproducible supplementaries, we think that this would be very useful for follow-up researchers. We think this is also our important contribution to the community. Thank you again for your valuable feedback and consideration. [1] Rafailov, Rafael, et al. "Direct preference optimization: Your language model is secretly a reward model." Advances in Neural Information Processing Systems 36 (2023)	Summary: The paper introduces DPO to fine-tune LLMs in two steps, which are self-verification and self-correction, and a special token [refine] is introduced. Simple and effective method. Claims And Evidence: All claims made in the submission supported by clear and convincing evidence. Methods And Evaluation Criteria: The evaluation dataset lacks OOD tests and it is unclear how well the fine-tuned model generalizes. Theoretical Claims: No Theoretical Claims. Experimental Designs Or Analyses: 1. The lack of OOD evaluations. 2. The lack of evaluation of LLaMA-8B on GSM8K. Supplementary Material: No Supplementary Material. Relation To Broader Scientific Literature: The introduction of special token [refine] is a novel idea. Essential References Not Discussed: No other references Other Strengths And Weaknesses: strength: 1. The proposed method is simple and effective. 2. The paper integrates self-verification and self-correction with DPO. Weakness: 1. The datasets employed and experimental designs are not sufficient; the paper proposes to make demonstrations in mathematics and coding domains in lines 81-82, but the actual experiments are only conducted in mathematics. 2. Without OOD validation, the generalization of LLMs after DPO may be somewhat compromised. 3. The concerns of paper on open source. 4. Does the multiple sampling process change the temperature? Given a question, what is the probability that the model always answer correctly? Other Comments Or Suggestions: No others. Questions For Authors: Please see weakness. Code Of Conduct: Affirmed. Overall Recommendation: 2	Rebuttal 1: Rebuttal: Dear reviewer Aquu, We sincerely appreciate your efforts and comments to improve the manuscript. We respond to your comment in what follows. --- [W1] The datasets employed and experimental designs are not sufficient; the paper proposes to make demonstrations in mathematics and coding domains in lines 81-82, but the actual experiments are only conducted in mathematics. In response to the concern about limited coverage of task domains, we conducted additional experiments in the coding domain using the MBPP benchmark, as initially proposed in lines 81–82. ReVISE, trained on the Llama 3.2-1B model, achieves 33.1%, outperforming the second-best baseline at 30.7%. Since MBPP lacks reasoning annotations, we generated ground truth reasoning using GPT-4o. These results complement our mathematics experiments and demonstrate that ReVISE generalizes effectively beyond mathematics tasks. \begin{array}{lc} \hline \textbf{Method} & \textbf{Pass@1} \newline \hline \text{3 Shots} & 24.5 \newline \text{SFT} & 30.0 \newline \text{RFT} & 29.6 \newline \text{STaR}^+ & 30.7 \newline \text{ReVISE (Ours) } & \textbf{33.1} \newline \hline \end{array} --- [W2] The lack of OOD evaluations. To address your concern and demonstrate robustness to domain shifts, we conducted an OOD evaluation by training ReVISE on the MATH dataset and evaluating it on GSM8K. As shown in the table below (Maj@1), ReVISE consistently outperforms other baseline methods (the gap decreases a bit though), including SFT, RFT, and StaR+, under the OOD setting. We will add the OOD results to the final draft. \begin{array}{lcc} \hline \textbf{Model} & \textbf{Method} & \textbf{GSM8K Acc.} \newline \hline \text{} & \text{SFT} & 7.3 \newline \text{Llama 3.2-1B} & \text{RFT} & 8.2 \newline \text{} & \text{STaR}^+ & 8.0 \newline \text{} & \text{ReVISE (Ours) } & \textbf{8.8} \newline \hline \text{} & \text{SFT} & 60.3 \newline \text{Llama 3.1-8B} & \text{RFT} & 60.3 \newline \text{} & \text{STaR}^+ & 58.7 \newline \text{} & \text{ReVISE (Ours) } & \textbf{61.5} \newline \hline \end{array} --- [W3] The concerns of the paper on open source. In the final draft, we will release the training and evaluation code for ReVISE, including all hyperparameter configurations, to ensure full reproducibility of the results presented in the paper. --- [W4] Concern about temperature consistency in the experiment. We clarify that we have used a consistent temperature value (t=0.7) throughout the entire experiment. We will include the information about temperature value in the final version of the paper. --- [W5] The lack of evaluation of Llama 3.1-8B on GSM8K. Following your suggestion, we have additionally trained and evaluated ReVISE using the Llama 3.1-8B on GSM8K. As shown in the table below (Maj@1), ReVISE consistently outperforms baseline methods under this larger model setting, demonstrating that our approach scales well with model size. \begin{array}{lc} \hline \textbf{Method} & \textbf{Accuracy} \newline \hline \text{SFT} & 58.2 \newline \text{RFT} & 58.9 \newline \text{STaR}^+ & 59.2 \newline \text{ReVISE (Ours) } & \textbf{61.6} \newline \hline \end{array}	Summary: This paper proposes a method to perform self-correction intrincically with two steps. First is a self-verifying stage, by leveraging SFT and DPO, the LLM will learn how to distiguish between correct reasoning and wrong reasoning. Second step is self-correction, when the LLM generates the refine token, then the LLM needs to refine its generation. The pipeline requires preference datasets to train and it can be served as the test-time refinement during inference stage. The proposed method is a natural way to decompose the refine process. Claims And Evidence: The experiments in this paper clearly supports that the proposed method is a clear and effective way to improve reasoning performance during inference stage. And the proposed method is also efficient because only incorrect responce needs to refine. Methods And Evaluation Criteria: The diversity of the benchmarks is limited, only math datasets are used in experiments. It would be better to increase the range of task types here to fully verify the effectiveness of the proposed method. Theoretical Claims: N/A Experimental Designs Or Analyses: The experiments are conducted on math datasets such as GSM8K and MATH-500. Except from performance on benchmarks, this paper also provides several ablation studies to verify the effectiveness of the proposed method and the necessity of several components of the pipeline. The overall performance shows that, in reasoning tasks (math problems in this case), ReVISE achieved comparable improvement over SFT, RFT and STaR+. And the proposed two stage training is essential for the refinement performance. One issue is that, even though in curriculum learning experiments, the authors shows that by optimizing verification and refinement loss together, the overall performance is weak, compared with proposed method. Since this model leverages reinforcement learning (specifically, DPO), it would be better to compare reinforcement learning setting in main experiment section. That is to say, without this two-stage refinement, how much performance gain can be achieved by RL finetuning (DPO, GRPO, etc.) only? Supplementary Material: N/A Relation To Broader Scientific Literature: N/A Essential References Not Discussed: N/A Other Strengths And Weaknesses: N/A Other Comments Or Suggestions: Typo: The caption in Figure 8b should be Llama-3.2-8B rather than Llama-3.2-1B Questions For Authors: The proposed method can only decide whether the reasoning trajectory is correct or not in the end of responce. Do you think this method can be extended to perform refinement within the reasoning trajectory? For example, when the model generate half of the response, it can realize that the current genereated text is not good enough. In tasks like math, for human, if the current reasoning trajectory has confliction, it's better to go back now and find the nearest position and minimal changes to give a better trajectory. So the second question raises, could this method be elastically extended as a "eraser"? Which means the verification model can detect which part in previous generation should be rewrite? That is to say, the model can perform self-correct in half-way during inference stage, worked in an intervention way. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Dear reviewer cTTG, We sincerely appreciate your efforts and comments to improve the manuscript. We respond to your comment in what follows. --- [W1] The diversity of the benchmarks is limited. It would be better to increase the range of task types here to fully verify the effectiveness of the proposed method. To address the concern about benchmark diversity, we added experiments on the MBPP coding benchmark. ReVISE, trained on the Llama 3.2-1B model, achieves 33.1%, outperforming the second-best baseline at 30.7%. Since MBPP lacks reasoning annotations, we generated ground truth using GPT-4o, which is used to train the baselines and ReVISE. These results further support ReVISE general applicability across domains. \begin{array}{lc} \hline \textbf{Method} & \textbf{Pass@1} \newline \hline \text{3 Shots} & 24.5 \newline \text{SFT} & 30.0 \newline \text{RFT} & 29.6 \newline \text{STaR+} & 30.7 \newline \text{ReVISE (Ours)} & \textbf{33.1} \newline \hline \end{array} --- [W2] As the baseline, how much performance gain can be achieved by RL finetuning only (specifically DPO)? Following your suggestion, we have additionally considered an RL-based baseline, specifically a DPO-trained model. To be more specific, we trained the DPO model from an SFT model and constructed a preference pair dataset that paired the ground truth as chosen and the wrong answer as rejected. As shown in the table below (Maj@1), ReVISE even outperforms the RL-based baseline, indicating the 22.7% in gsm8k and 10.8% in MATH-500. \begin{array}{lcc} \hline \textbf{Model} & \textbf{GSM8K} & \textbf{MATH} \newline \hline \text{DPO} & 22.7 & 10.8 \newline \text{ReVISE (Ours)} & \textbf{28.1} & \textbf{13.4} \newline \hline \end{array} --- [Q1] Can ReVISE be extended to perform, refinement within the reasoning trajectory? Thank you for your great question. It is true that the current version explicitly verifies after generating all reasoning traces and answers. We believe it will be a great future work if the model can detect errors during the reasoning trace generation, e.g., train the model to emit a [refine] token midway when there is an error in the reasoning trace where the error can be detected by using an LLM judge. We thank the reviewer for the question and will discuss this future direction in the final draft. --- Rebuttal Comment 1.1: Comment: Thank authors for the added experiment results. I will maintain my original positive score on this submission. --- Reply to Comment 1.1.1: Comment: Dear Reviewer cTTG, Thank you for letting us know! We are delighted to hear that our rebuttal addressed your questions well. We will add the additional experimental results and address the suggested question about future direction in the final draft. If you have any further questions or suggestions, please do not hesitate to let us know. Thank you very much, Authors	null	null	null	null	null	null	null	null
Compression via Pre-trained Transformers: A Study on Byte-Level Multimodal Data	Accept (poster)	Summary: This paper investigates the compression efficiency of foundation models when accounting for parameter size. Through extensive experiments on 165GB of text, image, and audio data, the authors demonstrate that relatively small transformer models (millions of parameters) can outperform standard compression algorithms like gzip and even domain-specific compressors like FLAC—achieving a 0.49 compression ratio on out-of-distribution audio data compared to FLAC's 0.54. While these smaller models can handle multiple trained modalities effectively, they show limited transfer capabilities to unseen modalities unlike their larger counterparts. Claims And Evidence: Although I appreciate the author's interesting findings that indicate a small transformer with massive training data can compress well to out-of-distribution data than general-purpose and even domain-specific compressors, the theoretical contribution is relatively weak for the ICML audience. Meanwhile, Deletang et al. actually have shown the performance of a transformer compressor trained from the scratch. Compared with Deletang et al., the main contributions of this paper lie on the usage of more multi-modality data and corresponding performance on cross-modality data, if I understand correctly. I still think the theoretical contributions are still weak to ICML audience. Methods And Evaluation Criteria: I think the method is very easy to follow. Authors leverage a small transformer with multiple domains for training. The out-of-distribution compression performance is focused on. Theoretical Claims: This paper lacks theoretical claims and main results are derived from empirical experiments. Experimental Designs Or Analyses: Indeed, there are some SOTA image lossless codecs are used for comparison. Please consider some representative SOTA image lossless codecs, such as JPEG-XL and WebP. Supplementary Material: I read the SM. Relation To Broader Scientific Literature: N/A Essential References Not Discussed: N/A Other Strengths And Weaknesses: Strengths: - This paper is well-written and easy to follow - The topic is interesting and the capacity of transformer-based model for lossless data compression is an important direction - The experimental settings are comprehensive, and the authors choose multiple modalities for lossless compression comparison. Weaknesses: - Although I appreciate the author's interesting findings that indicate a small transformer with massive training data can compress well to out-of-distribution data than general-purpose and even domain-specific compressors, the theoretical contribution is relatively weak for the ICML audience. Meanwhile, Deletang et al. actually have shown the performance of a transformer compressor trained from the scratch. Compared with Deletang et al., the main contributions of this paper lie on the usage of more multi-modality data and corresponding performance on cross-modality data, if I understand correctly. I still think the theoretical contributions are still weak to ICML audience. - I think it is necessary to compare with state-of-the-art lossless image compressor such as JPEG-XL. - How the authors to process the RGB images for lossless compression? Deletang et al. give the scheme of grayscale image. It is very interesting to claim this detail. - Overall, I think this paper needs to further justify the contribution compared to previous literature. I am happy to increase my score upon nice answers. Other Comments Or Suggestions: Please see the weakness. Questions For Authors: Please see the weakness. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We thank the reviewer for their careful assessment and constructive feedback. We are pleased that they think that our `topic is interesting and an important direction`, that our `experimental settings are comprehensive`, and that our `paper is well-written`. Could you also compare to state-of-the-art lossless image codecs such as JPEG-XL? Yes, thank you for the suggestion! We evaluated JPEG-XL on our image data and obtained a compression ratio of 0.26, which, as the reviewer correctly predicted, is slightly better than our model (and Bellard’s): \| Evaluation Modality \| Ours \| Bellard \| gzip \| LZMA2 \| PNG \| JPEG 2000 \| JPEG XL \| \| ------- \| ------- \| ------- \| ------- \| ------- \| ------- \| ------- \| ------- \| \| Image \| 0.285 \| 0.281 \| 0.698 \| 0.545 \| 0.426 \| 0.390 \| 0.260 \| We have updated all the tables and figures with these results in our revised manuscript. Note that the point of our paper is not so much that neural networks can outperform any domain-specific compressor but that they can be on par with some of the most widely used general-purpose and domain-specific compressors. I think that the theoretical contributions are too weak for the ICML audience Our work is a comprehensive empirical study, which is in scope for and frequently gets published at ICML. The theory underlying our work (and Delétang et al. (2024)) is standard textbook material in information theory. Accordingly, Delétang et al. (2024), which was published at ICLR 2024, did not introduce this theory. Instead, they provided a concise review of that theory, as we did in Section 2. What is the contribution compared to prior work? We investigated the open problem of whether small transformers pre-trained on large multimodal datasets can achieve competitive compression ratios across different modalities and whether there is transfer to unseen modalities (see Section 1), as observed in the large-scale model case. Prior work either considered large-scale, pre-trained models (Delétang et al., 2024) or models trained online (Bellard, 2021). As a result, we investigated a different regime that induces entirely different constraints on the optimal model architecture (in particular, its size) and for which it was a priori unclear whether competitive compression ratios would be achievable across different modalities. Accordingly, our contributions compared to the previous literature are (see also Table A1): * Small transformers can achieve competitive compression ratios on audio and image data (Delétang et al. (2024) only showed this for text data), even when comparing against domain-specific compressors, which the reviewer considers an `interesting finding`. * Small transformers can achieve competitive compression ratios across multiple domains, pointing towards the generality of relatively small models. * Unlike the results on large language models by Delétang et al. (2024), small transformers do not achieve transfer outside the training modalities. Moreover, unlike our work, Delétang et al. (2024) did not investigate in-modality out-of-distribution data (e.g., training on ImageNet and evaluating on CelebA) to show in-modality generalization. How do you process RGB images for lossless compression? As described in Appendix B.1, we use all three (RGB) channels, each represented as `uint8` (unlike Delétang et al. (2024), who compress grayscale images, i.e., use a lossy representation of the original image). We flatten the image and concatenate all flattened images to form our image byte stream from which we iteratively sample chunks where the chunk size depends on the model’s context size (typically only parts of a single image fit into our models’ context, and, occasionally, there may be parts of two different images in the context).	Summary: The paper shows that small decoder-only transformers trained on multimodal data are effective data compressors. This happens when the modality of the data being compressed (text, audio, video) belongs to the training set. In this multimodal setup, the authors show that it is possible to achieve compression ratios that are competitive with state-of-the-art algorithms (on 1GB of data), even considering the transformer parameters. Claims And Evidence: The paper is well written the claims are supported by convincing evidence. See the experimental design section. Methods And Evaluation Criteria: The methods and evaluation criteria are appropriate and sound. Theoretical Claims: No theoretical claims to discuss. Experimental Designs Or Analyses: A convincing and comprehensive set of experiments backs the paper. The paper examines various effects influencing the compression rations, including the training set composition Fig.2, 3 model size Fig. 4. It explores how the context size and sliding window approaches affect the data compression and how the compression ratio is affected by the size of the evaluation set Fig. 7. Taken together these are a convincing set of experiment supporting the claims of the paper. Supplementary Material: Only Briefly read. Relation To Broader Scientific Literature: The relation to the broader scientific literature is thoroughly discussed in Sec. 6 and expanded in Sec. A of the appendix. The literature itself is well presented in Sec. 3. Essential References Not Discussed: Essential references are discussed. Other Strengths And Weaknesses: The work is good and well-written, it is slightly incremental with respect to the previous studies on compression but addresses a relevant open question backed by a convincing and comprehensive set of experiments. Other Comments Or Suggestions: None; the paper is well written. Questions For Authors: I do not have any relevant concerns that could change my evaluation of this paper. Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: We thank the reviewer for their thorough assessment of our work. We are pleased that they think that our `work addresses a relevant open question backed by a convincing set of experiments` with `methods and evaluation criteria that are appropriate and sound`, and that they consider our `paper well-written`.	Summary: This paper studies byte language models as a means to compress data on multimodal data (text, audio, images). They show that by training small scale transformers data can be compressed better than with standard compression algorithms like gzip or domain-specific standards (JPEG). This is achieved without online training, i.e., the Transformers are not trained to compress the data they are evaluated on, unlike competing methods like Bellard. The obvious disadvantage of this method is speed (much slower than standard compression). Thus the practical utility of the method is limited to very specific cases (where compression ratio has to be minimized, no matter the computational cost). Yet the authors are open about this, thus this is more of a feasibility study. ## update after rebuttal I had initially given an "accept", conditional on the authors' response to clarify my questions (and concerns). The authors answered my questions, thus I retained my score. The work appears sound, novel and non-incremental, thus I am clearly in favor of acceptance. Claims And Evidence: There are four claims in the introduction which are all supported well by evidence: (1) Empirical study on compression of small Transformers (2) transformers are better at compressing than general-purpose compressors (3) Multimodal boosts compression on multimodal data (4) Poor transfer to unseen modalities However, there is one implicit claim where I see zero support: Can you demonstrate that the model is actually doing lossless compression and the original sequence can be recovered exactly? How do you ensure that compression is lossless? Is this by construction? E.g., if you ran an inference before even starting the training, would the "compressed" file still be lossless, just exactly as big (or bigger) than the source bytestream? For a text-only model, I fail to see how it can losslessly compress 1GB of image. Methods And Evaluation Criteria: The compression ratio metric makes sense, but it is the only metric reported throghout the paper. Results may be slightly richer if some additional metrics (like train/validation loss) were also shown Theoretical Claims: What is considered lossless compression? Are we talking about half, single, double precision? (I only saw that model weights are counted with half precision) Experimental Designs Or Analyses: Apologies for my lack of knowledge on compression but I would like to see more details on the training/inference workflow for the model. Maybe a figure could help? Training: If training is done with pure CE objective on next byte prediction, how is the compressed output extracted from the model? Training with standard next token (aka byte) prediction would yield a byte sequence of identical length to the input bytestream,. Inference: If you compress 1GB of data, with a context size of 4096 and no overlap, then, in practice you sequentially run 1M/4096 forward steps. How many bytes are you predicting in each of those steps? It's problematic to (1) cherry-pick and report the best performance over hyperparameter sweeps on the validation data (it seems that you did not do a train/validation/test split) and (2) report single-run results without any indication of confidence intervals. If you did only either (1) or (2) I wouldn’t raise this, but in combination, I find the results a bit brittle. I acknowledge that (1) prior art didn’t even make this distinction between train/validation and (2) the computational costs for such methods are very high. For the rebuttal I would like to see performance of all models, rather than only the best ones Supplementary Material: Some tables Relation To Broader Scientific Literature: Well related to broader literature in LM-compression space (Deletang, Bellard etc) and the byte-LM space (Megabyte, BLT etc). Out of curiosity, could the authors comment on the impact of larger context windows for compression algorithms? Megabyte has a context window up to 1M bytes, multiscale byte LMs (https://arxiv.org/pdf/2502.14553) can even go to 5M bytes -- would you expect that compression ratio can be increased significantly with a model that can fit the entire bytestream into the context window? Essential References Not Discussed: None Other Strengths And Weaknesses: Strengths: - Interesting findings that will impact the future of compression via LMs - Paper is clearly written and relatively easy to follow - Results are rich and multiple ablation studies were conducted Weaknesses: - The extraction of the bytes from the LM head is not clearly defined (see my comment above) Other Comments Or Suggestions: Minor things: - Introduction: "LLMs compress better when parameter count is not considered" -- according to which metric are LLMs worse at compression when the count is considered? I only understood later from equation 3 that you include the size of the compressor by encoding model weights in half precision. Maybe you can be more explicit in the intro - L196 - missing "is" Questions For Authors: None Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: We thank the reviewer for their thorough review and constructive feedback. We are pleased that they think our `interesting findings will impact the future of compression via LMs`, our `results are rich with multiple ablation studies`, and our `paper is clearly written`. How do you ensure that your compression is lossless? Is this by construction? Yes, it is lossless by construction as we use arithmetic coding (AC), a lossless compression algorithm that uses the next-symbol probabilities of a sequential predictor (i.e., our transformers) to compress (see Figure 1 in Delétang et al. (2024) and Hutter et al. (2024)). For any predictor, AC is optimal in terms of coding length, i.e., the compression performance only depends on the predictor. If the predictor is bad (e.g., an untrained network), the compressed size would be larger than the original — but the data would still be losslessly recoverable. To decompress, AC must use the same predictor, so we also have to communicate its parameters (we use half precision). The precision used to encode the parameters does not affect the compression's “losslessness”, only the performance. How can a text-only model losslessly compress images? As we convert all data into byte streams (no tokenization) and train our models on next-byte prediction, they can process any byte data. Images are simply byte streams with different statistics and can also be fed to models trained only on text bytes. If the model has learned general patterns, it will also predict the image byte stream well (and losslessly compress it well via AC). What is considered lossless compression (half, single, double precision)? Our compression is lossless by construction, and the numerical precision depends entirely on the AC, which can be arbitrarily high (at the expense of compression performance). We use the data’s precision, i.e., single precision (we compress bytes). The underlying data may be encoded at higher precision (e.g., `float32` images), which is losslessly recoverable from our byte streams. Do you have a train/validation/test split, or did you cherry-pick the best models? Our setup differs slightly from the standard train/validation/test splits as we always evaluate OOD data (e.g., train on ImageNet, evaluate on CelebA) to mimic the standard compressor setup. As the reviewer states, Figure 2 is a feasibility result, which is why we show the best performance. Figures 3 to 6 show all the models (the full hyperparameter sweeps), as the reviewer requested. How are the bytes extracted from the model’s head during training and inference? AC directly uses the model’s predictions over tokens (i.e., the logits) to encode/decode data (see Figure 1 in Delétang et al. (2024) for an overview). The model computes a distribution over the next byte for every input byte, and the AC then uses these predictions to losslessly compress the data. No separate head or extraction procedure is necessary. We train via standard log-loss minimization to perform next-byte prediction. At inference time, we perform standard autoregressive evaluation (using teacher forcing). We have added the above clarifications to our revised manuscript. Why are LLMs worse at compression when the parameter count is considered? LLMs are viable compressors depending on whether their parameter count is factored into the compression ratio (i.e., adjusted vs. unadjusted). Imagine that Alice wants to compress and send data to Bob, who wants to decompress it. If Alice trains a neural network to compress the data but does not communicate the model’s weights, Bob cannot decode the data. Thus, the parameter count needs to be factored into the compression ratio. We believe that the unadjusted compression ratio is not well suited to evaluate pre-trained neural networks as compressors. We have reformulated Section 1 to make this more explicit. What is the context window's impact on compression performance? We investigated this question in Figure 5. For text, increasing the model size is more beneficial than increasing the context length (short-term dependencies are most important). In contrast, large context sizes are generally beneficial for images (models with larger contexts can process larger fractions of an image). For audio, the relationship between model and context size is more complex. We expect MegaByte (Yu et al., 2023) or multiscale byte language models (Egli et al., 2025) to improve performance on some but not all domains. Why do you only report the compression ratio? As we train our models for lossless compression via AC (which is equivalent to log-loss minimization), the compression ratio is the only relevant metric (apart from more “practical” metrics such as running time, which we report in Table A3). The compression ratio and the log-loss are proportional (the additive factor is the model size) and can be recovered from each other. L196 misses "is". Fixed, thanks! --- Rebuttal Comment 1.1: Comment: I'd like to thank the authors for the clear explanations and congratulate to the great work! Last note: I stumbled over the point that all evaluations were done with teacher forcing as this is very different from standard LM evaluation. I see why this is not problematic here because you are always just modeling the "prompt" and never do any free generation, but I still think that this should be clarified in the final paper --- Reply to Comment 1.1.1: Comment: Yes, that's a very good point, and we will clarify this in the revised manuscript. Thank you for all your help in improving our submission!	Summary: 1. This paper empirically examines the effectiveness of small pre-trained transformers (with millions of parameters) as multimodal data compressors for text, images, and audio. 2. Trained on 165GB of data per modality, these models achieve compression ratios that surpass both general-purpose and domain-specific compression algorithms while remaining competitive with state-of-the-art online adaptive transformers. However, despite their strong performance on in-domain data, traditional compressors outperform them on out-of-distribution data. 3. The study also investigates the effects of multimodal training, revealing limited cross-modal transfer in small transformers—contrasting with trends observed in large-scale models. Claims And Evidence: yes Methods And Evaluation Criteria: Yes, The evaluation is thorough, leveraging appropriate benchmark datasets and comparing performance against both domain-specific and general-purpose compression algorithms. Theoretical Claims: Key findings: • Small pre-trained transformers can achieve compression rates comparable to both domain-specific and general-purpose algorithms. • Even with multimodal training, small transformers do not develop a universal compression ability that enables strong performance on unseen modalities. The authors present two key findings (as highlighted in the summary). Building on prior work [1][2], they conduct a comprehensive study on multi-modal training and perform extensive ablations over context size, dataset composition, and model size, ultimately deriving conclusions specific to small transformers. [1] Izacard G, Joulin A, Grave E. Lossless Data Compression with Transformer[J]. 2019. [2] Yu L, Simig D, Flaherty C, et al. Megabyte: Predicting million-byte sequences with multiscale transformers[J]. Advances in Neural Information Processing Systems, 2023, 36: 78808-78823. Experimental Designs Or Analyses: Yes, The authors compare to various standard compressors, both general-purpose, and domain-specific for audio data and PNG and lossless JPEG2000 for images. They also compare to the online transformer with the default v3.3 parameters, which is currently SOTA on the Large Text Compression Benchmark(LTCB). Supplementary Material: I have reviewed the detailed introduction to the training dataset and its construction methodology. Relation To Broader Scientific Literature: This is my main concern: the conclusions of the paper seem intuitive and straightforward. While there may not be prior work that explicitly derives these specific findings, existing literature on the multimodal generalization capabilities (in this case, compression abilities) of both large and small models already points toward similar conclusions. Essential References Not Discussed: no Other Strengths And Weaknesses: Strengths 1.The writing is clear and well-structured, making the study easy to follow. 2. This paper presents a comprehensive empirical study on the compression performance of small transformer models, particularly for multi-modal data. 3.Key findings: • Small pre-trained transformers can achieve compression rates comparable to both domain-specific and general-purpose algorithms. • Even with multimodal training, small transformers do not develop a universal compression ability that enables strong performance on unseen modalities. Weaknesses: 1. Limited novelty: The study appears to be an extension of [1], applying the pre-training of small transformers for text compression to a multimodal setting with additional ablation experiments. However, it does not seem to derive significantly more valuable insights or practical applications beyond this extension. 2. Intuitive conclusions: The conclusions of the paper seem intuitive and straightforward. While there may not be a prior work that explicitly derives these specific findings, existing literature on the multimodal generalization capabilities (in this case, their compression abilities) of both large and small models already points toward similar conclusions. The paper could be strengthened by going beyond empirical observations and offering optimization strategies—such as transfer learning—to improve small transformers' performance on unseen modalities, making the findings more actionable and impactful. [1] Delétang G, Ruoss A, Duquenne P A, et al. Language modeling is compression[J]. arXiv preprint arXiv:2309.10668, 2023. Other Comments Or Suggestions: no Questions For Authors: Please refer to weakness part. Ethical Review Concerns: no Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We thank the reviewer for their positive feedback and insightful comments. We are pleased that they think that our `paper presents a comprehensive empirical study`, which `leverages appropriate benchmarks`, and that our `writing is clear and well-structured`. What is the novelty over Delétang et al. (2024)? While our work is indeed inspired by Delétang et al. (2024), we believe that the unadjusted compression ratio that they primarily use to evaluate their models is not well suited to evaluate pre-trained neural networks as compressors since it does not capture the entire output of the compressor. The adjusted compression ratio, which is the one we investigate, induces an entirely different regime where large-scale models are no longer viable. Note that Delétang et al. (2024) are aware of this and, therefore, also report the adjusted compression ratio for their models, with the difference that the large language models (LLMs) they evaluate are not competitive in this regime. Moreover, Delétang et al. (2024) focus on off-the-shelf LLMs and only perform a single experiment where they train small transformers on enwik8 (100MB of text data) to obtain strong compression performance on enwik9. In contrast, we perform a `comprehensive empirical study` (in the reviewer’s words) in the multimodal setting with much larger datasets (165GB), where we not only show that small-scale transformers can achieve compression ratios on audio and image data that are on par with general-purpose and domain-specific compressors but also investigate the cross-modality transfer (in addition to a variety of ablations). We also improve the evaluation by always evaluating on out-of-distribution data (even within the same modality) to ensure a fair comparison with standard compression algorithms (overfitting to the training distribution is no longer possible). Accordingly, our contributions compared to the previous literature are (see also Table A1): * Small transformers can achieve competitive compression ratios on audio and image data (Delétang et al. (2024) only showed this for text data), even when comparing against domain-specific compressors. * Small transformers can achieve competitive compression ratios across multiple domains, pointing towards the generality of relatively small models. * Unlike the results on LLMs by Delétang et al. (2024), small transformers do not achieve transfer outside the training modalities. Moreover, unlike our work, Delétang et al. (2024) did not investigate in-modality out-of-distribution data (e.g., training on ImageNet and evaluating on CelebA) to show in-modality generalization. The conclusions of the paper seem intuitive and straightforward. While we agree that our results may not challenge the expectations and intuitions of experts in the field who know the literature well, we present novel quantitative results, which are significant and address an important open problem, i.e., whether small transformers pre-trained on large (multimodal) datasets can achieve competitive compression ratios across different modalities and whether there is transfer to unseen modalities, as observed in the large-scale model case (see Section 1). A priori, it was unclear whether we would attain similar conclusions to existing literature on multimodal generalization of small and large models since the compression viewpoint introduces an entirely different set of constraints on the models (most importantly with respect to their size). Finally, even some of our qualitative findings, e.g., the lack of out-of-modality transfer even for our largest models that we trained on multiple different modalities, were somewhat surprising to us. We agree that investigating more sophisticated training strategies to improve cross-modal transfer, e.g., via transfer learning, presents an interesting direction for future work and have mentioned this in the updated version of our manuscript. --- Rebuttal Comment 1.1: Comment: Thank you for the response. However, I still have concerns about whether the overall design of the paper and the conclusions are intuitive and straightforward. Although the authors provide systematic experiments to support their approach, further optimization is still lacking. Therefore, I will retain my original score.	null	null	null	null	null	null
Partially Observable Reinforcement Learning with Memory Traces	Accept (poster)	Summary: This paper addresses the problem of history summarization in POMDPs. Specifically, it proposes a new method to summarize the history with memory traces, which inspired by eligibility traces, in place of the ubiquitous finite-length window. Memory traces induce a representation that accounts for the whole history of observations with exponential discounting of the past. The paper first studies conditions for which the memory trace is an injective function of the history through an original geometric perspective. Then, it compares the properties of memory traces, namely estimation error and complexity, against finite windows in the problem of offline on-policy evaluation, showing that memory traces are competitive with windows when the forgetting is fast and potentially better than windows when the forgetting is slow. Finally, it provides an empirical evaluation in both a toy domain and an illustrative deep RL benchmark to back up the theory. Claims And Evidence: The claims are supported by theoretical derivations and a brief empirical analysis. Methods And Evaluation Criteria: Comparing the properties of different history summarization techniques in terms of policy evaluation makes sense. The choice empirical domains also fits the theoretical/conceptual nature of the work. Theoretical Claims: I only checked (briefly) the proofs reported in the main text. Experimental Designs Or Analyses: The experiments are conducted in simple domains, for which the considered design makes sense. Supplementary Material: I did not check the supplementary material, if not to look up for a few details mentioned in the main text. Relation To Broader Scientific Literature: To the best of my knowledge, the reported study is original and novel. Most of the (recent) theoretical literature on POMDPs focuses on structural assumptions on the emission functions that makes learning (with a window) statistically tractable. The study of this paper is mostly orthogonal to those results. In terms of methodology, I am not aware of previous works employing this kind of eligibility traces, although I am not familiar with methodological research in POMDPs. Essential References Not Discussed: The paper reports only a few references of a very large body of work on POMDPs. While a broader account of previous POMDP literature would be nice, I am not aware of any critical reference that should be discussed. The method is remarkably simple and I would not be surprised if someone came up with a similar ideas in prior works. There is a lot of works on eligibility traces in POMDP, but hard to tell whether they are related at all. I am more confident on the novelty of the reported analysis, as it employs arguments and techniques that I did not see in prior works. Other Strengths And Weaknesses: Strengths - Simple yet clever method for history summarization in POMDPs. - Original arguments and techniques; - Clear presentation of the ideas and compelling analysis. Weaknesses While I could not spot any major weakness in the work, my feeling is that more effort could have been made to connect the reported results to the literature of POMDPs (theoretical and empirical). Other Comments Or Suggestions: The work is really nice and original! I am happy to propose accepting it for the conference. The underlying idea is simple and compelling, well explained and analyzed with a fresh eye and original techniques. I think it could be made an even stronger work by including: - A more detailed account of how the presented results relate to recent theoretical advancements in POMDPs, e.g., under which structural properties on the emission function learning in POMDP with memory traces is nearly optimal; - A more detailed account of what the study suggests for POMDP practitioners. Practical methods include various approaches for handling long-term dependencies in the history, such as LSTM/GRU architectures (e.g., Hausknecht & Stone 2015 "Deep recurrent Q-learning for POMDPs"), history summarization with VAEs (like Dreamer, Hafner et al 2023 "Mastering diverse domains through world models"), transformers (Parisotto et al 2019 "Stabilizing transformers for reinforcement learning"). How does memory traces findings connect to those? Any rpactical takeaway from the analysis? An interesting aspect that is not touched in the paper is the following: Memory traces have a continuous hyper-parameter lambda, which seems easier to optimize from data online w.r.t. the size of the window. Especially, estimating the gradient of an "hyper-policy over lambda" looks doable... Memory traces may have another interesting use other than (general) POMDPs, such as RL with trajectory-dependent objectives: See Hazan et al 2019 "Provably efficient maximum entropy exploration", Chatterji et al "On the theory of reinforcement learning with once-per-episode feedback", Mutti et 2023 "Convex reinforcement learning in finite trials", Kausik et al 2024 "A theoretical framework for partially observed reward-states in RLHF" among others. Questions For Authors: Rewards depend on observations instead of states? Also, why the policy is Markovian and conditioned on true states!? The paragraph between lines 55-65 (right) is somewhat confusing. The reward is defined as a function from observations to reals, but in POMDP the reward is typically a function from states to reals. Perhaps is a typo there, or the authors mean a function of history of observations? Also, why the policy is a function between states and probability over actions? In POMDPs one typically considers functions from history of observations to actions... The lines 281-283 read "Thus, there exists no environment where windows outperforms memory traces in general". Are there any structural assumptions on the POMDP for which one or the other is preferable instead? In spirit, the results are saying: With $\lambda < 1/2$ windows and memory traces are on par. With $\lambda > 1/2$, there exist environments where traces outperform windows. The latter does not exclude the existence of environments where windows are better in the $\lambda > 1/2$ regime, or am I missing some nuances? Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: Thank you very much for your positive review! Below, we respond to your critical points and questions. Expanding the discussion on connections to prior work on POMDPs. We agree that our discussion on related works is relatively sparse. Based on your suggestions, as well as the other reviewers' suggestions, we will expand this section with a discussion on connections to existing empirical work that focuses on using RNNs and transformers for reinforcement learning in POMDPs. Why is the reward signal a function of the observations and not of the states? These two descriptions of POMDPs are equivalent. Given a POMDP with state space $\mathcal X$, observation space $\mathcal Y$, set of possible rewards $\mathcal R$, emission probabilities $p(y \mid x)$, and state-reward function $r: \mathcal X \to \mathcal R$, we can consider the equivalent POMDP with observation space $\tilde{\mathcal Y} = \mathcal Y \times \mathcal R$, emission probabilities $p(\tilde y = (y, r) \mid x) = p(y \mid x)[r = r(x)]$, and observation-reward function $\tilde r(\tilde y = (y, r)) = r$. We use the observation-reward definition because it emphasizes that rewards are also quantities that are observed by the agent. In this model, state and reward are conditionally independent given the observation. With the state-reward definition this is not the case, so rewards would technically need to be included explicitly in memory as they could also give information about the state. We are open to changing our definition if it is confusing. Why is the policy Markovian? If the policy $\pi$ is Markovian, then the combination of POMDP and $\pi$ describe a hidden Markov model with the same state space $\mathcal X$ as the POMDP. If the policy is not Markovian, then this is no longer true. However, this is irrelevant to our paper, and so we will change the definition in the final version as follows. Consider the general setup consisting of a POMDP with state space $\mathcal X$, observation space $\mathcal Y$, action space $\mathcal U$, transition dynamics $p(x_{t + 1}\mid x_t, u_t)$ and emission probabilities $p(y_t\mid x_t)$, and a general agent with agent state space $\mathcal Z$, agent state update probabilities $\pi(z_{t+1}\mid z_t, y_{t+1})$ and policy $\pi(u_t\mid z_t)$. Together, these describe a hidden Markov model with state space $\Psi = \mathcal X \times \mathcal Z$, observation space $\mathcal Y$, transition dynamics $$p(\psi_{t+1} = (x_{t + 1}, z_t) \mid \psi_{t} = (x_{t}, z_{t-1})) = \sum_{y_t}p(y_t\mid x_t)\pi(z_t\mid z_{t - 1}, y_t)\sum_{u_t}\pi(u_t\mid x_t)p(x_{t + 1}\mid x_t, u_t),$$ and emission probabilities $$p(y_t\mid \psi_t = (x_t, z_{t-1})) = p(y_t\mid x_t).$$ Thus, as none of our results depend on the state space of the HMM, this definition shows that our results also apply with non-Markovian policies. Are there any structural assumptions on the POMDP for which one or the other is preferable instead? This is an interesting question that we do not yet know the answer to. Our theoretical results suggest that it is always possible to use memory traces and perform at least as well as the best window-based approach. However, this is only true for the optimal choice of $\lambda$, which in general will not be known. We are interested in investigating if there is a way to connect properties of the transition and emission dynamics of the POMDP to the optimal choice for $\lambda$. If $\lambda > 1/2$, are there environments where windows outperform memory traces? Yes, there are (e.g., see example A.1). However, there is a "simple fix": just choose a different $\lambda$. If $\lambda$ is set to a value less than $1/2$, Theorem 5.5 guarantees that no window will outperform the memory trace. The T-maze, which we analyze in Theorem 5.8, is qualitatively different: there is no "simple fix" to make a window-based approach efficient here (e.g., by choosing a different $m$). Thus, there is no environment where a window-based approach outperforms memory traces for all $\lambda$. However, there are environments where a memory trace approach outperforms windows for all $m$ (e.g., the T-maze). Other suggestions. Thank you very much for your additional suggestions. We are working on a follow-up project right now, and will have a look at your references on RL with trajectory-dependent objectives. We are also examining if it is possible to learn $\lambda$ online. --- Rebuttal Comment 1.1: Comment: Dear authors, Thanks for the thorough replies to my comments and additional clarifications. I am even more convinced of my original evaluation: I will advocate for acceptance. Reward definition: No need to change the formulation, but perhaps reporting the equivalence argument in a footnote can avoid potential doubts!	Summary: The paper studies learning with memory traces as an alternative to finite length history windows to solve POMDPs. Memory traces are exponential moving average of observations. In offline RL, when the forgetting factor \lambda < 0.5, they are shown to be equivalent to learning with windows in capacity and sample complexity. If lambda is larger, they are significantly more efficient. The paper also shows that the memory traces can be easily incorporated into online RL algorithms and outperforms the windows approach. Claims And Evidence: The claims are well supported by theorems and proofs. The empirical performance of the memory traces approach is illustrated in Sutton's random walk experiment and in a Minigrid version of T-maze. Methods And Evaluation Criteria: The paper's main contributions are theoretical in nature. The key result that the memory traces are injective if lambda is rational is surprising. The sample complexity results are carefully proved using relevant mathematical machinery, e.g., Kirszbraun's theorem. The experimental results are based on relatively small domains and are proof-of-concept variety. Larger experimental domains would make the paper more attractive. Theoretical Claims: I have checked the proofs in the main paper but not those in the Appendix. The main proofs appear to be correct. Experimental Designs Or Analyses: The experimental results on the random walk domains and the T-maze domain validate the claims but are relatively small. The authors are encouraged to consider more complex and compelling experiments. Supplementary Material: No. Relation To Broader Scientific Literature: N/A Essential References Not Discussed: The paper cites all relevant prior work to the best of my knowledge. Other Strengths And Weaknesses: The paper's theoretical claims and proofs make a strong contribution to the theory of POMDPs. The paper also offers empirical evaluations in multiple domains, but these results are preliminary and can be strengthened. Other Comments Or Suggestions: The paper is well written in spite of its highly theoretical content. Questions For Authors: It appears that the effectiveness of the method relative to the windows method depends on the value of the forgetting factor. What determines the forgetting factor itself? Under what conditions do we need a forgetting factor > 1/2? Code Of Conduct: Affirmed. Overall Recommendation: 4 Ethical Review Concerns: ================= Post-Rebuttal Update ================= Thank you for the responses to the reviews. I stand by my evaluation and think that the paper should be accepted.	Rebuttal 1: Rebuttal: Thank you very much for your positive review! Below, we respond to your critical points and questions. > Larger experimental domains would make the paper more attractive. Indeed, the environments we consider in our experiments are more illustrative than realistic. We intend the main contributions of this paper to be theoretical, and we are working on a follow-up project in which we investigate memory traces empirically in more complex environments. The reason for this is that a more thorough empirical evaluation requires a lot more work. For example, the assumption of one-hot observation only makes sense in small tabular POMDPs. A proper treatment of these issues therefore goes beyond the scope of this paper. > It appears that the effectiveness of the method relative to the windows method depends on the value of the forgetting factor. What determines the forgetting factor itself? Under what conditions do we need a forgetting factor > 1/2? These are interesting questions that we do not yet know the answers to. All that our theoretical (and empirical) results suggest is that $\lambda$ should usually be larger than $\frac{1}{2}$, as otherwise a window could be used instead. In our follow-up work, we investigate whether it is possible to learn $\lambda$, and if there is a way to connect properties of the transition and emission dynamics of the POMDP to the optimal choice for $\lambda$.	Summary: The authors propose memory traces as an alternative to fixed-window histories, or “frame stacking,” for addressing partial observability in RL. The concept is loosely related to eligibility traces, amounting to an exponential moving average of the observation stream, which is then fed to the agent as input for the value function and/or policy. The authors prove conditions on $\lambda$ for injective-ness (when the trace is a sufficient statistic for the history), separability, and concentration. Analysis for offline on-policy sample complexity (in terms of minimum value error) is also given, including theorems that relate memory traces to fixed-length windows, and vice versa. The T-Maze environment is given as an instance where memory traces can be proved to be more efficient than windows. Finally, traces and windows are compared in a partially observable random walk, and again in the T-Maze environment using PPO (a deep RL agent). In these environments, memory traces are shown to achieve lower value error and higher average reward, respectively. Score raised from 2 to 3 after rebuttal Claims And Evidence: Claims are generally supported with convincing evidence. Methods And Evaluation Criteria: Overall, the methods and evaluation criteria are pretty good, aside from some experiment design concerns I have in Experimental Designs or Analyses. I think it would be beneficial to test in environments that have more partial observability, as T-maze requires remembering essentially 1 bit of information over just a few time steps. I also feel that some important baselines are missing, such as RNNs or attention. It is already well-known that a fixed-window strategy is the most naive approach for addressing POMDPs and that it does not scale well. Thus, strictly outperforming a window when there are more sophisticated techniques widely used does not feel sufficient to me. Theoretical Claims: The theoretical claims are correct, to my knowledge. ~However, the proof of Theorem 5.8 is surprising, as it prescribes setting $\lambda = (k-1)/k$ in the T-maze. In this case, the exponential average degenerates into an unweighted average of the past $k$ observations, sacrificing the injective guarantees of Theorem 4.1. Does this suggest that truly exponential traces are actually suboptimal in this environment? It seems to contradict the main message of the paper.~ Experimental Designs Or Analyses: - Random walk - The comparison is unfair here. If I am understanding correctly, the authors’ method uses linear function approximation to evaluate the memory trace, but the fixed-window baseline uses the (integer) history to index into a table. Clearly, the approximation method will perform better due to generalization. It would be far better to produce a window history by concatenating $m$ one-hot vectors; that way, both methods can use linear function approximation. Without this, I am skeptical of the results. - The step-size selection is not explained in sufficient detail. It is not reported what step sizes were used to generate Figure 4. The criteria for “best” step size is never defined. - Deep RL - For some reason, two memory traces are given to the authors’ method instead of one. One trace has $\lambda=(k-1)/k$ and the other has $\lambda=0$. This seems unfair for two reasons: ~it has a dynamic $\lambda$ and is not a true exponential average (as I discussed above) and~ it seems to give the agent an extra hint about the current observation. I cannot figure out why this was done other than to make the authors’ performance look better than reality. - The PPO optimizer is not discussed. It would not be possible to reproduce the results in the paper from their description. - Figure 5 says “average success rate” in the caption but the y-axis label says “average total reward.” I am not sure what the real metric is supposed to be. Supplementary Material: I reviewed the two counterexamples in Appendix A and the experiment details in Appendix C. I did not read the proofs in Appendix A and Appendix B. Relation To Broader Scientific Literature: There is a short related work section in which the authors cite three papers which theoretically analyzed windows of fixed length. It does not appear that any previous works studied exponential windows. Some deep RL papers which use windows as input are mentioned. There is no discussion of more sophisticated memory techniques, as far as I see. A short discussion regarding the inspiration from eligibility traces is also included. However, the relationship to eligibility traces is merely coincidental, in my opinion, and is overemphasized in the paper. TD($\lambda$) is technically not an exponential average; the weights do not sum to $1$ and nothing is being averaged. The approaches are orthogonal; it would be possible to have an eligibility trace in which the feature vectors are obtained using the memory trace proposed by the authors. Essential References Not Discussed: Deep RL using RNNs or attention, e.g., - DRQN: https://arxiv.org/abs/1507.06527 - DTQN: https://arxiv.org/abs/2206.01078 Other Strengths And Weaknesses: Strengths - The injective nature of memory traces (histories can usually be uniquely recovered) is surprising and interesting. I like the visualization of the trace space as a Sierpinkski triangle (Figure 2), which helped convince me that this is true. - The $\lambda$/$m$ sweep in Figure 4 is a nice comparison of the two different algorithms (traces vs windows) across two different hyperparameters, especially with how $m$ and $\lambda$ are lined up. Although the authors should note how they are doing this (it seems they are using the relation $m = 1/(1-\lambda)$, but it should be explained in the paper). Weaknesses - One limitation is that, despite the authors’ proof that memory traces are usually injective, the exponential decay of the traces will squash most useful information after more than a few time steps. This can be seen clearly in Figure 2, where even in a low-dimensional setting with just $\lambda = 0.7$, the points become very hard to distinguish. It is not clear to me that a function approximator would be able to meaningfully disentangle these histories without extreme overfitting. - It would be nice to see a comparison on harder, more partially observable environments. Would this scale, e.g., with image-based observations? The exponential average would smear moving or appearing/vanishing objects across the frame, and it is not clear to me if this would be useful or distracting to the agent. - I am confused by the decision to define sample efficiency in terms of the minimum-achievable value error, $\min \bar{VE}_\mathcal{E}$. Just because this value is lower does not mean that learning requires fewer samples, does it? For example, intuitively, I would think that a linear function does not have a low VE but would be easier to learn because it is convex. Other Comments Or Suggestions: - Typo in TLDR of paper: “We analyze the effectiveness of eligibility traces when used as memory a memory in POMDPs.” - Viewing Figure 6 causes my computer to lag significantly, for some reason. - Y-axis in Figure 5 is misleading, since it doesn’t start at 0. It exaggerates the difference between methods. - Typo: “A large $\lambda$ can then reduces” (line 358). - Proof of theorem 5.8 is only partial; it should be called a sketch. - Several parts of the paper use “cf.” to refer to a figure or a lemma, but “see” would be more accurate in these instances. - The proof of lemma 5.4 doesn’t seem necessary in the main paper. It takes up an entire page, but doesn’t appear to be a central result to the paper’s story. The space could be used to better explain the experiments in Section 5, for instance. - Notation $VE_\mathcal{E}$, where $\mathcal{E}$ means environment, seems incomplete. Doesn’t the minimum-achievable VE also depend on the policy, $\pi$? - Why is the reward function defined in terms of observations instead of states? This doesn’t seem to match standard POMDP formulations, which define the reward based on the underlying state. Questions For Authors: - Does the lack of injective guarantees for infinite memory traces limit the applicability of memory traces to continuing (i.e., non-episodic) environments? - ~“Thus, there exists no environment where windows outperform memory traces in general.” But is the reverse not true, i.e., traces cannot outperform windows, either? Consider a fully observable POMDP where $O_t = S_t$ always. Then wouldn’t a fixed window of $m=1$ be much easier to learn than the exponential average, which smears irrelevant information across time steps?~ Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Thank you very much for your thorough review of our paper! Below, we respond to your critical points and questions. Due to limited space, we cannot respond to every point, but we will do our best to incorporate all your suggestions in the final version. Proof of Theorem 5.8 and the choice of $\lambda = \frac{k - 1}{k}$ in the T-maze. The full proof of Theorem 5.8 is in Appendix B (p. 14). In this proof, as well as in our PPO experiment, we fix the forgetting factor to $\lambda = \frac{k - 1}{k}$, where $k$ is the corridor length of the T-maze. Importantly, this corridor length is fixed, and does not change during an episode; it is not to be confused with the time step $t$. Thus, $\lambda$ is not dynamic, and the memory trace is indeed an exponentially weighted average. Concerns about the PPO (T-maze) experiment - In the PPO experiment, we additionally give the memory trace agent access to the current observation (or, equivalently, we use a second memory trace with $\lambda = 0$). We did not do this to give an edge over the frame stacking agent. Indeed, the frame stacking agent also has access to the current observation. Instead, it was a heuristic choice and a demonstration that a practitioner is not constrained to using just one memory trace. We are happy to run additional experiments with only a single memory trace. - We use the Adam optimizer with a linear learning rate decay from $0.0003$ to $0$ as suggested by [Huang et al. 2022]. - In the T-maze minigrid, the agent receives a reward of $1$ if it succeeds, and a reward of $0$ if it does not (and $0$ in all nonterminal transitions). Thus, the "average success rate" is the same as the "average total reward". A random agent would achieve an average success rate of $0.5$. The observed performance slightly below $0.5$ is due to episodes exceeding the maximum episode length of $5(k + 2)^2$ steps in a T-maze with corridor length $k$. We will clarify this in the article. Does this address your concerns about the Y-axis in Figure 5? Concerns about the TD (random walk) experiment - Thank you for your feedback. In this experiment, our goal was to compare memory traces to the full window approach whose sample efficiency we analyze in Sec. 5. However, we agree that we could instead concatenate observations to improve sample efficiency, as we do in the PPO experiments. While we are not aware of this approach in the context of linear function approximation, we ran the experiments that you suggested, please see [here](https://anonymous.4open.science/api/repo/icml2025-rebuttal-trace/file/sutton-concat.pdf). All three algorithms ran for 100,000 steps (1/100th of Fig. 4) with a grid search over step sizes. We see that concatenation makes it possible to learn with very long windows, and that this approach almost reaches the best value error of memory traces. However, it requires almost 20 times the memory to achieve this, and it lacks the theoretical guarantees that we develop in Sec. 5. - The step size used in the original TD experiments (Fig. 4) for the window approach is $\alpha = 0.0001, 0.0002, 0.005, 0.05, 0.2, 0.5$ for $m = 1, 2, 3, 4, 5, 6$, respectively. These values were chosen by a grid search optimizing the average value error. For the memory trace, the step size was kept constant at $\alpha = 0.0002$ for all values of $\lambda$. This value was also determined by a grid search. Further points - We will expand Appendix C in the final paper. (optimizer, step sizes, ..) - Essential References. Thank you for these suggestions. We will include them in the final version. - Relation to eligibility traces. We do believe that there is a close connection to eligibility traces, and will include an extended discussion in the final version. - Definition of sample efficiency. A low minimum value error does not correspond to low sample efficiency. Could you please explain what gave this impression? We use Theorem 5.1 to tie sample efficiency to the metric entropy. - Definition of environment $\mathcal E$. In our definition of $\mathcal E$, the policy is assumed fixed (line 107). - More realistic experiments & observation-reward function. Please see our response to Reviewer tJLm. - Q1: Lack of injectivity guarantee. Could you please elaborate on this question? We provide one experiment in a continuing environment and one in an episodic environment. - Q2: "Traces cannot outperform windows". In a fully observable POMDP, we can use $\lambda = 0$ to achieve the same result. Theorem 5.5 guarantees that, if learning with windows is tractable, then learning with traces is also tractable. Please let us know if you still have any concerns, or if our responses were not satisfactory. If you agree that we have addressed your questions and provided the necessary clarifications, we kindly request raising our paper’s score based on the responses provided. We are happy to incorporate further feedback into the paper to improve clarity and remove ambiguity. --- Rebuttal Comment 1.1: Comment: Thanks for the rebuttal. I have crossed out any questions/concerns which are no longer applicable. I also follow up some more points below: --- > The full proof of Theorem 5.8 is in Appendix B (p. 14). Thanks for the clarification about the static $\lambda$. I see that the full proof is in the appendix, but my point was that the proof written in the main paper is abbreviated and should be labeled as a sketch to avoid confusion. Typically, this is done by writing Proof (sketch). --- > We are happy to run additional experiments with only a single memory trace. Please do if it is possible. I feel this is crucial to remain true to the theory and to fully connect the theory with the experiment results. Using two memory traces instead of one has all sorts of theoretical consequences not addressed by the paper (e.g., strengthening injectivity and information content) and it would be more appropriate for future work that analyzes dual traces, in my opinion. --- > Does this address your concerns about the Y-axis in Figure 5? Yes! Thank you, but please make sure to clarify this in the paper. --- > We see that concatenation makes it possible to learn with very long windows, and that this approach almost reaches the best value error of memory traces. However, it requires almost 20 times the memory to achieve this, and it lacks the theoretical guarantees that we develop in Sec. 5. --- The concatenation of observations is the standard approach for windows using function approximation, being exactly analogous to frame stacking with images and convolutional networks. It does greatly increase memory consumption and computation, but these are deficiencies of the window approach---which is is exactly why I wanted the experiment to be included. It demonstrates the benefits of memory traces while eliminating generalization as a confounder. > Relation to eligibility traces. We do believe that there is a close connection to eligibility traces, and will include an extended discussion in the final version. --- Mathematically, it is clear why memory traces look like eligibility traces, but I personally would refrain from calling it a close connection. (If you have a counterargument, though, I'd love to hear it.) Memory traces learn a value function over the trace itself, i.e., if $z_t = (1-\lambda) (x_t + \lambda x_{t-1} + \dots)$ is the memory trace, then it learns $V(z_t)$. Eligibility traces learn a value function over the original inputs, $V(x_t)$, using the reinforcement signal $\delta_t z_t$. The only similarity is the computation of the traces $z_t$, but their roles are completely different and orthogonal. For example, to learn $V(z_t)$ using eligibility traces, you would need an eligibility trace over memory traces: $z^\prime_t = (1-\lambda) (z_t + \lambda z_{t-1} + \dots)$ and then reinforce according to $\delta_t z^\prime_t$. One is changing the input space of the value function, the other is changing the reinforcement signal applied to each input and, as a consequence, the fixed point of the TD update. --- > Definition of sample efficiency. A low minimum value error does not correspond to low sample efficiency. Could you please explain what gave this impression? We use Theorem 5.1 to tie sample efficiency to the metric entropy. I was confused by the statement immediately after Theorem 5.1: "While this result does not guarantee that function classes with large metric entropy are less suitable for learning, it suggests that a good value function is more easily learned if both $VE(\mathcal{F})$ and $H_\epsilon(\mathcal{F})$ are small." Given that the start of section 5 said that the analysis would focus on sample complexity, the phrase "more easily learned" seemed to suggest that both a small value error and a small metric entropy would improve sample complexity/efficiency. --- > Q1: Lack of injectivity guarantee. Could you please elaborate on this question? We provide one experiment in a continuing environment and one in an episodic environment. Theorem 4.1 says that finite histories are needed for injectivity. This implies infinite histories (continuing environments) are not injective, but the paper doesn't discuss the ramifications of this. I was curious if it would limit the effectiveness of memory traces in non-episodic environments. --- Reply to Comment 1.1.1: Comment: Thank you again for your time in reviewing and responding! New PPO experiments. We ran the additional experiments that you requested: PPO in the T-maze with only a single memory trace (with the same forgetting factor $\lambda_k \doteq \frac{k - 1}{k}$ as before). Please see the results [here](https://anonymous.4open.science/api/repo/icml2025-rebuttal-trace/file/ppo2.pdf). We have also included a purely reactive agent as a baseline which should help put the other performances into perspective. It can be seen that a single memory trace is still preferable to frame stacking in long corridors, and that adding a second one ($\lambda = 0$) helps even more. For very long corridors, we see that the reactive agent struggles to even find the end of the corridor reliably before the time runs out. Relation to eligibility traces. The reason why we mention eligibility traces is that this is where the idea for memory traces stems from. Eligibility traces serve as a "memory" for the TD algorithm, where they are used for temporal credit assignment. However, you are completely right that it is possible to use memory traces and eligibility traces in parallel, and that they are designed for different purposes. We believe that there is a connection, because our empirical results (Fig. 4) show that TD(0) algorithm, when used with memory traces ($\lambda$ close to $1$), converges very close to the optimal memory trace solution. This is in contrast to the window/memoryless value functions, where the TD(0) fixed point is relatively far from the optimal solution. While memory traces indeed change the input space of the value estimate, we can still compare learned weight vectors for different $\lambda$. For example, given a linear (memory trace) value estimate $\hat v(z) = w^\top z$, we can define a state value estimate as $\tilde v(x) \doteq \mathbb E [w^\top z_t \mid x_t = x] = \tilde w^\top x$, with $\tilde w = (I - \lambda \hat T)^{-\top}E^\top w$, where $\hat T$ is the time-reversed transition kernel of the HMM, and $E$ is the emission matrix. Note that in the fully observed case ($E = I$), this expression reduces to the original weight vector if $\lambda = 0$. Thus, $\lambda$ indeed affects the convergence point, although it is in a different way than TD($\lambda$). As this connection is still somewhat unclear, we agree that it is best not to include it in this paper, and we will make sure to make the distinction between the two concepts as clear as possible. Definition of sample efficiency. We see why this sentence may be confusing, and we will change the phrasing in the final paper. The minimum achievable value error in $\mathcal F$ only plays a role in that, if it is very large, then it is impossible to learn a "good" value function in $\mathcal F$ (as none exists). However, it is unrelated to the sample complexity of learning. Injectivity. Thank you for clarifying. Injectivity may sound desirable at first, as it means that no information is lost, but this actually makes learning harder (it is equivalent to keeping the whole history). Injectivity still holds for infinite histories when $\lambda < 1/2$ (line 204, left column). It is for this reason that we analyze Lipschitz continuous functions of memory traces rather than general functions. The Lipschitz constant limits the "resolution" of the functions that we consider, and Theorem 5.4 shows that the metric entropy (and thus, the complexity of learning) increases as we allow larger Lipschitz constants $L$. Without limiting $L$ (or introducing some other constraint), we could therefore not learn efficiently (it would be equivalent to learning with complete, infinite-length histories). Thank you very much for showing interest in our work! We will make sure to address your remaining points in the final paper.	Summary: The authors propose a novel method for handling observations in reinforcement learning for partially observable systems. Their method represents the history of observations with an exponential moving average. The authors analyze sample complexity bounds for offline on policy evaluation. The novel method is compared with the traditionally used moving windows both theoretically and empirically. Claims And Evidence: All claims are supported by evidence. Methods And Evaluation Criteria: The authors use classical benchmark tasks that are well suited for the problem at hand. Theoretical Claims: I did not independently verify all the proofs in detail. Experimental Designs Or Analyses: The experiment contains classical benchmark tasks and compares to the traditional method of moving windows. The experiments for value evaluation and for control are sound. Supplementary Material: I did not review the supplementary material. Relation To Broader Scientific Literature: This paper is a theoretical contribution to the POMDP literature. While most current methods use neural network based approaches like RNNs or transformers, they lack theory. This paper contributes to the understanding of observation history representation in POMDPs. Essential References Not Discussed: I think it would have been interesting to discuss the use of RNNs and transformers to represent the history of observations. Other Strengths And Weaknesses: Strength: The authors effectively introduce the concept of memory traces with a well-designed example in Figure 1. This simple yet insightful illustration (using the T-maze environment) clearly demonstrates the motivation behind memory traces and their advantage over traditional window-based approaches. Weakness: The evaluation is on relatively simple tasks. Exploring a broader range of environments could further establish the generality of the approach. Other Comments Or Suggestions: It would be interesting to discuss how to chose $\lambda$ in different environments. Questions For Authors: Do you assume the agent remembers its actions? Actions also provide important context for the agent. I am more familiar with different descriptions of the POMDP setting, where the reward is a mapping from the latent state to the reward. Does this impact the proposed method? Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Thank you very much for your positive review! Below, we respond to your critical points and questions. > I think it would have been interesting to discuss the use of RNNs and transformers to represent the history of observations. We are happy to include a brief discussion of the connections to RNN and transformer-based methods. Indeed, it is possible to view memory traces as a kind of simplified RNN, while the window-based approach has a fixed context length like transformers. Based on the other reviews, we will include references to https://arxiv.org/abs/1507.06527 and https://arxiv.org/abs/2206.01078. > The evaluation is on relatively simple tasks. Exploring a broader range of environments could further establish the generality of the approach. Indeed, the environments we consider in our experiments are more illustrative than realistic. We intend the main contributions of this paper to be theoretical, and we are working on a follow-up project in which we investigate memory traces empirically in more complex environments. The reason for this is that a more thorough empirical evaluation requires a lot more work. For example, the assumption of one-hot observation only makes sense in small tabular POMDPs. A proper treatment of these issues therefore goeses beyond the scope of this paper. > It would be interesting to discuss how to choose $\lambda$ in different environments. We agree that this is an interesting question that is not fully addressed in the paper. All that our theoretical (and empirical) results suggest is that $\lambda$ should usually be larger than $\frac{1}{2}$, as otherwise a window could be used instead. In our follow-up work, we investigate whether it is possible to learn $\lambda$, and if there is a way to connect properties of the transition and emission dynamics of the POMDP to the optimal choice for $\lambda$. > Do you assume the agent remembers its actions? Actions also provide important context for the agent. In this paper, we define memory traces only based on the observations. However, it is easy to include actions in the traces as well by regarding them as observations, i.e., by considering the augmented observation space $\tilde{\mathcal Y} = \mathcal Y \times \mathcal U$. > I am more familiar with different descriptions of the POMDP setting, where the reward is a mapping from the latent state to the reward. Does this impact the proposed method? These two descriptions of POMDPs are equivalent, so it would not impact the proposed method. Given a POMDP with state space $\mathcal X$, observation space $\mathcal Y$, set of possible rewards $\mathcal R$, emission probabilities $p(y \mid x)$, and state-reward function $r: \mathcal X \to \mathcal R$, we can consider the equivalent POMDP with observation space $\tilde{\mathcal Y} = \mathcal Y \times \mathcal R$, emission probabilities $p(\tilde y = (y, r) \mid x) = p(y \mid x)[r = r(x)]$, and observation-reward function $\tilde r(\tilde y = (y, r)) = r$. We use the observation-reward definition because it emphasizes that rewards are also quantities that are observed by the agent. In this model, state and reward are conditionally independent given the observation. With the state-reward definition this is not the case, so rewards would technically need to be included explicitly in memory as they could also give information about the state. We are open to changing our definition if it is confusing.	null	null	null	null	null	null
LLaVA-ReID: Selective Multi-image Questioner for Interactive Person Re-Identification	Accept (poster)	Summary: This paper introduces a new task named interactive person re-identification (I-ReID), which aims to address the insufficient details in initial human descriptions. To support this task, the paper contributes a new dataset comprising multi-round dialogues generated using a customized approach with vision-language models (VLMs). Another key contribution is a novel interactive framework tailored for the ReID domain. The well-designed question model effectively identifies the most informative questions from the gallery, significantly enhancing performance. Experimental results demonstrate the superiority of this task-specific interactive framework over existing methods from other domains and show its ability to supplement missing details in text-based ReID methods. Claims And Evidence: Yes. The main technical claims are: (i) Representative Candidate Selection emphasizes critical differences between individuals. (ii) Informative Question Generation dynamically selects the most informative questions for supervision. Both claims are well-supported by extensive experiments. Methods And Evaluation Criteria: Yes. The paper proposes a multi-round dialogue benchmark for the interactive person ReID task. This benchmark includes three types of Q&A pairs, which could facilitate further research in this area. Theoretical Claims: The paper does not involve theoretical claims. Experimental Designs Or Analyses: Yes. I have reviewed all experimental designs and results. Table 1 and Figure 1 present performance comparisons against existing interactive retrieval methods in other domains. Table 2 highlights the effectiveness of the proposed method over existing text-based ReID methods, underscoring the necessity of interactive ReID for supplementing missing details. Additionally, ablation studies confirm the indispensability of each module. Supplementary Material: I have reviewed the supplementary materials, including details on the dataset and the implementation of the proposed method. Relation To Broader Scientific Literature: The contribution of the paper could be summarized in two main aspects. i) New task. Considering the practical demands of security and protection, the paper releases a novel task named interactive person reid, which involve progressively revealing the most relevant person according to the witness's description. ii) Novel approach. The proposed method could not only emphasize the critical differences between individuals, but also dynamically select the most informative questions as supervision. Extensive experiments verify the effectiveness of the method. More importantly, the experiment results show off that the interactive framework could bring performance gain for the existing text-based reid methods, demonstrating the insufficient details in the existing human-annotated data. Essential References Not Discussed: The authors discuss and compare a wide range of related methods. Other Strengths And Weaknesses: Strengths: 1) The paper introduces a novel and practical task: interactive person ReID. 2) It provides the first dialogue-based dataset for this task. 3) The proposed approach is novel, and experiments confirm its effectiveness over existing interactive methods from other domains. 4) The framework can be integrated into text-based ReID methods to mitigate the issue of insufficient human-annotated details, significantly improving performance. Major Weaknesses: 1) GPT-like VLMs are prone to hallucinations. Have the authors considered this issue in dataset construction? Could leveraging existing dataset annotations help mitigate hallucinations? 2) Why does the instruction for generating fine-grained captions start with coarse-grained captions? Would an alternative approach better leverage the VLM’s captioning capabilities? 3) Figure 3 needs revision: (i) The input to the text encoder should not be limited to the initial description, and (ii) the meaning of "clue" in the figure is undefined. 4) Will the text input exceed the maximum input length of the CLIP model? 5) It is unclear how the question model functions when the interactive framework is integrated with existing text-based methods. Minor Weaknesses: 1) Steps ii and iii in dataset construction appear somewhat redundant and could be merged for clarity. 2) The abbreviation "I-ReID" may be confused with the widely recognized image-based ReID. A different abbreviation is recommended. Other Comments Or Suggestions: Please see the weaknesses. Questions For Authors: Please see the weaknesses. Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: Thanks a lot for reviewing our paper and giving us valuable suggestions. We will answer the questions one by one. > Q1: Visual hallucination in VLM captioning. Thanks for your insightful comments. We acknowledge that GPT-like vision-language models (VLMs) are prone to hallucinations, particularly when generating fine-grained descriptions. Leveraging existing techniques, such as contrastive decoding [1], in data construction could further improve the accuracy and reliability of our descriptions. We will explore these enhancements in future work. [1] Leng S, Zhang H, Chen G, et al. Mitigating object hallucinations in large vision-language models through visual contrastive decoding[C]//Proceedings of the IEEE/CVF Conference on Computer Vision and Pattern Recognition. 2024: 13872-13882. > Q2: Explanation of coarse-to-fine captioning. In interactive ReID, we expect the witness to provide additional fine-grained discriminative information in the subsequent dialogue rounds. This information should not merely repeat what has already been stated. Therefore, we use the coarse description as a basis for generating the follow-up description. An alternative approach could be to generate a fine-grained description first and then remove the overlapping content with the initial description. However, our generation strategy simplifies this process of decomposing the description, making it more efficient and structured. > Q3: Revision of figure 3 (i) Thanks for your advice, we will change it to "Descriptions from Witness". (ii) The term "clue" refers to the embeddings of the context description $z_t$. We use this term to indicate that the candidates are selected based on the current "clue" we have at hand. We apologize for any confusion caused by this terminology and will revise the figure in the next version. > Q4: Long text encoding of CLIP model As mentioned in Appendix C, we interpolate the text positional embeddings from 77 to 192 and finetune fine-grained captions in Interactive-PEDES to obtain the Retriever. If the total text length exceeds 192 tokens, we truncate it accordingly. In practice, since the initial description has a maximum length of 48 tokens, the average length per turn in a five-round dialogue is (192-48)/5=28.8. This is sufficient for the current interaction setup, and we can also further interpolate it to longer encoding lengths. > Q5: Details about the question model functions when the interactive framework is integrated with existing text-based methods. Please refer to our response to Q1 from reviewer fi2Z. > Q6: Re-organize section 3.2 (dataset construction) Thanks for your valuable suggestions. We will revise this section to improve the clarity. > Q7: Abbreviation of interactive person re-identification. Thank you for pointing this out. We will update the abbreviation to "Inter-ReID" in the new version. --- Rebuttal Comment 1.1: Comment: The author's reply has mostly cleared up my questions, so I'll stick with the original score.	Summary: In this paper, a novel task is presented to address the limitations of traditional text-based ReID which rely on complete and one-time descriptions from witnesses. This work introduces interactive person re-identification (I-ReID) that employs multi-round question-answer dialogue to iteratively gather information of person. To achieve this, a question model is designed to generate context-aware questions based on both visual and textual cues. Additionally, the authors construct a dataset tailored to I-ReID and employs a looking-forward strategy to prioritize the most informative questions. Experimental results demonstrate its effectiveness. Claims And Evidence: The paper's central claim is that witnesses often struggle to provide complete and clear descriptions of a target person on their own. This claim is well-supported by researches in interactive cross-modal retrieval and is intuitively valid within the text-based ReID domain. Furthermore, experimental results validate that even datasets with human-annotated, fine-grained descriptions inevitably contain partial or ambiguous information. Methods And Evaluation Criteria: The proposed methods and evaluation criteria are appropriate for the problem setting. Recall and mAP are standard metrics in text-based person ReID, and BRI (introduced in recent interactive retrieval research) is also used to evaluate the effectiveness of the interactive refinement process. Overall, the proposed methodology and evaluation framework align well with the problem context and practical application. Theoretical Claims: The paper does not propose new theoretical claims. Experimental Designs Or Analyses: I have reviewed the experimental analyses, and the experimental design appears sound and well-structured. Supplementary Material: I have read the appendix which includes some statistics and visualization of the dataset, the prompt for dataset construction, the prompt fort training, and some case studies. The appendix is comprehensive. Relation To Broader Scientific Literature: This paper introduces an interactive setting for text-based person ReID. Previous studies mainly focus in improve the fine-grained matching capability and test on the static and complete description in existing dataset. However, real-world scenarios often involve incomplete or ambiguous descriptions provided by witnesses in isolation. This paper bridges that gap by proposing an interactive refinement approach, enhancing both applicability and robustness of text-based ReID in practical settings. Essential References Not Discussed: No Other Strengths And Weaknesses: ### Strengths 1. The interactive framework could be a new research direction for the community, improving the applicability of text-based ReID in real-world cases. 2. The paper constructs a new dataset with initial descriptions, fine-grained descriptions, and multi-round dialogues, enabling more effective training and evaluation of interactive ReID methods. 3. The proposed candidate selection model provides representative sample to the model and effectively benefit the question generation. Experimental results demonstrate the effectiveness of the proposed method. ### Weaknesses 1. The multi-images questioner will lead to additional computational overhead. The authors should provide a comparison of inference time between their method and baseline models. Additionally, the number of candidate images is likely a critical factor in performance; an ablation study on this aspect would strengthen the analysis. 2. The expression clarity of Gumbel top-k sampling should be improved. While the rationale behind using Gumbel top-k sampling is understandable, its role and the necessity of the Gumbel trick should be more clearly explained. Other Comments Or Suggestions: 1. There is a typo in section 5.2 (We compared…) 2. The author should add an interpretation of BRI (e.g. lower is better) in the caption of Table 1. Questions For Authors: 1. In section 5.3, what contextual information does the answer model use? Given that existing datasets lack additional fine-grained descriptions, how is this experiment conducted? 2. The figure 7 seems to be confusing. If the rank is 1, why is the target person not visible among the given images? Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: We appreciate the insightful questions and will address your concerns in the following. > Q1: Comparison of inference time and ablation study on the number of candidates. We conduct these experiments on NVIDIA RTX 3090 GPUs. The inference time for the 5-round question generation of LLaVA-ReID and other baseline methods are shown in the table below: \| Method \| Inference Time (second per person) \| R@1 \| \| -------------- \| ---------------------------------- \| ----------------- \| \| SimIRV \| 0.007 \| 61.3 \| \| ChatIR \| 0.216 \| 63.9 \| \| PlugIR \| 13.06 \| 65.4 \| \| LLaVA-ReID \| 0.621 \| 73.2 \| Our multi-image questioner does not add significant computational overhead and achieves the best performance. The retrieval results for different numbers of candidate images are shown in the table below: \| Number of Candidates \| R@1 \| R@5 \| R@10 \| mAP \| BRI \| \| -------------------- \| --------- \| -------- \| -------- \| --------- \| --------- \| \| 2 \| 72.4 \| 89.7 \| 94.5 \| 53.2 \| 0.738 \| \| 4 (ours) \| 73.2 \| 90.6 \| 96.0 \| 53.3 \| 0.719 \| \| 6 \| 71.4 \| 89.2 \| 94.2 \| 52.8 \| 0.764 \| \| 10 \| 71.6 \| 88.9 \| 93.8 \| 52.7 \| 0.772 \| The results indicate that setting $k=4$ provides the best balance between retrieval performance and computational efficiency. In our previous experiments, the reported BRI was computed using a logarithm with base 2. According to the recently released code of BRI[1], we have corrected this by using the natural logarithm (base $e$). While this change slightly affects the absolute values of BRI, the relative ranking and overall conclusions remain unchanged. > Q2: Introduction of Gumbel subset sampling. Thanks. To enable the selector to explore more possible combinations during the training stage, we employ a differentiable random sample strategy, namely, Gumbel-top-$k$ relaxations. This approach introduces randomness to increase the diversity of candidates while ensuring that the NLL loss gradient can be properly backpropagated for effective optimization. > Q3: BRI metric interpretation. BRI (Best Log Rank Integral) assesses the system’s ability to refine retrieval results over multiple interaction rounds. It measures the average area under the log-rank curve of all rounds. A lower BRI value indicates a more efficient and effective refinement process. We will make this clear in the next version. > Q4: Input of Answerer in section 5.3. The T-ReID datasets only provide caption-image pairs of individuals, we turn to the multi-modal LLM to simulate the users. Specifically, we use LLaVA-OneVision-Qwen2-7B-ov as the Answerer. It provides the follow-up descriptions, looking at the image of the target person. > Q5: Ambiguous figure of qualitative results. The 4 images of candidates in the figure are the selected candidates and the rank represents the similarity ranking of the target person within the gallery after current round. We will improve the clarity of Figures 7 and 8 in the next version.	Summary: This paper introduces interactive person re-identification, which refines partial text queries via dialogue interactions to better suit real-world scenarios. The proposed LLaVA-ReID generates discriminative questions using images and dialogue history, enhanced by an image selector and a looking-forward supervision strategy. Experimental results show significant improvements over existing methods. Claims And Evidence: In the motivation of this paper, the authors claims that users rarely provide a detailed and comprehensive account of the target person’s appearance, often resulting in partial and vague descriptions. This claim is well-founded, as it aligns with observations in real-world applications where initial queries are often incomplete. Methods And Evaluation Criteria: The method makes sense in the context of person re-id and the evaluation metrics are common. Theoretical Claims: N/A Experimental Designs Or Analyses: More analysis about visual and textual context should be provided. Supplementary Material: This paper provides statistics of the dataset, prompts, and visualization in the appendix. These additional materials effectively complement the main paper by providing deeper insights into the dataset characteristics and the model's behavior. Relation To Broader Scientific Literature: Prior work in this field largely assumes that query descriptions are complete and well-structured, which is often not the case in real-world applications. In contrast, the authors introduce an interactive cross-modal retrieval technique that explicitly accounts for the inherent misalignment between dataset queries and practical user inputs, and address the candidate selection and tailored supervision for this fine-grained question generation task. Essential References Not Discussed: N/A Other Strengths And Weaknesses: Strengths: It introduces an interactive approach to text-based person re-id that is applicable and user-friendly in real-world scenarios. The new benchmark is thoughtfully constructed to mirror actual questioning methods, thereby enhancing the practical relevance of the work. Moreover, by integrating traditional methods, the work reveals the task's potential to extract more detailed information about individuals, underscoring its innovative contribution to the field. Weaknesses: In Section 5.3, although it highlights the potential benefits of combining two retrieval models through an ensemble, how to apply the ensemble remains unclear. Additionally, the manuscript lacks clarity on how dialog is encoded within the retrieval model; it remains uncertain whether any preprocessing steps or LLM-based rewriting techniques were employed to adapt the training data. Other Comments Or Suggestions: N/A Questions For Authors: Please refer to the weaknesses. Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: Thank you for acknowledging the novelty of our method. We will answer the questions one by one. > Q1: Details about the ensemble. In our integration of LLaVA-ReID with the existing T-ReID framework, we use the human-annotated captions in the T-ReID datasets as the initial queries. We first encode an initial query $T$ using T-ReID model and compute the matching score between $T$ and gallery images: $$ \operatorname{score}(I_i\|T)=\operatorname{sim}(\phi^{base}_t(T), \phi^{base}_v(I_i)), $$ where $\phi_t^{base}$ and $\phi_v^{base}$ are text and visual encoder of T-ReID model, $I_i$ is the $i$-th image in gallery, and $\operatorname{sim}(\cdot, \cdot)$ denotes cosine similarity. Next, we perform 5 rounds of interaction and encode the dialogue history $D=\{T, A_1,\dots, A_t\}$ using our Retriever, then compute the matching score: $$ \text{score}(I_i\|D)=\operatorname{sim}(\phi_t(D), \phi_v(I_i)). $$ Then we re-rank the matching scores by simply averaging two scores: $$ \text{final\\_score}_i=\frac{1}{2}(\text{score}(I_i\|T)+\text{score}(I_i\|D)), $$ and the final score is used to compute the retrieval metrics. It’s important to note that the T-ReID dataset only provides caption-image pairs for persons. To simulate user interactions, we turn to a multi-modal LLM. Specifically, we use LLaVA-OneVision-Qwen2-7B-ov as the Answerer, which generates follow-up descriptions based on the image of the target person. > Q2: Preprocessing of dialogue. For dialogue preprocessing, we remove prefixes such as "Yes," "No," and multiple-choice options like "A)" and "B)" from the answers. The remaining responses are then directly concatenated and fed into the text encoder. While our current approach is straightforward, we believe that post-hoc techniques, such as dialogue rewriting, could be a promising strategy to enhance the system's ability to generalize to real-world, open-form responses.	Summary: The paper introduces a new task for person re-identification, an interactive person re-identification (I-ReID) framework that iteratively refines incomplete or vague descriptions through multi-round dialogues. The paper proposed LLaVA-ReID, a selective multi-image questioner that leverages both visual and textual contexts to generate targeted questions aimed at uncovering fine-grained differences among candidate images. The work is also supported by a newly constructed dataset which includes both coarse and fine-grained descriptions along with multi-round dialogue. Extensive experiments demonstrate its effectiveness over existing methods in both interactive and traditional text-based ReID tasks. ## update after rebuttal After rebuttal, I have no further questions. I am inclined to maintain the score as Accept. Claims And Evidence: The paper claims that interactive refinement via multi-round dialogues can significantly improve person re-identification accuracy compared to static, text-based approaches. These claims are verified by experimental evidence on the Interactive-PEDES dataset and integration with existing T-ReID frameworks. Methods And Evaluation Criteria: The proposed method for multi-round interactive retrieval is reasonable. The evaluation criteria about retrieval metrics and interaction efficiency are appropriate for assessing the system’s performance. Theoretical Claims: There is no theoretical claim. Experimental Designs Or Analyses: Experimental evaluations are comprehensive. Supplementary Material: The supplementary material is well-organized, providing dataset statistics, prompt for dataset construction, and the implementation details. Relation To Broader Scientific Literature: The work is well-situated within the fields of interactive cross-modal retrieval and text-based person re-identification. It builds upon recent approaches by addressing the fine-grained differences that traditional interactive retrieval methods have not adequately considered, thereby contributing meaningfully to the literature. Essential References Not Discussed: N/A Other Strengths And Weaknesses: Strength: 1. This manuscript presents an interactive framework for person re-identification that more closely mirrors real-world scenarios by engaging in multi-round dialogue to iteratively refine descriptions, thereby addressing a key limitation in traditional text-based ReID methods. 2. The construction of the Interactive-PEDES dataset with its detailed coarse and fine-grained descriptions and multiple dialogue rounds, providing a robust benchmark that can drive further research in the area, filling an important gap in available data. 3. The experimental evaluation is thorough, including integration with existing text-based ReID frameworks and detailed analysis of both image and question selection strategies. Weaknesses: 1. While the candidate selection mechanism particularly the use of Gumbel-top-k relaxation is effective, the paper provides limited in-depth analysis of its robustness. 2. The computational complexity associated with processing multiple images and iterative dialogue rounds may hinder real-time application. Other Comments Or Suggestions: Please refer to the "Strengths And Weaknesses" Questions For Authors: 1. Can you provide further analysis or experiments to assess the computational efficiency of your candidate selection module compared to baseline methods? 2. How do you define the parameter $k$ in the Gumbel-top-k relaxation within your selection strategy? 3. In the LLaVA-ReID framework, does the conversation get embedded into the LLaVA module before the candidate images are appended? 4. In Figure 3, could you explain the meaning of the term “clue”? Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: Thanks for your comments. We will answer your questions one by one in the following. > Q1: Can you provide further analysis or experiments to assess the computational efficiency of your candidate selection module compared to baseline methods? (As well as the question generation time) We conduct the experiment on the computation time of different select strategies, including top-k, k-means, and our selector. The experiment is performed on NVIDIA RTX 3090 GPUs, and we report the total selection time over five rounds in the table below: \| Select Strategy \| Time (second per person) \| R@1/R@5 \| \| --------------- \| ------------------------ \| --------- \| \| selector \| 0.002195 \| 73.2/90.6 \| \| k-means \| 0.028286 \| 72.5/90.1 \| \| uniform \| 0.000099 \| 72.7/90.0 \| \| top-k \| 0.000187 \| 72.5/89.8 \| Our lightweight transformer-based selector achieves the highest retrieval accuracy while ensuring no significant computational overhead compared to other methods. We also provide the inference time for 5-round question generation of LLaVA-ReID and other baseline methods are shown below: \| Method \| Time (second per person) \| R@1 \| \| -------------- \| ------------------------ \| ----------------- \| \| SimIRV \| 0.007 \| 61.3 \| \| ChatIR \| 0.216 \| 63.9 \| \| PlugIR \| 13.06 \| 65.4 \| \| LLaVA-ReID \| 0.621 \| 73.2 \| Our multi-image questioner does not add significant computational overhead, indicating its suitability for real-time applications. > Q2: How do you define the parameter $k$ in the Gumbel-top-k relaxation within your selection strategy? The number of candidate images plays a crucial role in providing rich visual context to the Questioner. If too few candidates are given, the Questioner may not receive sufficient fine-grained information between persons. Conversely, an excessive number of images can overwhelm the MLLM’s capacity, introducing redundancy and extra computational costs. To further analyze the impact of $k$, we present retrieval results for different numbers of candidate images in the table below: \| Number of Candidates \| R@1 \| R@5 \| R@10 \| mAP \| BRI \| \| -------------------- \| --------- \| -------- \| -------- \| --------- \| --------- \| \| 2 \| 72.4 \| 89.7 \| 94.5 \| 53.2 \| 0.738 \| \| 4 (ours) \| 73.2 \| 90.6 \| 96.0 \| 53.3 \| 0.719 \| \| 6 \| 71.4 \| 89.2 \| 94.2 \| 52.8 \| 0.764 \| \| 10 \| 71.6 \| 88.9 \| 93.8 \| 52.7 \| 0.772 \| The results indicate that setting $k=4$ provides the best balance between retrieval performance and computational efficiency. In our previous experiments, the reported BRI was computed using a logarithm with base 2. According to the recent released code of BRI [1], we have corrected this by using the natural logarithm (base $e$). While this change slightly affects the absolute values of BRI, the relative ranking and overall conclusions remain unchanged. > Q3: In the LLaVA-ReID framework, does the conversation get embedded into the LLaVA module before the candidate images are appended? As depicted in Equation 3, candidate images are inserted before the dialogue history, in accordance with the default configuration of LLaVA. For improved visual clarity, we modify the input order in Figure 3. > Q4: In Figure 3, could you explain the meaning of the term “clue”? The term "clue" refers to the embeddings of the context description $z_t$. We use this term to indicate that the candidates are selected based on the current "clue" we have at hand. We apologize for any confusion caused by this terminology and will revise it in the next version. [1] Lee S, Yu S, Park J, et al. Interactive Text-to-Image Retrieval with Large Language Models: A Plug-and-Play Approach[C]//Proceedings of the 62nd Annual Meeting of the Association for Computational Linguistics (Volume 1: Long Papers). 2024: 791-809. --- Rebuttal Comment 1.1: Comment: Thanks for the detailed response and I have no further questions. I am inclined to maintain the score as Accept.	null	null	null	null	null	null
Right Now, Wrong Then: Non-Stationary Direct Preference Optimization under Preference Drift	Accept (poster)	Summary: The paper introduces Non-stationary Direct Preference Optimization (NS-DPO) for preference learning on non-stationary offline datasets. With an assumption on the upper bound of preference drift and log-linear policies, the paper also shows that the method achieves a sample complexity of $O(n^{-1/4})$, or $O(n^{-1/2})$ when the upper bound of drift goes to zero. In experiments on synthetically-created temporally-varying preference datasets, the paper shows that NS-DPO achieves a better reward accuracy than vanilla DPO. In experiments on stationary datasets, experiments show that the two achieve comparable reward accuracy. Claims And Evidence: - The theoretical claims are well-supported, with careful enumeration of assumptions. - The claim that NS-DPO achieves comparable performance empirically is based on reward accuracy, which doesn't necessarily reflect how the policy model is used in practice. For instance, [Rafailov et al. 2024](https://arxiv.org/pdf/2406.02900) show that reward accuracy correlates poorly with win rate (Fig 4). Methods And Evaluation Criteria: - See above for note on the use of reward accuracy alone to assess performance in the experiments. - Even after reading the supplement, I was still a bit confused about the dataset construction and setup. Just double checking, for the gradual drift experiments, the datasets were constructed such that the model sees increasing new data during training, and evaluation occurs on a held-out timestep that's later than all the training data? Theoretical Claims: I skimmed but did not carefully check the proofs in the appendix. Experimental Designs Or Analyses: - See above for extending the evaluation beyond reward accuracy. - The sliding window DPO (SW-DPO) method seems like an important one to mention in the main paper. I appreciate the synthetic experiment comparing with it, but a further comparison seems important to justify the use of all the data and NS-DPO over a subset of the data and vanilla DPO. For instance, a characterization of when NS-DPO is preferred would improve this paper substantially. Supplementary Material: I skimmed through the entire supplement. Relation To Broader Scientific Literature: I appreciate the comparison to the literature on parameter drift in bandits, as well as other theoretical literature on DPO. Essential References Not Discussed: To my knowledge, the related work does a good job comparing to recent work studying and extending DPO. Other Strengths And Weaknesses: Strengths: - The theoretical analysis is precise and is well-situated within the existing literature (e.g., comparable setup to Chowdhury et al. 2024). Weaknesses: - More discussion about the practical implications of the theorems would be helpful. - The experimental analysis could be strengthened with the use of other evaluation metrics (e.g., win rate) and inclusion of the SW-DPO baseline in the main experiments. Other Comments Or Suggestions: The conclusion mentions ICL but I do not see any mention elsewhere. Is this perhaps a typo? Questions For Authors: 1. Could the authors provide more discussion on the implications of the theoretical results? 2. Could the authors additionally evaluate using win rate? 3. Could the authors include SW-DPO for further comparison? Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We thank the reviewer for their time and recognising the precision of our theoretical analysis. We address the questions and suggestions of the reviewer as follows. ## Response to the questions __(1) “For the gradual drift experiments, were the datasets constructed such that the model sees increasing new data during training? ”__ Please note that our setting considers __offline learning__ scenarios, so __all the datapoints with time step information are provided before the training starts__. Because the reward for determining preference is changing gradually, the preferences between responses are more likely to change at datapoints with later timesteps. It is correct that the evaluation is done with the preferences at a time step that is later than all the training datapoints. __(2) “Does the evaluation occur on a held-out timestep that's later than all the training data?”__ Yes, the evaluation is done with the preferences at a time step that is later than all the training datapoints. __(3) “The conclusion mentions ICL but I do not see any mention elsewhere”__ In page 7, left column, line 369-372, we explained that tDPO refers to the in-context learning baseline. tDPO is a variant of DPO where the time step information is explicitly mentioned in the prompt. As demonstrated in the experiment result (Figure 2, Figure 9), tDPO did not significantly improve from stationary DPO. ## Response to the suggestions __(1) “Could the authors provide more discussion on the implications of the theoretical results?”__ We believe the core implications of the theoretical results are sufficiently discussed in the paper. To recap and summarize: __(1-a)__ Preference drift negatively affects the performance of policies. (in the form of tracking error, Theorem 2 in page 5) __(1-b)__ When we only know the total amount of preference drift ($B_T$ in the paper) and the time steps in the paper, we can use exponential weighting to address the preference drift. The optimal value of the discounting parameter $\gamma$ can be computed when we know $B_T$. (line 293-294, page 6) __(1-c)__ As $B_T$ approaches zero, NS-DPO with optimally defined $\gamma$ becomes identical to stationary DPO. (Corollary 4 in page 6) __(2) “The experimental analysis could be strengthened with the use of other evaluation metrics (e.g., win rate)”__ __Win rate evaluation is in the appendix, where we find it correlates well with reward accuracy__. We point the reviewer to the UltraFeedback-LM dataset explained in Appendix C.2 and Appendix C.6 where we presented the results of win rate experiments. We used `llama-3.2-1b-it` for fully fine-tuning the policy within our compute limit. NS-DPO outperforms stationary DPO in terms of Length-Controlled Win rate (LCWR), similar to the reward accuracy comparisons. __(3) "inclusion of the SW-DPO baseline in the main experiments”__ We point the reviewer to the additional experiment we conducted with SW-DPO [__(link 1)__](https://anonymous.4open.science/r/nsdpo_icml2025-7DCE/imgs/swdpo_ultrafeedback_lm_optimalw.jpg), where we added SW-DPO results to Table 1 in page 18 of the paper. We trained policies with SW-DPO using the __optimal window sizes__ to only allow the datapoints after the preference change. __Despite using information not allowed in the setting of our work__, SW-DPO significantly underperforms NS-DPO in Length-Controlled Win Rate (LCWR) of AlpacaEval. We attribute this to SW-DPO __ignoring all the datapoints outside the window__. We also present the results for UltraFeedback-RM datasets extended from Figure 9, where we show that SW-DPO shows worse reward accuracy when window size is not optimal [__(link 2)__](https://anonymous.4open.science/r/nsdpo_icml2025-7DCE/imgs/swdpo_exp_w51_l27b_nbc_ufb_rho1.0.pdf) and similar accuracy when we assign optimal window sizes [__(link 3)__](https://anonymous.4open.science/r/nsdpo_icml2025-7DCE/imgs/swdpo_exp_optimalw_l27b_nbc_ufb_rho1.0.pdf). We hope our responses have addressed all the questions the reviewer had about our work. We respectfully ask the reviewer to reconsider their evaluation of our paper in light of our answers and additional experimental results. We are eager to help clarify any further questions the reviewer might have as we believe in the importance of the problem this paper seeks to address. --- Rebuttal Comment 1.1: Comment: Thank you for the response. The additional experiments as well as the clarifications to my questions are great, and I have raised my score.	Summary: This paper discusses a new approach called NS-DPO to address the issue of temporal preference drift in LLMs. Current LLM preference optimization algorithms do not account for changes in preferences over time, leading to misalignment. NS-DPO models time-dependent reward functions using a Dynamic Bradley-Terry model and introduces a computationally efficient solution by adding a single discount parameter in the loss function. This parameter enables exponential weighting, focusing learning on more recent and relevant data. The paper provides theoretical analysis of NS-DPO's convergence, offering upper bounds on estimation error and regret caused by non-stationary preferences. Experimental results demonstrate that NS-DPO fine-tuned LLMs remain robust under drifting preferences, outperforming baseline algorithms that ignore temporal changes, while maintaining performance in stationary scenarios. Claims And Evidence: The problem setting and direction of this research are intriguing, as current studies in LLMs are increasingly focusing on more complex and challenging scenarios. The overall claims made in the paper are valid, and the identified challenges, as well as the discussion of related works, are well-aligned with the evolving landscape of LLM research. Methods And Evaluation Criteria: However, the proposed method does not fully make sense to me for this challenging problem setting. The main difference between NS-DPO and DPO is the introduction of the decaying factor $\gamma$, which is sensitive to time $t$. While this design allows the LLM to focus more on recently collected data, it may fail to account for sudden changes in user preferences. This is because the decaying factor cannot detect or adapt to abrupt shifts in user preferences. If the LLM places more weight on learning recent data, historical data may become irrelevant; conversely, sudden changes in preferences could negatively impact the model's alignment. As a result, it is challenging to determine an appropriate value for $\gamma$ that effectively resolves this dilemma. Theoretical Claims: I appreciate this analysis of this paper, especially for leveraging the regret analysis in multi-armed bandits. Provide new insights for this RLHF community. Experimental Designs Or Analyses: The experimental design make sense and may create some dataset with different preference change strength. Supplementary Material: Briefly review the proof. Relation To Broader Scientific Literature: LLM, RLHF, and DPO. Essential References Not Discussed: No. Other Strengths And Weaknesses: No. Other Comments Or Suggestions: . Questions For Authors: Can NS-DPO be aware of the preference change of users? Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We thank the reviewer for their time and recognising the intriguing nature of this problem. We believe this will become a far more prevalent problem as LLM providers gather bespoke datasets over longer time frames and are keen to raise this within the LLM research community. As such, we are glad the reviewer agrees with us that this is aligned with the evolving direction of LLM research. __Response to the Concerns: “Adopting decay factor $\gamma$ may fail to account for sudden changes in user preferences.”__ We address this at two points in our manuscript: __(a)__ Firstly we direct the reviewer to Assumption 1 [Section 4]. __This assumption places no constraint on how the preference changes__, as such our theoretical analysis addresses the case the reviewer raises where preferences change suddenly. As seen in Theorem 3, the value of $\gamma$ is set by $B_T$ which can be thought of as the ‘size’ of the preference change. A large sudden change will result in a smaller value of $\gamma$ focusing the algorithm’s learning on points closer to the present. We also note that this setting and exponential weighting technique are thoroughly analyzed in the multi-armed bandits literature. We point the reviewer to line 99-105 of page 2, left column where we discuss the references. __(b)__ Secondly, __we explicitly test the setting where preferences change suddenly__ in our experiment section. We direct the reviewer to Figure 3 a) and Figure 4, in which we test NS-DPO when preferences change suddenly at a specific changepoint for a variety of different strengths of preference change (controlled by $\rho_\textrm{diff}$). We note that whilst DPO and IPO fail as the reviewer predicted, NS-DPO maintains its strong performance, even when we fixed the value of $\gamma$ for all sudden preference drifts! __Response to the Question: “Can NS-DPO be aware of the preference change of users?”__ Yes, while the information is limited. The setting we consider in our work only allows the knowledge of the __total amount of parameter drift, which is $B_T$__. NS-DPO requires the knowledge of $B_T$ to set its exponential weight $\gamma$ for the best possible performance. In practice, we additionally provide experiment results where we test NS-DPO under various strengths of preference drift with a __fixed value of $\gamma$__, which still showed significant performance improvement over stationary baselines. We hope our responses have addressed all the questions the reviewer had about our work and ask that they raise their score. We are eager to help clarify any further questions the reviewer might have as we believe in the importance of the problem this paper seeks to address.	Summary: This paper addresses the issue of temporal preference drift in training large language models (LLMs) using human feedback. The authors propose Non-Stationary Direct Preference Optimization (NS-DPO), which incorporates a Dynamic Bradley-Terry model to account for time-dependent reward functions. This method introduces an exponential weighting parameter to focus learning on more recent data points, improving model robustness under preference changes. Claims And Evidence: The claims made in the submission are generally supported by clear and convincing evidence. The authors provide theoretical analysis with proofs for the convergence and regret bounds of NS-DPO, showing its effectiveness in handling non-stationary preferences. They also conduct extensive experiments on various datasets with controlled preference drift, demonstrating that NS-DPO outperforms existing methods like DPO and IPO in different scenarios, especially when significant preference changes occur. Methods And Evaluation Criteria: The proposed methods and evaluation criteria in the paper are well-suited for addressing non-stationary preference optimization in LLM training. Theoretical Claims: While I did not verify the detailed proofs, the derivations and arguments presented are clear and logically consistent. Experimental Designs Or Analyses: The experimental designs demonstrate both merits and drawbacks. On the positive side: 1. The synthetic experiments offer controlled settings to assess NS-DPO under known preference shifts 2. Testing across multiple datasets showcases the method's broad applicability 3. Ablation studies effectively clarify the impact of key parameters However, limitations exist: 1. The paper primarily uses synthetic data for main experiments 2. Real-world datasets have artificially induced preference drift rather than naturally occurring shifts Supplementary Material: N/A Relation To Broader Scientific Literature: N/A Essential References Not Discussed: N/A Other Strengths And Weaknesses: see `Experimental Designs Or Analyses` Other Comments Or Suggestions: see `Experimental Designs Or Analyses` Questions For Authors: see `Experimental Designs Or Analyses` Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We thank the reviewer for their response and recognising that our conclusions are well supported by both theoretical evidence and extensive experiments that show NS-DPO’s effectiveness in handling non-stationary preferences. We think this is a super important problem, unaddressed within the literature, and that it will become more prevalent as companies build proprietary datasets over longer time frames. ## Response to Limitations __(1)__ To the best of our knowledge, we are the first to address the problem of non-stationary preferences within the LLM fine-tuning literature. As such we were __unable to find any publicly available datasets__ that exhibit this property, as most are well curated for specific goals e.g. Helpful Harmless, and not preference drift. __(2)__ To account for this we created datasets by introducing preference drift into pre-existing, realistic preference datasets. We specifically tested challenging preference drifts in our experiments i.e. the preference change is strong and occurs suddenly. In Figures 3a and 4 we explicitly test NS-DPO on such preference drifts, a sudden shift from one reward model to another over varying times and with increasing strengths, and show that NS-DPO is robust to such changes even in the most challenging settings. __(3)__ By drawing attention to this problem and providing a simple and effective solution, we hope to attract the attention of the wider research community and collaborate to create more realistic datasets, however that is beyond the scope of this initial work which clearly demonstrates the problems that non-stationary preference drift can have on algorithms designed from a stationary perspective. Once again we thank the reviewer for their time and ask that they consider raising their score further in light of these arguments. This problem is exciting and underexplored though it will be of great interest in the future, and we believe that our work addressed this in a simple and effective way. --- Rebuttal Comment 1.1: Comment: Thanks for your effort and reply and I will maintain my score.	null	null	null	null	null	null	null	null
No Soundness in the Real World: On the Challenges of the Verification of Deployed Neural Networks	Accept (spotlight poster)	Summary: The paper provides a detailed theoretical and empirical analysis on the soundness of neural network verifiers. The paper demonstrates that a number of State of the Art verifiers can produce misleading or even wrong results when considering the evaluation of NNs on modern hardware. ## update after rebuttal I stand with my opinion that this paper should be accepted, I appreciate the authors' responses. For the sake of completeness, I am copy-pasting my comment in the reviewer discussion below to make it available to the authors: It seems to me that a key difference in opinion between reviewers lies in the question of whether the results are surprising. I want to share my perspective on this question from two angles and would be very interested to hear your thoughts about this: 1. Necessity of Surprise For some of the solvers, I personally was not surprised that they are not floating point sound. However, despite the lack of surprise, I believe these results are timely and valuable because they empirically demonstrate a phenomenon that I suspected to be present, but have not seen evaluated to any degree as detailed as in the paper at hand. In my opinion, we should thus not only measure this publication by the degree to which we were surprised by the outcome, but also by the degree to which the empirical results are valuable information to the community. And in this instance, I believe there is clearly timely, important information that warrants dissemination: The results indicate that even four years after the publication by Zombori et al. NN verifiers still struggle with the same problems. One might even argue that this paper can be seen as a "call to arms" for the NN verification community to start addressing this critical challenge. 2. Level of Surprise Above, I mentioned that I was not surprised by the results for some solvers. However, the authors also show that there are instances in which, e.g., the solver DeepZ is unsound w.r.t. floating point arithmetic. On page 2 of [Singh et al. 2018] the DeepZ paper states, "Further, our transformers are sound w.r.t. floating point arithmetic.". This is, in fact, even mentioned in the abstract. Later on in the paper, this statement is made even more precise (page 3): "To ensure soundness with respect to different rounding modes and to account for the lack of algebraic properties such as associativity and distributivity in the floating point world [...]". However, it is precisely this lack algebraic properties (presumably associativity) that is the reason why DeepZ produces an unsound result for Order3 in Table 3 of the paper. In no way do I wish to attack the authors of DeepZ here, who have actually gone much further than most NN verification tools to achieve floating point soundness, but it is a prime example of just how difficult this is to achieve -- and a result which surprised me. A possible consequence might be that we can only provide guarantees w.r.t. concrete implementations/hardware configurations; there might also be other possible solutions. But I do not see it as a burden for the authors of this paper alone to find a solution to this issue, which spans most of the NN verification community. Instead, I see this as an instance where raising the issue and providing a precise problem formulation together with appropriate empirical results is a worthy contribution in and of its own. Claims And Evidence: The paper provides convincing support for the theses put forward by demonstrating its results both theoretically and empirically. The paper provides strong evidence for the observation that verifiers must do a better job at tieing their guarantees to the assumed implementation. Methods And Evaluation Criteria: The chosen methodology and evaluations are very convincing. Theoretical Claims: The arguments for the theoretical propositions are sound in my understanding. Only concerning the proof of Proposition 5.5 I have a question: For the multiset {$1.1,1.1,1.1,1.1,1.1,1.1,1.1,1.1,1.1,\omega$} you state that $U_r=\omega+18$. If I am understanding this correctly, because the smallest number after $\omega$ is $\omega+2$ we make a step of at least $2$ for each addition (because the floats become less and less dence), but could it not be the case that $U_r$ is larger than $\omega+18$? This does not invalidate the proof of course. Experimental Designs Or Analyses: The experiments underscore the theoretical contribution of the paper. I appreciate the evaluations of accuracy w.r.t. 8 different execution environments which nicely underscore the paper's point. Supplementary Material: No. Relation To Broader Scientific Literature: The paper correctly points out that the cited NN verification tools lack a principled treatment of (deployment-level) floating point behaviour. It may be of interest to the authors, that this issue is also discussed in [ESOP25] as the "Implementation Gap" in NN verification. Beyond the NN verifiers discussed in the paper, there also exists a line of work on quantized NN verification (e.g. [AAAI24] and implementation synthesis (e.g. [EMSOFT23]) which may provide partial answers to the problems discussed in this paper. Overall the paper does a good job at reviewing relevant literature. [ESOP25] https://arxiv.org/abs/2501.05867 [AAAI24] https://ojs.aaai.org/index.php/AAAI/article/view/30108 [EMSOFT23] https://dl.acm.org/doi/full/10.1145/3609118 Essential References Not Discussed: No. Other Strengths And Weaknesses: The paper delivers some hard, but necessary lessons for the NN verification community at large: It is paramount that NN verifiers put more effort into grounding their verification results w.r.t. implementation assumptions. Proposition 5.1 and 5.4 might provide some answers to this end: When fixing the execution order at execution, there might still be hope. To this end, it is worth noting that NN verification is of particular interest in control applications where NNs run in embedded systems. In such cases it should be possible to predetermine the execution order. This does not lessen the important contribution of this paper, which underscores the importance of this grounding with a striking clarity. Other Comments Or Suggestions: Proposition 5.1.: Missing word: "Let [...] be the interval evaluation" Page 5: Typo: "is a suitable choice for bounding" Questions For Authors: See "Theoretical Claims" Code Of Conduct: Affirmed. Overall Recommendation: 5	Rebuttal 1: Rebuttal: We thank the reviewer for the thorough and positive review and the many useful suggestions and pointers! We will incorporate these in the paper. While we agree with all of the comments, we elaborate on some of the specific points. Proof of Proposition 5.5. Indeed, if the number of bits of the floating point representation is very small, $U_r$ may become even larger. For example, when using the 8-bit minifloat format, $\omega=16$, so adding the 9th 1.1 will increase the sum by 4, resulting in $U_r=\omega+20$ (which, indeed, would not affect the validity of the proof). However, we mention in the appendix that we consider IEEE 754 representations. We made this more precise by stating that the proofs assume at least IEEE half-precision (or binary16) format, which is the lowest resolution IEEE 754 standard float. For a smaller number of bits and other alternative floating point definitions, the proofs are still valid with slight adjustments. Recommended references. We found the three included references very interesting and relevant, and we plan to incorporate them into our work. The ESOP 2025 accepted paper (parallel to our work) is particularly interesting as it also studies issues that stem from the difference between idealized descriptions and actual implementations. The paper is complementary to our work, approaching the problem from a different angle by focusing on the need for more accurate specifications for verification. We also agree that quantized neural networks (the remaining two references) are a promising approach if one wants to get rid of the floating point issues in verification, although it requires non-trivial future work to assess the trade-offs and limitations, as well as the potential remaining floating point issues involved in the quantization process itself.	Summary: The paper discusses a crucial problem with neural network verification: The networks are evaluated not as pure mathematical functions, but on real-world hardware that depends on specific floating point precision and computation orderings. However, this fact is often not taken into account by NN verification tools. Therefore, they may state that a network is robust to a certain perturbation, even though adversarial examples exist due to rounding errors. The authors state this property both in general, and demonstrate it in practice. They show that all tested verification tools give unsound results for specifically crafted adversarial networks. # Update after Rebuttal Thank you for your rebuttal. Based on your responses, as well as the clarifications to the questions raised by the other reviewers, I will increase my rating to "Accept". I recommend to spend part of the extra page that the camera ready version is allowed to have on further explaining why your contribution is important: Soundness cannot be restored by using arbitrary-precision verifiers, and the usually considered verification problem differs from the deployed version. This seems to be the biggest criticism raised. Claims And Evidence: The claim of the paper is demonstrated in practice on a set of experiments. The authors successfully generate network architectures that are incorrectly evaluated by a number of verification tools. Therefore, they are able to show that floating point errors are currently not correctly handled in existing work. Methods And Evaluation Criteria: The evaluation makes sense: They demonstrate the theoretical risk for unsoundness exists in practice by evaluating multiple verification tools on a number of adversarial networks. This succeeds at proving their point that existing verification tools are unsound for specific floating point rounding errors. Theoretical Claims: I did not check the correctness of the proofs. Experimental Designs Or Analyses: The experiments appear to be sound. Supplementary Material: I did not review the appendix. Relation To Broader Scientific Literature: The fact that verification tools may not be sound in the face of floating point errors was known, but not evaluated to the extend done in this paper. Some tools choose to ignore this issue completely, others claim to be sound to floating point errors. This paper does a good job at demonstrating the risks, and describing how to test future verification tools for soundness w.r.t floating point arithmetic. Essential References Not Discussed: I am not aware of specific literature that is missing. However, floating point arithmetic must be of interest to e.g. verification of C programs, too. How do those verifiers handle these issues? E.g., what would happen if the adversarial network is converted to a simple C program (by enumerating all operations for each neuron) and verified? The paper may benefit from looking into this in more detail. Other Strengths And Weaknesses: While the main point (tools not being sound w.r.t. floats) is not novel, the technique to design the adversarial network is. Its strength is demonstrated by the experimental evaluation, where it can fool all evaluated verifier. Therefore, I consider the paper to be original and of significance. Other Comments Or Suggestions: N/A Questions For Authors: 1) Is proposition 5.1 supposed to use $f([x, x])$? This would apply $f$ to the interval only containing $x$, which I did not expect here. 2) See my question in "Essential References Not Discussed": How do verifiers for other languages solve the floating point problem, e.g. for C programs? Could you fool them, too, using your adversarial architecture? If not, how do they solve this, and could NN verification tools implement similar safeguards? Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: We are happy to see that the reviewer considers the paper original and of significance. Let us address the issues raised. Issue 1: The main point is not novel. The reviewer correctly states that floating point issues have been shown to fool certain approaches to verification. However, some verifiers were claimed to be sound, and indeed, they cannot be fooled with the known approaches because they carefully consider floating point representation and computation, although only w.r.t. the idealized verification problem we present in Eq (1) but not in the deployed verification problem in Eq (2). So, we consider the theory behind our adversarial networks a novel contribution, shedding light on the specific issues with deployed neural networks. Question 1: Yes, the formulation is correct. The theoretical value $f(x)$ (thus, evaluated on a single input $x$) might not be representable, even if $x$ is representable in the given floating point representation. Therefore, even on a single representable input, IBP will compute an interval $[a,b]$ where both $a$ and $b$ are representable and, in general, $a<b$. Question 2: Numeric program verification is indeed a very similar problem (note also the ESOP 2025 reference included by reviewer Twzp that addresses exactly this idea). Accordingly, sound verifiers are frequently based on classical techniques and ideas (Miné, 2004). We are not aware of any works in the literature that would offer solutions to the problems we raised in the general case. If the program is deterministic (no parallelization, fixed floating point representation, and execution order), then the expression tree is fixed, and approaches like IBP will be sound. However, if there is true randomness (that is, not pseudo randomness), like a random ordering of some associative computations based on the current state of the environment, then verifying the program will be much harder. In the case of neural networks, where large associative expressions dominate in an inherently random environment due to paralllelization, hardware, load balancing, etc., this issue is central for provably sound verification. --- Rebuttal Comment 1.1: Comment: My previous comment regarding my score increase and recommendation for the final paper was supposed to be the rebuttal comment that I'm asked to submit.	Summary: This paper studies the problem of the gap between theoretical soundness and practical soundness of neural network verification, which is commonly seen in the deployment of neural networks. It also proposes adversarial networks based on such characteristics to fool the verifiers to compromise soundness. Experiments validate the findings of such unsoundness. ## update after rebuttal Thanks for the further clarification of the setting and the problem the paper is tackling. I feel like it is a borderline paper, and I am a bit conservative because the claims and findings in the paper are serious and are supposed to need more empirical results to justify them. I would like to give a score of 2.5 if it is allowed. Claims And Evidence: It is quite an interesting topic for neural network verification. However, it seems that the key findings are due to floating-point issues, which is not very impressive and surprising. Methods And Evaluation Criteria: - In Section 4.2, verified domain and verified property adopt different assumptions regarding the rounding issues, which seems to be not fair and needs more justification. - I agree the IBP suffers floating error because the bounds are concretized at each layer. However, in symbolic bound propagation verification methods (e.g. CROWN), the floating error seems to be intuitively alleviated because the bounds are concretized only at the last layer. Theoretical Claims: Yes, looks good to me. Experimental Designs Or Analyses: - One major concern regarding the experiments of adversarial networks lies in that it seems to be very easy to "defend" such attack, because it typically has larger weights or abnormal memory costs during inference. - Besides, since floating error can influence the general performance of neural networks [1], I wonder how the adverial networks perform regarding the clean accuracy, i.e. the normal and general performance. If the clean accuracy is also compromised due to such patterns, it is actually not harmful to verifiers because such neural networks themselves are flawed and there is no need to verify them. [1] Li et al. Reliability Assurance for Deep Neural Network Architectures Against Numerical Defects, 2023 Supplementary Material: Yes Relation To Broader Scientific Literature: Related to neural network verification Essential References Not Discussed: References look good to me Other Strengths And Weaknesses: See above Other Comments Or Suggestions: See above Questions For Authors: See above Code Of Conduct: Affirmed. Overall Recommendation: 2	Rebuttal 1: Rebuttal: We are pleased to read that the reviewer finds the topic interesting. Let us discuss the main issues raised here. Issue 1: The discovered issues are not surprising. Please refer to our answer to reviewer N1Xq that covers the same issue in detail. Issue 2: In symbolic methods, the floating point issue is alleviated. We specifically discuss symbolic approaches in Section 5.4, where we prove that they do not guarantee sound verification. This has to do with the fact that the deployment-related issues we study represent a problem even when computing the sum of inputs (arguably, the simplest possible function), as we explain at the beginning of section 5.1. In the case of the sum, symbolic approaches become essentially equivalent to IBP, regarding floating point error. We discuss them separately only because some specific symbolic methods use a slightly safer method to bound intervals, but we prove that this does not suffice. Therefore, unfortunately, symbolic approaches do not alleviate this specific problem. Issue 3: The Definitions in Section 4.2 need more justification. Since the discussion of the verified property does not make any assumptions, we believe the reviewer means the definition of the verified domain, where we use the definition $D_{p,\epsilon,{\cal E}}= D_{p,\epsilon}\cap X$, while in reality this is not perfectly correct, because this definition does not take into account that the p-norm cannot be computed exactly either, which in turn might make some different deployed domains (based on the exact p-norm) indistinguishable for certain verifiers. However, this slight simplification does not affect the validity of our theoretical results, because we study only single-point inputs (see also our answer to Question 1 of reviewer pP6j). Issue 4: Abnormal weights and memory costs make the attacks easy to detect. Our backdoored networks do not need abnormal amounts of memory. As for weights, we stress that our focus was not to provide undetectable attacks, instead, we wanted to provide existential proofs for the theoretical observations we made (namely, that none of the known verifiers are practically sound). However, the backdoors we used can be made more undetectable via distributing the operations over many neurons and many layers so that no individual weights are too large, as was done, for example, in (Zombori et al 2021). Such optimizations are out of the scope of the paper. Issue 5: Clean accuracy might be affected by the attack. Please recall that our backdoor design is not based on training on poisoned data; instead, we modify a trained network. Our backdoors are activated under certain circumstances (precision or operation order), depending on the deployment environment. Our simplest backdoor, for example, functions as a switch that is activated by floating point precision: the backdoor is active in 32-bit environments and inactive in 64-bit environments. When the backdoor is inactive, it does not affect the original clean network, thus, accuracy will stay the same. When the backdoor is active, it changes every prediction of the network by shifting the class label, which drastically reduces accuracy. We thank the reviewer for reference [1], which is an interesting paper, but it focuses on a rather different problem (detecting potential numeric errors (Inf, NaN) in the entire input domain as opposed to bounding error in a limited (safe) domain), besides, it uses IBP as well to examine numeric error, and so it does not take into account the deployment environment either. --- Rebuttal Comment 1.1: Comment: Thank you for the detailed clarification. It is indeed an interesting topic, however, I am still concerned about the lack of empirical justification to support the abnormal memory and clean accuracy with the modification of the trained network. Since this paper is to tackle the issues under the deployment environment, these empirical justifications are of more importance, and the non-sound claim needs more experimental evidence beyond discussion. I will keep my score as it is borderline, and more work can be done to strengthen the paper. --- Reply to Comment 1.1.1: Comment: Thank you for the comment. We feel that our answers to issues 4 and 5 were not formulated well enough, so we use this last opportunity to try and provide an even more informative answer. On the point of clean accuracy, let us try a different angle, reacting directly to the comment > If the clean accuracy is also compromised due to such patterns, it is actually not harmful to verifiers because such neural networks themselves are flawed and there is no need to verify them. One way to interpret this is assuming that the reviewer is suggesting that if a network is so bad that it is obviously useless then we need not verify it in the first place. True, but our networks are not obviously useless. The backdoor is activated only in certain environments, and the backdoored network passes verification, so it looks like a safe network. Also, in most environments, the backdoored network works well (when the backdoor is not active). What the verifier misses is that there are some environments in which it does not work well. This is, in fact, our main message. Verification should give us a guarantee in advance that the network will be fine everywhere it is going to be applied. It seems we did not understand the reference to abnormal memory usage, and unfortunately, we still don't. Indeed, the backdoored networks are slightly larger than the original networks due to adding the backdoor, but the number of extra parameters is relatively small and practically independent of the size of the original network. Also, this is irrelevant because our goals do not include creating networks indistinguishable from some reference network. Large weights are involved, too; however, as stated in our original rebuttal, this is not a problem here because our example networks still serve the purpose they were designed to serve and, as we mentioned, one could get rid of large weights with known techniques, but it was not the goal here either. We hope we were able to clarify at least some of the issues.	Summary: The paper discusses the soundness of neural network verifiers. In particular, it exploits the order of floating point operations which may lead to unsound bounds computed by a neural network verifier. Claims And Evidence: The paper wants to demonstrate the most current neural network verifiers cannot fully handle the floating point errors introduced in a neural network. The paper constructs a few networks which contain a backdoor triggered by floating point erros and then evaluates whether existing verifiers produce unsound results on these inputs. Methods And Evaluation Criteria: The basic technique used in this paper is to construct certain neurons as a “backdoor” whose calculation involves large numerical errors and then be detected to trigger a different behavior of the network. To evaluate the soundness of existing verifiers, some neural networks are constructed in this way and then verified using these verifiers to see if they are sound against such backdoors. If they claim the network is “safe”, then they are unsound. Theoretical Claims: The paper made some theoretical discussions on the floating point errors under standard IEEE representations. These claims look reasonable. Experimental Designs Or Analyses: Several neural network verifiers are tested against the different types of backdoored networks. Not surprisingly, many of the verifiers do not consider the floating point ordering issues in their implementation, and may output unsound bounds given the network prepared by the author. Supplementary Material: The supplementary materials contain code, which I did not run and check. Relation To Broader Scientific Literature: Neural network verification is an important topic for ensuring provable guarantees of neural networks in mission-critical systems. The soundness of neural network verifiers is the cornerstone of provable guarantees of neural networks, and is an important topic to study. Essential References Not Discussed: During the discussion period, I realized that the authors did not sufficiently discuss existing efforts from the formal methods community on dealing with floating point soundness. To improve the contributions of this paper, the best way is to discuss how to address these challenges in a practical way, specialized to the neural network verification settings. I realize that the paper did not discuss related works dealing with floating point soundness issues in formal verification, which may have caused the misinterpretation. I recommend these papers, which may help the authors to see what have been done on addressing this well-known issue and how they can be specialized to the NN verification setting. A Two-Phase Approach for Conditional Floating-Point Verification: https://mariachris.github.io/Pubs/TACAS-2021.pdf Scalable yet Rigorous Floating-Point Error Analysis: https://shemesh.larc.nasa.gov/fm/papers/SAFECOMP2017-draft.pdf Correct Approximation of IEEE 754 Floating-Point Arithmetic for Program Verification:https://shemesh.larc.nasa.gov/fm/papers/SAFECOMP2017-draft.pdf Floating-Point Verification using Theorem Proving: https://www.cl.cam.ac.uk/~jrh13/papers/sfm.pdf Automatic Estimation of Verified Floating-Point Round-Off Errors via Static Analysis: https://shemesh.larc.nasa.gov/fm/papers/SAFECOMP2017-draft.pdf Formal Verification of Floating-Point Programs: https://www.lirmm.fr/arith18/papers/filliatre-formal.pdf FORMAL VERIFICATION OF AN IEEE FLOATING POINT ADDER: https://www.df7cb.de/cs/publications/2001/fpadder-cb.pdf Automating the Verification of Floating-Point Programs: https://inria.hal.science/hal-01534533/document Other Strengths And Weaknesses: The finding of this paper is interesting, although it is not very surprising - any numerical solvers will have numerical errors, and give ill-conditioned inputs, we expect them to fail. I am also not sure about its practical importance - the constructed cases in this paper are quite artificial and can hardly be linked to real networks being verified, and the methodology is also straightforward. If such a soundness issue can be discovered in a more realistic scenario, the paper could have a better impact. Other Comments Or Suggestions: The usability and soundness tradeoff is well-known when applying formal methods - for example, when you verify a C program, do you want to verify down to the bit or gate level? Or just at the semantic level? The hardware (e.g., floating point unit) may have rounding errors during execution, and do we want to verify down to the logic gate level to ensure the correctness of the program? Technically, it is possible since all the actual circuits to implement these computations (whether it is a general computer program or a neural network) are implemented using logic gates, so the entire problem is a boolean satisfiability problem. If you verify exactly the hardware you execute your neural network, then there is no soundness issue. However, it is often not practical because of scalability of verifying to this level (floating point addition, multiplication etc result in very complex logic) and the diversity of hardware implementation. Instead, most neural network verifiers work at the semantic level, assuming the underlying hardware is accurate. By crafting artificial examples that exploit these assumptions, surely you will see the soundness issues reported in this paper. So I personally feel this result is not novel enough for publishing alone - more contributions, such as how to address this challenge, or demonstrate unsoundness in neural networks in production, will be helpful. Questions For Authors: Technically, we could implement a verifier to consider the worst-case floating point error but that will significantly reduce the scalability of neural network verifiers. This is currently not done since the biggest challenge in neural network verification is still the scalability to handle large networks, rather than floating point soundness. It’s always a tradeoff - just like in program verification, we don’t always verify down to bit-level accurate floating point numbers - it is simply too slow; yet, verifiers are still useful despite the fact they theoretically could be unsound. It is worthwhile to discuss how to efficiently improve floating point soundness in a verifier while maintaining its efficiency. Code Of Conduct: Affirmed. Overall Recommendation: 2	Rebuttal 1: Rebuttal: We are encouraged by the fact that the reviewer considers the paper interesting and the topic important. Before moving on to addressing the specific issues raised, let us recall that our specific interest lies in provably sound verification (a motivation shared by a sizable community) as opposed to heuristic verification. This is important because this determines what is interesting and what is less so in this context. Issue 1: The discovered issues are not surprising. Our goal was to shed light on an issue that has been in a blind spot because, although most works on provably sound verification give full consideration to floating point representation, features of deployment environments such as the stochasticity of associative operations have not been in focus. We have to admit that initially, we did find it a bit surprising that none of the current verifiers claimed to be provably sound are actually sound in deployment. This motivated us to dive deeper and prove this theoretically, and to demonstrate this in practice as well. Issue 2: Practical motivation is unclear. As stated above, our primary motivation was the theoretical problem of provably sound verification in deployment. Nonetheless, we demonstrated the issues through backdoored networks that reveal that it is practically feasible for an attacker to circumvent any verifier just by having enough information about the deployment environment. Indeed, our examples are artificial, but the “naturalness” can be enhanced with more distributed designs that avoid extremely large weights and other obvious patterns. This was not the focus of this work. Question: Is the efficient verification of provable soundness possible in deployment? We do not think so, at least not in the general case. In fact, this is one of our intended takeaway messages. As we mention in the paper, for example, covering all the possible orderings is not likely to be computationally feasible at scale. In extremely sensitive environments where provable soundness is required, one needs to control the execution tightly, and with such extra assumptions, provable soundness in deployment might indeed be feasible, at least no less feasible than the verification of the theoretical model of the network. --- Rebuttal Comment 1.1: Comment: Thank you for the response and I appreciate the discussion. I still find the paper interesting but not very surprising since numerically ill-conditioned inputs are well-known problems for any solvers/verifiers. Practically, it is really a tradeoff between usability and soundness - although we could, for example, run any verification algorithm using soft float with arbitrary precision to avoid the issue discussed in this paper, it is just not worthwhile in practical scenarios. The paper can be improved by either demonstrating more realistic concerns in practical networks (rather than manually constructed ill conditions), or proposing efficient and realistic solutions to improve numerical stability specialized to the NN verification setting (addressing the usability and soundness tradeoff). I hope the authors can consider these directions, and I unfortunately cannot support acceptance for the current version of this paper. --- Reply to Comment 1.1.1: Comment: Thank you for your reply, which helped us identify an important misunderstanding. Please note that using arbitrary precision during verification does not help us avoid the problem we raised, only if the network is also evaluated in arbitrary precision during deployment. Our work raises the problem that verifiers do not take into account the deployment environment; that is, current verifiers work on ill-specified versions of the verification problem. This means that even if they are provably sound (and for that, one does not even need full precision), they are verifying the wrong thing. This gap between idealized and actual specifications (Eqs. (1) and (2)) can be practically exploited by attackers (as we demonstrate). Also, a soundness-usability tradeoff is tricky to define because soundness is a binary concept (either you have it or you don't). One could define a continuous version of soundness by, for example, saying that the larger the (possibly negative) proven lower bound of $f(x)$ is, the more sound the method. However, in our case, an attacker can change the behavior of the network arbitrarily, that is, if one ignores these problems in the name of usability, then there is no soundness at all in this continuous sense either.	null	null	null	null	null	null
Video Prediction Policy: A Generalist Robot Policy with Predictive Visual Representations	Accept (spotlight poster)	Summary: This paper proposes to use the intermediate features of video diffusion model as a visual encoder for generalizable robot action prediction. Firstly, a pre-trained video generation model is fine-tuned on robotic dataset. Then, the latent features of the first denoising step are aggregated for down-steam action prediction. Experiments in simulator and real world proves the effectiveness of the method. Claims And Evidence: 1. Features from video diffusion model could better encode the dynamic information, thus are beneficial for action prediction. This claim is supported by the comparison with baselines and the ablation on different visual encoders. 2. Efficiency. The prediction speed is faster than previous video generation model based methods, which is proved by the control frequency. 3. Generalization. The setting of CALVIN and real-world experiments validate the generalization ability of this method. Methods And Evaluation Criteria: This paper uses two simulation environments and real-world experiments to evaluate the proposed method and baselines with same robotic data (excluding data for video model training). The metrics include successful rate and task completion length. The experiments are thorough for generalizable robot manipulation problems. Theoretical Claims: Do not apply. Experimental Designs Or Analyses: This paper uses the CALVIN benchmark with ABC-to-D setting and Metaworld to validate the effectiveness of the method in simulation. Real-world experiments on two different embodiments further evaluate the proposed approach. In each setting, all methods are trained with same amount of manipulation data. Seen and unseen tasks are both evaluated to show the generalization ability. Supplementary Material: The authors provide the code. Relation To Broader Scientific Literature: This approach is related to open-world manipulation. Specifically, the use of video diffusion model for robot manipulation and visual representation learning for manipulation. Essential References Not Discussed: No. Other Strengths And Weaknesses: ### Strength 1. Leveraging the features from pre-trained video generation model to better predict dynamics is well-motivated. Visual representations suitable for robot manipulation should encode both static and dynamic information. 2. The design of using latent features instead of the denoised video improves the efficiency and robustness of action prediction. 3. The experiments are thorough. The evaluations in real world are impressive, which shows the effectiveness of VPP. ### Weakness 1. The majority of tasks belongs to pick-and-place category, which is relatively simple. What's the percentage of each task category in training and testing set. Other Comments Or Suggestions: 1. Please clarify more about the improvement compared to GR-1 [1]. How much of the improvement is due to the use of diffusion model? 2. I am curious about the tool-using tasks in real-world evaluation. Does the training set include tool-using tasks? Since both the text and figure show no tool-using tasks in training set (line 361, line 402). Besides, could you please show some visualization of video prediction on tool-using. The current ones only show the hand approaching the tool (Figure 6). Questions For Authors: Please see above comments. Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: We sincerely appreciate your time and effort in reviewing our paper! Thank you for your support in our work! Q1: What's the percentage of each task category in the training and testing set? ANS: Thank you for the questions! The specific number of evaluated trajectories can be found in Appendix A in the original paper: \| Skill Name \| Pick(Grasp)\| Pick&Place \| Cup-upright \|Relocate/Pass \|Stack \|Drawer \| \| :-- \| -- \|-- \|-- \|-- \|-- \|-- \| \| Test percentage(evaluate) \| 21.1\%(100/475)\| 21.1\%(100/475) \| 5.26\%(25/475) \|5.26\%(25/475) \|5.26\%(25/475) \|5.26\%(25/475) \|5.26\%(25/475) \| \| Press \| Unplug \| Water pouring \| Hammer \| Drill \|Pipette \| Spoon \| \| 5.26\%(25/475) \| 5.26\%(25/475)\| 5.26\%(25/475) \| 5.26\%(25/475) \|5.26\%(25/475) \|5.26\%(25/475) \|5.26\%(25/475) \|5.26\%(25/475) \| We also count the trajectory numbers of each category in the training datasets: \| Skill Name \| Pick(Grasp)\| Pick&Place \| Cup-upright \|Relocate/Pass \|Stack \| Drawer \| \| :-- \| -- \|-- \|-- \|-- \|-- \|-- \| \| Train percentage \| 15.2\%\| 40.5\% \| 2.5\% \| 7.6\% \|10.1\% \| 5.1\% \| \| Press \| Unplug \| Water pouring \| Hammer \| Drill \|Pipette \| Spoon \| \| 2.5\% \| 2.5\%\| 5.1\% \| 1.2\% \| 1.2\% \| 2.5\% \|3.8\% \| --- Q2: Please clarify more about the improvement compared to GR-1 [1]. How much of the improvement is due to the use of the diffusion model? ANS: Thank you for your insightful question. To ensure a fair comparison between the diffusion-based approach and the autoregressive method, we conducted an ablation study in which we replaced the policy decoder in GR-1 with the same diffusion head used in VPP while retaining the original autoregressive video prediction component. The results on the CALVIN ABC-D benchmark are shown below: \| \| Avg.Len\| \| :-- \| -- \| \| GR-1 (Auto-regressive) \| 3.06 \| \| GR-1 (diffusion policy head) \| 3.42 \| \| VPP (ours) \| 4.33 \| We can summarize that the performance improvement brought by VPP stems from multiple factors, including the accurate future prediction enabled by the video diffusion model, the integration of the VideoFormer architecture, and the dynamic representations learned from diverse training data in pretrained SVD. --- Q3: I am curious about the tool-using tasks in real-world evaluation. Does the training set include tool-using tasks? Since both the text and figure show no tool-using tasks in training set (line 361, line 402). ANS: Initially, we did not include tool-use tasks in the training dataset. We observed that VPP could generate roughly correct trajectories (e.g., approaching the tool in Figure 6) in challenging tool-use tasks but consistently failed due to the high precision control required. To address this, we collected 50–200 demonstrations for each tool-use task and fine-tuned both the video and action models. All baselines were also trained with the newly collected demonstrations. After fine-tuning, our model achieved a higher success rate in tool-use tasks. For your convenience, we have visualized more video prediction results before/after finetuning on our website: https://sites.google.com/view/vpp-rebuttal --- Q4: Besides, could you please show some visualization of video prediction on tool-using. The current ones only show the hand approaching the tool (Figure 6). ANS: Yes! We have also visualized the more video prediction results for tool tasks at different stages on our website: https://sites.google.com/view/vpp-rebuttal --- Thank you once again for endorsing our work! We will continue refining it to meet the highest standards. --- Rebuttal Comment 1.1: Comment: Thank the authors for the rebuttal. It addresses most of my concerns. --- Reply to Comment 1.1.1: Comment: Dear Reviewer Y6gd: Thank you again for your time and effort! We really appreciate your support in our work! Best Regards, The Authors	Summary: This paper introduce Video Prediction Policy(VPP), a robotics framework that leverages video diffusion model to capture the dynamic presentation vital to policy training. VPP consists of a two-stage process: i) a general video model is fine-tuned into a text-guided video prediction (TVP) model using large-scale human and robotic manipulation datasets, ii) a robotic policy is trained on predictive representations from the TVP model, enabling implicit inverse dynamics learning. VPP is evaluated on both simulate and real-world environments against mainstream baselines. The comparison shows that VPP i) achieves a higher success rate in manipulation tasks ii) enable generalize in unseen tasks. ## update after rebuttal I confirm my score. Authors addressed comments and added clarity and results to the original submission. Claims And Evidence: - In the introduction part, the paper suggests that VPP requires few demonstrations to align the robot's action space with visual features, but the extent of this data efficiency is not well quantified. - While the results suggest that VDM-based representations capture useful motion dynamics, the paper does not explicitly demonstrate how these representations encode physical laws. Methods And Evaluation Criteria: VPP and evaluation crieria are generally appropriate and well-aligned with the problem of learning generalist robotic policies. VPP is evaluated in Calvin ABC-D, metaworld, and real-world robot arm and dexterous hand, which show its ability to generalize and do complex tasks. Theoretical Claims: The theoretical foundation of VPP is not formally established through rigorous proofs or mathematical derivations. Experimental Designs Or Analyses: The paper claims that VPP requires few demonstrations, but it does not test performance under limited-data conditions. Supplementary Material: Yes. Supplementary material provides code including instructions to evaluate VPP in Calvin ABC-D environment. Relation To Broader Scientific Literature: The main contribution of this paper is the Video Prediction Policy (VPP), a new approach to learning general robotic policies using predicted visual representations inside video diffusion models (VDMs). VPP achieves significant performance gains in both simulation and real-world tasks by learning an implicit inverse dynamics model on future representations predicted by VDMs. Essential References Not Discussed: No Other Strengths And Weaknesses: Strengths: - VPP achieves good performance in both simulation and real-world tasks by learning an implicit inverse dynamics model on future representations predicted by VDMs, and avoids the need for multiple denoising steps as in previous work, so it can run in closed-loop at high frequency. - Able to leverage physical knowledge from pre-trained video generation models and Internet manipulation datasets. Weakness: - VPP's performance is highly dependent on the quality and predictive power of the video diffusion model. If the video diffusion model cannot accurately predict future scenes, VPP's performance may be limited. - Fine-tuning the video diffusion model requires a lot of computing resources. Fine-tuning the video model takes 2-3 days on eight NVIDIA A100 GPUs. - It may still be difficult to accurately capture the complex physical dynamics over long time scales. Other Comments Or Suggestions: Some typos: Introduction part: “Since we direct use the internal representation and avoid the need for multiple denoising steps as in previous work”, “direct” should be “directly” Questions For Authors: Does the performance increase with the number of denoising steps increase? Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: We sincerely appreciate your time and efforts in reviewing our paper! Thank you for your support on our work! Q1: Regarding the data efficiency of VPP model ANS: Thank you for your constructive question! In Table 1 of the original paper, we conducted experiments on the CALVIN benchmark using only 10\% of the standard dataset. Even with this limited data, VPP achieved performance comparable to previous SOTA models trained on the full dataset. These experiments demonstrate the data efficiency of VPP compared to previous methods, which stems from its powerful video pretraining process. Below, we provide additional comparisons with other methods: \| CALVIN ABC-D \| Data percentage\| Avg. Len \| \| :-- \| -- \|-- \| \| GR-1 \| 10\% \| 1.41 \| \| GR-1 \| 100\% \| 3.06 \| \| 3d-diffuser actor \| 100\% \| 3.35\| \| CLOVER \| 100\% \| 3.53 \| \|Vidman (Concurrent)\| 100\% \| 3.42 \| \| VPP (ours) \| 10\% \| 3.25 \| \| VPP (ours) \| 100\% \| 4.33 \| --- Q2: While the results suggest that VDM-based representations capture useful motion dynamics, the paper does not explicitly demonstrate how these representations encode physical laws.* ANS: Thank you for your insightful question! To directly illustrate the physical dynamics encoded in the VDM representation, we visualize the one-step denoised VDM features in Figures 4 and 9 of the original paper. These visualizations show that the learned representations consistently maintain physical consistency and align with intuitive physical laws. For example, when a block is grasped, it moves along with the robot arm, and the color of the poured liquid matches the liquid in the bottle. We hope this analysis clarifies our claims. --- Q3: VPP's performance is highly dependent on the quality and predictive power of the video diffusion model. If the video diffusion model cannot accurately predict future scenes, VPP's performance may be limited. ANS: Thank you for your insightful comment—we agree with your observation! We have also noted that policy performance strongly correlates with video prediction quality. However, from another perspective, we believe this dependency can be a strength. As pretrained video models continue to improve, their enhanced prediction capabilities allow us to transfer generalization abilities learned from internet-scale data to embodied tasks, which is really a good thing in the data-limited robotics domain. --- Q4: Fine-tuning the video diffusion model requires a lot of computing resources, taking 2-3 days on eight NVIDIA A100 GPUs. ANS: Since the pretrained SVD model has 1.5 billion parameters, we use an A100 node for fine-tuning. However, by employing parameter-efficient techniques such as LoRA, we can further reduce the computational demand, which is also implemented in the code provided in the supplementary materials. --- Q5: It may still be difficult to accurately capture the complex physical dynamics over long time scales. ANS: Thank you for the insightful comment! As pretrained video models continue to improve, we believe their ability to predict complex dynamics will also improve. Furthermore, the VPP framework does not require long-horizon predictions, as the video model can perform high-frequency replanning (re-prediction). As described in Section 4.1, we predict 16 frames with a 0.2s time interval, resulting in a short prediction horizon of 3.2 seconds. --- Q6: Does the performance increase with the number of denoising steps? ANS: This is a great question! The number of denoising steps presents a trade-off: while more steps can lead to higher-quality RGB images, they also result in a much lower control frequency. We explored this in an ablation study presented in Table 10 (Ablation.2) of the original paper. Our findings show that using two denoising steps yields similar performance to a single-step approach but at nearly half the control frequency. To balance performance and efficiency, we ultimately adopted the one-step direct encoder in our main experiments. We did not experiment with higher denoising steps, as they would further reduce control frequency, making the policy impractical for real-world deployment. --- Thank you again for your endorsement in our work! We will keep polishing the work to make it meet the highest standard! --- Rebuttal Comment 1.1: Comment: Thank you for addressing my and other reviewers' comments. --- Reply to Comment 1.1.1: Comment: Dear Reviewer uxTn: We are delighted to receive your response! Thank you again for your valuable time in reviewing our paper! Best Regards, Authors	Summary: The paper is about fine-tuning a pretrained image to video diffusion model on video-caption datasets that focus on object manipulations. The image to video model is turned into an image plus text to video model through the fine-tuning. This diffusion model is then used as a feature extractor (no iterative de-noising) to obtain future frame representations for a given robotics task (defined by start frame and textual command). These future representations, tagged predictive visual representations, are used as inputs to train a separate diffusion policy model on various robotics tasks. The policy model is trained separately on ground-truth robot trajectories, generating action sequences given starting image and textual command. The two detached training phases allow the diffusion model to be trained on a large-scale with weak supervision, while the policy network is learned at a task level under full supervision. Experiments on two synthetic and two real-world benchmarks demonstrate the improved performance achieved by this method over existing work. ## update after rebuttal The authors have successfully addressed the concerns. Claims And Evidence: Yes. The key claim is that a video generation diffusion model, adequately fine-tuned, can provide representations useful for robotics downstream tasks. Extensive experimentation (on synthetic and real-world benchmarks) is provided as evidence to demonstrate usefulness of such representations. Methods And Evaluation Criteria: Yes. The method of using future prediction is well motivated (and is well explored in concurrent literature). Evaluation criteria follows standard settings and aligns with results in prior works. Theoretical Claims: N/A Experimental Designs Or Analyses: Follows standard evaluation settings from prior work. Supplementary Material: Yes, all of it (i.e., the appendix added at the end of the PDF and the linked videos). Relation To Broader Scientific Literature: Highly relevant to several recent works which explore similar settings. This work could serve as a strong motivation for various future works. Essential References Not Discussed: N/A Other Strengths And Weaknesses: Strengths * Interesting idea of using future predictions in representation space with efficient, non-iterative feature extraction from a video diffusion model. * Clear presentation of methodology: the representation learning as well as fine-tuning stages are explained well with good use of figures for explanation. * Clear experimental setup following established benchmarks from prior work. Easy to observe the improvements from video diffusion representations for robotics tasks. Weaknesses 1. Details on method * What diffusion time-step is used to extract TVP features during inference? 2. Additional ablations * In Table 4, do you have results with SVD pretrain, but only internet data training? I.e. the impact of SVD pre-training for the robotics tasks. 3. Inference speed comparison missing * Please add table comparing against inference speed of baselines Other Comments Or Suggestions: Proposing weak accept given the several minor concerns listed in weaknesses above. Questions For Authors: N/A Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: We sincerely appreciate your time and efforts in reviewing our paper! Based on your review, we added a detailed discussion and additional experiments. Q1: About the details on method: what diffusion time-step is used to extract TVP features during inference? Thank you for your question. In our pipeline, we set the SVD noise scale and diffusion timestep to 20. We conducted preliminary experiments with diffusion timesteps of 10, 20, and 30 and found that 20 yielded slightly better performance. However, the overall performance of VPP is not sensitive to the choice of timestep. The results for different timesteps are shown below: \| CALVIN ABC-D \| Avg.Len\| \| :-- \| -- \| \| VPP time-step 10 \| 4.21 \| \| VPP time-step 20 \| 4.33 \| \| VPP time-step 30 \| 4.25 \| --- Q2: In Table 4, do you have results with SVD pretrain, but only internet data training? I.e. the impact of SVD pre-training for the robotics tasks. ANS: Thank you for the insightful question! Following your suggestion, we fine-tuned the SVD model using only internet data, without incorporating downstream robotics data. As shown below, the results indicate a clear performance decline. We believe this is because video prediction quality plays a crucial role in action learning. In the VPP framework, fine-tuning the video model on robot datasets enhances video prediction quality within the specific domain, allowing it to better capture the dynamics of robotic data and potentially improve performance. \| \| Avg.Len\| \| :-- \| -- \| \| VPP w/o internet data \| 3.97 \| \| VPP w/o down-stream robot dataset (newly added) \| 3.31 \| \| VPP \| 4.33 \| --- Q3: Please add table comparing against inference speed of baselines. ANS: Thank you for the constructive suggestion! Follow your suggestion, We add a comparison of the inference speed here. All inference time is evaluated on single NVIDIA 4090 GPU and average on 100 runs. We can notice that VPP achieves the best performance while keeping high frequency. Other method containing video/imgae diffusion (e.g., Susie/Uni-Pi) requires long time to denoise a complete video. \| CALVIN ABC-D \| inference Time\| Avg. Len \| \| :-- \| -- \|-- \| \| Diffusion policy \| ~100ms \| 0.56 \| \| 3d-diffuser actor \| ~600ms \| 3.35 \| \| Susie \| ~5100ms \| 2.69 \| \| GR-1 \| ~90ms \| 3.06 \| \| MDT \| ~110ms \| 1.55 \| \| Uni-Pi \| ~5500ms \| 0.92 \| \| VPP \| ~140ms \| 4.33\| --- Thank you again for your time and effort in reviewing our work! We hope our clarification can solve all your concerns, and we are always ready to answer any further questions! --- Rebuttal Comment 1.1: Comment: Most of the concerns are addressed in the rebuttal. --- Reply to Comment 1.1.1: Comment: Dear Reviewer 6CJo: We sincerely appreciate your valuable comments and kind support. We will carefully consider your suggestions and revise the paper accordingly. Thank you once again for taking the time to review our manuscript！ Best Regards, Authors	Summary: The paper introduces the Video Prediction Policy (VPP), a versatile robotic policy that enhances robot control by utilizing predictive visual representations generated by text-guided video prediction models (TVPs). VPP employs a two-stage methodology: first, fine-tuning a text-guided video prediction model on manipulation datasets, and second, integrating these predictive representations into a diffusion policy. The results show that VPP surpasses existing methods across both simulated and real-world benchmarks, achieving significant gains in task success rates. Claims And Evidence: The claim regarding improved control frequency may be subject to scrutiny. For methods such as UniPi, which employ 'Video Prediction + Inverse Dynamics Model (IDM)', although multiple denoising steps are required to generate a full video sequence for enhanced downstream control, they typically only need to generate the video once (i.e., a video plan spanning a relatively long horizon). Subsequent multi-step closed-loop rollouts rely solely on the lightweight IDM, which can operate very efficiently. In contrast, VPP appears to invoke the large TVP model at every control step, potentially incurring higher computational costs. To substantiate claims about improved efficiency, evaluations focusing on the time consumed for task completion would provide a more meaningful and supportive metric. Methods And Evaluation Criteria: Leveraging inherent dynamics within video diffusion models is a promising approach for robotic control. The evaluation framework in this paper encompasses CALVIN, MetaWorld, and real-world assessments involving both gripper and dexterous hands, providing a comprehensive evaluation of the proposed method. Theoretical Claims: No theoretical claims are made in the paper. Experimental Designs Or Analyses: 1. The analysis provided in Table 3 lacks persuasiveness and cannot be regarded as a fair comparison on the 'Pre-training Type'. It is noteworthy that the largest model in Voltron is a ViT-Base architecture with approximately 83 million parameters, while the Stable Video Diffusion (SVD) model employed in the proposed method exceeds 1.5 billion parameters. This substantial discrepancy in model scale undermines the validity of the comparison and calls into question the robustness of the findings. 2. '3D Diffuser Actor' is no longer the state-of-the-art method in the CALVIN benchmark. Further inclusion and comparison with more advanced methods will highlight the superiority of the proposed method. Supplementary Material: I've reviewed part of the source code provided in the supplementary material. Relation To Broader Scientific Literature: Discussed in the 'Essential References' section. Essential References Not Discussed: A notable similarity exists between the proposed method and VidMan [1], as both approaches involve fine-tuning video diffusion models using robotic data and leveraging features derived from the denoising process, integrated with cross-attention mechanisms, for diffusion-based action prediction. Furthermore, the core motivation of this paper—leveraging predictive visual representations from video diffusion models for robotic tasks—has also been extensively explored and discussed in prior literature [2]. [1] Wen, Youpeng, et al. "Vidman: Exploiting implicit dynamics from video diffusion model for effective robot manipulation." NeurIPS 2024 [2] Xiao, Zeqi, et al. "Video diffusion models are training-free motion interpreter and controller." arXiv preprint arXiv:2405.14864. Other Strengths And Weaknesses: The evaluations with the dexterous hands are barely seen in recent literature, which is valuable for validating the proposed method. Other Comments Or Suggestions: Is line.117, 'we observe that the open-sourced SVD', "W" should be capitalized. Questions For Authors: 1. For the second stage of training as described in the paper, are the video former and DiT policy trained in an end-to-end manner with the TVP-based backbone, or can the TVP be frozen during this stage? Clarifying this would provide insight into the flexibility and efficiency of the training process. 2. It is worth exploring whether the TVP-based backbone can generalize to unseen environments. In the current version, the TVP is extensively trained on specific downstream datasets (i.e., CALVIN and MetaWorld). How well does it generalize to novel scenarios or different robotic embodiments? The authors could consider evaluating VPP on CALVIN by training it exclusively on CALVIN data during the second stage. 3. What is the prediction horizon (i.e., the time duration of predicted videos) of the TVP? Should this horizon be adjusted based on the control frequency of the system? To what extent will it affect the downstream performance? 4. The feature aggregation process appears to have a significant impact on performance, as evidenced by the performance drop on CALVIN from 4.33 to 3.6. It would be valuable to investigate which layer's representations provide the most informative features for robotic control. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We sincerely appreciate your time and efforts in reviewing our paper! Based on your review, we added detailed discussions and additional experiments: Q1: Control frequency comparisons to UniPi ANS: We are afraid misunderstandings exist on the UniPi work. In page 5, sec 3.2 of the original UniPi paper, the authors state: "we use an open-loop controller in all our experiments in this paper."The IDM model takes two predicted images as input without any feedback from the environment, making it an open-loop control system. In contrast, VPP can replan in close-loop based on current observation at high frequency(7-10Hz) by direct using representations in the first forward pass. --- Q2: About the comparison on Table 3: Voltron is only 83M while SVD is 1.5B ANS: We respectfully offer a different perspective on this comparison: Previous vision encoders for embodied control were trained with specifically designed objectives on small networks; Video diffusion models with billions of parameters are pretrained on large-scale internet datasets—why not leverage their power? Beside, pretraining these vision encoder with billions of parameters from scratch requires enormous computational resources, which we really can not afford. We hope this clarification can addresses your concern! --- Q3: About the SOTA on CALVIN benchmark ANS: We list several works that achieve strong performance on CALVIN, including some concurrent papers. Even considering these, to the best of our knowledge, VPP remains the SOTA method on CALVIN at the time of submission. \| CALVIN ABC-D \| Release Time\| Avg. Len \| \| :-- \| -- \|-- \| \| 3d-diffuser actor \| Feb. 16, 2024 \| 3.35 \| \| RoboUniview \| Jun. 27, 2024 \| 3.64 \| \| CLOVER \| Sep. 13, 2024 \| 3.53 \| \| Vidman (Concurrent) \| Nov.14, 2024 \| 3.42\| \| VPP \| \| 4.33\| In ICML guidelines, papers released within 4 months to the submission DDL are concurrent and author are not required to compare to them. --- Q4: Comparison and differences to Vidman ANS: (1) Performance: VPP significantly outperforms Vidman, even as a concurrent work. (2) Training strategy: Vidman does not fine-tune its video model on the downstream domain, likely leading to worse video predictions and lower performance. (3) Architecture: Vidman directly uses action tokens to attend to numerous video model tokens, whereas VPP employs a VideoFormer to aggregate tokens, assisting action learning. Ablations confirm that removing downstream fine-tuning and VideoFormer both degrade performance: \| \| Avg.Len\| \| :-- \| -- \| \| Vidman \| 3.42 \| \| VPP w/o video finetuned in domain \| 3.31 \| \| VPP w/o video former \| 3.86 \| \| VPP \| 4.33 \| --- Q5: Comparisons to the paper "Video diffusion models are training-free motion interpreter and controller. ANS: We carefully reviewed this paper and found that it focuses on video motion generation, which is fundamentally different from robotics tasks. While it explores controlling motion generation via video latent, our work emphasizes the predictive capability of video representations, which is crucial for embodied AI. --- Q6: How well does video model generalize to different robotic embodiments? Consider evaluating VPP on CALVIN by training TVP model exclusively on CALVIN data ANS: Thank you for the insightful question! As mentioned in Q4, removing CALVIN video in TVP fine-tuning reduces performance. However, in this setting, representation inside TVP models still outperform the representations from static SVD VAE model. We argue that fine-tuning the TVP model on collected robot data better utilizes the available robotic data. \| \| Avg.Len\| \| :-- \| -- \| \| SVD's VAE \| 2.58 \| \| VPP w/o video FT \| 3.31 \| \| VPP \| 4.33 \| --- Q7: Is video model freeze in the second stage of training? ANS: Yes! We will make it more clear in the method section. --- Q8: Prediction horizon of TVP and affection on the downstream tasks? ANS: Typically we set the prediction horizon longer than the action horizon. In Section 4.3, VPP predicts 16 video frames at 0.2s intervals while outputting 10 actions at 0.1s intervals. Ablating to a 0.1s × 16 frame prediction had only a slight effect on performance (4.33 → 4.21). --- Q9: Which layer's representations provide the most informative features. ANS: Thank you for the insightful suggestion! We perform additional ablation study by conditioning policy on different layers inside up-sampling block. The results shows that the most informative ones lie in the middle of the SVD model. Our feature aggregation mechanism avoids manual selection while achieving the best results. \| \| Avg.Len\| \| :-- \| -- \| \| Layer-3 \| 3.72 \| \| Layer-6 \| 3.88 \| \| Layer-9 \| 4.29 \| \| Layer-12 \| 4.05 \| \| VPP \| 4.33 \| --- Thank you again for your time and effort in reviewing our work! --- Rebuttal Comment 1.1: Comment: The detailed rebuttal and additional results are appreciated. I'd like to raise my socre accordingly. --- Reply to Comment 1.1.1: Comment: Dear Reviewer xoHf: Thank you for your review and feedback! We truly appreciate your time and effort, and we will carefully consider your suggestions in future revisions of our paper! Best Regards, Authors	null	null	null	null	null	null
Speculative Prefill: Turbocharging TTFT with Lightweight and Training-Free Token Importance Estimation	Accept (poster)	Summary: SpecPrefill proposes a prompt token pruning technique using speculation by a small model before forwarding the large model. This method is especially beneficial when the token length is medium (latency of attention and MLP are similar, so sparse attention methods do not do a good job) because it reduces the number of tokens. Claims And Evidence: They have some evidence, but I cannot find any comparison between baseline. They have only vanilla attention, while they still can compare their method with other pruning methods (such as sparse attention, MInference: https://github.com/microsoft/MInference, FlexPrefill: https://arxiv.org/abs/2502.20766) Methods And Evaluation Criteria: I think the method looks correct. However, the evaluation is weak due to a lack of baselines. Theoretical Claims: Yes. Experimental Designs Or Analyses: I think an ablation study on N should be in the paper, which is used in algorithm 1 line 3. Supplementary Material: I cannot see anything in the supplementary. I strongly suggest authors submit the code as a supplementary to find potential practical issues rather than showing it in only papers. Relation To Broader Scientific Literature: The key contribution is about speeding up the QPS of the LLM serving framework, which is widely used in various NLP research. I think this kind of topic is pretty important, and this method is tackling that issue. Essential References Not Discussed: I think they should compare it with the sparse attention method, even if they claim that MLP is a bottleneck in the middle and a little bit longer in context. I cannot fully agree that MLP is a significant bottleneck, so speeding up attention is not important, as declared in lines 108 and 121. I partially agree that MLP is a bottleneck in a somewhat short context (less than 8K tokens). However, these days, many applications require longer context to perform well (e.g., RAG, Image (costs 1-4K tokens per image), and Video (costs 100-1K tokens per frame) model). Therefore, I suggest the following works (that can speed up prefill) to compare: - MInference: https://github.com/microsoft/MInference - SnapKV: https://github.com/FasterDecoding/SnapKV - HiP Attention: https://github.com/DeepAuto-AI/hip-attention - SampleAttention: https://arxiv.org/html/2406.15486 - DuoAttention: https://github.com/mit-han-lab/duo-attention - FlexPrefill: https://openreview.net/forum?id=OfjIlbelrT Other Strengths And Weaknesses: I think the tested context lengths are too short compared to other modern LLM (Qwen 2.5=1M tokens, Llama 3.1=128K tokens ...) I think we should try at least up to 128K tokens, which is the context length of Llama3.1. The RULER and InfintieBench (https://github.com/OpenBMB/InfiniteBench) benchmark will be a great choice to test the effectiveness Other Comments Or Suggestions: Please refer to other sections. Questions For Authors: Please refer to other sections. Code Of Conduct: Affirmed. Overall Recommendation: 2	Rebuttal 1: Rebuttal: ### Summary We sincerely thank the reviewer for the effort in providing constructive comments. We addressed all the feedback from the reviewer, and believe that with these changes, the results in our paper become significantly stronger (added experiment result numbers in reviewer USDK’s rebuttal). ### Per-feedback detailed response > I cannot find any comparison between baseline. In the original submission, we included two RAG baselines where we put the conclusion in the experiment section 4.4 and detailed results in the Appendix B. We now move all results in T1 (reviewer USDK's comment) to the main body, along with two more baselines as suggested by the reviewer: 1. We evaluate LLMLingua 2 using LongBench. Similar to RAG, LLMLingua does not support query-aware compression, and therefore, we separate the context from the query and send it to the compression model. In T1 (reviewer USDK's comment), SpecPrefill outperforms LLMLingua and RAG Llama. 2. We benchmark MInference's quality on LongBench and its inference latency in vLLM for a more comprehensive view. In T1 (reviewer USDK's comment), the quality score of MInference can already be matched very closely with SpecPrefill with 10% token keep rate (0.3% loss) and is outperformed when we increase the rate to 30% and higher. *In T2 (reviewer USDK's comment) where we vary the batch size x sequence length products from 128 4K to 4 * 128K, we found that SpecPrefill is particularly effective in efficiency compared to MInference with similar or better quality (getting 2.54x - 6.54x relative speedup compared to MInference). The main reason why MInference might fall short is due to the overhead in dynamic index building, which gets significant when the batch size is large (this is also observed in paper https://arxiv.org/abs/2502.05431 and confirmed by the author in issue https://github.com/microsoft/MInference/issues/18). > I think an ablation study on N should be in the paper. We agree that ablation on N will provide more insights and are running a full ablation on N for the camera ready version. For our current results as in Figure 2 and Figure 5, we showcase the benefits of using LAH with steps = 8 (with LAH as the suffix in model names), which proves its usefulness especially for shorter context tasks. > I strongly suggest authors submit the code as a supplementary to find potential practical issues rather than showing it in only papers. We agree on this and we will upload code whenever OpenReview allows uploading again. We’re confident that our experiments are reproducible and implementations are highly optimized (see Appendix E). > I cannot fully agree that MLP is a significant bottleneck, so speeding up attention is not important, as declared in lines 108 and 121. I partially agree that MLP is a bottleneck in a somewhat short context (less than 8K tokens). Sorry for the confusion! We fully agree that attention is a significant bottleneck (in both short-context and especially long context) and SpecPrefill also helps skip the attention part as well, as shown in T2 (reviewer USDK’s comment) when we move on to 128K. What we hoped to convey was that there are many existing techniques to optimize attention in various regimes but optimizing MLP hasn't attracted too much attention, which is where SpecPrefill stands out. We revised the wordings to make this point clear. > I think we should try at least up to 128K tokens... The RULER and InfintieBench benchmark will be a great choice to test the effectiveness. We understand the reviewer’s concern on longer context performance. We increase the RULER results in the original paper from 32K to 64K and observe consistent trends (T3 reviewer USDK’s comment). We will present the result on 128K for the camera-ready version and believe the same conclusion to hold (it is still currently running due to large models and limited cards). > Essential References Not Discussed. We thank the reviewer for providing relevant works: 1. MInference, SnapKV, HiP Attention, SampleAttention, DuoAttention, and FlexPrefill are awesome work. However, they focus primarily on the attention module while keeping the MLP part intact. We include those in our camera-ready version for more context. 2. For MInference, we added additional experiments to show that SpecPrefill achieves better speedup with better quality. 3. MInference, SnapKV, and DuoAttention were originally in our draft and we added more context and discussion in our camera-ready version. We truly agree with the concerns and feedback from the reviewer and hope our responses can help address some of those. With the added results, we are confident that SpecPrefill can be applied and benefit many real world applications and the contributions are novel and fully reproducible. We’d love to hear from the reviewer on further suggestions if any to make the paper better! --- Rebuttal Comment 1.1: Comment: Thank you for the rebuttal. However, I still have concerns regarding the empirical evaluation. > MInference, SnapKV, and DuoAttention were originally in our draft I could not find any results or evaluations involving MInference, SnapKV, or DuoAttention in the original draft. If I missed them, please clarify where they appear. > For MInference, we added additional experiments to show that SpecPrefill achieves better speedup with better quality. I appreciate the added experiments. However, the overall evaluation still lacks sufficient empirical comparison against relevant baselines (Still lacks the baselines in RULER; just two baselines are provided for LongBench with only a single model family, no detailed latency reports, and reduction analysis). The draft would benefit significantly from a more comprehensive and balanced comparison across a wider range of methods. > (it is still currently running due to large models and limited cards). If resource constraints are a challenge, I wonder why the authors chose to focus primarily on very large models such as 70B and 405B. While these models are impressive, evaluating on smaller models (e.g., 8B or 14B) could help demonstrate the effectiveness of the proposed method more broadly and allow for more complete comparisons under limited compute. > enforce_eager=True in L923 This raises a critical concern. Disabling graph compilation can significantly impact decoding latency and overall throughput. Since QPS is a major performance metric in this paper, this decision may lead to exaggerated runtime measurements. The potential impact on reported results should be carefully examined and discussed. Finally, while the additional Table T1 from the USDK evaluation is a helpful step, it is not sufficient to address the broader concern about limited baseline comparisons. I strongly encourage the authors to provide a more thorough empirical study across a range of tasks and methods to better support the claims of the paper. --- Reply to Comment 1.1.1: Comment: Thank you for expressing your concern! ### Code with Reproducible Experiments Here is our [code](https://anonymous.4open.science/r/speculative_prefill-1E26) ### Answers to Concerns > I could not find any results or evaluations involving MInference, SnapKV, or DuoAttention in the original draft. They were properly cited and discussed (L119) as suggested by the initial review. We added more discussion below and in our final version. > enforce_eager=True in L923 1. enforce_eager=True will not change anything about prefill. Second, vLLM has a buggy implementation for this for many versions: - So many [Issue 1](https://github.com/vllm-project/vllm/issues/10559), [Issue 2](https://github.com/vllm-project/vllm/issues/13536), [Issue 3](https://github.com/vllm-project/vllm/issues/9670), [Issue 4](https://github.com/vllm-project/vllm/issues/8494), [Issue 5](https://github.com/vllm-project/vllm/issues/2229) etc about: wrong output related to eager mode. - [Issue](https://github.com/vllm-project/vllm/issues/3874) about memory. - Minference uses enforce_eager=True as well: [see](https://github.com/microsoft/MInference/blob/9ee9d4bbc725a5ab8c992a8a6cbce3601c6e8deb/experiments/benchmarks/benchmark_e2e_vllm_tp.py#L65) 2. We explicitly mentioned the reason for doing so in Appendix C. 3. The reason we found this was that we previously tried setting it to False and gave us wrong outputs, but the improvement on QPS is consistent because it is mostly bounded by the TTFT as analyzed in section 4.6.1 (since for most tasks the prompts are way longer than the outputs). All other efficiency plots are setting output_len=1, so the results won’t be different. > If resource constraints are a challenge … We believe that trying large models is an advantage rather than disadvantage, showing the scaling power of SpecPrefill under the most demanding applications. ### About Our Current Results > However, the overall evaluation still lacks sufficient empirical comparison against relevant baselines… 1. We evaluated (T1 from USDK’s comment) four instead of two baselines: - Instruct baseline - Rag baseline (two variants in Appendix B) - LLMLingua (text compression) - Minference (sparse attn). 2. We spent the whole section 4.6 + T2 (USDK) + Appendix E for the efficiency report with real world setup: - vLLM concurrency + large models. - Consistent QPS flows + API communication. - Real queries with scheduling + large batch size. 3. Our central claim that SpecPrefill greatly improves TTFT (and hence maximal QPS) with minimal loss in quality has been sufficiently shown in LongBench & RULER even just by comparing with baseline alone (>= 64K below) (we did not overclaim betterness than non-comparable methods, see in next section): \| \| \| Retrieval \| Multi-hop \| QA \| Aggregation \| Avg w/o Agg \| \|---\|---\|---\|---\|---\|---\|---\| \| baseline 70B \| 64k \| 98.5 \| 99.9 \| 65.1 \| 65.6 \| 87.9 \| \| \| 128k \| 76.5 \| 56.1 \| 48.2 \| 41.3 \| 60.3 \| \| SpecPrefill 10% \| 64k \| 99.5 \| 99.8 \| 71.9 \| 54.9 \| 90.4 \| \| \| 128k \| 85.8 \| 55.6 \| 55.3 \| 48.3 \| 65.6 \| ### About Baselines To begin with, we hope to first convince the reviewer why we included some and didn’t include other baselines. Any efficiency arguments about inference should be made based on highly optimized impl for a fair comparison: - We chose MInference because it has vLLM support with 70B. - We chose RAG and LLMLingua because they preprocess the inputs and can feed directly to vLLM servers. - SnapKV doesn’t improve prefill, and is written in [HF only](https://github.com/FasterDecoding/SnapKV/blob/main/experiments/LongBench/pred_snap.py). - DuoAttention falls to the same category of MInference we tested, is written in [HF](https://github.com/mit-han-lab/duo-attention/blob/main/scripts/efficiency.sh) only, and evaluated with [bs = 1](https://github.com/mit-han-lab/duo-attention/blob/fe93c314ae87306ef6629dc16713250b4718ffe7/eval/efficiency/benchmark_static.py#L46) Running any model of the same size in vLLM will surely be faster than in HF by a magnitude. Implementing a fast and scalable framework itself should be considered as a part of our core contribution rather than disadvantage. And we are not responsible for providing optimized implementation for other methods. Nonetheless, we give a super detailed analysis to compare DuoAttn and SnapKV [here](https://anonymous.4open.science/r/speculative_prefill-1E26/COMPARE.md)**. All results support our main claim that SpecPrefill makes QPS + Prefill faster with minimal quality loss and scales to 405B. And we’re confident that current results (including newly added baselines) positively support the effectiveness of SpecPrefill with the most fair and realistic setting. Could you please double-check our results and re-evaluate the comprehensiveness and soundness of experiments? We are happy to hear more feedback.	Summary: This paper introduces Speculative Prefill, an innovative training-free framework that elegantly addresses efficiency challenges in language model inference. By leveraging a lightweight model to speculate on important tokens based on context, the approach impressively enhances time-to-first-token performance. The results are quite remarkable, achieving up to 7x higher queries per second and a 7.66x improvement in TTFT. Claims And Evidence: The paper presents its claims with well-supported evidence throughout, providing a convincing foundation for the proposed approach. Methods And Evaluation Criteria: The method strikes an excellent balance between simplicity and effectiveness, offering an elegant solution to the prefill optimization problem. The evaluation framework thoughtfully considers both task performance scores and TTFT metrics, which provides a comprehensive view of the inevitable trade-offs between accuracy and efficiency that such approaches entail. Theoretical Claims: The theoretical underpinnings of the work appear sound and well-reasoned, with clear connections between the conceptual framework and practical implementation. Experimental Designs Or Analyses: The experimental design demonstrates careful consideration across multiple dimensions. The comparison of different token keep percentages on LongBench and Ruler offers valuable insights, while the efficiency evaluations provide a holistic view of the method's practical benefits. Overall, the experimental approach nicely balances breadth and depth. Supplementary Material: I've had the opportunity to review all the supplementary materials, which nicely complement and strengthen the main paper's findings. Relation To Broader Scientific Literature: Not addressed in this review. Essential References Not Discussed: I haven't identified any significant omissions in the paper's references. Other Strengths And Weaknesses: Strength: 1. The speculative prefill concept is particularly compelling, offering an insightful approach to identifying important tokens using a smaller model's predictions as input for the larger model. 2. The paper presents its ideas with clarity and thoughtful organization. 3. The experimental section offers comprehensive and nuanced analysis of the method's performance. Weakness: 1. While the approach is quite innovative, it would be interesting to see more exploration of how it compares with alternative attention sparsity methods such as minference, especially considering the different optimization strategies they employ. Other Comments Or Suggestions: No additional comments. Questions For Authors: 1. I'm curious about how this approach might compare with attention sparsity methods like minference. Both approaches optimize different aspects of the inference process, and while this method also addresses MLP computation, I wonder if you could share any insights or perhaps preliminary comparisons on the relative advantages of each approach? This could help readers better understand the positioning of your contribution within the broader landscape of inference optimization techniques. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: ### Summary We thank the reviewer for the constructive and insightful feedback! We addressed all feedback and believe that incorporating all comments makes this paper significantly stronger: ### Per-feedback detailed response > It would be interesting to see more exploration of how it compares with alternative attention sparsity methods such as Minference… As the reviewer has mentioned, SpecPrefill not only reduces the computation on the attention but also on the MLP while sparse attention primarily focuses on the attention module alone. In order to provide a more comprehensive comparison between the two routes, we conducted experiments comparing ours against MInference as requested by the reviewer. We adopt the pre-searched optimal pattern from MInference’s official repo for the 70B model and benchmark’s its quality on LongBench in T1 (see below). As we can see SpecPrefill can achieve 99.7% quality of MInference while keeping only 10% tokens and surpasses it when using 30% or more tokens. Because MInference is an attention based sparsity optimization, we benchmark its latency for a fair comparison in terms of acceleration and quality. In T2 (see below) where we vary the batch size x sequence length products from 128 * 4K to 4 * 128K, we found that SpecPrefill is particularly effective in efficiency compared to MInference with similar or better quality (getting 2.54x - 6.54x relative speedup compared to MInference). The main reason why MInference might fall short is due to the overhead in dynamic index building, which gets significant when the batch size is large. We do want to emphasize that Minference is an excellent work and its advantage starts to shine when the sequence becomes ultra long, at least 128K+ (or the ratio between sequence length and batch size gets large enough). Another trade-offs we want to mention between our methods and sparse attention approaches are the decision of whether we want to compute / store all the KV caches. Besides, MLP generally dominates the prefill part for large batch size + decent context lengths (at least within our tested 128K). This becomes essentially important based on the application scenario (e.g whether the prefill/decode is disaggregated and hence requires KV transmission). Overall, we believe that since both methods require no-training and can be switched on and off on the fly, they are complementary to each other and can hence meet a wider range of requirements when combined together. With the added results, we are confident that SpecPrefill can be applied and benefit many real world applications and the contributions are novel and fully reproducible. We’d love to hear from the reviewer on further suggestions if any to make the paper better! ### Newly added experiment results: LongBench comparison with baselines (T1): \| Model \| Compression Rate \| Single-Doc QA \| Multi-Doc QA \| Sum \| Few-shot Learning \| Code \| Synthetic \| Avg \| \|---\|---\|---\|---\|---\|---\|---\|---\|---\| \| baseline 70B \| N/A \| 50.57 \| 53.11 \| 25.84 \| 66.93 \| 52.33 \| 72.50 \| 53.55 \| \| RAG \| 10.90% \| 32.32 \| 41.17 \| 18.86 \| 45.40 \| 44.76 \| 30.42 \| 35.49 \| \| \| 28.60% \| 38.43 \| 47.41 \| 21.42 \| 50.53 \| 45.80 \| 35.50 \| 39.85 \| \| \| 46.80% \| 40.53 \| 46.64 \| 22.45 \| 49.52 \| 46.00 \| 43.15 \| 41.38 \| \| \| 65.10% \| 41.40 \| 47.43 \| 23.30 \| 52.21 \| 46.19 \| 47.22 \| 42.96 \| \| \| 83.40% \| 43.25 \| 48.16 \| 23.56 \| 51.44 \| 45.92 \| 53.04 \| 44.23 \| \| LLMLingua \| ~10% \| 26.50 \| 32.94 \| 20.95 \| 37.40 \| 45.00 \| 16.33 \| 29.85 \| \| \| ~30% \| 38.83 \| 44.02 \| 23.37 \| 42.23 \| 47.27 \| 37.00 \| 38.79 \| \| \| ~50% \| 43.64 \| 50.67 \| 24.77 \| 50.96 \| 49.05 \| 60.33 \| 46.57 \| \| \| ~70% \| 45.90 \| 52.88 \| 25.44 \| 59.77 \| 51.48 \| 68.50 \| 50.66 \| \| \| ~90% \| 45.94 \| 53.91 \| 25.87 \| 60.46 \| 54.06 \| 72.00 \| 52.04 \| \| Minference \| N/A \| 50.46 \| 53.23 \| 25.83 \| 66.36 \| 52.48 \| 69.00 \| 52.89 \| \| SpecPrefill \| 10% \| 47.64 \| 52.96 \| 21.74 \| 64.52 \| 63.33 \| 66.25 \| 52.74 \| \| \| 30% \| 49.47 \| 53.39 \| 24.41 \| 65.83 \| 62.62 \| 67.83 \| 53.92 \| \| \| 50% \| 50.18 \| 52.56 \| 25.10 \| 65.60 \| 59.91 \| 68.17 \| 53.59 \| \| \| 70% \| 50.06 \| 52.44 \| 25.51 \| 65.77 \| 58.08 \| 68.67 \| 53.42 \| \| \| 90% \| 50.26 \| 53.25 \| 25.65 \| 66.35 \| 53.47 \| 70.67 \| 53.27 \| Latency comparison (T2): \| \| 128 * 4k \| 64 * 8k \| 32 * 16k \| 16 * 32k \| 8 * 64k \| 4 * 128k \| \|-----------------\|----------\|---------\|----------\|----------\|---------\|----------\| \| 70B Instruct \| 22.6 \| 23.7 \| 25.9 \| 30.1 \| 38.7 \| 56.0 \| \| Minference \| 46.6 \| 45.3 \| 42.5 \| 40.8 \| 38.3 \| 34.6 \| \| SpecPrefill 10% \| 7.1 \| 7.0 \| 7.2 \| 8.0 \| 9.8 \| 13.6 \| \| SpecPrefill 30% \| 11.8 \| 11.7 \| 12.1 \| 13.2 \| 15.7 \| 20.9 \| \| SpecPrefill 50% \| 16.2 \| 16.4 \| 17.1 \| 19.0 \| 22.7 \| 30.7 \| RULER 64K (T3): \| \| Retrieval \| Multi-hop \| QA \| Agg \| Avg w/o Agg \| \|---\|---\|---\|---\|---\|---\| \| baseline 70B \| 98.5 \| 99.9 \| 65.1 \| 65.6 \| 87.9 \| \| SpecPrefill 10% \| 99.5 \| 99.8 \| 71.9 \| 54.9 \| 90.4 \| --- Rebuttal Comment 1.1: Comment: Thank you for your reply. I will keep my score. --- Reply to Comment 1.1.1: Comment: Thank you for recognizing our work. According to Reviewer JHsj's comment, we further added comparison with DuoAttention and SnapKV with 8B model here: [analysis](https://anonymous.4open.science/r/speculative_prefill-1E26/COMPARE.md) and 128K RULER in JHsj's comment. We also uploaded our [code](https://anonymous.4open.science/r/speculative_prefill-1E26/README.md) in case it can help better assess our work's validity. We appreciate your time in reviewing our work!	Summary: This paper propose SpecPrefill, that identifies the important tokens during the pre-fill stage via accumulating the attention scores in a 8-steps look-ahead window, calculated with a small model as the speculator. This approach can achieves a speedup of about 3x and also maintains a comparable performance compared to full attention. Claims And Evidence: - Methods And Evaluation Criteria: - Theoretical Claims: - Experimental Designs Or Analyses: This is method aims to optimize the pre-filling stage unlike the existing sparse attention, instead it uses a speculator to find the critical tokens and only involve these in the actual attention computation. The strength of the paper: 1. good system design. the proposed method reuse the speculative decoding framework, which extend the speculative decoding to the per-fill stage, so the large model not only benefit from the decoding proposal, but also the sparse pre-fill. This also makes this method to be easily adopted in systems with spec-decoing supported. 2. good performance on most of tasks. spec-prefill achieves comparable performance against full attention on long-bench and ruler, with 50% tokens perserved. it achieves good speedup (2x speedup when 50% tokens perserved). 3. a novel attempts for pre-fill acceleration that may inspire future works. The limitation of the paper: 1. not a single baseline was included in the experiment. This proposed method uses a draft/small model to evaluate the importance of the tokens from the prompt, is pretty much similar to the idea of prompt comparession and kv cache compression. Prompt compression, in particular, also aims to accelerate the pre-filling acceleration, which should definitely be compared against spec-prefill. In fact, spec-prefill is simply a prompt compression technique with a 8-step look-ahead window. In addition, dynamic sparse attention that build sparse index online for faster pre-fill is also very relevant to spec-prefill, which is a must to compare with. the missing of these baselines is a big limitation of this paper. 2. this token-level sparse attention is previously studied to be less robust in real production environment, especially in multi-round scenarios. SCBench demonstrates that the critical tokens of a prompt can be dramatically different for different queries. In other words, the look-ahead window in spec-prefill can be sub-optimal when the conversation goes on and move to the next query. The benchmarks used in the experiments fail to prove that the proposed method can tackle such a limitation. Supplementary Material: - Relation To Broader Scientific Literature: - Essential References Not Discussed: You should cite: Li, Y., Dong, B., Lin, C., & Guerin, F. (2023). Compressing Context to Enhance Inference Efficiency of Large Language Models. Conference on Empirical Methods in Natural Language Processing. for prompt compression in addition to llmlingua series of model. You should test the proposed method in SCBench to see how well the method perform under multi-turn scenarios: Li, Y., Jiang, H., Wu, Q., Luo, X., Ahn, S., Zhang, C., Abdi, A.H., Li, D., Gao, J., Yang, Y., & Qiu, L. (2024). SCBench: A KV Cache-Centric Analysis of Long-Context Methods. ArXiv, abs/2412.10319. It may also help to show how well the method works on more challenging long-context tasks such as gsm-infini. Zhou, Yang et al. “GSM-Infinite: How Do Your LLMs Behave over Infinitely Increasing Context Length and Reasoning Complexity?” (2025). Other Strengths And Weaknesses: - Other Comments Or Suggestions: - Questions For Authors: 1. try compared spec-prefill against prompt compression methods, and dynamic sparse attention approaches. 2. try test spec-prefill on multi-turn long context benchmarks such as SCBench. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: ### Summary We sincerely thank the reviewer for the time and constructive feedback! We addressed all feedback and believe that it makes this paper significantly stronger (added experiment result numbers in reviewer USDK’s rebuttal). Specifically, we addressed the feedback by: 1. We moved the original main results for our RAG-baselines to the main body and created a table to compare all methods including two newly added baselines: LLMLingua and MInference. SpecPrefill achieves higher quality and better efficiency than all of them. 2. We agree with the application of multi-turn situations and believe that SpecPrefill will be able to solve it with the full knowledge of the speculator. We will add results in the camera-ready version (running the experiments). 3. We added more context and discussions for the essential references in our camera-ready version. ### Per-feedback detailed response: > Not a single baseline was included in the experiment… Try comparing spec-prefill against prompt compression methods, and dynamic sparse attention approaches. In the previous draft, we compared two RAG-based methods in the Appendix. We should have done a better job in making them more visible -- to do this, we will add a summary of baseline comparison in T1 (reviewer USDK's comment) in the main paper body. In addition, we follow the advice from the reviewer by adding LLMLingua (text-level prompt compression, https://arxiv.org/abs/2310.05736) and MInference (sparse attention, https://arxiv.org/abs/2407.02490) to complement our original RAG baseline. We evaluate all three baselines on LongBench, and the result is shown in T1 (reviewer USDK's comment). SpecPrefill outperforms RAG and LLMLingua by margins when keeping the same tokens from the prompt (i.e. same tokens ~= similar speedup). Comparing MInference requires a more careful design due to the fact that it is a sparse attention optimization that does not change the computation of the MLP and needs to compute all KVs. Therefore, we benchmark MInference’s prefill latency in T2 (reviewer USDK's comment) where we vary the batch size x sequence length products from 128 * 4K to 4 * 128K. We observe that MInference has substantial overhead when the batch size is large and only gets amortized when the sequence length gets ultra long (at least > 128K with small batch size < 4, this is also observed in paper https://arxiv.org/abs/2502.05431 and confirmed by the author in issue https://github.com/microsoft/MInference/issues/18). Overall, SpecPrefill can achieve 2.54x to 6.54x relative speedup compared to MInference with 99.7% quality and surpasses MInference’s quality when keep rate is at least 30%. > Try test spec-prefill on multi-turn long context benchmarks such as SCBench. We fully agree that multi-turn tasks are important applications to test SpecPrefill. Unlike many prompt compression methods, SpecPrefill maintains the full KV for the speculator, which makes it possible to revive dropped tokens during the first round of conversation. This allows us to re-estimate token importance when a new turn comes in and let the base model fill-in the missing KVs as needed. We are currently running evaluations and will include results for the camera-ready version (due to new implementation and evaluation time, we can’t finish it during the rebuttal window). In addition, here’s our detailed description of what we’re running: We outline the high-level algorithm here: 1. Check if it is the first turn. If so we just call our standard SpecPrefill and return the results. If not, move to step 2. 2. Let the speculator first process the new N-token context and estimate important tokens just like in the first prefill. 3. Identify missing KVs based on slot-mapping and position information. 4. For positions missing KVs, we simply keep those ids. 5. For the base model, we will recompute the KVs if some ids are not in the cache. Return the new results. The total number of KVs that will be computed and stored will not exceed the context length, which means there is no waste of “recomputation”. Nonetheless, we’d like to mention that our initial starting goal for SpecPrefill is to tackle large-batch offline (no further interaction) prefill acceleration that targets a large traffic of requests such as bulk document summarization, QA, etc. > Essential reference not mentioned. All of these are awesome add-ons and have been included in appropriate places for reference. We are confident that SpecPrefill can be applied and benefit many real world applications and the contributions are novel and fully reproducible. We’d love to hear from the reviewer on further suggestions if any to make the paper better!	null	null	null	null	null	null	null	null
Diffusion models for Gaussian distributions: Exact solutions and Wasserstein errors	Accept (poster)	Summary: This paper presents a mostly-theoretical study of four sources of error in diffusion sampling, in the special case of multivariate Gaussian distributions. First they derive exact solutions for the diffusion reverse SDE and ODE for a Gaussian, and then apply these to study the initialization, discretization, truncation, and score approximation error (the latter is actually studied empirically). Update after rebuttal Thank you for the response, including the nonzero mean results, which I think are a nice addition to the paper. I maintain my initial positive rating. Claims And Evidence: Yes Methods And Evaluation Criteria: Yes Theoretical Claims: No Experimental Designs Or Analyses: No Supplementary Material: No Relation To Broader Scientific Literature: For multivariate Gaussian data distributions, the solution of the forward SDE (Prop 1) and the score (eq 10) are of course well-known. The exact solutions for backward SDE and probability flow ODE in the special case of multivariate Gaussians under VP schedule (Prop 2 and 3) have not been previously published as far I know. In related work, [Bradley Nakirran 24] (Appendix A.5) gives exact solutions to backward SDE and probability flow ODE for 1D Gaussians under VE schedule. Also, [Chidambaram 24] contains some similar ODE analysis for Gaussian mixtures. (However, I believe this paper may have appeared earlier on arXiv and also the works cover slightly different cases.) The Wasserstein bounds are also new as far as I know. [Bradley Nakirran 24] Classifier-Free Guidance is a Predictor-Corrector (https://arxiv.org/pdf/2408.09000) [Chidambaram 24] What does guidance do? A fine-grained analysis in a simple setting (https://arxiv.org/pdf/2409.13074) Essential References Not Discussed: Please see Relation To Broader Scientific Literature for some related works. Other Strengths And Weaknesses: Strengths: The paper is clear and well-written. I appreciate the project of carefully identifying and analyzing various sources of error. I am also happy to see the reverse SDE and ODE solutions for multidimensional Gaussians clearly laid out. Weaknesses: --Single Gaussian data distribution is a very special case that may not tell us much real data distributions. At a minimum, Gaussian Mixtures (GM) at least capture the notion of multimodality, which is a key aspect of real data. -- Conclusions that e.g. SDE is better than ODE, Heun is best sampler, etc. are not very surprising. -- Score approximation is noted as being the most important source of error but theoretical analysis not available, which is a bit of a disappointment given the stated project of the paper (I understand that this is difficult). Other Comments Or Suggestions: L129 “sensible” = “sensitive”? L148: Assumption 1: I am curious why you need to assume a centered (mean = 0) Gaussian? Could the results be extended to arbitrary mean? (Are you not doing this because it is trivial, or because it is hard?) L435 "unable to derive exact solutions to the backward SDE or the flow ODE under GMM assumption" -- [Chidambaram 24] contains some ODE results for GMM that may be helpful/of interest (not exact solutions but bounds) Questions For Authors: N/A Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We sincerely thank you for your feedback. > L129 “sensible” = “sensitive”? Thank you for noticing this typo, which we have corrected. > L148: Assumption 1: I am curious why you need to assume a centered (mean = 0) Gaussian? Could the results be extended to arbitrary mean? (Are you not doing this because it is trivial, or because it is hard?) We assumed a zero mean Gaussian for two reasons: first, to align with the machine learning framework, where data is typically normalized as a preprocessing; second, to simplify the notation of the equations. Nonetheless, all the results can be trivially extended to the case of a nonzero mean. Essentially, the solutions are shifted, and the 2-Wasserstein error includes an additional bias norm component. For the sake of completeness, if $p_\text{data} = \mathcal{N}(\boldsymbol{\mu},\boldsymbol{\Sigma})$, \begin{equation} p_t = \mathcal{N}(e^{-B_t}\boldsymbol{\mu},\boldsymbol{\Sigma}_t) \end{equation} and the solution of Proposition 2 becomes \begin{equation} \boldsymbol{y}\_t = e^{-B_{T-t}}\boldsymbol{\mu}+ e^{-(B\_T - B\_{T-t} )}\boldsymbol{\Sigma}\_{T-t}\boldsymbol{\Sigma}^{-1}\_T(\boldsymbol{y}\_0-e^{-B_T}\boldsymbol{\mu}) +\boldsymbol{\xi}\_t, \quad 0 \leq t \leq T \end{equation} where $\boldsymbol{\xi}_t$ is defined in Equation (13). Similarly, the solution of Proposition 3 becomes $$ \boldsymbol{y}\_t = e^{-B_{T-t}}\boldsymbol{\mu}+\boldsymbol{\Sigma}^{-1/2}\_T \boldsymbol{\Sigma}^{1/2}\_{T-t}(\boldsymbol{y}\_0-e^{-B_T}\boldsymbol{\mu}), \quad 0 \leq t \leq T. $$ We propose to discuss this nonzero mean case in a dedicated appendix to clarify that there is no difficulty to extend our result to this setting. > L435 "unable to derive exact solutions to the backward SDE or the flow ODE under GMM assumption" -- [Chidambaram 24] contains some ODE results for GMM that may be helpful/of interest (not exact solutions but bounds) Thank you for this interesting reference that further strengthens the arguments of our sixth section Discussion and limitations, we propose to cite it. --- Rebuttal Comment 1.1: Comment: Thank you for the response, including the nonzero mean results.	Summary: 1. Under the assumption of a Gaussian data distribution, the authors derive exact solutions for both the backward stochastic differential equation (BSDE) and the probability flow ordinary differential equation (ODE) in the VP-SDE diffusion model. 2. This paper systematically analyzes the convergence properties of diffusion models by identifying four primary sources of error, all of which are quantified using Wasserstein-2 distance ($W_2$): - Initialization Error: This arises from approximating the final forward-distributed sample $p_T$ using a standard Gaussian distribution $\mathcal{N}(0,I)$. - Truncation Error: In practice, the backward integration is started at a small time $\varepsilon>0$ instead of $t=0$ to avoid numerical instability, introducing additional bias. - Discretization Error: Since the SDE or ODE is solved numerically using numerical schemes such as Euler, Heun, and RK4, numerical approximation errors accumulate. - Score Approximation Error: In real-world applications, the score function is learned via a neural network, and training errors impact the final generation quality. 3. The authors compute exact $W_2$-initialization errors of the SDE and ODE samplers respectively, which provides an inequality of $W_2$-distance. 4. They investigate $W_2$-discretization errors in various numerical schemes in both CIFAR-10 Gaussian data and ADSN distribution data settings, which are expressed by the eigenvalues of the covariance matrix at specific steps. Claims And Evidence: Theoretical Claims and Evidence: 1. The authors provide thorough analysis both theoretically and numerically of the VP-SDE diffusion model, thanks to the assumption of Gaussian data. In particular, the $W_2$ error inequality between the SDE and ODE samplers (Proposition 4) is intriguing. However, I am not sure if these results can help to investigate in more general cases. After all, the Gaussian assumption is not sufficiently general and the real-world data can be much more complex. I know theoretical analysis in general cases is almost impossible, while I hope this can be generalized to Gaussian mixture models. There are several reasons: - If the data distribution is a mixture of Gaussian distributions, by the linearity and solvability of the VP-SDE, it is straightforward to prove that for any time $t>0$, $X_t\sim p_t$ is also a mixture of Gaussian distributions. - Write $GMM_d(K)$ the subset of $\mathcal{P}(\mathbb{R}^d)$ made of probability measures on $\mathbb{R}^d$ which can be written as Gaussian mixtures with less than $K$ components (such mixtures are obviously also in $\mathcal{P}_p(\mathbb{R}^d)$ for any $p>1$). Denote $GMM_d(\infty)=\cup_{K\geqslant 0} GMM_d(K)$. Then $GMM_d(\infty)$ is dense in $\mathcal{P}_p(\mathbb{R}^d)$ for the metric $W_p$, hence the Gaussian mixture model is sufficiently general to study the real-world data. - $W_2$ distance between Gaussian mixtures is difficult to calculate, while analyzing $MW_2$ distance can be a feasible choice. Details can be found in [J. Delon et al. 2020]. Additionally, the score function also has an explicit expression in Gaussian mixture model settings. See [Wang B et al. 2024] 2. Commutativity of covariance matrices $\Sigma_{t_1}$ and $\Sigma_{t_2}$, where $X_{t}\sim p_{t}=\mathcal{N}(0,\Sigma_{t})$, is frequently used in proofs of propositions, such as equation (52), (93). This commutative property can be proved directly by independence of the Gaussian noise, while the proof of this property still needs to be supplemented for the sake of proofs' completeness. Additionally, if $Cov(y_0)$ and $\Sigma$ commutes, the proof of commutativity of $Cov(y_0)$ and $\Sigma_t$ (for any $t>0$) needs to be supplemented. This property is used in equation (48), (59). Experimental Designs： The authors have conducted sufficiently detailed experiments, investigating the impact of various numerical schemes, different truncation times, and the number of score function evaluation (NFE) on the Wasserstein-2 error, on the CIFAR-10 Gaussian dataset and the ADSN model respectively. However, according to the Theoretical Claims and Evidence above, in the ADSN model experiments, the actual Wasserstein-2 distance should be $\sqrt{3}$ times the value depicted in Figure 5. Nevertheless, this does not affect the experimental conclusions. References: - [J. Delon et al. 2020] J. Delon, and A. Desolneux. A Wasserstein-Type Distance in the Space of Gaussian Mixture Models, SIAM journal on imaging sciences, 13(2), pp. 936–970, 2020. - [B. Wang et al. 2024] B. Wang, and J. J. Vastola. The Unreasonable Effectiveness of Gaussian Score Approximation for Diffusion Models and its Applications[J]. arXiv preprint arXiv:2412.09726, 2024. Methods And Evaluation Criteria: See Claims And Evidence. Theoretical Claims: See Claims And Evidence. Experimental Designs Or Analyses: See Claims And Evidence. Supplementary Material: Yes Relation To Broader Scientific Literature: Theoretical Analysis: 1. While prior research (e.g., [V. De Bortoli et al. 2021]; [Chen S et al. 2022]) derived upper bounds on 1-Wasserstein or total variation distances between the data and the model distributions under suitable assumptions, these were often worst-case bounds. In contrast, this paper provides exact analytical Wasserstein-2 errors under the Gaussian assumption. 2. The connection between probability flow ODEs and optimal transport has been discussed in prior works ([Khrulkov et al. 2022]; [Lavenant et al. 2022]). However, this paper provides an explicit demonstration of how the probability flow ODE corresponds to an optimal transport map in the Gaussian case, strengthening this theoretical link. Numerical Considerations: The analysis of different numerical discretization schemes for diffusion models builds upon prior empirical studies ([Karras et al. 2022]), which recommended Heun’s method based on experimental performance. The stochastic Euler-Maruyama (EM) method has been widely used in diffusion-based generative models ([Song et al. 2021]), but its theoretical properties have remained underexplored. This paper demonstrates that SDE-based samplers are more robust to initialization errors compared to ODE-based samplers under the Gaussian data assumption, providing a clearer understanding of why EM can sometimes outperform deterministic ODE solvers in practical applications. References: - [V. De Bortoli et al. 2021] V. De Bortoli, J. Thornton, J. Heng, and A. Doucet. Diffusion schrödinger bridge with applications to score-based generative modeling. In Advances in Neural Information Processing Systems, volume 34, pp. 1769517709. Curran Associates, Inc., 2021. - [Chen S et al. 2022] Chen S, Chewi S, Li J, et al. Sampling is as easy as learning the score: theory for diffusion models with minimal data assumptions[J]. arXiv preprint arXiv:2209.11215, 2022. - [Khrulkov et al. 2022] Khrulkov V, Ryzhakov G, Chertkov A, et al. Understanding ddpm latent codes through optimal transport[J]. arXiv preprint arXiv:2202.07477, 2022. - [Lavenant et al. 2022] Lavenant H, Santambrogio F. The flow map of the fokker–planck equation does not provide optimal transport[J]. Applied Mathematics Letters, 2022, 133: 108225. - [Karras et al. 2022] Karras T, Aittala M, Aila T, et al. Elucidating the design space of diffusion-based generative models[J]. Advances in neural information processing systems, 2022, 35: 26565-26577. - [Song et al. 2021] Song Y, Sohl-Dickstein J, Kingma D P, et al. Score-based generative modeling through stochastic differential equations. In International Conference on Learning Representations, 2021. Essential References Not Discussed: None Other Strengths And Weaknesses: Strengths: The authors provide relatively detailed proofs and comprehensive experimental results, which are convenient for understanding. Weakness: While the Gaussian setting allows for exact analytical results, real-world data distributions are highly non-Gaussian. Thus, while the theoretical insights are valuable, their direct applicability to practical generative modeling tasks remains uncertain. Other Comments Or Suggestions: 1. In Appendix H, the authors study the covariance matrix of the ADSN distribution, and provide the computation of the empirical Wasserstein error in the ADSN covariance diagonalization basis. These proofs are generally not problematic, but there are many small typos and errors: - $dt$ is missing in equation (23) in the term $\beta_t e^{B_t} x_t$. - All instances of $\xi \in \mathbb{R}^{M\times N}$ and $\omega \in \mathbb{R}^{M\times N}$ should be replaced with $\xi\in M\times N$ and $\omega\in M\times N$, respectively. - The notations $v^{j,\xi}$ and $\hat{v}^{j,\xi}$ are used alternately after equation (107), which constitutes the abuse of notations that needs to be rectified and every notation needs to be thoroughly rechecked. - Equation (101) should be replaced with $$ \widehat{\Sigma v}_{i}=\hat{t_{i}}\odot \left( \bar{\hat{t_1}}\odot \hat{v_1}+\bar{\hat{t_2}}\odot \hat{v_2}+\bar{\hat{t_3}}\odot \hat{v_3} \right) $$ otherwise the dimensionality of the vectors does not match. In addition, $\widehat{\Sigma v_{i}}$ and $\widehat{\Sigma v}_{i}$ are difficult to be distinguished for readers who are new to them, which can cause difficulties in understanding this proof. Hence a clear explanation is needed. Furthermore, this formula depends on a fact, where $\widehat{u\overleftarrow{v}}=\hat{u}\odot \bar{\hat{v}}$ ($\overleftarrow{v}$ refers to reversing the arrangement of elements in a vector $v$). A detailed explanation is needed in order to help readers understand the proof. - $\lambda_{1}^{\xi}$ should be $\lambda_{j}^{\xi}$ in equation (116). - In equation (121)~(124), the coefficient should be $MN$, not $3MN$. Hence the empirical Wasserstein distance in equation (125) is indeed wrong. 2. There are some word errors in the paper: - konwn* should be known in Proposition 4. - inependent should be independent in equation (120). Questions For Authors: 1. I am curious about whether there truly have been no prior works exploring the explicit solutions of the VP-SDE and PF-ODE in the Gaussian data setting, as their solutions are not particularly complex and can essentially be found in any standard textbook on stochastic processes. 2. For the eigenvalue contribution to the Wasserstein error, almost in all the numerical schemes, the function $\|\sqrt{\lambda^{scheme}}-\sqrt{\lambda}\|$ have a zero point near $\lambda=1$. And this function manifests convexity in a small neighborhood of every zero point. I wonder if there are theoretical explanations. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We sincerely thank you for your feedback. ## Answers to questions > I am curious about whether there truly have been no prior works exploring the explicit solutions of the VP-SDE and PF-ODE in the Gaussian data setting, as their solutions are not particularly complex and can essentially be found in any standard textbook on stochastic processes. In the literature, the solution to SDEs is generally provided in 1D, which makes their generalization to diffusion models for image synthesis non-trivial. > For the eigenvalue contribution to the Wasserstein error, almost in all the numerical schemes, the function $\|\sqrt{\lambda^{scheme}}-\sqrt{\lambda}\|$ have a zero point near $\lambda=1$. And this function manifests convexity in a small neighborhood of every zero point. I wonder if there are theoretical explanations. Thank you for these observations. The different schemes exhibit highly diverse behaviors, even when plotted in logscale as in Figure 2. Our code, available in the supplementary material, could be used for more precise plots around any point of interest for each numerical scheme. ## Theoretical Claims and Evidence section > I know theoretical analysis in general cases is almost impossible, while I hope this can be generalized to Gaussian mixture models. There are several reasons: > - If the data distribution is a mixture of Gaussian distributions, by the linearity and solvability of the VP-SDE, it is straightforward to prove that for any time $t>0$, $X_t\sim p_t$ is also a mixture of Gaussian distributions. > - Write $GMM_d(K)$ the subset of $\mathcal{P}(\mathbb{R}^d)$ made of probability measures on $\mathbb{R}^d$ which can be written as Gaussian mixtures with less than $K$ components (such mixtures are obviously also in $\mathcal{P}p(\mathbb{R}^d)$ for any $p>1$). Denote $GMM_d(\infty)=\cup{K\geqslant 0} GMM_d(K)$. Then $GMM_d(\infty)$ is dense in $\mathcal{P}_p(\mathbb{R}^d)$ for the metric $W_p$, hence the Gaussian mixture model is sufficiently general to study the real-world data. > - $W_2$ distance between Gaussian mixtures is difficult to calculate, while analyzing $MW_2$ distance can be a feasible choice. Details can be found in [J. Delon et al. 2020]. The difficulty to extend our work to GMMs is discussed in Section 6. Discussion and limitations. The solution, derived in Proposition 1. is indeed true for very general data distributions but the solutions of the backward SDE and probability-flow ODE do not extend to the GMM case. > Commutativity of covariance matrices $\Sigma_{t_1}$ and $\Sigma_{t_2}$, where $X_{t}\sim p_{t}=\mathcal{N}(0,\Sigma_{t})$, is frequently used in proofs of propositions, such as equation (52), (93). Additionally, if $Cov(y_0)$ and $\Sigma$ commutes, the proof of commutativity of $Cov(y_0)$ and $\Sigma_t$ (for any $t>0$) needs to be supplemented. This property is used in equation (48), (59). We do not understand the main point you want to emphasize: It appears clear that with $\boldsymbol{\Sigma}_{t} = e^{-2B_t} \boldsymbol{\Sigma} + (1-e^{-2B_t})\boldsymbol{I}$, $\boldsymbol{\Sigma}\_{t_1}$ and $\boldsymbol{\Sigma}\_{t_2}$ commute. Similarly, if $Cov(\boldsymbol{y}_0)$ and $\boldsymbol{\Sigma}$ commute. ## Comments Or Suggestions > In addition, $\widehat{\Sigma v_{i}}$ and $\widehat{\Sigma v}_{i}$ are difficult to be distinguished for readers who are new to them, which can cause difficulties in understanding this proof. Hence a clear explanation is needed. > Furthermore, this formula depends on a fact, where $\widehat{u\overleftarrow{v}}=\hat{u}\odot \bar{\hat{v}}$ ($\overleftarrow{v}$ refers to reversing the arrangement of elements in a vector $v$). We have added sentences to clarify these important points. Thank you for noticing them. > In equation (121)~(124), the coefficient should be $MN$, not $3MN$. Hence the empirical Wasserstein distance in equation (125) is indeed wrong. > However, according to the Theoretical Claims and Evidence* above, in the ADSN model experiments, the actual Wasserstein-2 distance should be $\sqrt{3}$ times the value depicted in Figure 5. Indeed, thank you for your careful proofreading. Let us precise that this typo was not present in our code (no factor 3) so all reported results in Table 2 are valid, which explains the closeness between the theoretical and empirical Wasserstein distances. We hope that this clarification could convice you to raise your score. ## Typos > $dt$ is missing in equation (23) > All instances of $\xi \in \mathbb{R}^{M\times N}$ and $\omega \in \mathbb{R}^{M\times N}$ should be replaced > Equation (101) should be replaced with [...] > $\lambda_{1}^{\xi}$ should be $\lambda_{j}^{\xi}$ in equation (116). > The notations $v^{j,\xi}$ and $\hat{v}^{j,\xi}$ are used alternately after equation (107) Thank you again for your careful proofreading. We have corrected all the mentioned typos and carefully rechecked the full appendix regarding componentwise products and vector indices.	Summary: The paper diffusion-based generative models assuming that the data distribution is a known Gaussian distribution. Since the data distribution is Gaussian the diffusion process score is linear and known in closed form, which allows the authors to: 1. Solve in closed form the reverse (noise → data) SDE and ODE since they are linear. 2. compute the Wasserstein-2 metric between the model distribution and the data distribution since the model distribution is Gaussian, and the Wasserstein-2 metric between two Gaussians is available in closed-form. Using these closed-form metrics and ODE/SDEs, the authors then proceed to study: 1. the initialization error 2. the error introduced by numerical ODE and SDE solvers 3. the effect of step-size 4. the error induced due to truncation, stopping the sampling process at $t = \varepsilon > 0$. In section 5, the authors then learn the score model (parameterized by a U-Net) for a Gaussian distribution to see the effect of the score function approximation error on sampling. Table 1 shows that: 1. using RK4, a higher-order ODE solver, produces lower error 2. using more NFE, a lower step-size for the solver, produces lower error Claims And Evidence: - On line 420-422, right panel: the theoretical analysis leads to the conclusion that Heun’s method is the “best numerical solution”: - That finding is also contracted by numerical methods literature, which states that RK4 and other higher order solvers are better numerical solvers - claim finding is also contradicted by the experiment in section 5, where EM leads to a lower value using the author’s proposed metric. - on line 424-427, the authors show claim that the experiment in section 5 demonstrated that the score approximation error “may be the most important one in practice”: - The experiment in section 5 however does not highlight the impact of score function approximation error on the distribution metrics reported. The authors study the effect of sampling parameters on the distribution metrics, not the effect of higher or lower score approximation error. Methods And Evaluation Criteria: The paper proposes that analyzing diffusion-based generative models for Gaussian data allows for an evaluation of any numerical sampler. However, 1. There is a well-studied framework for analyzing numerical solvers 2. The authors do not show that any inference gained from the Gaussian setting transfers to other data distributions. Moreover, the experiment in section 5 disagrees with the findings in section 4. Theoretical Claims: The reverse ODE and SDE solutions are correct. Experimental Designs Or Analyses: In section 4, the experiment studies the multiple sources of error and sampling parameters as mentioned for a gaussian distribution, with covariance computed on Cifar10 samples. In section 5, since the model distribution is not Gaussian anymore the authors make use of other metrics, such as FID and a problem-specific Wasserstein metric, proposed by the authors. 1. These metrics assume the model distribution is Gaussian, however other metrics/divergences such as the kernel Stein discrepancy, maximum mean discrepancy, etc can be estimated without the Gaussian assumption. 2. The model required for FID scores is not trained on data of the type generated by ADSN. Therefore, are the FID scores reliable? In section 5, the finding regarding the stochastic EM sampler outperforming Heun’s method contradicts with the findings in table 1, where Heun’s leads to lower error, although the score function was known in closed-form. It is not clear what the added benefit of the experiment in section 5 was for the paper. On lines 424-427, the authors show claim that the experiment in section 5 demonstrated that the score approximation error “may be the most important one in practice”. However, this experiment does not demonstrate that since they do not show the effect of the score function approximation error on the distributional metrics. Supplementary Material: i checked the correctness of the ODE and SDE solutions. Relation To Broader Scientific Literature: - The findings in table 1 study are already well-studied in the numerical methods literature as well as the diffusion modeling literature: - Using a higher-order ODE solver such as RK4 is more accurate than lower-order sampler - using a lower step-size leads to lower error is a well-known fact Essential References Not Discussed: Relevant references are discussed. Other Strengths And Weaknesses: See claims and evidence, Methods And Evaluation Criteria and Experimental Designs Or Analyses Other Comments Or Suggestions: None Questions For Authors: The main limitation I believe is the "framework" being proposed, since as the authors acknowledge studying Gaussian data distribution is already a well established practice and exact scores, velocities for mixture of Gaussian data have been computed in several prior works, it is not clear what insight can be gained from this work. - can the authors explain wha insight into diffusion models can be gained from the exact score, ODE and SDE in the Gaussian data framework that was not already known. Code Of Conduct: Affirmed. Overall Recommendation: 1	Rebuttal 1: Rebuttal: We sincerely thank you for your feedback. > The experiment in section 5 however does not highlight the impact of score function approximation error on the distribution metrics reported. The authors study the effect of sampling parameters on the distribution metrics, not the effect of higher or lower d. We consider this part to be a study of the effect of score approximation error on the samplers because we have mapped the impact of each type of error in the use of the schemes. Then, we introduce this final error and observe that it causes all our errors to explode. > The model required for FID scores is not trained on data of the type generated by ADSN. Therefore, are the FID scores reliable? We have chosen to use the standard metric. All the reported FID values vary consistently with other Wasserstein metrics. The FID metric compares the statistics of image features, allowing it to discriminate between one distribution relative and another. Within the scope of our paper, without comparing our FID values to those from other tables in different contexts, this measure appears to be relevant. > On lines 424-427, the authors show claim that the experiment in section 5 demonstrated that the score approximation error “may be the most important one in practice”. However, this experiment does not demonstrate that since they do not show the effect of the score function approximation error on the distributional metrics. Precisely, this section highlights a significant difference between theoretical analysis and practical implementation. > can the authors explain wha insight into diffusion models can be gained from the exact score, ODE and SDE in the Gaussian data framework that was not already known. We must highlight an important subtlety regarding our work: we do not compare different schemes from an asymptotic perspective (with ($\Delta_t \to 0$), as has been extensively done in the literature and as you have rightly pointed out. Instead, we focus on: - The robustness of the schemes with respect to initialization and truncation errors, which is not commonly studied in the literature, as existing works typically assume a known initialization. On the contrary, these errors are central in our paper - The behavior of the schemes under a fixed NFE budget. Interestingly, we manage to obtain results comparable to those of asymptotic studies found in textbooks, even though this was not an a priori objective when considering the practical use of these models—particularly with a maximum budget of 1000 NFE. - The study of high-dimensional schemes, particularly stochastic ones, which are rarely analyzed in textbooks. In particular, we consider very general covariance structures that may lead to distributions lacking a density. - Exact Wasserstein errors rather than bounds, which may otherwise be excessively large. --- Rebuttal Comment 1.1: Comment: _Precisely, this section highlights a significant difference between theoretical analysis and practical implementation._ The authors have still not made it clear the usefulness of the proposed framework. Their own experiment shows that in 'practical' settings, errors in modeling the score are more important. 1. Experimenting on data distributions with tractable solutions is an old practice. 2. Any insight gained from the paper is already well studied in the numerical analysis literature. In the diffusion modeling literature. _We consider this part to be a study of the effect of score approximation error on the samplers because we have mapped the impact of each type of error in the use of the schemes._ The paper does not analyze how the error in score function approximation interacts with the other sources of error they consider. Hence, it is not clear what one can takeaway from the Gaussian data framework to any other setting where the scores are not known exactly. If the authors can _clearly state_ any new insight, practical advice that this framework can provide that is not already known and has been studied, I can consider raising my score. --- Reply to Comment 1.1.1: Comment: Thank you for your response. 1. We disagree with the assertion that our results are already well-studied in the literature. Several other reviewers have acknowledged the novelty of our work. We are unaware of any references that establish exact Wasserstein errors in the diffusion models literature. Could you please provide precise references to support your remark? 2. Regarding new insights and takeaways, we do not claim to revolutionize diffusion models in practice. Our scientific contribution is to establish undisputable and rigorous mathematical results within the framework of Gaussian distributions. This allows us to confront standard practices of the diffusion model literature to a framework that is theoretically fully understood. Quoting the abstract: "Our second contribution is to compute the exact Wasserstein errors between the target and the numerically sampled distributions for any numerical scheme. This allows us to monitor convergence directly in the data space, while experimental works limit their empirical analysis to Inception features." We believe our results are of interest to the part of the ICML community dealing with the challenging theoretical analysis of diffusion models.	Summary: The article studies different types of errors when implementing diffusion models (DM) by constructing a Gaussian DM, for which the solution is known in closed form, and then measuring the errors between the exact and approximated solutions using the Wasserstein distance. They analyse the sensitivity of the error wrt different factors. ## update after rebuttal I have a positive view of this work, which I maintain after the discussion period. Claims And Evidence: The contributions of the paper are both theoretical and experimental. They apply to, what is defined in the paper as, _the Gaussian assumption_. The former reveals that the ODE solution is better than the SDE solution, when it comes to sampling from p_data. The latter provides many insights regarding the effects of different approximations in the solution of the DM. The paper does a good job within its declared scope. Understanding the theoretical performance of DMs is lacking in the literature, and this work points in this direction. The claims and evidence are well supported in that sense. Methods And Evaluation Criteria: The experiments are not comprehensive, but that is because the setting laid out is a simple one. To me, this is well justified by the aims of the paper. The evaluation provided here makes complete sense for this work. Theoretical Claims: The theoretical claims are clear for the setting considered, this is well explained by the authors. How the results of the paper extend to more general settings (i.e., non-Gaussian DMs) is unknown and beyond the scope of this paper, but the theoretical claims of this article can be an interesting starting point. Experimental Designs Or Analyses: Experiments are appropriate for the claimed contribution Supplementary Material: No Relation To Broader Scientific Literature: Good account of other methods Essential References Not Discussed: Not that I know Other Strengths And Weaknesses: I find this work a good contribution to the literature. Perfectly within scope for ICML and at the expected conceptual/experimental depth. Other Comments Or Suggestions: NA Questions For Authors: - In Proposition 2, the authors present one of the manuscript's main contributions. They claim that, for any starting distribution, the reverse SDE (assuming Gaussian p_data) is Gaussian. I am not sure I understand this. In the author's setting (i.e., Gaussian p_data, or "the Gaussian assumption"), the forward SDE constructs p_T in a way that it'll also be Gaussian (a sequence of linear transformations starting from a Gaussian). Therefore, when the authors say "any starting dist" do they refer to any "Gaussian" distribution? If not, how could the solution of the reverse SDE, say $p_t$, be Gaussian if starting from any, e.g., a multimodal, p_T? - The paragraph on line 208 (left) could probably be a Remark? - At some points, the authors seem to downplay their own contribution. Early in the paper they say that considering Gaussian DMs might not make much sense and then in the discussion they also say that "the limitation of their work is that they only consider Gaussians". Though a stylistic issue only, I do not agree with this: I think this work is important. Its contribution is limited, true, but all contributions are limited to their own specified area. If I am not mistaken, this work has value for the community and should be recognised as such. - One of the final observations of the paper (the score approximation being the most important error in practice) should be emphasised earlier in the paper to highlight the practical findings of the work. Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: We sincerely thank you for your thoughtful and positive feedback. We are pleased that the you find our work a meaningful contribution to the theoretical understanding of diffusion models (DMs) and recognize its relevance within the broader literature. Below, we address your specific questions and suggestions. Answers to questions: >They claim that, for any starting distribution, the reverse SDE (assuming Gaussian p_data) is Gaussian In Proposition 2, the expression of the strong solution in Proposition 2 remains true without assuming that $\boldsymbol{y}_0$ is Gaussian but $\boldsymbol{y}_t$ does not necessarly has a Gaussian distribution even if we can write its covariance matrix. We propose to clarify the assumption in Propositions 2 and 3 by writing explicitly "Supposing that $p\_\text{data} = \mathcal{N}(0,\boldsymbol{\Sigma})$". > The paragraph on line 208 (left) could probably be a Remark? Thank you for this suggestion, which we have added. > At some points, the authors seem to downplay their own contribution. Early in the paper they say that considering Gaussian DMs might not make much sense and then in the discussion they also say that "the limitation of their work is that they only consider Gaussians". Though a stylistic issue only, I do not agree with this: I think this work is important. Its contribution is limited, true, but all contributions are limited to their own specified area. If I am not mistaken, this work has value for the community and should be recognised as such. > One of the final observations of the paper (the score approximation being the most important error in practice) should be emphasised earlier in the paper to highlight the practical findings of the work. Thank you for acknowledging the importance of our contributions. In case of acceptance, we will take into account your advice to better highlight our results. We do not want to downplay the importance of our work, but we want to ensure that readers understand that generalizing our results to more complex cases is very challenging. --- Rebuttal Comment 1.1: Comment: Thanks for the rebuttal, I maintain my recommendation	null	null	null	null	null	null
A Meta-learner for Heterogeneous Effects in Difference-in-Differences	Accept (poster)	Summary: The paper introduces novel orthogonal meta-learners for estimating the conditional average treatment effect of the treated (CATT) in a difference-in differences (DID) setting. The main contributions include the proposed orthogonal loss, theoretical guarantees in form of doubly robust rates, and extensions to generalized settings. The proposed learner is evaluated using synthetic and real-world data. Claims And Evidence: The claims (orthogonality, double robustness) are clearly formulated and backed up with both theoretical and empirical evidence. Only one question: is the identifiability result from Proposition 2.3. novel? If not, a clear reference would be needed. Methods And Evaluation Criteria: Evaluation criteria follow standard practices in the causal inference literature. Theoretical Claims: I did not verify the correctness of the theoretical results in detail. However, I am quite familiar with similar work on orthogonal learning and the results look reasonable to me. Experimental Designs Or Analyses: Results are mostly on synthetic data as common in causal inference (evaluation on real-world data is often impossible). The case-study on real-world data is in my opinion not entirely necessary (could be moved to the appendix). Supplementary Material: I did not verify the correctness of the proofs. Relation To Broader Scientific Literature: Key literature seems to be cited (even though I am not an expert when it comes to DID). Essential References Not Discussed: See above. Other Strengths And Weaknesses: Strengths: - Versatile framework that allows the use of arbitrary machine learning models for causal inference DID settings with nice theoretical guarantees Weaknesses: - While the meta-learner is novel, the derivation follows an established framework that has been leveraged for many other causal estimands already. New ideas remain relatively limited. - As is common for doubly robust learners, the proposed learner may become unstable in low-overlap settings. It might be interesting to extend the methodology to overlap-weighted orthogonal learners (e.g., R-learner for DID). In sum, a nice paper leveraging an existing framework for a new causal estimand. The result is a solid methodology that fills a gap in the literature. Other Comments Or Suggestions: It would be nice if the authors could add a discussion section to the camera-ready version of the paper, discussion limitations and future work (e.g., as above). Questions For Authors: No further comments Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: Thank you for the helpful reviews! The result of Proposition 2.3 follows as a simple extension of the ATT identification strategy under conditional parallel trends. The reviewer is right that we should not claim this as a result of this work. We will reference for instance, in the preamble of the theorem the recent survey of [1], where a variant of this formula (when $X=W$) also appears (e.g. Equation (11) in [1]). The extra projection step on $W$ is a simple adaptation of that formula. Regarding to the comment that there are limited new ideas, while we acknowledge that our methods stems from the idea of debiasing the nuisance functions, we want to highlight that our method provides a framework that allows one to debias nuisance functions that is learned on a different distribution (i.e. under covariate shift) from the target distribution for the final estimand, and this allows us to generalized the framework to many other estimands as described in Section 4. As pointed out by many reviewers, we were not able to include a detailed discussion section in the initial submission due to length constraints. In the camera-ready version, we will provide more discussions on the limitations of the proposed method including the unstable performance in low-overlap regimes, which is common for doubly robust learners. As you have mentioned, it is an interesting future direction to looking into overlap-weighted orthogonal learners. If one is interested in estimating overlap weighted projections of the true CATT, then we suspect that a simple adaptation of our loss, where one weights each sample by an appropriate weighting function of $W$, will cancel out the large variance of the density ratio, while maintaining Neyman orthogonality of the loss and will lead to a weighted MSE projection guarantee, weighted by the function of W that was used to reweight the loss at the sample level. Finally, we really appreciate the time you put into reviewing our paper, and the constructive feedback that will help us improve our work! References - [1] Roth, Jonathan, et al. "What’s trending in difference-in-differences? A synthesis of the recent econometrics literature." Journal of Econometrics 235.2 (2023): 2218-2244.	Summary: The paper proposes a doubly robust metalearner for the Conditional Average Treatment Effect on the Treated for panel data. The method is targeted for binary treatments and builds upon the parallel trends assumptions common in Difference-in-Differences settings. Furthermore, the paper proposes a robust meta-learning framework for the estimation of general conditional functionals under covariate shift. Claims And Evidence: Yes Methods And Evaluation Criteria: Yes. However, experiments are only conducted on the setting with a specific treatment timestep, i.e., T=2. Empirical evaluation of the method for greater time horizons would be of interest. Theoretical Claims: The proofs of the claims in the main paper. Experimental Designs Or Analyses: Yes Supplementary Material: Sections D (proofs) and E (experimental details). Relation To Broader Scientific Literature: The paper is related to a recent literature stream on Neyman-orthogonal learning for various causal effects (e.g., the popular CATE DR- or R-learner). It extends the idea of constructing such an orthogonal meta-learner to estimate the conditional average treatment effect on the treated on panel data. Essential References Not Discussed: / Other Strengths And Weaknesses: Strengths: - The idea is novel and relevant. - The paper is well written and, in most parts, easy to follow for readers with sufficient background. Weaknesses: - The method assumes that all covariates are time-invariant. However, this is barely the case in real-world settings. - The paper does not discuss the proposed method in terms of limitations or future work - The paper does not provide a general literature review, making it difficult for readers not very familiar with orthogonal (CATE) meta-learners to assess the differences to existing works and the novelty of the proposed method Other Comments Or Suggestions: - Line 121: Typo "problem of estimating" - Theorem 3.6: R should be defined - Theorem 4.7: typo in title - Please format the paper in a revised version: The running title is still the one from the template; Figures and tables are not were they are supposed to be - The supplementary material has many typos Questions For Authors: - Definition 3.1: What is the difference to Neyman-orthogonality and why is conditional Neyman-orthogonality necessary here? In my opinion, the text in the definition describes normal NO, whereas the formula describes conditional NO. - What is the benefit of the Lagged Dependent Outcome Alternate Assumption? Why is this introduced here? Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: Thank you for the helpful reviews! We apologize for any typos and will definitely fix them for the camera-ready version. As pointed out by many reviewers, we were not able to include a detailed discussion and literature review sections in the initial submission due to length constraints. In the camera-ready version, we will expand on the related literature on CATE meta-learners to provide more background, and also provide more discussions on the limitations including the assumption that the covariates are time-invariant. First, we acknowledge that this is often not the case in real world applications. In such cases, one solution is to only use the pre-treatment covariates as in [1]. Alternatively, if there are other time varying variables that are also believed to be important for the time trends, one solution is to concatenate the covariates at the two different time points, and include all of them in the conditioning set for the conditional parallel trends conditions. But one must be careful to remove any covariates that are downstream from the treatment (i.e. descendents of the treatment in the context of a causal graph, these can be potential mediators) for the validity of the causal interpretation of the CATT. Regarding the Lagged Dependent Outcome assumption - this is also a common assumption that is widely used in economics when analysing panel data [2]. Depending on the context, this assumption might be more plausible than the parallel trends assumption, e.g. salary increase might be strongly correlated with the baseline salary level. While the parallel trends assumption might be seen as a special case of this assumption, many think of them as different assumptions, and the difference in the identification will result in different doubly robust estimation procedures when learning the conditional ATT on the full set of covariates $X$. In the case where the covariates of interest are a strict subset of the full set $X$, they can be estimated using the same framework. Hence, we include this setting in the appendix for comprehensiveness. In Section 5 of the paper, we discussed how to extend the learner to the multiple-time period settings. One solution is to learn a separate model for each lag period as in [1]. In this case, looking at more time periods is essentially the same task as in the two time period setting. An alternative would be to treat the lag period as an additional covariate to include in the conditioning set for the conditional parallel trends assumption. Practically this is what people can do. Qualitatively the insights from our current work should extend to this setting, even though the data are no longer i.i.d.; we believe that this also allows one to study the heterogeneity of the ATT with respect to the lag-periods. In this framework, the lag period may be seen as any other covariate used in the model. For this reason, we believe that results from simulation experiments in the two time-period setting should also generalize to the multiple time period setting. Note that our main theorems 3.6 and 4.7 do not really depend on the i.i.d. nature of the data. They are meta-theorems that state that as long as we have an ML algorithm that achieves a plug-in excess risk bound, then this translates to a mean-squared-error bound for the target causal estimand. Whether data are i.i.d. or not would be important when proving plug-in excess risk bounds, which would be easier for i.i.d., while for time-series or panel datasets, one would need to invoke martingale analysis to prove such excess risk bounds. Irrespective, our robustness conclusion will remain valid and is versatile, allowing for an arbitrary argument for the plug-in excess risk. On the clarification of conditional Neyman orthogonality we point out our response to Reviewer q3LX, who raised the same question. Finally, we really appreciate the time you put into reviewing our paper, and the constructive feedback that will help us improve our work! References - [1] Callaway, B., & Sant’Anna, P. H. (2021). Difference-in-differences with multiple time periods. Journal of econometrics, 225(2), 200-230. - [2] Angrist, J. D., & Pischke, J. S. (2009). Mostly harmless econometrics: An empiricist's companion. Princeton university press. - [3] Foster, Dylan J., and Vasilis Syrgkanis. "Orthogonal statistical learning." The Annals of Statistics 51.3 (2023): 879-908. --- Rebuttal Comment 1.1: Comment: Thank you for the clarification! I will raise my score to 4.	Summary: The paper develops a Neyman-orthogonal meta learner for estimating a conditional average treatment effect on the treated (CATT) in the framework of difference-in-differences (DiD). This framework casts the problem of CATT estimation as a convex risk minimisation that involves auxiliary (nuisance) models. The authors leveraged Neyman-orthogonality to further make the framework robust to the misspecification of the auxiliary models. Additionally, the authors provided several extensions of the method to (1) general functionals under covariate shift and (2) an instrumental DiD setting with non-compliance. At the end, the authors empirically demonstrated the superiority of their method. Claims And Evidence: The claims in the paper seem valid and are well supported. The authors provided the proofs for all the theoretical statements in the paper. Also, they provided the empirical evidence that the proposed approach is superior to existing methods. Methods And Evaluation Criteria: The contribution of the paper is rather theoretical. Yet, as a causal ML paper, the work follows a well-established practice of (semi-)synthetic evaluation. Theoretical Claims: I did not carefully check the proofs, but the overall approach follows the Neyman-orthogonality theory from [1].   References: - [1] Foster, Dylan J., and Vasilis Syrgkanis. "Orthogonal statistical learning." The Annals of Statistics 51.3 (2023): 879-908. Experimental Designs Or Analyses: See Methods And Evaluation Criteria. Supplementary Material: I skimmed over the appendices and they look fine. Relation To Broader Scientific Literature: The proposed approach fills the gap of meta learners in the DiD setting. The authors also extended it further to the covariate shift problem and the instrumental DiD. Essential References Not Discussed: It is not clear, why the conditional Neyman-orthogonality is required for estimating CATT and the regular (marginal) Neyman-orthogonality wouldn’t suffice (it seems to me that the conditional Neyman-orthogonality is a strictly stronger condition). Many existing learners like DR-/R-learners for CATE only rely on the marginal Neyman-orthogonality [1, 2], where in [2], any subset $W \subseteq X$ can be considered as the second-stage model input. Hence, I strongly encourage the authors to provide the discussion on why the conditional Neyman-orthogonality (and conditional Riesz Representer) are essential for this work. References: - [1] Foster, Dylan J., and Vasilis Syrgkanis. "Orthogonal statistical learning." The Annals of Statistics 51.3 (2023): 879-908. - [2] Morzywolek, Pawel, Johan Decruyenaere, and Stijn Vansteelandt. "On a general class of orthogonal learners for the estimation of heterogeneous treatment effects." arXiv preprint arXiv:2303.12687 (2023). Other Strengths And Weaknesses: Strength: - I really like the scope of the paper and its extensions to the covariate shifts and the instrumental DiD settings. Weaknesses (can be fixed during the rebuttal): - I found the structure of the paper slightly confusing. The authors often switch back and forth between (i) assumptions, (ii) identification formulas, and (iii) estimation approaches (e.g. in Sec. 3 and 5). I would suggest having a clear cut between all three and present the corresponding sections in the sequential manner. Other Comments Or Suggestions: I found some notational inconsistencies (e.g., the lower indices of $D$ in all the sections). I encourage the authors to carefully check the notation and fix it during the rebuttal. Questions For Authors: - Do we need a new term for the nuisance functions: auxiliary models? Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: Thank you for the helpful reviews! We will fix the inconsistent notations and restructure the paper for the camera-ready version. We introduced “auxiliary models” in the abstract to also accommodate for audiences that are not very familiar with the field. That being said, given the target audience, we might change it to “nuisance functions” for clarity. On the clarification of conditional Neyman orthogonality: in [1,2], neyman-orthogonality is referenced as a property of the loss, and is defined by: $$D_g D_{\theta} \mathcal{L} (\theta^, g_0)[\theta - \theta^, g - g_0] = 0 \quad \forall \quad \theta \in \Theta, \quad g \in \mathcal{G}$$ In Definition 3.2 of our paper, Neyman orthogonality is introduced as the property of the moment (see also [3]). Since it is a conditional moment restriction, it is natural that the directional derivatives vanish even conditioning on $W$. A conditionally Neyman orthogonal moment implies a Neyman orthogonal loss, if the gradient of the loss is associated with the moment. Thus conditional Neyman orthogonality of the moment suffices for a Neyman orthogonal loss, but as the reviewer suggests it is not necessary. However, if the target model space Theta is completely unstructured, then the two become equivalent. $$D_g D_{\theta} \mathcal{L} (\theta^, g_0)[\theta - \theta^, g - g_0] = 2D_g \mathbb{E} [m(\theta, g_0) (\theta - \theta^)] [g - g_0] = 2D_g \mathbb{E}\left[\mathbb{E} [m(\theta, g_0)\|W] (\theta - \theta^)\right] [g - g_0]$$ where $m(\theta, g) = \widehat{Y}(g) - D\theta(W)$ is the score function for the conditional moment restriction that we proposed. Since this has to hold for an arbitrary $\theta$, we have $D_g D_{\theta} \mathcal{L} (\theta^, g_0)[\theta - \theta^, g - g_0] =0$ if and only if $D_g \mathbb{E}[m(\theta, g_0)\|W] [g - g_0]=0 $ for all $g$ with measure 1 (since we can take $\theta=\theta^* + \delta$, where $\delta$ is the Dirac-delta function at a particular $W$). Similarly, since we are working with a conditional moment restriction (since the estimand is the CATT instead of the ATT), we also need the conditional Riesz Representer. Constructing Neyman orthogonal losses by first constructing a conditional Neyman orthogonal moment and finding the loss whose gradient is associated with this moment is a typical way of constructing an orthogonal loss. The meta-learners that the reviewer references can also be viewed through this lens. They correspond to Neyman orthogonal losses, because their gradient is associated with a moment restriction that satisfies conditional Neyman orthogonality (see e.g. the [4] for this fact, where also conditional Neyman orthogonality is used for both DR and R Learner style estimators of CATEs via forests). Moreover, this sufficient condition is satisfied for all the applications that our work is motivated by (e.g. DiD CATTs and all the applications of the general framework of conditional linear functionals with covariate shift). Finally, we really appreciate the time you put into reviewing our paper, and the constructive feedback that will help us improve our work! References - [1] Foster, Dylan J., and Vasilis Syrgkanis. "Orthogonal statistical learning." The Annals of Statistics 51.3 (2023): 879-908. - [2] Morzywolek, Pawel, Johan Decruyenaere, and Stijn Vansteelandt. "On a general class of orthogonal learners for the estimation of heterogeneous treatment effects." arXiv preprint arXiv:2303.12687 (2023). - [3] Chernozhukov, V., Chetverikov, D., Demirer, M., Duflo, E., Hansen, C., Newey, W., & Robins, J. (2018). Double/debiased machine learning for treatment and structural parameters. - [4] Oprescu, Miruna, Vasilis Syrgkanis, and Zhiwei Steven Wu. "Orthogonal random forest for causal inference." International Conference on Machine Learning. PMLR, 2019.	null	null	null	null	null	null	null	null
CoCoA-Mix: Confusion-and-Confidence-Aware Mixture Model for Context Optimization	Accept (poster)	Summary: The authors explore the prompt tuning problem of vision-language models and propose a training method, CoCoA-Mix, to improve generalization and specialization simultaneously. CoCoA-Mix consists of a confusion-aware loss to enhance specialization for confusing classes and a confidence-aware temperature strategy that aims to improve generalization. The authors provide a theoretical derivation for the proposed method. Moreover, the authors provide experimental results based on CLIP to demonstrate the effectiveness of CoCoA-Mix. Claims And Evidence: Yes. Methods And Evaluation Criteria: Yes, I think the proposed method makes sense for the fine-tuning problem of VLMs. Theoretical Claims: I check the proof of Theorem 3.2 and I think it is correct. However, I have doubts about the introduction of the target domain. The paper [1] shows a distribution shift between the target domain and the source domain. This shift generally does not refer to the gap between the empirical error and the expected error. [1] Kl guided domain adaptation, Nguyen et al., ICLR 2022. Experimental Designs Or Analyses: Yes, I checked the results and settings, and the authors provided the source code. Supplementary Material: Yes, I reviewed the section A, C, D, E, and F, and the authors provided the source code. Relation To Broader Scientific Literature: This submission discusses the weakness of previous prompt tuning methods and proposes CoCoA-Mix to improve generalization and specialization simultaneously. Essential References Not Discussed: No. Other Strengths And Weaknesses: Strengths: 1. The authors study prompt tuning problems and propose CoCoA-Mix to enhance generalization and specialization simultaneously. 2. The authors provide theoretical support to make the method more convincing. Weakness: 1. The writing is not clear. The detailed description of Confidence-Aware Temperature for Generalization without Trade-Offs in the submission is too confusing, which makes it difficult for readers to intuitively understand its content. In addition, the authors did not provide a description of the overall process of the method, and even a description of the overall loss function. (e.g., q only appears once in Eq. 12 but has no specific description.) 2. There are too few works in the related work section, which basically only include a few comparative methods, and cannot give readers a full picture of the field. 3. Lack of baseline CoCoOp. Why is the 4-shot setting used in the experiment in Table 1 instead of the commonly used 16-shot setting? Other Comments Or Suggestions: please refer to Other Strengths And Weaknesses. Questions For Authors: please refer to Other Strengths And Weaknesses. Code Of Conduct: Affirmed. Overall Recommendation: 2	Rebuttal 1: Rebuttal: ## `Theoretical Claims` In our paper, we refer to Eq. 12 in [1], which relates distributional shift to generalization performance: $$ l\_\\text{test} \\leq l\_\\text{train} + \\frac{M}{\\sqrt{2}} \\sqrt{\\text{KL} [p\_T(z)\|p\_S(z)] +\\mathbb{E}\_{p\_T(x)}\\left[ \\text{KL}[p\_T(y\|x)\|p\_S(y\|x)] \\right] }, $$ where $l\_\\text{train}=\\mathbb{E}\_{(x,y)\\sim p\_S(x,y),z\\sim p(z\|x)}[-\\log\\hat{p}(y\|z)]$; $l\_\\text{test}=\\mathbb{E}\_{p\_T(x,y)}[-\\log\\hat{p}(y\|x)]$; $p\_S$ and $p\_T$ are joint data distributions of source and target domains, respectively; and $z$ is a representations derived from $x$. In our setting, $l_\text{train}$ and $l_\text{test}$ correspond to $\epsilon_S(\hat{p})$ and $\epsilon_T(\hat{p})$ by *Eq. 2. We assume the CLIP encoder yields sufficiently informative representations via large-scale pretraining, satisfying Assumptions 1 and 2 in [1]. This allows us to apply Eq. 12 in [1] to bound the target error $\epsilon_T(\hat{p})$ as follows: $$ \epsilon_T(\hat{p}) \leq \epsilon_S(\hat{p}) + \frac{M}{\sqrt{2}} \sqrt{ \text{KL}(p_T(\mathbf{z})\|p_S(\mathbf{z}))+\lambda }. $$ We hope this clarifies our method. If we misunderstood your point, we would appreciate further clarification. [1] Kl guided domain adaptation, Nguyen et al., ICLR 2022. --- ## `W-1` [Confidence-Aware Temperature for Generalization without Trade-Offs]* We would appreciate clarification on which part of the 'detailed description' was confusing so that we can address it more precisely in the final version. To clarify, CoA-Temp adjusts the weight between specialized and generalized predictions based on whether the class is in the in-class or out-class domain. The in-class is defined as the set of classes in the training dataset, while the out-class consists of random words not included in the training dataset. The in-class weight $\alpha_\text{in}$ is optimized using cross-entropy loss on in-class training samples (*Eq. 15), while the out-class weight $\alpha_\text{out}$ is optimized using an entropy-based loss (Eq. 16) under Assumption 3.4, which assumes generalized predictions are more reliable in out-class domains. For details on $\alpha$ optimization and its use during inference, see our responses to Reviewer AKUY* (`W-2`) and (`W-4`), respectively. [Overall process] Our method optimizes three components and each component is optimized simultaneously with a separate loss function and optimizer : 1. Prompt $\boldsymbol{v}$ via cross-entropy and CoA loss *(Eq. 9), 2. In-class temperature $\tau_{\boldsymbol{v}}^\text{in}$ via a cross-entropy loss (Eq. 15), 3. Out-class temperature $\tau_{\boldsymbol{v}}^\text{out}$ via an entropy-based loss (Eq. 16). [Clarification on $q$ in Eq. (12)]* $q$ is the probability that a target sample belongs to the in-class domain $\mathcal{D}_T^\text{in}$ (L250–251). It is used only in the theoretical analysis (Eq. 12) to decompose the target error into in-class and out-class components. --- ## `W-2` [Prompt mixture models in VLMs] Recent works such as Allingham et al. (ICML'23) [2] and Lu et al. (ICML'24) [3] have explored prompt ensembling using hand-crafted prompts or multiple backbones to improve generalization. These methods generally do not target specialization and often require additional inference-time costs. In contrast, our method (1) explicitly improves specialization and generalization and (2) is more efficient than backbone-level ensembling [3], requiring no extra forward passes during inference, and (3) provides a mathematical framework for specialization and generalization in prompt tuning. We also compared CoA-Temp with the mixing strategy proposed in [3] and the results are provided [here](https://anonymous.4open.science/r/CoCoA-Mix-B466/Table_II-mixing_strategies.png). While the sample-aware weight generator in [3] requires $205,204$ learnable parameters, CoA-Temp achieves superior performance using only two parameters. [2] J. U. Allingham, et al. “A simple zero-shot prompt weighting technique to improve prompt ensembling in text-image models,” in ICML, 2023. [3] Z. Lu, et al. “Beyond sole strength: Customized ensembles for generalized vision-language models,” in ICML, 2024. --- ## `W-3` We have included CoCoOp in our evaluation under the same setting as *Table 1. The average performance is as follows: \| \| Base \| New \| H \| \| --- \| --- \| --- \| --- \| \| CoCoOp \| 77.23 \| 68.56 \| 71.33 \| Our goal is to demonstrate that CoCoA-Mix performs well even under challenging low-shot conditions*. We found that the benefits of our method are more pronounced when the training data is scarce. Nevertheless, we evaluated the 16-shot setting (results available [here](https://anonymous.4open.science/r/CoCoA-Mix-B466/Table_III-16shots_results.png)). Despite fewer learnable parameters, CoCoA-Mix achieved competitive performance on Base and clearly outperformed others on New.	Summary: This paper proposed a series of techniques to tackle the problem of improving specialization in prompt tuning, including confusion-aware loss, mixture-model using confidence-aware temperature. Extensive experiments are conducted to show the performance of the proposed method. Claims And Evidence: Yes. The paper claimed that it focuses on the problem of improving specialization for specific domains. Based on this motivation, the authors proposed several techniques to help prompts adapt to the target domains better. Methods And Evaluation Criteria: The method part is basically reasonable, because it focuses on the task-specific ability in prompt tuning and the generalization of universal embedding, and the loss ideas it uses are similar to some uncertainty-aware loss function ideas in the field of domain adaptation. The disadvantage is that the loss function is not novel enough, because similar ideas have already appeared in the traditional field of domain adaptation. The more interesting point is the proof related to the mixture-model and the setting of confidence-aware temperature. Theoretical Claims: I checked the corresponding proof and found no errors. The corresponding proof makes use of Jensen inequality and simple splitting, and its assumption is reasonable. Experimental Designs Or Analyses: The experiments are extensive, with a total of 11 datasets tested. I have no doubts about the experimental performance of the method. Supplementary Material: Yes. Relation To Broader Scientific Literature: This article solves the adaptation problem of prompt-tuning for different tasks to a certain extent, and provides some new analysis for the combination of domain adaptation and prompt-based methods. Essential References Not Discussed: None. Other Strengths And Weaknesses: The experimental performance of the method is very good, which is worthy of recognition. What needs to be discussed is that the performance of $CoCoA-Mix$ is lower than that of $CoA-Loss$ in the three data sets in the experiment, and the author needs to make some clarification and discussion in this regard. Other Comments Or Suggestions: I don't know if it's possible to do some statistical experiments on the Assumption $3.4$, such as using a certain data set to see if the Assumption $3.4$ is met. Although I intuitively think that the assumption is reasonable, it may need further verification. Questions For Authors: None. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: ## `Other Strengths And Weaknesses` First, the "CoA-Loss" in *Table 1* corresponds to a naive ensemble model with a fixed $\\pi=\\{0.5,0.5\\}$. This naive mixture prediction can perform well when the equal weighting is near-optimal for a given dataset. In contrast, CoCoA-Mix optimizes CoA-Temp based on the class domains, thereby enhancing specialization and generalization. In some datasets, the advantage over fixed-weight ensembles may appear limited, particularly under few-shot settings with high variance. To verify this, we evaluated both methods across six random seeds. The results (see below) show that CoCoA-Mix consistently matches or outperforms the naive ensemble across all datasets when averaged over more trials. This suggests that the lower performance on the three datasets is mainly due to variance resulting from limited trials. \| \| Caltech101 \| \| \| OxfordPets \| \| \| EuroSAT \| \| \| \| --- \| --- \| --- \| --- \| --- \| --- \| --- \| --- \| --- \| --- \| \| \| Base \| New \| H \| Base \| New \| H \| Base \| New \| H \| \| CoA-Loss (w/o mixture model) \| 97.2±0.1 \| 94.1±0.5 \| 95.7 \| 94.6±0.7 \| 97.3±0.3 \| 96.0 \| 84.5±0.8 \| 62.7±1.5 \| 72.0 \| \| CoA-Loss (seed1,2,3) \| 97.9±0.1 \| 94.5±0.2 \| 96.2 \| 94.9±0.5 \| 97.9±0.1 \| 96.4 \| 83.4±0.5 \| 70.1±2.5 \| 76.1 \| \| CoCoA-Mix (seed1,2,3) \| 98.0±0.0 \| 94.4±0.1 \| 96.2 \| 95.2±0.4 \| 97.6±0.1 \| 96.4 \| 83.5±0.7 \| 69.1±3.1 \| 75.5 \| \| \| Caltech101 \| \| \| OxfordPets \| \| \| EuroSAT \| \| \| \| --- \| --- \| --- \| --- \| --- \| --- \| --- \| --- \| --- \| --- \| \| \| Base \| New \| H \| Base \| New \| H \| Base \| New \| H \| \| CoA-Loss (seed1,2,3,4,5,6) \| 98.1±0.2 \| 93.6±1.4 \| 95.8 \| 94.6±0.5 \| 97.6±0.7 \| 96.2 \| 84.1±1.4 \| 66.9±4.1 \| 74.4 \| \| CoCoA-Mix (seed1,2,3,4,5,6) \| 98.2±0.2 \| 94.3±0.4 \| 96.2 \| 95.0±0.4 \| 97.6±0.3 \| 96.3 \| 84.4±1.4 \| 66.9±3.6 \| 74.5 \| --- ## `Other Comments Or Suggestions` We appreciate the suggestion. To empirically verify *Assumption 3.4, $\\epsilon\_{T\_v^\\text{in}}(\\hat{p}\_v)\\leq \\epsilon\_{T\_v^\\text{in}}(\\hat{p}\_h)$ and $\\epsilon\_{T\_v^\\text{out}}(\\hat{p}\_h)\\leq\\epsilon\_{T\_v^\\text{out}}(\\hat{p}\_v)$, we conducted a statistical experiment using the CIFAR-100 and the CLIP model. We randomly split the 100 classes into 50 in-class and 50 out-class domains, trained $\hat{p}_v$ using prompt tuning on the in-class subset, and compared it with the zero-shot $\hat{p}_h$ on both domains. This process was repeated over 10 random splits. A box plot summarizing the results is available [here](https://anonymous.4open.science/r/CoCoA-Mix-B466/Assumption3.4-statistical%20experiment-boxplot.png). The results show that $\hat{p}_v$ consistently outperforms $\hat{p}_h$ on in-class samples, while $\hat{p}_h$ achieves better performance on out-class samples. To assess statistical significance, we conducted one-sided paired $t$-tests on the per-split accuracy gaps. The resulting $p$-values were $p_{\text{in}} = 9.25 \times 10^{-12}$ and $p_{\text{out}} = 2.06 \times 10^{-10}$, both well below the standard threshold of 0.05. These results allow us to reject the null hypothesis and confirm that the inequalities in Assumption 3.4* hold with strong statistical significance. We will include a summary of this verification and the corresponding visualizations in the appendix of the final version. --- ## `Methods And Evaluation Criteria` Thank you for your feedback. If you could point us to the specific uncertainty-aware loss functions you are referring to, we would be happy to provide a detailed comparison and clarify the differences or contributions of our approach. Additionally, we provide a comparison with focal loss, generalized cross-entropy, and MAE in *Appendix D.3*, including both formulation and impact on specialization.	Summary: This paper addresses the challenge of improving both specialization and generalization in prompt tuning for vision-language models. It proposes a confusion-aware loss (CoA-loss) that refines decision boundaries between confusing classes, enhancing specialization. Additionally, they introduce a confidence-aware temperature (CoA-temp) mechanism within a mixture model to improve generalization by adjusting prediction weights based on confidence levels. The proposed method, CoCoA-Mix, integrates these components and demonstrates superior performance over state-of-the-art approaches in balancing specialization and generalization. Claims And Evidence: The claim that the provided mathematical framework demonstrates that specialization and generalization can be improved simultaneously is not supported by convincing theoretical evidence. The inequality derived in Theorem 3.2 ensures that $ \epsilon_{T}(\hat{p}_t^{\pi}) = \min_i \epsilon_T(\hat{p}_{t_i}) $ when $ \pi $ is optimized. However, it does not guarantee that $ \epsilon_{T}(\hat{p}_t^{\pi}) < \min_i \epsilon_T(\hat{p}_{t_i}) $. Consequently, Theorem 3.2 does not establish that specialization and generalization can be improved simultaneously. Methods And Evaluation Criteria: Yes Theoretical Claims: Yes, the proofs for the theoretical results are correct. Experimental Designs Or Analyses: Yes, there are no outstanding issues in the designs and analyses of this paper. Supplementary Material: Yes, I have reviewed the theoretical proofs in the supplementary material. Relation To Broader Scientific Literature: The mixture model in prompt tuning is straightforward and has been explored in previous literature; therefore, the contributions of this work to the relevant community are relatively modest. Essential References Not Discussed: No. Other Strengths And Weaknesses: Strengths: 1. The proposed mixture model is straightforward and effective in achieving a better trade-off between specialization and generalization in prompt tuning for vision-language models. 2. The empirical results demonstrate the superiority of the proposed methods over state-of-the-art prompt tuning approaches. Weaknesses: 1. The inequality derived in Theorem 3.2 ensures that $ \epsilon_{T}(\hat{p}_t^{\pi}) = \min_i \epsilon_T(\hat{p}_{t_i}) $ when $ \pi $ is optimized. However, it does not guarantee that $ \epsilon_{T}(\hat{p}_t^{\pi}) < \min_i \epsilon_T(\hat{p}_{t_i}) $. Consequently, Theorem 3.2 does not establish that specialization and generalization can be improved simultaneously. 2. The design of confidence-aware temperature requires further clarification: why is the weight $\alpha$ in the mixture model adjusted by optimizing the temperature rather than optimizing $\alpha$ directly? 3. The classification of in-class and out-class domains requires further discussion. In the implementation stage, are the optimization problems in Equations (15) and (16) solved simultaneously or separately in different cases? 4. The details of how to calculate the predictive probability of input images using the tuned mixture model at the inference stage should be discussed in Section 3. 5. Some visualization results in the evaluation section should be included to interpret the superiority of the proposed mixture model over existing methods, such as by visualizing the features on which the proposed algorithm relies. Other Comments Or Suggestions: Please refer to the weaknesses listed in the previous section. Questions For Authors: Please refer to the weaknesses listed in the previous section. Code Of Conduct: Affirmed. Overall Recommendation: 2	Rebuttal 1: Rebuttal: ## `W-1` We agree that Remark 3.3 should state $\\epsilon\_T(\\hat{p}\_t^\\pi)=\\min\_i\\epsilon\_T(\\hat{p}\_{t\_i})$, not $\leq$. However, our main claim regarding the simultaneous improvement of specialization and generalization relies on Theorem 3.2 and our method, not Remark 3.3. The figure [here](https://anonymous.4open.science/r/CoCoA-Mix-B466/Equation-target_error_bounds.png) illustrates how $\alpha_\text{in}$, $\alpha_\text{out}$, and $\\epsilon\_{S\_v}(\\hat{p}\_v)$ determine the upper bound of the target error in the mixture model. CoA-Loss reduces $\\epsilon\_{S\_v}(\\hat{p}\_v)$ and enhances specialization, while CoA-Temp optimizes $\alpha_\text{in}$ and $\alpha_\text{out}$ via *Eq. 15* and *Eq. 16* to improve generalization. Consequently, CoA-Loss and CoA-Temp jointly reduce the upper bound of $\epsilon_T(\hat{p}_t^\pi)$, thereby enhancing specialization and generalization simultaneously. Even without CoA-Temp, $\\epsilon\_{T\_v^\\text{out}}(\\hat{p}\_t^\\pi)=\\min\_i\\epsilon\_{T\_v^\\text{out}}(\\hat{p}\_{t\_i})$ and $\\epsilon\_{T\_v^\\text{in}}(\\hat{p}\_t^\\pi)=\\min\_i\\epsilon\_{T\_v^\\text{in}}(\\hat{p}\_{t\_i})$ guarantee performance at least as good as zero-shot CLIP for out-class domains and learned prompts for in-class domains simply by setting $\alpha_\text{out}=0$ and $\alpha_\text{in}=1$. This demonstrates that the mixture model can preserve both specialization and generalization. With CoA-Loss and CoA-Temp, these can be further improved simultaneously. *This is also supported by the empirical results in Tables 1 and 3**, where CoCoA-Mix consistently outperforms CLIP across both Base* and New domains. --- ## `W-2` As described in L222–224 (right column), $\tau_{\boldsymbol{h}}$ is fixed to the temperature of the pre-trained CLIP model. Therefore, optimizing $\tau_{\boldsymbol{v}}$ is sufficient to determine both $\alpha$ and $\tau$ via *Eq. 14: $\tau=\frac{\tau_h\tau_v}{\tau_h+\tau_v}$ and $\alpha=\frac{\tau_h}{\tau_h+\tau_v}$. The design was chosen to ensure compatibility with CLIP's standard temperature scaling framework. We also evaluated the direct optimization of $\alpha$ using a softmax.* The results can be found [here](https://anonymous.4open.science/r/CoCoA-Mix-B466/Table_I-optimization_strategies.png). Specifically, we fixed the pre-softmax logit of $\boldsymbol{h}$ to zero (i.e., $\alpha_h'=0$) and set $\tau$ to the temperature of the pre-trained CLIP model. Table I shows that both approaches yield similar performance, indicating that our objective is not sensitive to the choice of optimization strategy for $\alpha$. --- ## `W-3` The temperatures $\tau_{\boldsymbol{v}}^\text{in}$ and $\tau_{\boldsymbol{v}}^\text{out}$ are optimized simultaneously in the same loop, but each temperature is optimized with its own loss function and optimizer, as described in "[Overall process]" of our response to Reviewer P3tC’s comment `W-1`. --- ## `W-4` At inference time, given the optimized prompt $\boldsymbol{v}$ and the temperatures $\\tau\_{v}^\\text{in}$ and $\\tau\_{v}^\\text{out}$, we compute the mixture weight as follows: $$ \\alpha(l)=\\begin{cases} \alpha\_\text{in} = \\tau/\\tau\_{v}^\\text{in}&\\text{if $l\\in\\mathcal{Y}\_{S\_v}$} \\\\ \alpha_\text{out} =\tau/\tau_{v}^\text{out}&\text{otherwise} \end{cases}. $$ The predictive probability is then: $$ \hat{p}_{t}^{\pi}(l) = \\frac{\\exp\\left((1-\\alpha(l))\\boldsymbol{s}\_{h}(l)/\\tau+\\alpha(l)\\boldsymbol{s}\_{v}(l)/\\tau\\right)}{ \\sum\_{l'\\in\\mathcal{Y}}\\exp\\left((1-\\alpha(l))\\boldsymbol{s}\_{h}(l)/\\tau+\\alpha(l)\\boldsymbol{s}\_{v}(l)/\\tau\\right)}. $$ --- ## `W-5` We provide ScoreCAM visualizations comparing CoCoA-Mix with CLIP and CoOp to improve interpretability. The visualization results are available [here](https://anonymous.4open.science/r/CoCoA-Mix-B466/Figure_I-scoreCAM.png). In Flowers102 (New), CoCoA-Mix attends more accurately to semantic cues in out-class domains, highlighting that CoA-Temp improves generalization. In FGVC Aircraft (Base), CoA-Loss attends to fine-grained details such as wing text more effectively than zero-shot CLIP. These results show that CoA-Temp and CoA-Loss enhance generalization and specialization, respectively. --- ## `Relation To Broader Scientific Literature` While prompt mixtures have been studied in prior work, our method differs notably in design and objective. Please see our response to Reviewer P3tC (`W-2`) for a detailed comparison. Furthermore, most existing prompt tuning methods are designed for specialization-generalization trade-offs or incremental learning, making it difficult to achieve both within a single framework. In contrast, as shown in *Table 2*, our method naturally extends to incremental learning without catastrophic forgetting, bridging the two objectives. Therefore, we believe this work makes a meaningful contribution to prompt tuning.	null	null	null	null	null	null	null	null
AdvAgent: Controllable Blackbox Red-teaming on Web Agents	Accept (poster)	Summary: The paper introduces AdvAgent, a black-box red-teaming framework that uses RL to optimize adversarial prompts, injecting them into HTML to mislead web agents. It achieves high attack success rates on GPT-4V and Gemini 1.5, revealing the limitations of prompt-based defenses. 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: NA Essential References Not Discussed: No. Other Strengths And Weaknesses: Strengths： 1. The paper proposes a novel black-box attack framework combining RL with adversarial prompt injection, which is relevant to web agent security. 2. Experimental results demonstrate high ASR across different web domains. Weaknesses： 1. The paper lacks theoretical justification, as it does not adequately explain why DPO was chosen over other RL methods. 2. The evaluation scope is limited, with experiments focusing on specific tasks, making it unclear whether the method generalizes well. 3. There is no analysis of computational cost, leaving the efficiency of AdvAgent for real-world applications unaddressed. 4. The defense analysis is weak, as it only evaluates prompt-based defenses without exploring stronger security mechanisms like robust optimization or model distillation. 5. There is an issue in Figure 5, which illustrates the prompt optimized by AdvWeb rather than the proposed method, AdvAgent. Other Comments Or Suggestions: See weaknesses above. Questions For Authors: See weaknesses above. Ethical Review Flag: Flag this paper for an ethics review. Ethics Expertise Needed: ['Research Integrity Issues (e.g., plagiarism)'] Ethical Review Concerns: The paper closely resembles preprint paper [1], and the name "AdvWeb" in Figure 5 from [1] has not been modified. Furthermore, the provided code differs from the publicly available code of [1]. If the author of [1] had submitted this paper, they should have used an anonymous code repository to upload the original code rather than significantly altering it. This raises concerns that the paper may be plagiarizing [1]. If it is confirmed that there was no intention to plagiarize, I will revise my evaluation accordingly. [1] Xu, Chejian, et al. "Advweb: Controllable black-box attacks on vlm-powered web agents." arXiv preprint arXiv:2410.17401 (2024). Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We sincerely thank the reviewer for their thoughtful and constructive feedback. Below, we address each of the concerns raised: > Q1: More clarifications on the usage of DPO optimization in AdvAgent. Thank you for the interesting question! We'd like to clarify that our reinforcement learning setup only receives binary signals as rewards. Specifically, we assign a binary reward based on whether the agent successfully performs the targeted adversarial action (e.g., selecting a target stock). A successful misbehavior is labeled as positive; otherwise, it is negative. These binary labels make other RL optimization methods such as GRPO—which rely on continuous and dense process reward signals [2]—unstable. However, binary feedback is well-suited for constructing pairwise preference data. Therefore, we adopt DPO as a more signal-efficient approach for training our adversarial prompter model. > Q2: Expanded evaluation tasks. We appreciate this insightful suggestion and fully agree that broader evaluation is essential for demonstrating the generality of AdvAgent. While our primary evaluation focuses on SeeAct agent with the Mind2Web dataset—selected for its realism and established use in the web agent community—we have extended our study to include the BrowserGym agent [3] in the WebArena environment [4], which offers a distinct set of agent architecture and web environment. As shown in Table A below, AdvAgent achieves high attack success rates (ASR) when applied to BrowserGym, confirming that our attack strategy generalizes across different web agents and environments. Table A: Attack results on 3 domains in WebArena with BrowserGym agent \| Agent \| D1 \| D2 \| D3 \| Mean ± Std \| \|-------------\|------\|------\|------\|----------------\| \| BrowserGym \| 95.1 \| 80.8 \| 44.6 \| 73.5 ± 21.2 \| These results reaffirm that AdvAgent generalizes across both agent designs (e.g., SeeAct, BrowserGym) and web interaction environments (e.g., Mind2Web, WebArena). We will include these expanded experiments and corresponding analysis in the final version of the paper to better highlight the flexibility and impact of our framework. > Q3: Clarifications of computational cost. Thank you for the suggestion. Our method is efficient—generating an adversarial prompt takes 2.2 seconds per task on average. Unlike optimization-based baselines requiring task-specific tuning, it uses a single forward pass, making it suitable for real-time red-teaming. We will include this in the final paper. > Q4: Evaluations of stronger defense strategies. We appreciate the reviewer’s suggestion to evaluate stronger defenses. To this end, we tested our AdvAgent framework on the SeeAct agent using GPT-4o-mini as the backend model. GPT-4o-mini is specifically optimized for robustness against jailbreak-style attacks through enhanced alignment techniques, including instruction hierarchies that guide the model to avoid unsafe or conflict behaviors during inference. These instruction hierarchies are designed to suppress potentially harmful actions by aligning the model’s response with different hierarchies of roles. As part of the model’s robust training, behaviors indicative of jailbreaking are explicitly suppressed. The results, summarized in Table B below, show that instruction hierarchies provide stronger defense compared to prompt-based strategies previously shown in our paper. Nonetheless, AdvAgent still achieves a relatively high average attack success rate (ASR) of ~59%, indicating that even models with advanced alignment mechanisms remain vulnerable to our attacks. Table B: Effectiveness of instruction hierarchy defense \| SeeAct Backend \| D1 \| D2 \| D3 \| D4 \| Mean ± Std \| \|----------------\|-------\|-------\|-------\|-------\|----------------\| \| GPT-4V \| 100.0 \| 94.4 \| 97.6 \| 98.0 \| 97.5 ± 2.0 \| \| GPT-4o-mini \| 56.9 \| 60.5 \| 83.3 \| 34.1 \| 58.7 ± 17.4 \| [1] Shao, Zhihong, et al. "Deepseekmath: Pushing the limits of mathematical reasoning in open language models." arXiv preprint arXiv:2402.03300 (2024). [2] Lightman, Hunter, et al. "Let's verify step by step." ICLR 2023. [3] Drouin, Alexandre, et al. "Workarena: How capable are web agents at solving common knowledge work tasks?." ICML 2024. [4] Zhou, Shuyan, et al. "Webarena: A realistic web environment for building autonomous agents." ICLR 2024. --- Rebuttal Comment 1.1: Comment: Thank you for your detailed response and clarifications. I appreciate the effort to address my concerns, particularly the expanded experiments and additional explanations. However, the paper would benefit from a more robust theoretical foundation to better support the findings, which would enhance its overall impact. As such, I am inclined to maintain my current evaluation. While the work shows promise, it would greatly benefit from further theoretical exploration in future research directions. --- Reply to Comment 1.1.1: Comment: We sincerely thank the reviewer for taking the time to read our response and for the thoughtful follow-up! We’re glad to hear that the expanded experiments and clarifications were helpful. We fully agree that developing a stronger theoretical foundation is a valuable and exciting direction for future work. However, the primary objective of this paper is to propose and empirically validate a practical red-teaming framework for web agents. To that end, we focus on demonstrating the effectiveness of AdvAgent through extensive evaluations. Our results show that AdvAgent consistently outperforms strong baselines across diverse attack scenarios, remains highly effective even against well-aligned models like GPT-4o-mini with instruction hierarchy, and generalizes well across different environments (e.g., WebArena) and agent architectures (e.g., BrowserGym), underscoring its robustness and real-world applicability. While theoretical analysis is beyond the scope of this work, we will explicitly include a discussion of it as a promising future direction in the revised version. Once again, we thank the reviewer for their thoughtful feedback and constructive suggestions.	Summary: This paper introduces AdvAgent, a black-box red-teaming framework designed to systematically uncover vulnerabilities in foundation model-based web agents, which are increasingly used to automate complex tasks but also pose significant security risks. The key contribution of AdvAgent is its use of a reinforcement learning-based pipeline to train an adversarial prompter model. This model generates optimized adversarial prompts that exploit weaknesses in web agents while maintaining stealth and controllability. The framework is evaluated extensively, demonstrating high success rates in compromising state-of-the-art GPT-4-based web agents across various tasks. The study also reveals that existing prompt-based defenses offer limited protection, leaving agents highly vulnerable to AdvAgent's attacks, with attack success rates (ASRs) exceeding 88.8% even after applying defenses. Claims And Evidence: This paper made various claims upon the constraints and challenges on the attacks against web agent. Some are supported by existing literature and others are based on the authors' own knowledge. Based on my background of knowledge, I think those claims generally make sense. Methods And Evaluation Criteria: This work leverages reinforcement learning from AI feedback (RLAIF)-based framework for black-box red-teaming against web agents. The overall pipeline is reasonable. The key concern to me is that this work only uses SeeAct as the victim model, and the experiments are performed on only one dataset, Mind2Web. The generality of the results is not clear. Given that fact that there are many choices of agent models and benchmark datasets, the paper could be strengthened with more comprehensive evaluation. Theoretical Claims: There is no theoretical claim in this paper. Experimental Designs Or Analyses: The overall experimental designs or analyses are sound to me. However, I would suggest more comprehensive analysis on agent models and datasets to show the generality of the approach. Supplementary Material: Yes. I have reviewed Appendix A-E. Relation To Broader Scientific Literature: This paper is closely related to the broader research area of (M)LLM agents and safety. Existing studies have revealed various security risks of the agents. This paper could facilitate existing studies with a controllable black box red-teaming framework. The framework could be generally effective across related fields. 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: 4	Rebuttal 1: Rebuttal: We thank the reviewer for their positive assessment and thoughtful feedback. We appreciate your recognition of the novelty and effectiveness of AdvAgent, and your acknowledgment that the proposed RL-based framework is reasonable and promising. Below, we respond to your main concern regarding generality: > Q1: The paper only uses SeeAct agent and the Mind2Web dataset. The generality of the results is not clear. More comprehensive evaluation across agents and datasets is suggested. We appreciate this insightful suggestion and fully agree that broader evaluation is essential for demonstrating the generality of AdvAgent. While our primary evaluation focuses on SeeAct agent with the Mind2Web dataset—selected for its realism and established use in the web agent community—we have extended our study to include the BrowserGym agent [1] in the WebArena environment [2], which offers a distinct set of agent architecture and web environment. As shown in Table A below, AdvAgent achieves high attack success rates (ASR) when applied to BrowserGym, confirming that our attack strategy generalizes across different web agents and environments. Table A: Attack results on 3 domains in WebArena with BrowserGym agent \| Agent \| D1 \| D2 \| D3 \| Mean ± Std \| \|-------------\|------\|------\|------\|----------------\| \| BrowserGym \| 95.1 \| 80.8 \| 44.6 \| 73.5 ± 21.2 \| These results reaffirm that AdvAgent generalizes across both agent designs (e.g., SeeAct, BrowserGym) and web interaction environments (e.g., Mind2Web, WebArena). We will include these expanded experiments and corresponding analysis in the final version of the paper to better highlight the flexibility and impact of our framework. [1] Workarena: How capable are web agents at solving common knowledge work tasks? ICML 2024. [2] Webarena: A realistic web environment for building autonomous agents. ICLR 2024. --- Rebuttal Comment 1.1: Comment: Thanks for the response. I appreciate the authors' efforts in addressing my major concern on the generality. After reading the other reviewers' comments and the author response, I think it is reasonable to perform HTML injection in this work as a widely used paradigm (though I agree that visual attack would be quite promising, too -- but this could be falling into different reseach lines due to the diversity of backbone LLMs or MLLMs). I believe that this is a solid paper.	Summary: The paper introduces AdvAgent, a black-box red-teaming framework designed to red team web agents against prompt injection attacks.These agents, while enhancing productivity, pose security risks due to their autonomous decision-making capabilities. The method first starts by collecting the dataset of successful/unsuccessful prompt injections by prompting target model. Afterwards, AdvAgent employs SFT followed by DPO to train an adversarial prompter model on that dataset. The framework is evaluated against GPT-4V based web agent (only text), achieving high success rates in various tasks, and revealing that these models are susceptible to these types of attacks. The study highlights the need for stronger security measures to protect web agents from adversarial attacks. Claims And Evidence: - Vulnerability of web agents and need for stronger defenses: The paper claims that current web agents, particularly those based on foundation models like GPT-4, are vulnerable to prompt injection attacks (or in general adversarial attacks), which can lead to severe consequences in high-stakes domains such as finance and healthcare. Prompt-based defense is certainly not enough. I agree with this claim and evidences provided in this paper partially confirm this. That said, community is developing various methods to fight against it. For example, instruction hierarchy proposed by OpenAI is specifically designed for this type of scenario and I strongly encourage authors to consider that defense mechanism in their experiments. It is implemented in GPT-4o-mini: https://openai.com/index/gpt-4o-mini-advancing-cost-efficient-intelligence/ - AdvAgent Framework: It introduces AdvAgent, a novel black-box red-teaming framework that effectively identifies and exploits vulnerabilities in web agents by generating adversarial prompts through a SFT+DPO pipeline. The position as a general method. However, I strongly disagree that this argument holds. Although web agents became a buzz word and there is no standard on the mode of its operations, web agents seem to be converging towards screenshot-based operation mode (OpenAI Operator, Claude computer use agent, etc.). And given the fact that the method can only operate on non-visual elements (via HTML injection), I don't think it can be considered as general as authors claim. Indeed, experiments do not contain any proper web agent, only scaffolding around GPT-4V. I'd suggest positioning this paper as red teaming method for text-based agents (e.g. tool usage or via API). - High Success Rates: The paper claims that AdvAgent achieves high attack success rates against state-of-the-art web agents across diverse tasks, significantly outperforming existing baseline methods. I don't think that the comparison with GCG was conducted in a fair way. Why LLaVa was used as a proxy whitebox model? As I mentioned above, the considered threat model only applicable to text-based models. Ones needs to optimize GCG in this particular setting (using the same inputs and targets). I simply cannot believe that GCG would achieve 0 in this scenario! Moreover, since the agents are text-based, I'd also include some of the chatbot attack methods as baselines. - Limited Defense Effectiveness: It asserts that current prompt-based defenses provide limited protection against the types of attacks generated by AdvAgent, indicating a critical need for more robust security measures. While I partially agree with this statement, more advanced defense mechanisms (e.g. instruction hierarchy as described above) necessary to validate this. - Stealthiness and Controllability: AdvAgent is claimed to maintain stealthiness and controllability in its attacks, allowing adversaries to modify attack targets easily without re-optimization. While this is true for the method itself, threat model assumes Attacker can control arbitrary HTML elements of the web page. This is only achievable for untrusted web resources (e.g. attacker creates its own website). However, current web agents operates only on white-listed web apps, where attacker has a limited control. Methods And Evaluation Criteria: Overall, evaluation metrics are fine to me. I've listed several issues above and some of them applicable here (baselines, defense mechanisms). Moreover, I strongly believe that considering GPT-4 based agent is not enough as evidence. Experiments should also include "real" web navigation agents available at hand. Theoretical Claims: N/A Experimental Designs Or Analyses: see methods and evaluation criteria; claim and evidences Supplementary Material: - Qualitative results; - Implementation details; Relation To Broader Scientific Literature: - the method is addressing an important problem and novel in the aspect of proposing red-teaming methodology for web agents. Essential References Not Discussed: N/A Other Strengths And Weaknesses: discussed in other sections above Other Comments Or Suggestions: --------- Post-Rebuttal ----------- Authors provided additional experiments with Instruction Hierarchy (IH) defense mechanism. IH seems to significantly reduce the efficacy of the attack, although overall ASR is still high (~60%). That said, results on strong baselines such as GCG was not presented. Moreover, I'm still not sure how realistic the threat model described above. Afaik, all commercial agents do not use invisible html elements as observations so it is unclear if the method will be relevant for that. With this big two disclaimers, I'm increasing my score as the paper seems to be the first in this series and ML community might benefit on that. Though my concern on threat model is quite important. Questions For Authors: - How do you handle the case if there is a sparse signal for attacks? I'd imagine future agent will be more robust and the method receives more negative signals rather than positive ones. This is a fundamental problem in RL. - I did not get why optimization search space is reduced? You still need to optimize over vocabulary of tokens (to generate prompt) + location to put the attack? - what exactly are positive/negative rewards? Is it a binary indicator based on model output? Please, define it explicitly. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We thank the reviewer for their thoughtful and constructive feedback. We appreciate the recognition of the novelty and importance of our work in red-teaming web agents. We address the specific concerns and suggestions below: > Q1: Generality of AdvAgent and experiments on additional web agents. We appreciate the insightful comment! We acknowledge that purely screenshot-based web agents (e.g., OpenAI’s Operator) have recently demonstrated promising performance in everyday tasks like ticket booking. However, we would like to emphasize that text- and screenshot-based web agents remain one mainstream approach, particularly for tasks that demand precise data perception, such as data management in ServiceNow [1] or spreadsheet manipulation in WebArena [2]. These applications involve handling large volumes of structured data, where agents leveraging both textual/code and screenshots show superior performance [1,3,4]. Therefore, AdvAgent is broadly applicable to these generalist web agents, which are especially well-suited for data-intensive scenarios. Empirically, beyond evaluating SeeAct, we also test the BrowserGym agent [1] in the WebArena environment [2] to further validate the effectiveness of AdvAgent as a general red-teaming framework. Results and analysis are shown in Q1 of our response to Reviewer WJQ8, where we show AdvAgent is general and able to attack other web agents in other environments. > Q2: More clarifications on GCG and evaluation on additional baselines. Thank you for the valuable comment! Our GCG optimization uses the same inputs (HTML + SeeAct prompt [3]) and targets the same malicious behaviors as AdvAgent. We chose LLaVA as the proxy model since it's the default in SeeAct [3] and performs well in the context. However, its poor results in our setting highlight limited transferability to GPT-4V backends, pointing to the need for better black-box optimization methods. In addition to the two agent-specific black-box optimization methods (Agent-Attack and InjecAgent), we evaluate two additional state-of-the-art general-purpose black-box attack methods for LLMs: PAIR [5] and TAP [6]. We attack the SeeAct agent with GPT-4V as the backbone. As shown in Table A, the results indicate that AdvAgent still outperforms strong black-box attack methods for LLMs. Table A: Additional baselines \|Algorithm\|D1\|D2\|D3\|D4\|Mean±Std\| \|-\|-\|-\|-\|-\|-\| \|PAIR\|25.7\|17.1\|31.4\|28.6\|25.7 ± 5.3\| \|TAP\|51.4\|57.1\|80.0\|37.1\|56.4 ± 15.4\| \|AdvAgent\|100.0\|94.4\|97.6\|98.0\|97.5 ± 2.0\| > Q3: Testing with defenses such as instruction hierarchy. Thank you for the suggestion. Due to space constraints, we address this question in Q4 of our response to Reviewer oVuF, where we show that AdvAgent still achieves a relatively high ASR against instruction hierarchy. > Q4: More clarifications on the threat model. We appreciate the reviewer’s concern. Like [7, 8], our threat model assumes agents operate in untrusted or semi-trusted environments—e.g., browsing third-party sites or interacting with embedded services—where supply-chain attacks and hidden HTML manipulations (e.g., via `aria-label` or `id`) are realistic risks. We acknowledge this may not apply to fully whitelisted settings and will clarify the scope in the revision. > Q5: Clarification on reward signal and sparse feedback. Thank you for these interesting questions! We assign a binary reward: positive if the agent performs the targeted adversarial action (e.g., selects the specified stock), negative otherwise. When positive signals are extremely sparse—especially with highly safety-aligned models—we train the adversarial prompter using online RL to dynamically collect signals during training. In parallel, we incorporate off-policy guidance [9, 10] from a less safety-aligned model and easier data points. This proxy supervision helps the model learn the structure of successful jailbreaks more efficiently. Online exploration further amplifies positive signals over time. We will expand on this in Section 4.2 in the revision. > Q6: Clarification on the optimization search space reduction Thank you for the question. We reduce the search space by fixing the injection position, avoiding the need to optimize over multiple locations. [1] Workarena: How capable are web agents at solving common knowledge work tasks? ICML 24. [2] Webarena: A realistic web environment for building autonomous agents. ICLR 24. [3] Gpt-4v(ision) is a generalist web agent, if grounded. ICML 24. [4] Agent workflow memory. arXiv 2024. [5] Jailbreaking black box large language models in twenty queries. arXiv 2023. [6] Tree of attacks: Jailbreaking black-box llms automatically. NeurIPS 2024. [7] Eia: Environmental injection attack on generalist web agents for privacy leakage. ICLR 25. [8] Attacking Vision-Language Computer Agents via Pop-ups. arXiv 2024. [9] Hindsight experience replay. NeurIPS 2017. [10] Reinforcement learning with sparse rewards using guidance from offline demonstration. ICLR 22. --- Rebuttal Comment 1.1: Comment: Thanks for submitting rebuttal and performing additional experiments. I really appreciate that! My impression form the results on gpt-4o-mini is that IH works reducing ASR almost two times (although not clear since we don't have results without it). Also, what are the performances of baselines (gcg, tap, etc.) on gpt-4o-mini? --- Reply to Comment 1.1.1: Comment: We thank the reviewer for carefully reading our rebuttal and for the thoughtful follow-up! We're glad the additional experiments were helpful, and we appreciate the suggestion to report baseline performance on GPT-4o-mini. Below, we provide further clarifications and new results. > Instruction Hierarchy Effectiveness and Baseline Performance on GPT-4o-mini Indeed, instruction hierarchy (IH) plays a significant role in reducing the attack success rate (ASR). In our main experiments with GPT-4V as the backend, AdvAgent achieves an ASR of 97.5%. When switching to GPT-4o-mini, which incorporates IH and other alignment mechanisms, the ASR drops to 58.7%. This demonstrates that IH can significantly reduce adversarial behaviors and provide meaningful mitigation. However, the fact that AdvAgent still succeeds in nearly 60% of cases under this stronger defense highlights its continued effectiveness and adaptability, even against models with advanced alignment mechanisms like instruction hierarchy. To further contextualize this, we additionally evaluated baseline methods on GPT-4o-mini under the same settings. As shown in Table A, AdvAgent consistently outperforms all baseline methods, including general-purpose black-box attacks (PAIR, TAP) and agent-specific attacks (Agent-Attack, InjecAgent). The performance gap is substantial—AdvAgent improves over the best baseline (InjecAgent) by 28% on average, demonstrating its robustness even against agents with stronger alignment defenses. Table A: ASR (%) on SeeAct agent powered by GPT-4o-mini with instruction hierarchy defense. \| Algorithm \| D1 \| D2 \| D3 \| D4 \| Mean ± Std \| \|---------------\|-------\|-------\|-------\|-------\|----------------\| \| PAIR \| 2.9 \| 0.0 \| 2.9 \| 0.0 \| 1.5 ± 1.5 \| \| TAP \| 14.3 \| 0.0 \| 8.6 \| 0.0 \| 5.7 ± 6.1 \| \| Agent-Attack \| 17.14 \| 28.57 \| 57.14 \| 8.57 \| 27.9 ± 18.3 \| \| InjecAgent \| 28.57 \| 33.33 \| 38.10 \| 22.86 \| 30.7 ± 5.6 \| \| AdvAgent \| 56.9 \| 60.5 \| 83.3 \| 34.1 \| 58.7 ± 17.4 \| For ease of comparison, in Table B, we provide the results previously presented in the paper and earlier in our rebuttal for the GPT-4V backend (without IH). This comparison highlights the impact of instruction hierarchy: all methods see a sharp ASR drop under GPT-4o-mini, but AdvAgent remains significantly more effective than all alternatives across both settings. Table B: ASR (%) on SeeAct agent powered by GPT-4V without instruction hierarchy defense. \| Algorithm \| D1 \| D2 \| D3 \| D4 \| Mean ± Std \| \|---------------\|-------\|-------\|-------\|-------\|----------------\| \| PAIR \| 25.7 \| 17.1 \| 31.4 \| 28.6 \| 25.7 ± 5.3 \| \| TAP \| 51.4 \| 57.1 \| 80.0 \| 37.1 \| 56.4 ± 15.4 \| \| Agent-Attack \| 26.4 \| 36.0 \| 61.2 \| 58.0 \| 45.4 ± 14.6 \| \| InjecAgent \| 49.6 \| 47.2 \| 73.2 \| 87.2 \| 64.3 ± 16.7 \| \| AdvAgent \| 100.0 \| 94.4 \| 97.6 \| 98.0 \| 97.5 ± 2.0 \| We sincerely thank the reviewer again for encouraging us to strengthen both the experimental scope and comparative clarity. We hope this clarifies the performance impact of instruction hierarchy and further reinforces the strength and adaptability of AdvAgent, even in modern, defense-aware deployment settings.	null	null	null	null	null	null	null	null
Tilted Sharpness-Aware Minimization	Accept (poster)	Summary: This paper introduces Tilted Sharpness-Aware Minimization (TSAM), a novel extension of Sharpness-Aware Minimization (SAM) designed to further enhance generalization in deep learning models. While SAM aims to minimize the worst-case local solutions, it overlooks many neighboring regions that may also contribute to significant losses. TSAM addresses this limitation by exponentially tilting the loss landscape, assigning greater weight to neighbors with higher losses. The authors theoretically demonstrate that as the tilt scalar $t$ increases, TSAM favors flatter minima. Additionally, they prove that TSAM achieves a tighter generalization bound than SAM for modest $t$. Extensive experiments validate the effectiveness of the proposed method. Claims And Evidence: Yes. Methods And Evaluation Criteria: - In Alg. 1, at each training step, the method samples $s$ random perturbations via HMC algorithm (Alg. 3). This process requires one backpropagation to compute the gradient $\nabla L(\theta^i_j)$ for each $j$, resulting in a total of $s$ backpropagations. Additionally, updating $\theta_i$ requires another $s$ backpropagations to compute $\nabla L(\theta^i + \epsilon_j)$ for each $j$. In total, a single parameter update requires $2s$ backpropagations, leading to a high computational cost that may be unbearable. Theoretical Claims: Yes. Experimental Designs Or Analyses: - Some popular SAM variants, such as ASAM [1], GSAM [2], GAM [3], are not included as baselines in the experiments. - The experiments are primarily conducted on small-scale datasets. Larger-scale datasets, such as ImageNet, should be used to further validate the effectiveness of the proposed method. ----- [1] ASAM: Adaptive Sharpness-Aware Minimization for Scale-Invariant Learning of Deep Neural Networks, ICML 2021 [2] Surrogate Gap Minimization Improves Sharpness-Aware Training, ICLR 2022 [3] Gradient Norm Aware Minimization Seeks First-Order Flatness and Improves Generalization, CVPR 2023 Supplementary Material: Yes. Relation To Broader Scientific Literature: The proposed method contributes to the broader scientific literature by introducing the idea of leveraging exponential tilting to reweight local minima, thereby addressing the drawbacks of SAM. Essential References Not Discussed: No. Other Strengths And Weaknesses: Strengths - The idea of leveraging exponential tilting to reweight local minima is novel. - The paper provides a series of theoretical analyses to further validate the effectiveness of the proposed method. Other Comments Or Suggestions: - There are some typos. For example, the title should be corrected from "Reweighting Local Mimina with Tilted SAM" to "Reweighting Local Minima with Tilted SAM". Additionally, in line 26, the phrase "such algorithms (and its variants) that reply on one or few steps" should be "such algorithms (and its variants) that rely on one or few steps". Questions For Authors: Please see above. Code Of Conduct: Affirmed. Overall Recommendation: 2	Rebuttal 1: Rebuttal: We thank the reviewer for the time and valuable comments. We hope our response below can address the reviewer's concerns. [more experiment results] We appreciate the reviewer’s suggestions for adding more baselines. We have cited the papers mentioned by the reviewer in related work. We did not compare them in our original submission mainly because they are proposed to solve a SAM-like minimax style objective, where TSAM proposes a new objective function than SAM along with an algorithm to solve it. As plotted in Figures 3 and 4 in the appendix, even if we can solve the minimax SAM objective perfectly (in that particular toy problem, we did a brute-force search of the optimal parameters in the one-dimensional space), TSAM solutions still demonstrate more desirable properties than SAM solutions (more smooth). However, we agree more results will strengthen our experiments, and we compare with both GAM [3] and GSAM [2]. We leave out ASAM because GSAM achieves better performance than it (Figure 5 of the GSAM paper). For GSAM [2], we tune all the hyperparameters including the alpha parameter from a grid of {0.01, 0.02, 0.03} as suggested by the paper. The GAM algorithm [3] can be expensive as it requires to compute Hessian vector products. We implemented its non-expensive approximation, as explained in the GAM paper and actually implemented in its open-sourced code. Results are shown in the table below. We report the best performance of each baseline on each dataset. For instance, in noisy CIFAR100, both GSAM and GAM overfit to noise at the later stage of training and we apply early stopping to obtain the best test performance. \| Method \| CIFAR100 w/ WideResNet \| CIFAR100 w/ ResNet18 \| noisy CIFAR100 w/ ResNet18 \| noisy CIFAR100 w/ WideResNet \| DTD w/ ViT \| DTD w/ WideResNet \| \|----------\|-------------------------\|------------------------\|------------------------------\|-------------------------------\|------------\|--------------------\| \| SGD \| 73.22 \| 71.39 \| 61.01 \| 57.02 \| 66.38 \| 16.97 \| \| TSAM \| 80.85 \| 77.78 \| 69.98 \| 70.26 \| 68.82 \| 18.63 \| \| GSAM [2] \| 78.21 \| 77.95 \| 66.84 \| 70.35 \| 68.67 \| 18.13 \| \| GAM [3] \| 78.01 \| 77.55 \| 67.26 \| 65.32 \| 68.28 \| 17.97 \| [1] ASAM: Adaptive Sharpness-Aware Minimization for Scale-Invariant Learning of Deep Neural Networks, ICML 2021. [2] Surrogate Gap Minimization Improves Sharpness-Aware Training, ICLR 2022. [3] Gradient Norm Aware Minimization Seeks First-Order Flatness and Improves Generalization, CVPR 2023. [compute cost] We agree that TSAM requires more gradient evaluations per iteration, as discussed and acknowledged in the paper. However, we have evaluated TSAM and all the baselines with the same computational budget (Section 5), e.g., by letting baselines run 3$\times$ or 5$\times$ longer than TSAM, or optimizing for the inner max of SAM in a more fine-grained way using more gradient computation (ESAM2). We see that TSAM still outperforms those approaches on a variety of tasks and models. The trend still holds even if we further increase the runtime of ERM (SGD) or SAM. In addition, TSAM is inherently easy to parallelize since all the perturbations of model parameters are independent of each other. If we optimize our implementation by sampling perturbations in parallel, TSAM would incur the same per-iteration runtime as the vanilla SAM algorithm. [typos] Thanks for pointing out the typos in the submission. We will fix them in the next version.	Summary: Authors propose Tilted SAM (TSAM) that builds upon SAM in order to smooth out the optimization process using exponential tilting. Unlike SAM, which focuses on the worst-case loss within a neighborhood, TSAM reweights local solutions based on their loss values, favoring flatter minima. Authors claim that this makes TSAM easier to optimize and improves generalization performance across image and text tasks. They develop an algorithm using Hamiltonian Monte Carlo to efficiently estimate gradients for TSAM. Empirical results show that TSAM achieves better test performance and flatter minima compared to SAM and ERM. Claims And Evidence: There are several claims made in the paper which are well-supported, including that TSAM leads to flatter solutions by averaging over multiple perturbations. While TSAM is backed by strong theoretical analysis, the claim about TSAM achieving better generalization performance is still quite strong whereas the gap in performance seems marginal in most experiments. Authors also show that the smoothness introduced by TSAM reduces optimization difficulties, however, it still takes more time (at least 3x) to compute as compared to ERM and SAM. Methods And Evaluation Criteria: * Overall, the methodology is described clearly and backed by detailed analysis on several toy examples. * The authors propose sampling multiple $\epsilon$’s from a distribution to obtain an empirical gradient estimation, with the idea that the full gradient is a tilted average of the original gradient. While the idea is interesting, it introduces significant computational challenges, as efficiently sampling and computing gradients from this distribution can be resource-intensive and slow. Are there other techniques to avoid this issue? Theoretical Claims: The proposed method is well-grounded in theory (with proofs provided for major claims). Experimental Designs Or Analyses: - The experiments involve different types of datasets and models and TSAM shows marginal improvements in all the cases. - The additional analysis on hyper-parameters and ablations are quite insightful. Supplementary Material: - Overall, the provided implementation details are comprehensive and sufficient for ensuring reproducibility. - After looking at the runtime comparison, it is quite clear that the overhead involved in TSAM is quite significant. - Why would scheduling $t$ won’t have any effect on the performance? Can the authors elaborate on this? Relation To Broader Scientific Literature: The idea behind TSAM is to improve SAM by smoothing the optimization process using exponential tilting to prioritize higher-loss perturbations. This is related to several earlier works on flat minima for improved generalization. It also leverages Hamiltonian Monte Carlo (HMC) for efficient gradient estimation. TSAM extends ideas from average-perturbed sharpness and noise-perturbed loss techniques to improve generalization and optimization stability. Essential References Not Discussed: I think the literature review is sufficient, and the authors have effectively supported their ideas with relevant references and prior research. Other Strengths And Weaknesses: Please refer to my previous comments. Other Comments Or Suggestions: Please refer to my previous comments. Questions For Authors: Please refer to my previous comments. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We thank the reviewer for the time and valuable comments. [expensive computation] We would like to clarify that the runtime numbers in Table 5 are reported for the same number of iterations of all methods (to illustrate the per-iteration cost), while the final test performance in the experiment section (Section 5) is obtained by letting all methods run the same amount of wall-clock time. Across all datasets, we consistently observe that under the same runtime, TSAM outperforms other algorithms. In addition, TSAM is inherently easy to parallelize since all the perturbations of model parameters are independent of each other. If we optimize our practical implementation in this way, TSAM would incur the same per-iteration runtime as the vanilla SAM algorithm (consisting of one-step of gradient ascent and one step of gradient descent each iteration). [scheduling $t$] We note that scheduling $t$ with a fixed constraint set (defining the neighborhood of model parameters) does not change final performance significantly as long as we start from or end with the same values of $t$. When $t$ is zero, TSAM reduces to an average-perturbation-based sharpness-aware objective, which still accounts for some notions of sharpness of the loss surface. In the future, we plan to further investigate scheduling $t$ together with the radius parameter of the constraint set where it is possible to cover vanilla ERM with a mini-batch SGD optimizer. --- Rebuttal Comment 1.1: Comment: Thank you for clarifying my concerns. Based on the responses from the authors, I'll maintain my original score.	Summary: The authors propose TSAM, which is a version of SAM where, instead of taking a max over the loss around a point in parameter space during training, the authors propose to take a weighted average. Since the method is not tractable for weight functions, the authors develop an approximation by sampling. It is then shown that this leads indeed to (modest) gains in generalization performance. The authors also put some effort in theoretical analysis. Claims And Evidence: The claim that TSAM leads to flatter minima and better generalization peformance is well-supported by experiments and theoretical analysis. However, the gains in performance are very small and and not entirely consistent (see Table 1). Methods And Evaluation Criteria: The authors compare to several other methods and over a wide range of datasets. This part of the paper is sufficient. Theoretical Claims: While I did not follow all mathematical analysis in detail, the general methods and results seems to be in line with the existing literature. Experimental Designs Or Analyses: No. Supplementary Material: No. Relation To Broader Scientific Literature: The work presents an incremental improvement over SAM. Together with the theoretical foundations I think this is not a problem, however. Essential References Not Discussed: Some important papers in the field are not cited, especially Pittorino et. al: "Entropic gradient descent algorithms and wide flat minima ", which seems to have the same setup as the authors (see below). Other Strengths And Weaknesses: - I think the basic idea is novel and the execution in the paper is good. - The experiments are well done and wide-ranging, even though the results are not entirely convincing (see above) - The paper is well written - The theoretical aspect is well developed Other Comments Or Suggestions: I would suggest exploring different measures of flatness to make the work stronger. Questions For Authors: The central definition for TSAM (eq. 3) seems to be mathemetically equivalent to the local entropy in [1] (see first equation there and replace w' by w + epsilon), up to the choice of measure/distance function. The paper [1] has and the preceding work has some extensive analysis of this kind of setup and I think it would be good to relate these streams (just to be clear, the work in [1] is quite different after that basic definition, so there is no issue in being too similar, but at the same time it's clearly related and it is not cited/discussed). Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: We thank the reviewer for the time and positive assessment of our work! We would like to address the remaining questions/concerns as follows. [experimental improvements] We observe statistically significant improvements of TSAM compared with the baselines. In terms of the test loss, TSAM outperforms baselines by a large margin (Table 3 in Appendix C.3). Furthermore, as TSAM is a new objective function minimizing a weighted combination of bad losses, we can further improve the current algorithm by combining it with other optimization techniques such as applying the idea of variance reduction to obtain better estimated gradients, or incorporate adaptivity to precondition the estimated gradients. We leave more fine-grained exploration of solvers as future work. [other measures of sharpness and related work] Thanks for the suggestions and for pointing out the related work. In our work, we have explored two metrics of sharpnesses, as discussed in Section 5.2. The first sharpness measure (results visualized in Table 2) is closely related to the local entropy notion mentioned in the related work (Pittorino et. al.) and we agree the formulations are conceptually related as well. We will add discussions around the connections with Pittorino et. al. Our formulation is inspired by exponential tilting, which inherently has rich connections with different areas such as information theory, applied probability, and optimization [1]. We are certainly interested in developing other sharpness measures based on the properties of our objectives leveraging connections with prior works, and we will add discussions on this in the next version. [1] On Tilted Losses in Machine Learning: Theory and Applications, JMLR.	Summary: This paper proposes Tilted SAM (TSAM) as a smoothed version of SAM using exponential tilting. Its smoothness enbles an easier optimization and a better generalization. Claims And Evidence: All the claims are clear to me except one: "Empirically, TSAM arrives at flatter local minima and results in superior test performance than the baselines of SAM and ERM across a range of image and text tasks." It's not clear to me the connection between a flatter local minima and a superior test performance. It would be nice to refer to some papers or add explanation when it's first claimed. Methods And Evaluation Criteria: Yes. They use test accuracy for classification tasks and sharpness when comparing to ERM and SAM. Theoretical Claims: Yes, I checked theorem 3.6 in the main text. Experimental Designs Or Analyses: Yes. I checked all of their experiments. I have a question on one experiment in appendix: In figure 7, the CIFAR100 test accuracy of t=20 seems still increasing . What happens after 200 epochs? Supplementary Material: Yes, Appendix A B.1, and C. Relation To Broader Scientific Literature: This paper propose applies exponential tilting to smooth SAM, which is a novel combination. Essential References Not Discussed: See "Claims And Evidence" Other Strengths And Weaknesses: Strengths: The theoretical part is solid. Weakness: [limited impact] According to Table 5, the running time of TSAM of cifar100 is 10 times larger than running ERM and 5 times larger than SAM. Meanwhile, the improvement by TSAM is not significant (~1-2%) as shown in table1 for various tasks. Other Comments Or Suggestions: NA Questions For Authors: Do you have insights on why the algorithm still works even with N=1 and "accept the generated ϵwith probability 1"? Code Of Conduct: Affirmed. Overall Recommendation: 2	Rebuttal 1: Rebuttal: We thank the reviewer for the time and valuable feedback. [connections between flat local minima and improved generalization] Note that we do not intend to claim ‘flat local minima leads to a better generalization in all cases’ by claiming “TSAM arrives at flatter local minima and results in superior test performance…” The exact relations between the two for deep learning is still an open question, as pointed out in our submission citing several related works (Section 2). Our study is partly motivated by the empirical success of a series of SAM works under which sharpness of local minima is significantly reduced (under various notions of sharpness), and we aim to develop a better formulation along this line by considering and reweighting multiple local minima in a principled framework. We will further clarify this in the next version. [runtime of TSAM] We agree that TSAM requires more gradient evaluations per iteration, as discussed and acknowledged in the paper. However, we have evaluated TSAM and all the baselines with the same computational budget (Section 5), e.g., by letting baselines run 3$\times$ or 5$\times$ longer than TSAM, or optimizing for the inner max of SAM in a more complicated way with more gradient computation (ESAM2). We see that TSAM still outperforms those approaches on a variety of tasks and models. The trend still holds even if we further increase the runtime of ERM (SGD) or SAM. In addition, TSAM is inherently easy to parallelize since all the perturbations of model parameters are independent of each other. If we optimize our implementation in this way, TSAM would incur the same per-iteration runtime as the vanilla SAM algorithm. [other questions] (a) The performance of both TSAM and SAM would improve very slightly after 200 epochs, but TSAM still outperforms SAM. (b) When $N=1$, we are running gradient ascent once to locate the regions with (relatively) large losses, where the first-order gradient information serves as a strong signal to guide the areas to sample from. Additionally, the gap between losses can be magnified by using a large value of $t$ during reweighting. We will explain the intuition in more detail in the next version. --- Rebuttal Comment 1.1: Comment: Thank you for your replies. However, we have evaluated TSAM and all the baselines with the same computational budget (Section 5), e.g., by letting baselines run 3 or 5 longer than TSAM Could you point out in which table/figure you run ERM or other baselines longer than TSAM? Also I notice in section 5, you mentioned that Despite the existence of adaptive methods for SGD and SAM (Kingma & Ba, 2014; Kwon et al., 2021), we do not use adaptivity for any algorithm for a fair comparison. Does it mean that in all the ERM results, the SGD was used instead of Adam/AdamW? --- Reply to Comment 1.1.1: Comment: We thank the reviewer for the time and additional questions. In almost all numbers presented in our main result, we use the same computation budget for the baselines and TSAM. For instance, in Table 1 on both image and text data, except for SAM that runs the same number of iterations as TSAM, all other baselines (ESAM1, ESAM2, PGN, RSAM) use the same number of gradient evaluations as TSAM. ESAM1 refers to SAM running longer. We explained the protocol in Section 5.1, and will further clarify this in the next version. Yes, we use SGD instead of adaptive optimizers for ERM for a fair comparison, which is also a standard baseline in prior SAM related works [e.g., 1,2,3]. If we use adaptive optimizers to solve ERM, we would need to incorporate adaptivity into all methods for solving SAM and TSAM as well, which the current baselines (e.g., PGN, RSAM) and the TSAM algorithm do not account for. [1] Kwon et al., ASAM: Adaptive Sharpness-Aware Minimization for Scale-Invariant Learning of Deep Neural Networks. [2] Liu et al., Random Sharpness-Aware Minimization. [3] Foret et al., Sharpness-Aware Minimization for Efficiently Improving Generalization.	null	null	null	null	null	null
Vision-Language Model Selection and Reuse for Downstream Adaptation	Accept (poster)	Summary: The paper deals with Model Label Learning (MLL) to select and reuse pre-trained VLMs for specific downstream tasks. It addresses the challenge of choosing the best VLMs from numerous options, each with varying performance on different tasks and different classes. The MLL approach includes model labeling, selection, and reuse, utilizing a predefined concept pool to bridge the understanding of those concepts from candidate VLMs and target tasks. Claims And Evidence: 1. The contribution of this work appears to be weak. The so-called "new benchmark" is not a separate contribution, as it is inherently tied to the task or paradigm presented. Therefore, they should be considered a single contribution rather than two distinct ones. 2. The validation and analysis provided in the paper are weak (see Experimental Designs Or Analyses). Additionally, the improvements demonstrated by the proposed model are limited: In the best set of experiments (0.6639, k=3), the author proposed method outperformed the comparison method in only half of the downstream tasks. This raises concerns about the effectiveness of the proposed model selection method. Methods And Evaluation Criteria: The process of constructing the reference dataset, profiling the target dataset, and conducting multi-model inference, replying on a combination of language generation models, embedding models, and similarity computation, is complex and time-consuming. As can be seen in Tab.2, a suboptimal choice of k can lead to a decline in results. Plus the details of this experiment are missing, it is important to question how robust the selection of k=3 is across 17 different downstream tasks. If the value of k is uncertain unless given a validation split, it becomes challenging to demonstrate how effective the procedures could be in practical applications. Theoretical Claims: The proposed method is straightforward and, for the most part, clearly explained. Two minor suggestions: 1. The logic from eq6 to eq7 is hard to follow. 2. \mathcal{T}_m(D) should be \mathcal{T}_m(d) in eq2. Experimental Designs Or Analyses: The submission has not been well validated, and analysis is weak and not insightful enough. Besides above mentioned weakness, 1. important baselines are missing. For example, since ensemble typically enhances performance and random sampling can ensure diversity in recognizing different classes, it is crucial to conduct random ensemble with majority voting / prob. distribution average / etc as ablation study, other than the parameter analysis presented in Section 5.3. 2. how do the randomly selection reference images affect the robustness of the proposed method? 3. how do specific downstream tasks correlate with different model candidates? For example, why does the method show significant improvement on datasets DMLab, RESISC45 and FER2013, while performing at a comparable level on other datasets? Supplementary Material: I've reviewed the 2-page appendix. Relation To Broader Scientific Literature: The proposed method, while simple and straightforward, lacks convincing validation and practical applicability. The method's effectiveness is limited even after model ensemble. It also raises important questions about the robustness and practicality of its approach, especially considering the complexity and uncertainty involved in key processes like target benchmark profiling, model selection and dataset correspondence. These factors suggest that while the paper addresses a relevant and meaningful task, its contributions may not significantly advance the field without further validation and refinement. Essential References Not Discussed: Given that the authors present the proposed paradigm as one of their main contribution, it is essential to thoroughly evaluate its effectiveness compared to other training-free methods for VLMs, such as but not limited to test-time adaptation. Other Strengths And Weaknesses: While the importance of the task is acknowledged, the presented method has not been convincingly validated and appears to be impractical. Other Comments Or Suggestions: Please see comments above. Questions For Authors: How is X_v determined for each v that is randomly collected? Is there a one-to-one correspondence for each v, as defined by WordNet, across all 5 datasets? Code Of Conduct: Affirmed. Overall Recommendation: 2		Summary: This paper presents a framework for organizing models that facilitates the storage, labeling, and reuse of vision-language models (VLMs). This system enhances overall performance compared to using a single VLM. A model labeling process is introduced to precisely describe the functionality of each VLM, enabling subsequent identification and reuse. The authors propose a comprehensive benchmark involving 49 VLMs and 17 target tasks to evaluate and demonstrate the effectiveness of the proposed method. Claims And Evidence: The authors claim that improved performance can be achieved with the proposed model organization framework because different Vision-Language Models (VLMs) have their own advantages in handling various models, and the proposed method can fully utilize these advantages. The experiments conducted in this paper have thoroughly demonstrated the authors' claim. They not only show that the proposed method achieves better overall performance on 17 tasks but also indicate that as the number of models increases, the overall performance can further improve. Methods And Evaluation Criteria: The proposed method seems to be work. To evaluate the performance of the method, the authors introduce a semantic graph with labels and corresponding images to pre-test the performance of each model. Subsequently, when reusing each model, the authors propose a model identification strategy to locate each model in an embedding space and ensemble models for subsequent tasks. The overall framework has potential to demonstrate the effectiveness of a collection of models. The benchmark and evaluation in this paper are valid and can reflect the performance of each method. Theoretical Claims: N/A Experimental Designs Or Analyses: Both the experimental design and analyses are comprehensive. The experiments are conducted on multiple datasets with up-to-date comparison methods. Moreover, the authors give scalability and ablation studies to further demonstrate the effectiveness of proposed methods. Supplementary Material: The supplementary material includes the code associated with this paper, which is satisfactory. Relation To Broader Scientific Literature: The method presented in this paper is significant, as it can be utilized to manage existing Vision-Language Models (VLMs) to address new downstream tasks with improved performance, rather than constructing new VLMs, which is costly. These techniques can assist platforms like HuggingFace in better organizing models. Essential References Not Discussed: No necessary reference is omitted. Other Strengths And Weaknesses: Strengths: 1. The problem addressed in this paper is significant and intriguing. Managing large Vision-Language Models (VLMs) in the model hub is crucial because training new models for new downstream tasks is costly, whereas existing models can be utilized to handle these tasks. 2. The proposed method is logical, as the pipeline of pre-testing, model identification, and model reuse appears effective. With a more comprehensive semantic graph and an increased number of models in the model hub, this method can achieve better performance. 3. The experiments in this paper are thorough. The authors have developed a benchmark with 49 VLMs and 17 tasks, which thoroughly evaluates the performance of each method. The proposed method achieves the best overall performance, demonstrating the effectiveness of the proposed framework. Weakness: The primary limitation of this paper is that the model hub is not sufficiently large to fully enhance the effectiveness of the proposed method. Nevertheless, I believe the current benchmark is adequate to assess the effectiveness of each method and demonstrate the proposal's effectiveness. In this context, I do not perceive any significant weaknesses in the paper. Other Comments Or Suggestions: Please see the strengths and weaknesses above. Questions For Authors: - Have you made the computational cost analysis for the proposed method? Is the proposed method more efficient or slower than the previous works? Code Of Conduct: Affirmed. Overall Recommendation: 4		Summary: The paper explores a practical VLM reuse problem and proposes Model Label Learning (MLL), an efficient approach for selecting and reusing pre-trained Vision-Language Models (VLMs) for downstream tasks. The framework comprises three modules: (1) Model Labeling, which assigns labels to VLMs based on their capabilities; (2) Model Selection, which matches these labels to task requirements; and (3) Model Reuse, which employs an ensemble of selected models. Additionally, a large-scale benchmark, including 49 VLMs and 17 datasets, is introduced to evaluate MLL’s effectiveness. Experimental results demonstrate its promising scalability and performance. Claims And Evidence: The paper claims that the performance of VLMs can vary significantly depending on the dataset domain. To support this claim, the authors conduct extensive experiments, as shown in Figure 1. Specifically, Figure 1(a) illustrates that VLMs exhibit different strengths across various visual tasks, with no single model consistently outperforming all others across every task. Figure 1(b) demonstrates that even within the same task, different VLMs achieve varying levels of performance across specific classes. Methods And Evaluation Criteria: To achieve effective reuse of VLMs, the paper proposes Model Label Learning (MLL), an efficient approach for selecting and reusing pre-trained Vision-Language Models (VLMs) for downstream tasks. Specifically, the framework consists of three modules: (1) Model Labeling, which assigns labels to VLMs based on their capabilities; (2) Model Selection, which matches these labels to task requirements; and (3) Model Reuse, which employs an ensemble of selected models. The proposed framework is reasonable for addressing this problem. Additionally, a large-scale benchmark, including 49 VLMs and 17 datasets, is introduced to evaluate the effectiveness of MLL. Theoretical Claims: NA Experimental Designs Or Analyses: The paper presents comprehensive experiments involving 49 VLMs and 17 target task datasets, along with sufficient analysis. The experimental results demonstrate the effectiveness of the proposed method in selecting and reusing VLMs. In addition to the experiments mentioned above, the authors should provide more experimental results to further validate the proposed method. For example, for each target dataset, the highest performance achieved by any model in the model hub should be included as a reference. This would help assess the effectiveness of the proposed method in selecting models. Supplementary Material: The supplementary material provides detailed information about the proposed benchmark, including the datasets used, along with their domain and task specifications. It also includes model-related details, such as architecture, pre-trained datasets, and other relevant information. Relation To Broader Scientific Literature: Unlike other VLM studies, this paper explores a practical VLM reuse problem, aiming to effectively reuse existing models to improve performance on target datasets. Essential References Not Discussed: NA Other Strengths And Weaknesses: The main strength of this work is that the problem it explores is both practical and meaningful. Additionally, it demonstrates good scalability, as the use of a semantic graph enables MLL to expand as new models or tasks are added, making it adaptable to diverse visual tasks. The main weakness is that more experimental results should be provided. Please refer to Experimental Designs Or Analyses for details. Other Comments Or Suggestions: In addition to VLMs for image classification tasks, more VLM studies have explored dense-level recognition tasks, such as detection and segmentation. The authors could consider incorporating more types of VLMs into the proposed framework, enabling it to handle a wider range of tasks. Questions For Authors: Please refer to above sections for details. Code Of Conduct: Affirmed. Overall Recommendation: 3		Summary: This paper introduces Model Label Learning (MLL) for selecting and reusing pre-trained VLMs for downstream tasks. This method aims to address the challenge of choosing the best VLM from a growing hub, given their diverse performance across tasks and primarily it is impractical to evaluate them exhaustively. The core idea of MLL is to assign "model labels" to each VLM, describing its capabilities based on pre-testing on a semantic graph of visual concepts. MLL then utilizes these labels to efficiently select and reuse VLMs for new tasks by semantically matching task requirements to model labels. The MLL paradigm consists of three modules: model labeling (pre-testing VLMs on a semantic graph and creating labels), model selection (matching task descriptions to model labels for VLM selection), and model reuse (ensembling selected VLMs). In addition, the authors introduce a new benchmark for VLM selection, comprising 49 VLMs and 17 downstream datasets. Experimental results on this benchmark show the effectiveness of MLL compared to baselines like ImageNet Baseline (INB) and ModelGPT, demonstrating improvement in zero-shot downstream tasks. ## update after rebuttal My questions have been addressed by the rebuttal and I have thus increased my score. Claims And Evidence: ### C1: MLL is effective for selecting and reusing VLMs for downstream tasks, leading to improved performance. - E1: Tables 1 and 2 show improved average accuracy and F1-score compared to INB and ModelGPT across 17 downstream tasks for both single model (k=1) and ensemble (k=3) settings. This provides initial evidence. Then, Table 3, 4 demonstrate the robustness to hyper-parameters. - P1: I think this claim might be strengthened by including statistical significance test. It would help determine whether the average improvement across 17 datasets (1.86% over INB, 2.53% over ModelGPT) represents a meaningful pattern. ### C2: MLL is computationally efficient in the model selection process. - E2: The paper states that model labeling is target task independent and pre-computed, making the selection process efficient. This is a design feature suggesting methodology efficiency. - P2: However, empirical evidence of the actual computational time for model selection and comparison to baselines is not provided (although Table 4 hints at interface time costs). The cost of labeling stage itself is not quantified. ### C3: MLL is scalable as the model hub grows. - E3: Figure 3 shows that average performance generally increases as the number of VLMs in the hub grows, suggesting scalability. - P3: The rate of performance improvement with hub size and the saturation point are not fully explored. The computational cost of maintaining and updating model labels as the hub grows is not discussed. Moreover, the experiment in Figure 3 is based on random expansion, which might not fully reflect real-world hub growth scenarios, such as chronological additions based on when models are published, preferential inclusion of higher-performing models first, or somehow strategic additions based on identified performance gaps. I personally think that the random expansion approach does not capture these realistic growth patterns, this likely matters because the order in which models are added could significantly affect the performance improvement curve. For instance, if high-performing models happen to be added early in many random schemes, this could show rapid initial improvements that might not be achievable in practice. In brief, the claims made are initially supported by the presented data, but it is better to be strengthened with more empirical evidence, statistical validation, and more detailed analyses of costs and scalability. Methods And Evaluation Criteria: The proposed methods and evaluation criteria are generally sensible and appropriate for the problem of VLM selection and reuse. The MLL method with its three modules is a logical approach to address the VLM selection problem. Semantic labeling provides a structuredway to understand VLM capabilities without task-specific evaluation. Semantic matching for selection is an efficient alternative to exhaustive search. Ensemble reuse leverages the strengths of multiple selected models. The introduced benchmark of 49 VLMs and 17 downstream datasets is a strong evaluation criterion, covering a range of domains and tasks relevant to VLMs. The authors propose to use accuracy and F1-score, which are standard metrics for the evaluated tasks. Comparison against INB and ModelGPT provides relevant baselines. Theoretical Claims: There are no explicit theoretical claims made in the submission excerpt that require proof checking. The paper is primarily methodologically and empirically driven. Claims of efficiency and scalability are based on the design of the method and empirical observations, not formal theoretical derivations. Experimental Designs Or Analyses: The experimental designs and analyses are sound in principle but require more detailed reporting and validation. #### Soundness Using INB and ModelGPT as baselines is appropriate and allows for comparison to a simple baseline and a relevant existing VLM selection method. The use of a diverse benchmark is a strength. The ablation studies on $\alpha$ (table 3) and model count $k$ (table 4) demonstrate an effort to understand the impact of key hyperparameters and design choices. #### Issues and areas for improvements: 1. statistical significance: as aforementioned, this submission lacks mention of significance test to validate the observed performance differences. 2. more detailed result: while average performance is reported, the readers might also wonder: are the improvements consistent across all datasets? Also, are there specific datasets or task types where MLL excels or underperforms? 3. computational cost: the analysis of the cost of model labeling should also be reported. Supplementary Material: I appreciate that the authors provide their source code in the supplementary material is source code. I did not run the code. Relation To Broader Scientific Literature: This paper appears to be relating to three research areas: VLM: The paper directly relates to a challenge in VLMs - how to efficiently and effectively utilize the increasing number of pre-trained models. Model Selection: The paper also relates to literature on model selection, particularly for pre-trained models. It acknowledges and contrasts with existing methods like NCE, LEEP, LogME, and ModelGPT. Learnware/Model Hubs: The paper explicitly connects to the "learnware" paradigm and the concept of model hubs. It builds upon the idea of model specification and efficient model selection in heterogeneous model repositories. MLL can be viewed as a specific instantiation of learnware principles tailored for VLMs. Essential References Not Discussed: Primarily I don't think there are significant missing of essential literature; however, to strengthen the literature context and ensure comprehensiveness, the authors might consider discussing and citing works in the following more specific areas: - semantic similarity measures: as MLL relies on semantic similarity measure for comparing captions, discussing relevant papers on semantic textual similarity and different metrics would be beneficial. - ensemble methods for VLMs: If the ensemble reuse module could be extended to more ensembling techniques, making a discussion on relevant works on ensemble methods, would also be important. Other Strengths And Weaknesses: I summarize the strengths and weaknesses I identified below. They may overlap with the previously discussed points: ### strengths 1. The paper addresses a practical problem that will become increasingly important as more pre-trained VLMs become available. 2. The MLL method is conceptually simple, with clearly separated components for labeling, selection, and reuse. 3. The approach is computationally efficient for users, as the potentially expensive model labeling process occurs only once when models are added to the hub 4. The benchmark will be valuable for future research in VLM selection ### Weaknesses: 1. The approach depends heavily on the the quality of the constructed semantic graph, but the graph construction process isn't explored in depth. 2. The computational overhead of the model labeling process itself isn't thoroughly discussed, which could be significant for large models 3. More empirical results (e.g., statistical significance tests) should be reported as well. 4. Analysis of failure cases where MLL does not perform very well would also be meaningful. Other Comments Or Suggestions: I have no more comments except for the existing sections. Questions For Authors: 1. how sensitive is the approach to the choice of nodes in the semantic graph, and would a different semantic graph graph construction lead to significantly different results? 2. What is the computational overhead of the model labeling process, particularly for large models? 3. How would the framework handle non-classification tasks? 4. The entropy-based ensemble weighting scheme is relevant to model overconfidence, but have you explored other weighting strategies? Code Of Conduct: Affirmed. Overall Recommendation: 4		null	null	null	null	null	null
Collapse or Thrive: Perils and Promises of Synthetic Data in a Self-Generating World	Accept (poster)	Summary: This paper investigates model collapse under different data regimes: 1) when we train the model on the latest synthetic data (the setting used in Shumailov et al.) 2) when we accumulate the synthetic data at each iteration (keeping the original data in the first iteration) 3) when we accumulate and subsample to obtain a fixed dataset size at each iteration. The authors show that in 2) the test losses do not diverge, and in 3), the test losses do not diverge or the divergence is slow. Another contribution is the investigation of the importance of the size of the real data vs its proportion in the training set. Update after rebuttal: I keep my rating of 3. Claims And Evidence: All the claims are validated with experiments, and some of them with theory. The empirical evidence encompasses three data settings: 1) multivariate gaussian modeling 2) kernel density estimation 3) SFT of LLMs The theroretical evidence encompasses the univariate gaussian modeling setting (accumulate workflow), KDE (replace and accumulate workflow). However, no result is given for the accumulate + subsample setting. Methods And Evaluation Criteria: The datasets choice mimicks the one adopted in Shumailov et al. The gaussian modeling and KDE experiments feel more like sanity checks (for which some theoretical results can be proven) than realistic settings where model collapse might appear. Theoretical Claims: Yes, no issue. Experimental Designs Or Analyses: Yes, no issue. Supplementary Material: I read the appendix. Relation To Broader Scientific Literature: In the first part of the paper, the objective of the analysis is to extend some insights which were given in Gerstgrasser et al. ([1]) (namely that the accumulate workflow might not lead to divergence) to the experimental setup used in Shumailov et al. ([2]). Section 4 looks at the importance of the cardinality of the real data vs its proportion. This section is empirical, but previous theoretical results in [3] shared common insights on the potential benefits of synthetic data up to a certain point, when real data is scarce. Another important reference is [4] which also studies model training on real and synthetic data (with the slight difference that there is no accumulation in [4], as the synthetic data from the latest iteration is mixed with the real data). [1] Gerstgrasser, M., Schaeffer, R., Dey, A., Rafailov, R., Korbak, T., Sleight, H., Agrawal, R., Hughes, J., Pai, D. B., Gromov, A., Roberts, D., Yang, D., Donoho, D. L., and Koyejo, S. Is model collapse inevitable? breaking the curse of recursion by accumulating real and synthetic data, 2024. [2] Shumailov, I., Shumaylov, Z., Zhao, Y., Papernot, N., Anderson, R., and Gal, Y. Ai models collapse when trained on recursively generated data. Nature. [3] Dohmatob, E., Feng, Y., Yang, P., Charton, F., and Kempe, J. A tale of tails: Model collapse as a change of scaling laws. In Forty-first International Conference on Machine Learning, 2024. [4] Bertrand, Q., Bose, A. J., Duplessis, A., Jiralerspong, M.,and Gidel, G. On the stability of iterative retraining of generative models on their own data. The Twelfth International Conference on Learning Representations, 2024. Essential References Not Discussed: Most of the works related to this paper are cited, but the related work section in the appendix could be improved to make the objective and distinctness of each work more clear, namely the experimental setup considered (how is the synthetic data mixed with real data) and the theoretical results. Other Strengths And Weaknesses: The paper is well-written and easy to follow. Other Comments Or Suggestions: NA Questions For Authors: Do the authors have some intuition on possible preliminary theoretical results for the accumulate-subsample workflow, even in a very simplified setup? Could the authors be more clear on how the theoretical results in Dohmatob et al. differ from the insights shown (experimentally) in Section 4? Can the authors provide results for a more realistic setting than the one used the gaussian and kde experiments. The SFT one conducted in the paper is a good example of realistic scenario. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Thank you for your thoughtful review and recommendation. We appreciate your recognition that our paper is well-written and that our claims are properly validated. ### Theoretical Results for Accumulate-Subsample You raise an excellent question. The accumulate-subsample workflow presents significant analytical challenges because of subsampling the data at each model-fitting iteration. We welcome any suggestions you might have for tackling this theoretical challenge, as we believe it represents an important open problem for the field. ### Clarification of Relationship to Dohmatob et al. in Section 4 > Could the authors be more clear on how the theoretical results in Dohmatob et al. differ from the insights shown (experimentally) in Section 4? Dohmatob et al. 2024 show in Corollary 3.3 that in a simplified mathematical setting, the test error on real data scales as $(T_{real} + T_{AI})^{-(1 - 1/\beta)} + k^{-(\beta -1)}$. This means that in this setting, AI-generated data can help improve performance. Directly comparing our empirical results to their theoretical results is difficult because our generative models differ. Additionally, their result decouples the amount of data $T_{real} , T_{AI}$ from the tail cutoff $k$, whereas decoupling these two factors in real data would be difficult (and potentially not possible). We see our results as complementary, but different, and want to give appropriate credit to prior work. We will clarify these distinctions in the revised paper. ### Realistic Settings > Can the authors provide results for a more realistic setting than the one used in the gaussian and kde experiments. The SFT one conducted in the paper is a good example of realistic scenario. We appreciate this feedback. To explain why we used these classical statistical models, at least three previous papers have studied multivariate Gaussians, making this setting crucial for consistent comparison against their results. These settings offer analytical tractability for theoretical results while still demonstrating the key phenomena. We’d also like to highlight that our paper contains results from pretraining sequences of language models on real text (TinyStories), as shown in Figure 4. Could you please clarify what "realistic" properties you're looking for that our current experiments don't address? Is it a matter of the particular generative model? If so, what model and data combination would you like us to run experiments for? We'd be happy to expand the language model experiments with additional details in the revision or to conduct new experiments if you have specific suggestions. --- Rebuttal Comment 1.1: Comment: Thank you for your rebuttals and for your clarification regarding Dohmatob et al. Regarding the more realistic settings, I was thinking about a tabular setting (for example UCI datasets), and some commonly used model (eg. TabDDPM, CTGAN, TVAE,...) --- Reply to Comment 1.1.1: Comment: Thanks for the suggestion! We investigated the code base and found that TabDDPM’s code base is currently broken (19 open issues) and we were unable to fix it on short notice to run this experiment. Though we appreciate your suggestion, we would like to point out several things: - We include two "realistic” settings already (pre-training and SFT), which have recently generated great excitement surrounding the use of synthetic data [1,2]. - Pre-training is run on 4 different models across 3 different collapse paradigms. - The SFT experiments also include 3 models with 3 seeds across 3 different model collapse paradigms. - The paper also contains 3 sets of statistical experiments (again with 3 settings and 3 seeds each) replete with proofs of asymptotic behavior. We do not know of any other model collapse papers on language models that run experiments that are this extensive. We apologize for being unable to run TabDDPM experiments on short notice, but we hope you’ll understand that our paper already excels when it comes to the breadth and thoroughness of its experiments, both ``realistic” and theoretical. [1] https://arxiv.org/abs/2409.07431 [2] https://arxiv.org/pdf/2501.19393	Summary: This paper examines the phenomenon of model collapse in generative learning, where models are trained on data that includes synthetic generations from previous iterations. The authors investigate three training paradigms - Replace, Accumulate, and Accumulate-Subsample - and find that Replace leads to model collapse, Accumulate prevents it, and Accumulate-Subsample slows degradation but does not fully eliminate it. The paper provides empirical evidence across multiple generative model settings including multivariate Gaussian estimation, kernel estimation and language model fine tuning. Claims And Evidence: main claims: - Replace leads to model collapse, where test loss diverges across iterations. This is demonstrated in multivariate Gaussian modeling, kernel density estimation (KDE), and language model fine-tuning experiments. - Accumulate prevents collapse, as models trained on both real and synthetic data remain stable. - Accumulate-Subsample reduces but does not eliminate degradation, acting as a middle ground between Replace and Accumulate. Issues: - The paper presents accumulate-subsample as a new paradigm, but prior work (e.g., Dohmatob et al. 2024, Bertrand et al. 2024) already studied real-vs-synthetic data trade-offs in iterative training. - The paper claims that synthetic data can improve performance in some settings, but this was already explored in Dohmatob et al. (2024) and Seddik et al. (2024). - Definition of Model Collapse: The paper presents collapse as "test loss divergence", ignoring alternative definitions such as scaling law deviations (Dohmatob 2024), loss of rare modes (Shumailov 2024), and knowledge degradation (Peterson 2024). Methods And Evaluation Criteria: Although the experimental setup is well-structured, with multiple model classes tested across generative settings, but the experiments focus on data quantity (real vs. synthetic ratios) but ignore data quality. This is an important step which is ignored. Evaluation criteria are relevant but incomplete, as long-term performance degradation is not analyzed rigorously beyond several iterations specifically for LLMs experiments. Theoretical Claims: Theoretical results are only for Gaussian and KDE models. No theoretical proof for why Accumulate-Subsample prevents full collapse. And prior work by Bertrand et al. (2024) already provided mathematical stability conditions for iterative training on synthetic data. Experimental Designs Or Analyses: The main issues I see with the experiments is that: - The paper does not analyze synthetic data quality or filtering, which are key considerations in real-world. For example most text that enters the internet does have some human evaluation on top of it. So I think all the setups in the paper are to some extend unrealistic. - There is no long-term stability analysis, making it unclear how performance evolves after many more iterations. Supplementary Material: Please move the related work section to the main text. Relation To Broader Scientific Literature: - The paper overstates its originality and does not fully acknowledge prior research on model collapse. - A more comprehensive literature review is needed to position the contributions in relation to existing studies. Essential References Not Discussed: The paper does discuss and cite many of the relavent work but I believe it does not do just in citing the previous findings. Other Strengths And Weaknesses: - The main contributions lack novelty relative to prior work. - The definition of model collapse is too narrow. - The paper does not address synthetic data filtering or quality. Other Comments Or Suggestions: See below. Questions For Authors: 1 - How does this work differ from Dohmatob et al. (2024), which already studied real-vs-synthetic data trade-offs? 2 - Why does the paper not discuss alternative definitions of model collapse (e.g., rare mode loss, scaling law deviations)? 3 - Can the authors justify why accumulate-subsample prevents collapse beyond empirical results? Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: ### Definitions of Model Collapse You raise an excellent point. A recent review (https://arxiv.org/abs/2503.03150) identifies multiple definitions of model collapse. We focused on test loss divergence as it addresses an existential threat: all future generative models becoming useless. We'll expand our discussion to acknowledge alternative definitions and clarify our specific focus. ### Novelty in Accumulate-Subsample Paradigm We appreciate the opportunity to clarify what distinguishes our work from prior research: 1. Practical Framing: We specifically examine accumulate-subsample through fixed compute per model-fitting iteration, which directly models real-world ML development constraints. This framing is absent from the papers cited but is absolutely critical. One can study all manner of different workflows for data, but their importance depends on how closely they model the real world. 2. Training Methodology: Bertrand et al. (2024) studies _iterative retraining_, where each model is initialized from the previous model and each optimizer is initialized from the previous model’s optimizer state. The iterative retraining approach in Bertrand et al. mitigates model collapse because models are constrained from wandering too far from their predecessors. However, this doesn't reflect how frontier models are developed in practice. In comparison, we model the scenario where successive model generations are trained independently. 3. Data Evolution: We consider synthetic data accumulation across multiple model generations, whereas prior work typically only considers synthetic data from the most recently trained model e.g., Bertrand & Alemohammad. We will improve our manuscript to clarify. ### Related Work > How does this work differ from Dohmatob et al. (2024), which already studied real-vs-synthetic data trade-offs? Our work differs substantially from both Dohmatob papers. One examines linear regression specifically, while the other investigates scaling laws. Both are largely theoretical. In contrast, our work is more empirical and spans multiple generative paradigms (Gaussian modeling, KDE, language model fine-tuning) and examines different data treatment workflows across these diverse settings. > Please move the related work section to the main text. If accepted, we will move Related Work into the main text after the Introduction. We placed it in the Appendix due to the 8-page limit. We will expand our related work to include additional relevant papers discovered during the review process e.g., Gillman et al. 2024 and better clarify the positioning of our contributions. ### Understanding Accumulate-Subsample > Can the authors justify why accumulate-subsample prevents collapse beyond empirical results? The accumulate-subsample setting is difficult to study analytically and we were not able to prove satisfactory results. Intuitively, accumulate-subsample slows collapse because each new training batch contains a fraction of real data that provides an "anchor" to the true distribution. ### Benefits of Synthetic Data Our contribution isn't showing that synthetic data can help performance - we agree this possibility is well-known across many papers. Rather, one contribution is that such a result holds for kernel density estimation - a simple yet fundamental statistical model - without sophisticated data manipulations. Another contribution is assessing the role of cardinality or proportionality of synthetic data , which to our knowledge was previously unexplored. Upon careful review of Seddik et al. (2024), we couldn't find where they demonstrate synthetic data improves performance. ### Realistic Data Quality Our experimental design deliberately aimed to model how synthetic data proliferates on the internet in practice: - Content on the internet is not systematically filtered. Vast amounts of web data is garbage, spam, AI-generated slop, etc. - By studying the "pessimistic" scenario without filtering, we establish a baseline understanding of collapse dynamics. Filtering can only improve the quality of models. - That said, we agree data quality is an important factor, and we view our work as complementary to research on data quality research. Indeed, we write "Our experiments take a pessimistic viewpoint, in the sense that our experiments pay no attention to the quality of data, whereas in practice, engineers heavily filter data based on various indicators of data quality, e.g., (Brown et al., 2020; Lee et al., 2023; Wettig et al., 2024; Penedo et al., 2024; Li et al., 2024b; Sachdeva et al., 2024); for a recent review, see Albalak et al. (2024)." > There is no long-term stability analysis, making it unclear how performance evolves after many more iterations. We ran most experiments for 100 iterations across most settings. Running language modeling pretraining for longer proved beyond our limited compute budget. We're open to extending our experiments.	Summary: The paper investigates model collapse (a phenomenon observed when generative models are trained with output generated from such models) in 3 different settings (replace, accumulate, and accumulate-subsample). They find that model collapse occurs in the replace and the accumulate-subsample setting (but slower). They do not observe model collapse in the last setting (accumulate). Additionally, they investigate how the portion of real and synthetic data in a dataset influences model performance in a supervised fine-tuning regime. ## Update after rebuttal: ## I would like to thank the authors for their response. However, my concerns about novelty have not been lifted and some of my questions have not been addressed. Therefore, I will keep my initial score. Claims And Evidence: The claims of the paper (see summary) are supported by a wide range of experiments and in some cases theoretical analyses. The experiments are convincing and support the claims. I do not agree with the authors that model collapse is avoided in the accumulate-subsample case (judging from their experimental data) but rather slowed down. Methods And Evaluation Criteria: The authors evaluate their claims for multivariate gaussian models, kernel density estimation, and supervised fine-tuning of language models for the replace and accumulate setting. They also provide theoretical insights in those cases. For the accumulate-subsample setting, they provide experiments for the 3 aforementioned cases as well as linear regression and pretraining language models. For the last part (section 4) experiments for supervised fine-tuning are presented. Theoretical Claims: Theoretical results are provided for the results in section 2. I did not check the detailed proof in the appendix for correctness. Experimental Designs Or Analyses: The experimental design seems to be extensive and convincing. Supplementary Material: I did check the supplementary material; however, I did not go through the full proof in the appendix. Relation To Broader Scientific Literature: - My biggest concern with the paper is its novelty. It builds heavily on Gerstgrasser et al. and section 2 (a large part of the paper) only provides new results for different kinds of generative models with equal conclusions. The second part of the paper (accumulate-subsample) provides empirical insights that mixing real and generated data slows down model collapse. This has been observed and discussed in literature as early as Bertrand et al., Alemohammad et al. and even for the case of language models in Briesch et al. The last section 4 is also close to the results of Dohmatob et al. A (as the authors note correctly). - I also want to note that the literature is not unanimous on the claim that accumulating data prevents model collapse. That is an ongoing discussion. (e.g. Dohmatob et al. B). Essential References Not Discussed: I suggest that the authors discuss other work more that investigates mixing real and generated data in the model collapse setting (see above). Other Strengths And Weaknesses: While I found the results and experiments in section 4 interesting, it seems to me that this section is another topic than the main paper. It felt out of place reading this section after the paper so far. To me section 4 is more about how to mix data in a dataset but leaves out the context of model collapse. Other Comments Or Suggestions: References: - Alemohammad, S., Casco-Rodriguez, J., Luzi, L., Humayun, A. I., Babaei, H., LeJeune, D., ... & Baraniuk, R. Self-Consuming Generative Models Go MAD. In The Twelfth International Conference on Learning Representations. (2024) - Bertrand, Q., Bose, J., Duplessis, A., Jiralerspong, M., & Gidel, G. On the Stability of Iterative Retraining of Generative Models on their own Data. In The Twelfth International Conference on Learning Representations. (2024) - Briesch, M., Sobania, D., & Rothlauf, F. (2023). Large language models suffer from their own output: An analysis of the self-consuming training loop. arXiv preprint arXiv:2311.16822. - Dohmatob, E., Feng, Y., Yang, P., Charton, F., & Kempe, J. (2024, July). A tale of tails: model collapse as a change of scaling laws. In Proceedings of the 41st International Conference on Machine Learning (pp. 11165-11197). - Dohmatob, E., Feng, Y., Subramonian, A., & Kempe, J. (2024). Strong model collapse. arXiv preprint arXiv:2410.04840. - Gerstgrasser, M., Schaeffer, R., Dey, A., Rafailov, R., Sleight, H., Hughes, J., ... & Koyejo, S. (2024). Is model collapse inevitable? breaking the curse of recursion by accumulating real and synthetic data. arXiv preprint arXiv:2404.01413. - Gonzalo Mart´ınez, Lauren Watson, Pedro Reviriego, Jose Alberto Hern ´ andez, Marc Juarez, and Rik ´ Sarkar. Towards understanding the interplay of generative artificial intelligence and the internet. arXiv preprint arXiv:2306.06130, 2023. Questions For Authors: - Q1: The paper focuses heavily on test loss in their experiments. Did the authors also consider other metrics and evaluations that are important for generative models (e.g. diversity biases as mentioned in Martinez et al., Briesch et al., and Guo et al. or)? Code Of Conduct: Affirmed. Overall Recommendation: 2	Rebuttal 1: Rebuttal: ### On Novelty > My biggest concern with the paper is its novelty. It builds heavily on Gerstgrasser et al. and section 2 (a large part of the paper) only provides new results for different kinds of generative models with equal conclusions. We disagree with this characterization. Our Section 2 identifies and resolves a fundamental tension in the literature where competing papers have reached contradictory conclusions about model collapse. This systematic evaluation across multiple generative settings provides valuable scientific evidence about the generality of these phenomena. Moreover, we make several fundamental contributions: 1. We discovered that in KDE settings (Figure 2), certain combinations of real and synthetic data actually outperform models trained on real data alone - a counterintuitive result not previously reported for KDEs. KDEs are appealing because they are a widely used statistical model that are straightforward to experiment with and analytically tractable to study. 2. We provide novel theoretical results (Theorem 1) on the limiting distribution for univariate Gaussians under the accumulate training workflow, proving that both the covariance and mean errors converge to non-zero constants - in stark contrast to the replace setting where they diverge. This theoretical result mathematically characterizes why the accumulate workflow avoids collapse. 3. Our work is the first to systematically compare all three workflows (replace, accumulate, accumulate-subsample) across five different generative settings, providing a more comprehensive understanding of when and how model collapse occurs. ### On Accumulate-Subsample and Prior Work > The second part of the paper (accumulate-subsample) provides empirical insights that mixing real and generated data slows down model collapse. This has been observed and discussed in literature as early as Bertrand et al., Alemohammad et al. and even for the case of language models in Briesch et al. We should do a much better job explaining how our approach contributes to the literature. While others do study mixing real and generated data, our work pushes the field forward in important ways: Reason #1: We frame our analysis from an extremely practical real-world engineering constraint: finite compute. Other papers study model-data feedback loops in ways that aren't clearly motivated by practical considerations. This framing is important. Reason #2: Other papers add complications that make drawing clear insights difficult. For instance, Bertrand et al. 2023 studies _iterative retraining_, where each new model is initialized from the previous model's parameters and the each new model’s optimizer is initialized from the previous model's optimizer’s state This helps mitigate model collapse because each model is then limited in how far it moves from the preceding model, but this iterative retraining poorly matches real-world conditions as frontier models aren't (to the best of our knowledge) initialized from their predecessors' parameters. Reason #3: The real+synthetic data loops of previous papers e.g., Bertrand and Alemohammad both focus on real data plus synthetic data drawn only from the most recent model. But in reality, if one is scraping the web, we know of no way to filter the collected data for data generated by the most recent generation of models. Our Accumulate-Subsample setting is meant to more faithfully model reality: synthetic data are added online, and are vacuumed up with real data to train the next model. Reason #4: Briesch et al. 2023 is difficult to interpret because the results of their v1 and v2 Arxiv manuscripts (specifically, the key Figure 4) appear to reach slightly contradictory conclusions that the authors don't address. In the revised manuscript, we will better contextualize our contributions relative to these prior works, explicitly highlight the practical relevance of our approach, and more clearly explain how our findings extend beyond what was previously known. ### Definitions and Realistic Assumptions > I also want to note that the literature is not unanimous on the claim that accumulating data prevents model collapse. That is an ongoing discussion. (e.g. Dohmatob et al. B). We agree that the field doesn't have a consensus. This is partially because the field has defined model collapse in multiple and sometimes conflicting ways (a point made by a recent position paper https://arxiv.org/abs/2503.03150) and partially because different papers make assumptions that are unrealistic. This is why we feel it is so important to construct experiments in a way that emulates reality as faithfully as possible. In our opinion, the field has drawn conclusions from experimental setups that are oftentimes not well grounded in real-world considerations.	Summary: The manuscript studies three ways of using synthetic data, both empirically and theoretically. The manuscript starts by examining Gerstgrasser et al. 2024's two claims with the proposed three generative modeling settings in section 2, where some well-established settings and tasks are directly used, making the exact contribution of sec 2 unclear. Section 3 considers a slightly different setting, namely training with a fixed compute budget, and then studies the value of synthetic data for reducing test loss on real data depending on the amount of real data. Claims And Evidence: It is hard to distinguish between the authors' contributions and the existing papers. E.g., * The manuscript argues that "Following Shumailov et al. (2023); Alemohammad et al. (2024); Bertrand et al. (2024), we study what happens when one iteratively fits multivariate Gaussians and samples from ..." and "Shumailov et al. (2024) proved that as t → ∞". It seems like the manuscript just reproduces these experiments in a unified setting with some take messages. Similar comments can be applied to Sec 2.2 and Sec 2.3. * The evidence in Sec 4 is not very rigorous to answer the key open question mentioned in the first paragraph of Sec 4. E.g., * it is unclear why we can compute the $\log (real / (real + synthetic))$ to best capture the relationship between the fraction of real data and the log-likelihood. * it is unclear how to get the value of $1,024$ to support the claim that "when the number of real data is 1024 or lower, we find that there is a small but non-zero amount of synthetic data that improves the test loss when it is included." Methods And Evaluation Criteria: Looks ok. The main concern here is that evaluations and settings in Sec 2 reuse the existing work. Theoretical Claims: The reviewer checks the theorem in the main text and does not spot the issues. Experimental Designs Or Analyses: Yes. See comments above. Supplementary Material: Yes. The reviewer reviewed the proof (Sec A & B & C) and checked some additional experimental results in Sec D & E. Relation To Broader Scientific Literature: NA Essential References Not Discussed: NA Other Strengths And Weaknesses: ## update after rebuttal Strengths: - The paper is well-structured. It considers problems like Multi-variate Gaussian Modeling, Kernel Density Estimation, Linear Regression, and Language Modeling. Weaknesses: - The reviewer acknowledges the additional experiments provided by the manuscript. However, the reviewer does not think it has made sufficient contributions to make it above the bar of ICML acceptance. - The reviewer believes in adding extensive results on various configurations/settings of recursive training image diffusion models and language autoregressive models. For example, settings include but are not limited to different numbers of training samples in the original real dataset, the different ratios between real and synthetic datasets, and different types of real-world datasets. Other Comments Or Suggestions: ## update after rebuttal It would be great if the authors could include more numerical results. For example, in section 4, fine-tuning different base models on various real datasets with different dataset sizes would be very helpful. - The training hyper-parameters used in the experiments are unclear. It would be great if the authors could report these and provide a comprehensive ablation study. Questions For Authors: See comments above. Code Of Conduct: Affirmed. Overall Recommendation: 1	Rebuttal 1: Rebuttal: While we appreciate your review, you are mistaken about your claim that we primarily replicated experiments from other works, and the questions that you asked were largely answered in the paper. To explain line-by-line. > It seems like the manuscript just reproduces these experiments [from Bertrand, Alemohammad, and Shumailov] in a unified setting with some take messages. This is false. Shumailov: Shumailov proves that model collapse occurs for KDEs and Gaussian fitting in the REPLACE SETTING. A main point of our paper is that if you repeat these experiments IN THE ACCUMULATE SETTING, then collapse does not occur. We are the first to do this, and thereby directly compare and contrast the replace and accumulate settings. Alemohammad: This paper again tests model collapse for generative image models in the replace setting. We don’t test generative image models at all in this paper, and we don’t use the replace setting. Bertrand: Bertrand tests model collapse for language models in a variation of the accumulate setting. In this case, the proportion of real data is fixed but non-zero throughout all iterations. We allow the fraction of real data to go to 0 in our version of the accumulate setting, which marks a significant conceptual difference from Bertrand’s setup. All experiments in this paper are original, except for the pretraining experiment, which we extend from Gerstgrasser et. al. to include more model-fitting iterations. Overall, our Section 2 makes a novel and important contribution by identifying seemingly contradictory claims in the model collapse literature and comparing them in a head-to-head manner to resolve them. >The evidence in Sec 4 is not very rigorous to answer the key open question mentioned in the first paragraph of Sec 4. We provide an F-test of whether the proportion or the cardinality of real data dictates model performance. This is a standard and fully rigorous statistical evaluation. The high statistical significance (p-values of $6.9e-25$ and $4.6e-25$ strongly supports our conclusions. If you disagree, please let us know why and what you would recommend instead. > It is unclear how to get the value of $1,024$ to support the claim that "when the number of real data is 1024 or lower, we find that there is a small but non-zero amount of synthetic data that improves the test loss when it is included." This value is our result, shown in Figure 5, where the curves for real data samples ≤1024 show improvement with synthetic data addition, while curves for samples >1024 do not show this benefit. We are not making a theoretical claim about the number 1024; we are reporting the empirical result we observed across multiple experimental runs. We believe these clarifications help address the reviewer's concerns and demonstrate both the novelty and rigor of our work. Additionally, the review does not discuss any strengths of the paper, and you left most of your review sections blank. We hope that you can provide more information about why you gave such a low score and also provide specific constructive criticism for how we can improve the manuscript.	null	null	null	null	null	null
Intersectional Fairness in Reinforcement Learning with Large State and Constraint Spaces	Accept (poster)	Summary: The paper addresses intersectional fairness in reinforcement learning (RL) with exponentially many constraints arising from overlapping groups. The authors propose oracle-efficient algorithms for three settings: 1) tabular MDPs, 2) large MDPs with structured groups (via separator sets), and 3) general groups (using Fictitious Play). The key idea is to reduce the constrained RL problem to a minimax game between a learner (optimizing policies) and a regulator (enforcing group fairness), leveraging optimization oracles to handle large constraint sets. Theoretical guarantees include sublinear regret and convergence to approximate equilibria. Experiments on a preferential attachment graph MDP demonstrate that their method ensures minimum reward guarantees for all groups, balancing fairness and total reward. Claims And Evidence: see the comments below Methods And Evaluation Criteria: see the comments below Theoretical Claims: see the comments below Experimental Designs Or Analyses: see the comments below Supplementary Material: see the comments below Relation To Broader Scientific Literature: see the comments below Essential References Not Discussed: NA Other Strengths And Weaknesses: Strengths: - Novel integration of optimization oracles for exponentially many constraints. - Theoretical contributions in oracle-efficient RL with intersectional fairness. Weaknesses: - Practical reliance on strong oracles (e.g., Lin-OPT) without discussing implementability. - Limited empirical scope (one synthetic MDP). - No discussion of computational complexity for large-scale deployments. Other Comments Or Suggestions: NA Questions For Authors: - The theory supports exponential groups, but experiments use only three. How does the performance scale with $d$? A response showing linear/polynomial scaling would strengthen the claim. - How does the method compare to the baseline methods? Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Dear Reviewer Gqfm, Thank you for your positive assessment of our work. Empirical Scope As we highlight in Section 5 on Future Work, we completely agree that moving towards more realistic scenarios with these algorithms poses an interesting future direction for our work. However, the current manuscript is largely a theoretical contribution and we believe that moving to more complex oracle settings will come with its own challenges and open questions. These include studying the effects of potentially sub-optimal oracles in practice, which will likely warrant a different type of publication. Our experiments primarily aim to verify the effectiveness of our FairFictRL algorithm. This algorithm is easy to implement but it does not come with with polynomial-time guarantees. Thus, our experiments validate that this easy version of the algorithm might be a feasible alternative in practice. Optimization Oracle Assumption Our optimization oracle assumption is mainly stating that we are able to do linear optimization efficiently in practice. Algorithms to achieve this exist in practice. For example, in the case of continuous space, interior point methods or barrier methods work well and in the case of conjunctions, integer linear programs and mixed integer programs, etc. work effectively in practice. For best response oracles one may hope to resort to deep reinforcement learning algorithms that may return policies close to optimal. We are happy to extend the discussion on this by adding text akin to the previous sentences to the paper. Computational Complexity and Scaling Since we provide oracle efficient algorithms, the run time (which we bound in our lemmas) is the core component of our computational complexity. Our algorithms mainly make O(T) oracle calls total, comprising the majority of the computation within each round; the only other computation is the sampling of noise vectors of size $O(d)$ or $O(\|S\|)$ at each round for the Follow the Perturbed Leader base algorithms. We will update our paper to include a statement highlighting the computational complexity of our algorithms. Lemma $3.3$ shows that the computational complexity of our algorithm for tabular MDPs scales logarithmically in $\|\mathcal{G}\|$ and polynomially in $\|S\|$. Lemma $3.6$ shows that the computational complexity of our algorithm for continuous spaces and groups with separator structor scales with the size of the separator set $d$ and $\ln(\|\mathcal{G}\|)$. We believe that the impact of the number of groups on scaling to larger settings in practice would be negligible. Baseline Methods We appreciate the question. We have not implemented any baselines in this setting and we are not aware of any baselines that would be suitable. We view the main claim of the experimental section as validating that our proposed FairFictRL algorithm works. We do not believe that the addition of baselines would strengthen this claim substantially.	Summary: This paper investigates an interesting problem of intersectional fairness in RL. Unlike standard fairness approaches in RL, this work formulates fairness as a multi-objective optimization problem. Specifically, the goal is to optimize fairness and efficiency by maximizing the utility of the least advantaged group when demographic groups are available. The authors propose oracle-efficient algorithms for solving both tabular and large-scale MDPs. Theoretical results are provided, and experiments on a synthetic graph MDP validate the approach. Claims And Evidence: Most of the paper claims are well-supported through theoretical results and empirical validation in synthetic graph MDP. However, the claim that the method achieves Pareto dominance in the synthetic graph MDP is questionable. Optimizing only for the minimum group utility ignores the needs of other groups, which may sacrifice overall efficiency and Pareto optimality. Methods And Evaluation Criteria: While the paper addresses an important gap in fair RL, its practical applicability and scalability require further investigations. The experiments are limited to simple, small, tabular MDP, which may not generalize well to more complex RL settings. Theoretical Claims: The theoretical results, particularly the no-regret guarantees in Theorems 3.1 and 3.2, appear correct to me. The discussion in the main paper is clear, but I have not verified the full proofs in the appendix. Experimental Designs Or Analyses: The paper lacks fair RL baseline comparisons. While related works (e.g., Satija et al., 2023) are cited, they are not included as baselines in the experiments. The experimental evaluations are also limited. I believe testing the method on real-world environments such as college admissions, healthcare, or loan approval etc would significantly strengthen the paper. Supplementary Material: I briefly reviewed Appendix A for the proofs, but did not check in details. Relation To Broader Scientific Literature: The paper makes a significant theoretical contribution by introducing intersectional fairness in RL, a relatively unexplored area. It adapts a technique from classification fairness (fictitious play) to sequential decision-making in RL and demonstrate its applicability to RL. While the theoretical insights are valuable, additional empirical validation would enhance its impact. Essential References Not Discussed: The paper adequately discusses related work. Other Strengths And Weaknesses: Strengths: * The paper introduces an important and novel problem of intersectional fairness in RL. * The theoretical results, particularly the no-regret guarantees, are well-establish and provide enough justification for the proposed method. * The paper proposed oracle-efficient algorithms that scale to both tabular and large-scale MDPs. * The approach adapts fictitious play from classification fairness to RL, demonstrating its applicability to sequential decision-making with large state spaces. Weaknesses: * The paper focuses on group fairness (specifically minimax) but does not consider individual fairness, which is often more practical in RL and real-world applications. Could the approach be extended to an individual fairness setting? * The minimax objective optimizes for the worst-off group but may sacrifice total utility and fail to ensure proportional or Pareto-optimal fairness. * The experimental evaluations are only in a synthetic MDP with only three groups, which does not reflect the complexity of real-world RL applications with a large number of demographic groups. * Moreover, the paper also lacks comparisons to fair RL methods. Other Comments Or Suggestions: See above. Questions For Authors: * Can the proposed method accommodate other fairness notions, such as leximin or proportional fairness, beyond minimax? * How does the proposed method scale with a higher number of objectives (e.g., 10)? In such cases, the number of intersectional groups could be 1024. Would the approach remain computationally tractable? * How would Lin-OPT/OPT be approximated in practice for large group sizes? * Are there relevant baseline methods that could be included for comparison, both in terms of fairness and efficiency? * How does the method generalize to real-world RL environments, where state/action spaces are large or continuous? Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Dear Reviewer zwEM, Thank you for acknowledging the significant theoretical contribution of our work and the detailed feedback on our submission. Individual Fairness The notion of fairness we consider represents a middle ground between fully statistical notions of fairness and fully individual notions. By considering a sufficiently rich set of subgroups (rather than just the $d$ individual attributes or all individuals), we are able to provide algorithms that are tractable even for large state spaces while having meaningful guarantees for more fine-grained portions of the population. We believe this to be a valuable step towards methods that deal with the great variety of preferences and characteristics that individuals can exhibit, reflecting the vast diversity found within human sub-populations. Pareto Optimal Fairness This is a great point. You are correct in that the minimax optimization does not imply pareto optimality. However, what we can claim is that the minimax solution Pareto-dominates the solution that tries to equalize rewards across groups. We will clarify this in the text. We also do agree (as Figure 3 shows) that overall efficiency or optimality may be sacrificed when trying to optimize with fairness constraints in mind. This may unfortunately be unavoidable in many settings. Empirical Scope As we highlight in Section 5, we completely agree that more realistic scenarios pose an interesting future direction. However, the current manuscript is largely a theoretical contribution and we believe that moving to more complex oracle settings will come with its own challenges and open questions. These include studying the effects of potentially sub-optimal oracles, which will likely warrant a different type of publication. Our experiments primarily aim to verify the effectiveness of our FairFictRL algorithm. This algorithm is easy to implement but it does not come with polynomial-time guarantees. Thus, our experiments validate that this algorithm is a feasible alternative in practice. Baseline methods We appreciate the feedback on this. We view the main claim of the experimental section to be that our proposed FairFictRL algorithm is practical and we do not believe that the addition of baselines would strengthen this claim substantially. Other Notions of Fairness This is a great point. We agree that other notions like leximin fairness are very interesting. In fact, an idea for future work might be to adapt our method to iteratively solve for leximin fairness as in [1]. However, even in this classification setting, leximin fairness is a very subtle and technically unstable concept. In addition, it can become computationally challenging when the number of groups is large as one may have to iterate over all groups. Instead, our method is able to handle a broad class of linear/convex fairness constraints or objectives and can be implemented efficiently. That being said, there are still many other interesting fairness notions that one could explore and we are excited about doing so in the future. Group/Objective Scaling Our proposed method scales with the log of the number of groups as can be seen in Lemma $3.3$ for tabular MDPs and Lemma $3.6$ for large state spaces. This is one of the key strengths of our contribution as it allows us to handle exponentially many groups. Approximate Lin-OPT Our optimization oracle assumption is mainly stating that we are able to do linear optimization efficiently in practice. For this, interior point methods or barrier methods work well in the case of continuous spaces and in the case of conjunctions, integer linear programs and mixed integer programs work effectively. We are happy to extend the discussion on this by adding text akin to the previous sentences to the paper. Large and continuous state-action spaces Our methods already give provable guarantees for large spaces as we are able to make use of Algorithm $3$, which gives poly-time guarantees when we have group separator structure, or Algorithm $4$ for spaces without any group structure assumptions, but with an asymptotic guarantee. Here, one challenge would be to implement the policy oracle as mentioned before. One could hope to approximate solutions via standard deep RL techniques, which in many settings may be feasible. Yet, in various problems these algorithms may not return optimal policies in every execution [2]. As stated before we believe that moving to more complex oracle settings will come with its own challenges that lie beyond the scope of this manuscript. [1] Lexicographically Fair Learning: Algorithms and Generalization. Emily Diana et al. FORC 2021. [2] Deep Reinforcement Learning that Matters. Peter Henderson et al. AAAI 2018. --- Rebuttal Comment 1.1: Comment: Thanks for the detailed response to my comments. While most of my concerns have been addressed, I still believe that including baselines and conducting additional experiments would strengthen the paper. Since my current score already indicate a weak accept, I will maintain it in light of the authors' response.	Summary: This paper studies a constrained RL problem in the episodic setting that generalizes the problem of minimax group fairness, allowing for exponentially many group fairness constraints due to the intersection of grouping functions. The authors focus on developing oracle-efficient algorithms for solving this problem in large state and constraint spaces. Their key contribution lies in providing solutions for three scenarios: tabular MDPs, large state space MDPs with separator sets assumed groups, and large state space MDPs with general groups. They propose two FTPL-based algorithms for the first two settings, and a Fictitious Play-based algorithm for the third. Theoretically, they provide regret bound for the first two settings. The effectiveness of the third algorithm is demonstrated empirically through a graph-based simulation. Claims And Evidence: The claims presented in the paper are supported by clear and convincing evidence. Methods And Evaluation Criteria: The proposed method provides a reasonable solution to the problem. Theoretical Claims: I did not verify the correctness of the proofs. Experimental Designs Or Analyses: The numerical studies would benefit from further experimentation. Specifically, given the paper's focus on large state and constraint spaces, experiments should be added to examine such scenarios. Additionally, simulation studies should be conducted to verify the validity of the two FTPL algorithms. Supplementary Material: I reviewed the supplementary material, excluding the correctness of the proofs. Relation To Broader Scientific Literature: This work relates to prior research in fair RL and constrained RL. Rather than solving constrained RL problems by enumerating the constraints, the authors propose oracle-efficient algorithms. Essential References Not Discussed: No. Other Strengths And Weaknesses: Strengths: 1. The paper studies a interest problem in fair RL with a large number of intersecting groups. 2. The authors provide oracle-efficient algorithms that can handle a large number of constraints efficiently, which is crucial in practical where the number of groups can be very large. 3.The graph-based simulation study is novel and easy to understand. Weakness: 1. The paper would benefit from additional numerical experimentation to further validate the proposed algorithms. Other Comments Or Suggestions: It would be beneficial for readers to have a clearer explanation of how the separator assumption impacts the computational efficiency of Algorithm 3. Questions For Authors: 1. Could you please clarify how Algorithm 4 is implemented in the numerical study? For instance, could you provide details on the implementation of the Best Response and Optimization oracles? 2. If the MDP is not accessible, do you have any insights on how your algorithms could be adapted? Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Dear Reviewer sNea, Thank you for your positive assessment of our work and your feedback. Additional Experimental Simulations The experimental study that we provide is used to highlight the applicability of our FairFictRL algorithm. Fictitious Play is easy to implement in practice because it only relies on Follow the Leader for both players and does not require noise generation that scales with the dimension of the action space. However it does not come with polynomial-time guarantees and our experiments aim to verify that it is still a good choice in practice. The Follow the Perturbed Leader-based algorithms themselves already have provable guarantees to converge, and we believe that adding additional experiments here may distract from the main message of the experimental section. Optimization Oracles and Experiments In our experiments we consider a tabular MDP, for which the best response oracle is implemented via value iteration. The regulator can select the group that minimizes the past cumulative cost by iterating over the groups, because the number of groups is small in this experiment; in practice would need to use a stronger optimization oracle that is able to do linear optimization efficiently. In the case of conjunctions, this might also involve Integer Linear Programs or Mixed Integer Programs. Regarding MDP access, none of our algorithms require direct access to the MDPs. We only assume access to the MDP in our experimental section, in which we use value iteration to implement our best response oracle. We will update the wording in the manuscript to make this more clear. Note that to implement the best response oracle, we simply need to be able to optimize a given specified reward function within an MDP, which can be done with standard RL methods. These do not need to depend on access to the MDP. We simply choose value iteration because the goal of the experimental section is not to evaluate different oracles but rather to evaluate our FairFictRL algorithm under the proposed assumptions. Separator sets The separator assumption directly affects our computational efficiency via the dependence of d in the bound given in Lemma 3.6. Since we are providing oracle-efficient algorithms, our primary computational- complexity analysis comes from the number of rounds our algorithm runs for given that we make O(T) oracle calls.	Summary: This paper explores the problem of intersectional fairness in reinforcement learning (RL) with large state and constraint spaces, proposing several oracle-efficient algorithms to optimize multiple objectives simultaneously while ensuring fairness across intersecting demographic groups. The authors provide theoretical guarantees for their algorithms and validate their effectiveness through experiments on a preferential attachment graph MDP. Claims And Evidence: good Methods And Evaluation Criteria: good Theoretical Claims: good Experimental Designs Or Analyses: good Supplementary Material: good Relation To Broader Scientific Literature: good Essential References Not Discussed: no Other Strengths And Weaknesses: see questions Other Comments Or Suggestions: see questions Questions For Authors: This paper explores the problem of intersectional fairness in reinforcement learning (RL) with large state and constraint spaces, proposing several oracle-efficient algorithms to optimize multiple objectives simultaneously while ensuring fairness across intersecting demographic groups. The authors provide theoretical guarantees for their algorithms and validate their effectiveness through experiments on a preferential attachment graph MDP. I am unfamiliar with this specific area of research, so my comments may not be highly technical, but I have a couple of concerns. Firstly, why did the authors not conduct experiments using deep reinforcement learning algorithms? Given that deep RL is widely used in complex, high-dimensional problems, it would be interesting to see how well the proposed methods perform in such settings. This could provide more insights into the scalability and practical applicability of the algorithms. Secondly, I am interested in the potential applications of this work. The authors mention fairness in RL, which is a critical issue in many real-world scenarios. However, it would be helpful to discuss more specific scenarios where this algorithm could be particularly impactful. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Dear Reviewer xri7, We appreciate the positive assessment of our work. Deep RL experiments As we highlight in Section 5 on Future Work, we completely agree that deep learning poses an interesting future direction for this type of work. However, the current manuscript is largely a theoretical contribution and we believe that moving to deep learning will come with its own challenges and open questions such as studying the effects of potentially sub-optimal oracles in practice, which will likely warrant a different type of publication. Our experiments primarily aim to verify the effectiveness of our FairFictRL algorithm. This algorithm is very easy to implement but, unlike our other algorithms, it does not come with with polynomial-time guarantees. Yet, our experiments validate that this easy version of the algorithm might be a feasible alternative in practice. Applications Fairness in Reinforcement learning plays a large role in various applications such as healthcare or loan approval. However, we believe that one of the most interesting applications in our current timeline is the application to Reinforcement Learning from Human Feedback (RLHF). Our technique could be a step towards preventing LLMs from outputting discriminatory or toxic prompts to various (intersectional) groups. We will update the paper to include additional discussion of this application.	null	null	null	null	null	null
Efficient Noise Calculation in Deep Learning-based MRI Reconstructions	Accept (poster)	Summary: The authors propose a scheme for efficient voxel-wise noise estimation for Deep-learning based accelerated MRI algorithms. The method builds upon estimating the noise covariance from the DL-models Jacobian by using an unbiased estimator for the diagonal elements (of the cov-matrix) via the proposed Jacobian sketching approach. Claims And Evidence: The work includes claims to accurately reconstruct voxel-based noise levels in DL multi-coil based accelerated MRI reconstruction agnostic to the method and forward operator, which as to my opinion are fulfilled by the conducted experiments. Methods And Evaluation Criteria: One notable weakness of the paper is that the presented method is only evaluated in the domain of MRI reconstruction, leaving its performance on other modalities like CT untested. This especially interesting since CT has Poisson distributed noise, which is a significant difference to the assumptions in MRI. Demonstrating the performance across different (medical) imaging techniques would significantly enhance the work’s contribution. Furthermore, the evaluations conducted do not provide evidence that the estimated noise levels improve performance in downstream tasks. While the method efficiently and accurately reconstructs voxel-wise noise variance, it remains unproven whether these estimations actually translate into benefits for tasks like non-blind denoising or segmentation. Demonstrating an improvement in downstream applications is critical to validate the practical utility of the proposed technique. However, despite this shortcoming, the method is evaluated on a broad range of reconstruction approaches, including supervised, self-supervised, fully data-driven, and physics-driven methods. Theoretical Claims: The theoretical part of the manuscript seems sound and well-presented. Experimental Designs Or Analyses: As mentioned above, for the task of mere noise estimation in MRI reconstruction, the experimental design appears valid. However, the evaluation lacks evidence that the estimated noise levels benefit downstream tasks or works on other modalities/noise distributions. Supplementary Material: The provided supplementary material contains the codebase for the presented work. Relation To Broader Scientific Literature: The contribution to the broader scientific field of medical imaging seems somewhat limited due to the shortcomings addressed above. Essential References Not Discussed: The manuscript seems to include essential references. Other Strengths And Weaknesses: See above. Other Comments Or Suggestions: As mentioned above, the work conducted is solid. However, in my opinion, to justify a publication, the authors should consider extending the work as addressed above. Questions For Authors: No further questions/remarks from my side. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We appreciate the reviewer’s thoughtful comments and recognition of our extensive experimentation across diverse DL reconstruction methods and MR imaging scenarios. Below we explicitly address each concern, highlighting the relevance and impact of our approach in downstream medical imaging via extended discussion and new experiments. We then describe generalizability the other medical imaging tasks and modalities. We’d like to also refer the reviewer to 1. Novelty and Technical Contributions and 2. Clinical Motivation and Importance of Noise-Variance (NV) Estimation points in the rebuttal for reviewer SQro. We believe these points, holistically clarifies our study’s contributions to the broader scientific field of medical imaging. ## 1. Utility of Noise Variance Estimation on Downstream Tasks Voxel-wise NV estimation has been extensively shown to enhance downstream imaging tasks such as denoising and segmentation across modalities including MRI, CT, and ultrasound. For example, classical adaptive filters like BM3D significantly benefit from NV information by effectively removing noise without compromising clinical details [1,2]. Similarly, adaptive filters that incorporate spatially varying noise variance improve diagnostic information in low-dose CT and ultrasound imaging [3,4]. In deep learning contexts, explicitly incorporating voxel-wise NV maps consistently improves performance by reducing false positives and increasing accuracy in segmentation and denoising networks [5,6]. [1] Hanchate, SN Appl Sci., 2020 [2] Li, Med Phys, 2014 [3] Hariharan, Phys Med Biol, 2020 [4] Yu, IEEE TIP, 2002 [5] Dou, NMR Biomed., 2025 [6] Wang, Eng Appl AI, 2022 ## 2. Additional Downstream Task Experiments To directly demonstrate the practical value of our method, we have added two new downstream proof-of-concept experiments in the revised manuscript: - 1. Non-blind Denoising: A Noise2Noise network was trained on the reconstructed brain images (a) assuming uniform image noise and (b) leveraging our predicted voxel-wise variance maps as noise-level priors. The variance-informed network achieved a 0.9 dB gain in PSNR, highlighting direct improvements from accurate local variance estimation. - 2. Variance-Guided Segmentation: A U-Net was trained for cartilage segmentation with the predicted variance maps included as additional input channels, resulting in a 1.1% improvement in Dice coefficient and fewer false positives, demonstrating how noise-aware segmentation enhances clinical accuracy. These experiments provide clear evidence that our analytical voxel-wise NV estimates are not merely theoretical metrics but actively enhance clinically relevant imaging tasks. ## 3. Extension Beyond MRI for Other Medical Imaging Tasks and Modalities We agree that extending our voxel-wise noise variance (NV) estimation approach to imaging techniques beyond MRI (particularly CT with its Poisson-like noise characteristics) would further demonstrate the generalizability and impact of our method. However, our primary goal in this study was to specifically address multi-coil accelerated MRI due to its complex acquisition model and the widespread adoption of DL-based reconstructions, where explicit noise propagation has been relatively understudied. Notably, our framework is fundamentally generalizable and is not limited solely to Gaussian noise assumptions. The method requires only: A known forward operator $A$ describing the measurement process (e.g., X-ray projections in CT). An appropriate noise covariance $\Sigma_k$ reflecting the modality-specific noise statistics. For instance, extending to CT could involve incorporating Poisson-Gaussian noise models or variance-stabilizing transformations directly into $\Sigma_k$. Thus, while we consider such extensions an important future direction, the current manuscript lays the foundational theoretical and computational framework necessary to address these broader applications. --- Rebuttal Comment 1.1: Comment: I thank the authors for addressing most of my concerns. As the suggested method appears to have a positive impact on downstream tasks, I will raise my score. However, I am still not fully convinced that the contribution is substantial enough to justify publication in its current form. Extending the work to CT, as suggested in the discussion, would significantly strengthen the contribution. --- Reply to Comment 1.1.1: Comment: We appreciate the reviewer’s acknowledgement of our method’s positive impact on downstream tasks and welcome the continued interest in the broader applicability of our framework. While our approach is fundamentally extensible to any modality with a linear forward operator and known noise covariance, our present study specifically targets multi-coil accelerated MRI due to: 1. Complex Acquisition Operator. Multi-coil MRI relies on coil sensitivity maps, Fourier encoding, and undersampling masks, creating a high-dimensional, correlated noise model not fully addressed by existing uncertainty quantification methods. 2. Widespread Adoption of Deep Learning Reconstructions. Recent advances in deep MRI reconstruction have rapidly entered clinical and research pipelines, yet voxel-wise noise propagation in these networks remains relatively understudied. 3. Page Limits and Scope. Given the complexity of multi-coil MRI and the page constraints of this submission, we chose to focus on a rigorous analysis and validation in this setting, rather than diluting the results across multiple imaging modalities. That said, we argue that extending to CT, PET, or other modalities is a natural next step, not a fundamental limitation. As discussed in Theory section, our framework fundamentally depends on (1) a linear forward operator and (2) a noise covariance matrix, thus making it adaptable to imaging modalities beyond MRI. In CT, for instance, the forward operator $ \mathbf{A} $ would represent the Radon transform (mapping attenuation coefficients to projection data). While CT measurements exhibit predominantly Poisson-like noise, one can employ a variance-stabilizing transform (e.g., the Anscombe transform) to approximately convert that noise into a Gaussian form. Specifically, if we transform the measured projections $ \mathbf{y} $ to $ \mathbf{y}_{\mathrm{trans}} $, then our noise model can treat $ \mathbf{\Sigma}_k $ as a (potentially diagonal) covariance matrix reflecting the stabilized data’s variance. Concretely, in step 2 of Algorithm 2 in Appendix, we transform the random matrix $ \mathbf{V}_S \in \mathbb{C}^{m \times S} $ via: $$ \mathbf{W}_S = \mathbf{\sigma}_k \,\mathbf{V}_S, \quad \widetilde{\mathbf{W}}_S = \mathbf{A}^H \,\mathbf{W}_S. $$ For CT, $ \mathbf{\sigma}_k $ would encode the (approximate) covariance of the transformed sinogram data, ensuring the subsequent Jacobian sketching step accurately captures how Poisson-like noise propagates through the deep reconstruction network. In Theorem 3.1 and Lemma 3.2, we show that our estimator of $ \mathrm{diag}(\mathbf{\Sigma_x}) $ is unbiased when the random vectors $ \mathbf{v}\in\mathbb{C}^m $ satisfy $ \mathbb{E}[\mathbf{v}] = \mathbf{0} $ and $ \mathbb{E}[\mathbf{v}\,\mathbf{v}^H] = \mathbf{I} $. These requirements are agnostic to the underlying physical noise distribution, as long as $ \mathbf{\Sigma}_k $ correctly models it. Therefore, whether the noise is approximately Gaussian (as in MRI) or stabilized Poisson (as in CT), our procedure—via random-phase or Gaussian vectors—remains statistically valid for diagonal variance estimation. We agree with the reviewer that a demonstration on CT would indeed strengthen our contribution by verifying performance under Poisson-like conditions. However, our current manuscript focuses on establishing the theoretical foundation and computational framework in the (multi-coil, correlated) MRI setting as outlined above. The modular design of our approach—based on abstract linear algebraic principles—makes it naturally extendable to CT, PET, or other modalities. We are actively exploring these future directions, confident that the same Jacobian-based random sketching and diagonal estimation procedure will hold under the appropriate $ \mathbf{A} $ and $ \mathbf{\Sigma}_k $ for each modality." In the revised manuscript, we will incorporate a dedicated subsection within the Discussion section titled 'Extension to Other Modalities: CT and Beyond,' where we will elaborate on the practical considerations and theoretical adaptations necessary for applying our method to CT. Specifically, we will detail how our randomized sketching algorithm and noise modeling adapt to different forward operators (e.g., the Radon transform for CT) and noise distributions (e.g., Poisson-like). This discussion will outline practical considerations such as using the Anscombe transform for approximate Gaussianization and incorporating the appropriate noise covariance. We believe these additional clarifications will demonstrate the generality of our core method.	Summary: The authors have developed a computational- and memory-efficient estimator of the voxel-wise variance in MRI reconstruction for uncertainty quantification in the reconstruction. The method is evaluated on MRI data and compared to Monte Carlo-simulations. The method is simple and easy to understand and computationally efficient while providing very similar results compared to Monte Carlo. Claims And Evidence: The claims made are proven in a clear and straight-forward way. The empirical evidence supports the utility of the proposed method. Methods And Evaluation Criteria: I think the results are fairly clear, but the noise map estimates can be difficult to visiaully evaluate. I would encourage the authors to provide other means as well to illustrate the reconstruction and highlight when it works well and when/where it fails. For instance, why not make a scatter plot with the uncertainties as a function of different voxel intensities. This would highlight that the uncertainties (likely) increase as the image intensities increase, for instance. You say that a t-test was performed on the "difference between noise distributions", but it is not clear what test was actually performed, and where are those results presented? In this case, it would be better to compare the distributions rather than the means (through the t-test). The uncertainty profiles could be quite different, even though the means be the same. Theoretical Claims: The proofs were easy to follow and appears correct. Experimental Designs Or Analyses: To increase the evidence in favour of your method, I would encourage you to include at least one more experiment. I would also add a quantification of the results, for instance a comparison between the estimated variances as mentioned above. Supplementary Material: The supplementary material contained much more details and additional results. This is nice, and in principle fine, but it would be good to outline in the main paper what is in the supplementary, so that it is clear to the reader that they (perhaps) should look there as well. Relation To Broader Scientific Literature: I'm missing an exposition of and comparison to previous work in uncertainty quantification in MRI reconstruction. There is quite some work done in this field. It would also be good to compare the proposed method to other noise estimation methods, to further strengthen the evidence in favour of the proposed method. Essential References Not Discussed: As mentioned above, I think an exposition of and comparison to previous work in uncertainty quantification in MRI reconstruction is missing. Other Strengths And Weaknesses: The paper is well-written and clear. It is said that the proposed method was used before, by Pruessmann et al. (1999), but this is not discussed under related methods. What are the differences, and what in the present work makes it novel compared to previous work? Other Comments Or Suggestions: Some minor comments: - The distinction between \Sigma_x and \Sigma_k could be stated explicitly. - Line 150, left column: Double ending parenthesis. - Line 156, right column: Cross-reference should be equation (6) and not (8), right? - Line 208, right column: It would be good to make it clear that the algorithm description is in the appendix. - Results: It would be better if you presented standard errors instead of standard deviations, so that the results can be directly compared. - Line 368, left column: "4.1" should perhaps be "Section 4.1" instead. - I would recommend that you clean up the references. - Line 1362: Lower case t after full stop. Questions For Authors: Line 259, right column: What is R? Needs to be explained. If you make the novelty of the contribution clear, especially in relation the existing works, I would consider increasing my score. Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: We thank the reviewer for the positive feedback. Thanks to the reviewer for thorough examination of the manuscript, we implemented all suggested corrections (typos, cross-refs, terminology) and cleaned up the references. We also added an appendix overview outlining its structure for improved readability. We addressed your valuable suggestions, and clarifed novelty and contributions of our study, especially in relation the existing works which we have discussed in great detail below, with newly included references. For a detailed breakdown of our contributions, please also see rebuttal to reviewer SQro: 1. Novelty and Technical Contributions. Per your recommendation, we also included new additional experiments outlined in the rebuttal to reviewer viwd: 2. Additional Downstream Task Experiments. ## 1. Extended Related Work and Clarification of our contributions While Pruessmann [8] analytically computed noise variance for linear SENSE with Cartesian sampling, our method addresses nonlinear deep reconstructions with complex operators and random undersampling—where noise propagation is significantly more challenging. Unlike our approach, Wen [1] uses a conformal prediction framework that constructs distribution-free uncertainty intervals at the level of downstream task outputs, without modeling voxel-level uncertainty or incorporating the physics of MRI acquisition. Their approach treats the reconstruction pipeline as a black box and requires calibration data to guarantee finite-sample statistical coverage. They do not estimate how acquisition noise propagates through multi-coil systems or nonlinear reconstructions. Edupuganti [2] introduced a VAE-based probabilistic framework that models epistemic reconstruction uncertainty in a latent space and utilizes SURE-based estimators—relying on approximate Jacobian traces—and Monte Carlo (MC) sampling to compute uncertainty maps under the assumption of uncorrelated, i.i.d, single-coil noise. In contrast, our approach analytically propagates correlated multi-coil MRI noise through nonlinear deep reconstruction networks using network’s Jacobian as an operator via randomized sketching. In addition to these, in our revised submission, we will include references to additional studies [2–7] that were discussed under Uncertainty Quantification in MRI in Related Work section but inadvertently omitted from the bibliography. Our work uniquely closes a longstanding gap by providing the first analytical framework to quantify how acquisition noise in multi-coil k-space propagates through nonlinear deep MRI reconstructions. Existing methods do not analytically model this process, and thus do not solve the same problem. Consequently, direct comparisons are not appropriate; our MC baseline sufficiently represents these methods’ performance within the multi-coil setting, while our analytical estimator addresses a distinct, previously unresolved challenge in aleatoric uncertainty quantification. ## 2. Additional Visualizations We performed additional visualizations of voxel-wise noise maps ([link](https://postimg.cc/Mn49Rcgx)): 1. A histogram of the relative estimation error reveals the full distribution of voxelwise deviations, showing that most errors cluster near zero. 2. A scatter plot of the calculated noise maps vs. voxel intensity demonstrates a moderate positive correlation, consistent with typical MRI acquisition where noise can scale with signal magnitude. 3. A scatter plot of the absolute estimation error vs voxel intensity likewise shows a mild positive correlation, confirming the reviewer’s hypothesis that noisier regions often coincide with brighter intensities. As the reviewer suggested, these visualizations indeed offer an improved quantitative perspective on how closely our method aligns with empirical references and where noise tends to concentrate, supplementing direct map comparisons. ## 3. Statistical Tests for Noise Variance Distribution Comparisons We initially reported the results of a two-sample t-test result on page 5, line 264. Following the reviewer’s suggestion, we expanded our analysis to include further statistical tests: - Normality Check A Shapiro–Wilk test yielded a p=0.01<0.05, indicating that the distribution of voxelwise variance differences does not follow a normal distribution. - Since normality was violated, we employed a Wilcoxon signed-rank test to check whether the variance maps from our method and the MC reference originate from the same distribution. We found no statistically significant difference between these two distributions (p=0.75>>0.05). Hence, our variance estimates align with the MC reference at both the mean and distributional levels, despite the non-normality in voxelwise differences. [1] Wen ECCV 2024 [2] Edupuganti TMI 2020 [3] Hoppe ECCV 2024 [4] Edupuganti TMI 2021 [5] Tezcan TMI 2020 [6] Narnhofer TMI 2021 [7] Küstner MRM 2024 [8] Pruessmann MRM 1999 --- Rebuttal Comment 1.1: Comment: Thank you for the clear response and edits. I am satisfied with the additions you've made and will increase my score. --- Reply to Comment 1.1.1: Comment: We are very grateful to Reviewer q9G3 for their positive feedback and for raising their score to 4. We thank them for their detailed review and for acknowledging that our clarifications regarding novelty, related work, and the additional visualizations and statistical tests have been satisfactory. We appreciate their time and effort in helping us improve the manuscript.	Summary: Authors propose a technique to calculate voxel-wise variance for quantifying uncertainty that stems from acquisition noise in accelerated MRI reconstructions. Authors propose to estimate the noise covariance using an approximation to the Jacobian of the neural network. The approximation is done through an unbiased estimator for the diagonal of the covariance by a sketching via random-phase vectors. The sketching algorithm is evaluated on knee and brain MRI datasets for data and physics driven networks trained in supervised and unsupervised manners. Method is shown to be robust against varying input noise levels, acceleration factors, and diverse under-sampling schemes. Claims And Evidence: Several claims do not have convincing evidence. 1) In the conclusion section authors mention "... even if global metrics indicate high reconstruction quality, a locally elevated noise variance in diagnostically relevant ROIs could compromise clinical interpretation.". However, there is no concrete evidence provided in the paper to support these reasoning. 2) Although in real-valued matrix sketching Rademacher vectors are known to have lower estimator variance compared to Gaussian vectors, the choice of using complex Rademacher vectors is not ablated. It is not clear whether it is strictly better than complex Gaussian random vectors for estimating noise maps both empirically and theoretically. Methods And Evaluation Criteria: Benchmark datasets and the evaluation criteria makes sense for the problem at hand. Theoretical Claims: Yes, verified the proofs for Theorem 3.1 and Lemma 3.2. Although they are correct, they are unnecessarily long. Experimental Designs Or Analyses: As mentioned in the "Claims and Evidence" section, I have some concerns with the experimental analysis. Please refer there to avoid duplication. Supplementary Material: Yes, I have reviewed Appendix B (existence of network Jacobian) and F-to-J to check various experimental configurations (undersampling patterns and different network architectures) Relation To Broader Scientific Literature: The estimation of the noise variance serves as a measure of uncertainty quantification. This is relevant to a line of work that uses network Jacobian and SURE estimator [1], and [2] which utilizes tools from conformal prediction to provide uncertainty quantification. [1] Edupuganti, Vineet, et al. "Uncertainty quantification in deep MRI reconstruction." IEEE Transactions on Medical Imaging 40.1 (2020): 239-250. [2] Wen, Jeffrey, Rizwan Ahmad, and Philip Schniter. "Task-Driven Uncertainty Quantification in Inverse Problems via Conformal Prediction." European Conference on Computer Vision. Cham: Springer Nature Switzerland, 2024. Essential References Not Discussed: Some of the missing citations are: [1] which quantifies the risk in the reconstructed images using Stein's Unbiased Risk Estimator (SURE) via the end-to-end network Jacobian. [2] using tools from conformal prediction to obtain risk maps. [1] Edupuganti, Vineet, et al. "Uncertainty quantification in deep MRI reconstruction." IEEE Transactions on Medical Imaging 40.1 (2020): 239-250. [2] Wen, Jeffrey, Rizwan Ahmad, and Philip Schniter. "Task-Driven Uncertainty Quantification in Inverse Problems via Conformal Prediction." European Conference on Computer Vision. Cham: Springer Nature Switzerland, 2024. Other Strengths And Weaknesses: *Strengths:* * Paper is easy to read. * Application of matrix sketching as a means to estimate noise variance in MRI reconstruction setting is interesting. * Experimental results are conducted over a diverse set of configurations. * Weaknesses:** * Technical contribution is weak. The paper essentially boils down to applying matrix sketching ideas to MRI reconstruction networks. * The theorems and lemmas (in chapter 3) are unnecessarily cluttered. * The need for estimating the voxel-wise noise variance is not motivated enough. * Please see the suggestions and questions for more. Other Comments Or Suggestions: *Suggestions:* * The proofs for Theorem 3.1 and Lemma 3.2 can be made significantly shorter with the simple observation that $a \odot b = diag(ab^T)$ when $a$ and $b$ are vectors. Then the proofs become single line. * Typos:** * $v^*$ vs. $v^H$ usage is not consistent. Questions For Authors: 1) Authors mention that "... even if global metrics indicate high reconstruction quality, a locally elevated noise variance in diagnostically relevant ROIs could compromise clinical interpretation.". Is there a concrete example of such a case? How is this work alleviating the issue? While I understand the interpretation of the noise maps as uncertainty quantification, my main concern is that this work does not go beyond trying out existing matrix sketching ideas in the context of MRI reconstruction. 2) How does sketching with random-phase vectors compare against random Gaussian vectors? In practice do you observe significant enough difference in the estimation error? 3) Why is the noise map in Figure 6 for the MoDL method look significantly different than the others? 4) Are there bounds on the sketching error? How does it depend on the properties of the linear operator and the Jacobian? Code Of Conduct: Affirmed. Overall Recommendation: 2	Rebuttal 1: Rebuttal: Thank you for your thoughtful review, and valuable feedback which we believe significantly enhanced our work. We addressed your valuable suggestions, and clarifed of our novelty and contributions. ## 1. Novelty and Technical Contributions We respectfully disagree with the assertion that our paper merely reuses existing matrix-sketching techniques. Our work introduces three key innovations: 1. We provide the first rigorous, first-principles derivation of how k-space acquisition noise propagates through both the MRI physics model and nonlinear DL networks. Prior approaches have largely relied on Monte Carlo sampling—computationally expensive and lacking interpretability. Instead—our approach yields a scalable, interpretable solution with mathematical transparency grounded in imaging and statistical theory. 2. We show that exact voxel-wise variance requires the full network Jacobian—computationally intractable in MRI. Our key innovation is a statistically rigorous unbiased estimator that efficiently approximates this covariance without explicitly forming the Jacobian. Crucially, we handle complex-valued signals, multi-coil encoding, physics-based forward models, and deep networks simultaneously—the first viable approach for quantifying acquisition-induced uncertainty in deep MRI reconstruction. 3. We implement our estimator via an efficient and practical matrix sketching algorithm that probes the Jacobian with random-phase vectors. Our method leverages Jacobian-vector products, enabling fast, memory-efficient uncertainty quantification at scale, while being DL model agnostic. In practice, this removes a major bottleneck in bringing noise-aware reconstruction into clinical and research pipelines. This suite of theoretical, algorithmic, and applied innovations represents a substantive advancement in uncertainty quantification for DL-based MRI. ## 2. Motivation for Noise Variance Calculation We appreciate the reviewer’s concern and agree that the clinical motivation for voxel-wise noise variance estimation merits clarification. Voxel-wise noise variance estimation is crucial in MRI because global metrics can obscure significant localized noise variations that impact diagnosis [1-3,8]. Studies show that localized noise impedes detection of subtle pathologies despite good global quality metrics [3,7]. Rubenstein et al. demonstrated that cartilage defects remain undetected with insufficient local SNR, even when global metrics appear acceptable [2]. Furthermore, global SNR and CNR don't consistently correlate with diagnostic accuracy [8]. This issue is particularly relevant in deep-learning MRI reconstructions, where spatially varying noise profiles create diagnostic uncertainties that global metrics fail to capture [4-7]. Our method efficiently provides accurate spatially resolved noise variance maps that highlight regions with elevated uncertainty, enabling radiologists to review diagnostically vulnerable areas and supporting better clinical decisions [6,7]. For additional evidence, we refer to 2. Utility of Noise Variance Estimation on Downstream Tasks in our response to reviewer viwd. [1] Sijbers, MRI, 1998 [2] Rubenstein, AJR, 1997 [3] Lerski, MRI, 1993 [4] Dou, NMR, 2025 [6] Kiryu, Radiographics, 2023 [7] Knoll, MRM, 2020 [8] Ohlmann et al, Br J Radiol, 2016 ## 3. Ablation Study on the choice of probing vectors Thanks to your valuable inquiry, we now conducted an ablation study, and found that our theoretical findings (Appendix D) match with new empirical findings; Proposed random-phase vectors (test set NRMSE of 0.7 for knee, 0.5 for brain) yields lower errors than their Gaussian counterparts (1.1 for knee, 0.8 for brain), indicating lower estimator variance. ## 4. Length of proofs We thank the reviewer for suggesting the identity to streamline our proofs. Applying this improved the brevity and conciseness. ## 5. Missing citations We kindly refer the reviewer to rebuttal for reviewer q9G3 for discussions on 1. Extended Related Work and Clarification of our contributions, including Edupuganti et al. (2020) and Wen et al. (2024). ## 6. Error Bound for Diagonal Estimator Our estimator $r_m(\Sigma_x)$ (using $m$ complex random-phase sketches) satisfies: $$ \\|r_m(\Sigma_x)-\operatorname{diag}(\Sigma_x)\\|_2 \leq c\sqrt{\tfrac{\ln(2/\delta)}{m}}\\|\overline{\Sigma}_x\\|_F\quad\text{(w.p.}\geq 1-\delta)$$where $\overline{\Sigma}_x=\Sigma_x-\operatorname{diag}(\Sigma_x)$. - Error scales as $\mathcal{O}(1/\sqrt{m})$ with $\\|\overline{\Sigma}_x\\|_F$. - Large $\\|A^H\\|$ or $\\|J_f\\|$ increase off-diagonal coupling, amplifying $\\|\overline{\Sigma}_x\\|_F$; well-conditioned systems reduce it. (Proof in revised manuscript.) ## 7. We hypothesize that distinct MoDL noise map reflect coil geometry and undersampling patterns via the iterative CG data-consistency step, rather than being driven by image features. ## 8. - $()^$: Complex conjugation for scalars - $()^H$: Hermitian operator for matrices --- Rebuttal Comment 1.1: Comment: I would like the thank the authors for their thorough responses. Some of my concerns and questions are alleviated. Please see below for further questions, comments and clarification: 1) Unfortunately I will have to challenge the claims about technical contribution to some extent. I agree with the authors that the work provides a rigorous derivation of how k-space acquisition noise propagates through both the MRI physics model and nonlinear DL networks. In that sense, it is a novel application of matrix sketching tailored towards noise variance estimation in MRI reconstruction setting (which I have acknowledged before). The extent of technical contributions, however, is still mostly limited to crafting the correct matrix to sketch in my opinion (which turns out to be $J_f A^H \sigma_k$). That said, I think that I was unfairly harsh in my initial review. The introduction of random complex phase vectors suits the particular problem nicely and the recent ablation study provided by the authors demonstrate its effectiveness. I will revise my score to 2 for now to reflect this change. 2) Thank you for your explanation on why estimating noise variance is an important problem. I appreciate the problem setting more now. 3) Thank you for ablating the choice of probing vectors. Previously it was not obvious to the reader how much better Rademacher probing vectors would be compared to Gaussian counterparts. The ablation suggests there is quite a bit of a gap. 4) Could you please provide the proofs for the error bound? I couldn't find it in the PDF (not sure if it is already revised). If not, could you provide it in an anonymous link? 5) Re notation consistency: I would like to apologize from the authors. In line 194, I misread it as $vv^$ thinking * is used instead of H. --- Reply to Comment 1.1.1: Comment: We sincerely thank the reviewer for carefully revisiting their assessment and for acknowledging that our rebuttal effectively addressed their original concerns. Regarding the theoretical error bounds and their proof, since manuscript updates were not permitted during the rebuttal stage, we now provide the requested detailed proof (which will be included upon publication) via the following anonymous link: [Proof](https://limewire.com/d/LYgcm#8XBN1vNcEu) Finally, we would like to further clarify our technical contributions, especially regarding the notion that our method’s novelty primarily lies in "crafting the correct matrix to sketch." Our work did not originate with the premise of tensor sketching. Instead, our estimator arose organically from rigorous first-principles derivations based explicitly on multi-coil MRI physics, complex-valued Fourier transforms, correlated noise modeling, and the nonlinearities inherent in deep-learning reconstruction architectures. It was only after establishing a robust theoretical foundation and confronting the computational complexities posed by our high-dimensional data (k-space: $2\times16\times384\times384$, images: $2\times384\times384$, covariance and Jacobian matrices of dimension $(2\times384\times384)^2$) that we turned to scalable computational methods. To address this significant computational barrier, we recognized the potential of leveraging Jacobian-vector products (JVPs) efficiently provided by modern deep learning frameworks. This insight led us to innovatively implement our estimator as a form of tensor-sketching approach, effectively harnessing JVP for computational efficiency and memory scalability. Thus, we did not simply select or "craft" a convenient matrix to sketch; rather, our final formulation emerged naturally as a necessary step to make the theoretically sound estimator practically scalable. Furthermore, this practical realization itself is a substantive technical advance. Our estimator achieves at least an order-of-magnitude computational speed-up compared to traditional Monte Carlo methods, avoids excessive memory overhead from storing multiple reconstructed images, and provides unbiased voxel-wise noise variance estimates scalable to large clinical imaging problems. We believe these practical gains directly addresses longstanding computational and interpretability bottlenecks in noise quantification for deep MRI reconstructions. We further highlight that many successful matrix-sketching works, particularly in the context of high-dimensional data, involve not just choosing matrices to sketch, but rigorously deriving these matrices from domain-specific knowledge and demonstrating their statistical and practical effectiveness. This is exactly what we have done here by synthesizing multi-coil MRI physics, Fourier transforms, undersampling, and deep-learning reconstruction theory. While sketching methods have appeared in the ML literature primarily to accelerate optimization or approximate matrix factorizations, as noted in our original Related Work section, prior studies typically consider significantly simpler scenarios. These include simpler settings-MLP architectures or convex optimization problems [1,2] or/with lower-dimensional matrices [4,5], often assuming pre-sketched observations readily available [3,6]. In stark contrast, our work rigorously derives and enables explicit noise propagation through large-scale, complex-valued convolutional neural networks that incorporate iterative, physics-driven data-consistency operations—a setting previously unaddressed by existing sketching methods. Furthermore, we provide detailed practical instructions on performing this high-dimensional sketching efficiently, filling a critical gap between theoretical concepts and applied implementation. Taken together, we believe our approach bridges theoretical insights from numerical linear algebra and machine learning (tensor-sketching) with practical computational solutions for complex medical imaging problems (MRI reconstruction). This enables accurate estimation of voxel-level uncertainty unprecedented scale, thus offering substantial advancements relevant to both tensor sketching and MRI reconstruction communities. [1] Pilanci, M., Iterative Hessian Sketch: Fast and Accurate Solution Approximation for Constrained Least-Squares. JMLR 2016 [2] Fishkov, A. Scalable Computation of Prediction Intervals for Neural Networks via Matrix Sketching. arXiv (2022). [3] Bahmani, S. Sketching for Simultaneously Sparse and Low-Rank Covariance Matrices. Proceedings of Asilomar Conference. 2015 [4] Lopes, M. E., Bootstrapping the Operator Norm: Error Estimation for Randomized PCA and Covariance Matrix Sketching. Annals of Statistics. 2022 [5] Woodruff, D. P. Sketching as a Tool for Numerical Linear Algebra. Foundations and Trends in Theoretical Computer Science. (2014) [6] Sesia, M. Conformal Frequency Estimation with Sketched Data. JMLR (2022)	null	null	null	null	null	null	null	null
NeuralCohort: Cohort-aware Neural Representation Learning for Healthcare Analytics	Accept (poster)	Summary: The paper proposes NeuralCohort, a cohort-aware neural representation learning method for healthcare analytics. It introduces two modules: (1) a Pre-context Cohort Synthesis Module to derive fine-grained cohorts via pseudo patient similarity, and (2) a Biscale Cohort Learning Module to integrate intra- and inter-cohort information. The method is evaluated on EHR datasets (MIMIC-III, MIMIC-IV, Diabetes130) for tasks like hospital readmission and length-of-stay prediction, demonstrating performance gains of up to 8.1% in AUROC when integrated with backbone models like ClinicalBERT and Med2Vec. Claims And Evidence: The claims are partially supported by experiments showing consistent improvements over baselines. However: Problematic Claim: The assertion that NeuralCohort "simultaneously fulfills fine-grained cohort division and information exploitation" lacks direct validation. While ablation studies show performance drops when modules are removed, there is no qualitative analysis of cohort granularity or clinical interpretability. Unjustified Choices: Hyperparameters (e.g., $\lambda_{p e s}$ =0.1) and cohort derivation methods (e.g., Jensen-Shannon divergence) are not rigorously justified. Sensitivity analyses for these parameters are missing. Methods And Evaluation Criteria: Methods: The hierarchical modeling of EHR data (diagnoses, medications, lab tests) and pseudo-similarity training are appropriate for temporal healthcare data. However, the cohort derivation process is under-detailed, and the reliance on pseudo-labels (without validation against expert annotations) is a limitation. Evaluation: Standard tasks (readmission, LOS) and metrics (AUROC, AUPRC) are well-chosen. However, baselines like KNN and K-Means are outdated; comparisons with recent methods (e.g., contrastive learning or graph-based models) are missing. Theoretical Claims: Lack of theoretical proof. Experimental Designs Or Analyses: Verified: The ablation study (Table 3) confirms the contribution of each module. The consistent gains across datasets (Tables 1–2, 8–11) support generalizability. Issues: The cohort visualization (Figure 8) lacks clinical context (e.g., what distinguishes the cohorts in practice?). Supplementary Material: Yes, Code. Relation To Broader Scientific Literature: The work connects to EHR representation learning (e.g., Med2Vec, ClinicalBERT) and patient similarity research. However, it overlooks recent advances: Missing References: Temporal graph networks (e.g., TGN) for dynamic EHR modeling, contrastive learning frameworks (e.g., SimCLR) for patient similarity. Gaps: No discussion of how NeuralCohort compares to dynamic cohorting methods (e.g., longitudinal clustering). Essential References Not Discussed: See Relation To Broader Scientific Literature Above Other Strengths And Weaknesses: pros: S1: Novel integration of cohort dynamics into neural representation learning. S2: Modular design compatible with diverse backbones. S3: Rigorous evaluation across multiple datasets and tasks. cons: W1: Limited novelty. This work only makes incremental modifications based on GRASP. I believe that GRASP's network architecture is also capable of utilizing both local intra-queue information and global inter-queue information, ultimately extracting comprehensive queue information. W2: Lack of interpretability analysis for generated cohorts (e.g., clinical relevance). W3: Incomplete baseline comparisons (e.g., state-of-the-art graph models). W4: Insufficient details on cohort derivation and hyperparameter sensitivity. Other Comments Or Suggestions: N/A Questions For Authors: Q1: Were ROC-AUC improvements statistically significant (e.g., via bootstrapping or permutation tests)? Q2: How were hyperparameters (e.g., learning rate, dropout) selected during fine-tuning? Q3: How do confounding factors (e.g., medication use) explain inverse lab test correlations (e.g., LDL)? Code Of Conduct: Affirmed. Overall Recommendation: 2	Rebuttal 1: Rebuttal: Thanks for the detailed reviews. This is the link to our supplemented results: https://anonymous.4open.science/r/ICML2025-93F9. Q1: Lack validation of fine-grained cohorts. No qualitative analysis of cohort granularity or interpretability; visualizations lack clinical context. In practice, clinicians typically use coarse-grained cohorts (Sec. 4.4), making fine-grained grouping like that in Appx. K difficult to define manually. NeuralCohort enables the automatic discovery of such cohorts and identifies key features for clinical insight and decision support. Please refer to Appx. K, Q1, Q2 of Reviewer 6GpW and Q2 of Reviewer 8wHJ for the distinctive features of cohorts on three datasets. Q2: Hyperparameter and cohort derivation choices lack justification; no sensitivity analysis or tuning details. We conducted sensitivity analysis (Tables F and C), varying one hyperparameter at a time while keeping others fixed. JS divergence outperformed KL. The optimal values are: $\lambda_{pcs}$=0.1, $\lambda_{JS}$=0.1, $\lambda_{co}$=0.1, dropout=0.1, and learning rate=1e-3. When training, dropout is set to 0.1, and the setting of other parameters is shown in Appx. G. Q3: Cohort derivation lacks detail, and reliance on pseudo-labels without expert validation is a limitation. Please refer to Q3 of Reviewer 8wHJ for cohort derivation details. Pseudo-labeling is widely used in representation learning[1], especially in EHR, where manual labeling is costly and impractical. Expert-defined similarity requires extensive clinical review, which is challenging at scale. Our method remains flexible and can incorporate expert input in future semi-supervised or clinician-in-the-loop settings. Q4: Baselines are outdated; recent methods and references are missing. No comparison to temporal graph models, contrastive learning, or dynamic cohorting approaches. We briefly discuss related methods and will expand in revision. TRANS[2] models EHR as a temporal heterogeneous graph to capture both temporal and structural information. SimSig[3] uses a contrastive learning approach to learn similar embeddings of patients with physiological signal data. Longitudinal K-Means[4] presents K-Means approaches for subtyping opioid use trajectories from EHR data and interprets the resulting subtypes using decision trees. We clarify that temporal graph networks for EHR modeling are complementary to our method and could serve as backbones rather than baselines. Comparisons with SimSig and Longitudinal K-Means in Table G show they underperform our method. Q5: Limited novelty; the method appears to be an incremental extension of GRASP, which may already capture both local and global cohort-level information. Unlike GRASP's flat KNN graph, NeuralCohort introduces a distinct, bi-level architecture that explicitly models both intra-cohort and inter-cohort structures through dedicated modules. This enables fine-grained cohort discovery and more effective cohort-aware representation learning. Unlike GRASP, NeuralCohort integrates medical semantics into the learning process, which our experiments show leads to more stable performance—whereas GRASP may degrade backbone performance due to less clinically grounded similarity signals. Q6: Were ROC-AUC improvements statistically significant? We evaluate AUROC difference with MIMIC-III dataset on long LOS task in Table H, showing statistically significant improvements. Q7: How do confounding factors explain inverse lab test correlations? Counterintuitive correlations, such as low LDL linked to worse outcomes, may result from confounding factors like medication use. Patients with low LDL often have prior cardiovascular risk and are treated with statins, making low LDL a marker of treated high-risk status rather than low risk. NeuralCohort captures such latent clinical structures by modeling intra-cohort similarities and inter-cohort differences. For instance, it can distinguish between statin-treated high-risk patients and untreated low-risk individuals, offering more clinically meaningful stratification than models treating patients independently. Please refer to Appx. K, Q1, Q2 of Reviewer 6GpW and Q2 of Reviewer 8wHJ for practical applications. [1] Xi, Liang, et al. "Semi-supervised time series classification model with self-supervised learning." Engineering Applications of Artificial Intelligence 116 (2022): 105331. [2] Chen, Jiayuan, et al. "Predictive modeling with temporal graphical representation on electronic health records." IJCAI: proceedings of the conference. Vol. 2024. 2024. [3] Shanto, Subangkar Karmaker, et al. "Contrastive Self-Supervised Learning Based Approach for Patient Similarity: A Case Study on Atrial Fibrillation Detection from PPG Signal." arXiv preprint arXiv:2308.02433 (2023). [4] Mullin, Sarah, et al. "Longitudinal K-means approaches to clustering and analyzing EHR opioid use trajectories for clinical subtypes." Journal of biomedical informatics 122 (2021): 103889.	Summary: This paper introduces the NeuralCohort framework, a novel method for neural cohort generation and selection based on two distinct strategies that model and generate (local) intra- and (global) inter-cohort information using a pre-context synthesis module employing pseudo similarity and a biscale cohort learning module to fuse and predict downstream classification tasks. Claims And Evidence: The authors provide interesting experiments and ablation studies for NeuralCohort. Firstly, they claim and demonstrate that NeuralCohort can consistently perform with different backbone neural architectures in their experiments and can outperform current state-of-the-art embedding/clustering methods for two classification tasks, namely "cross-visit Hospital Readmission Prediction" and "within-visit Long Length-of-Stay". This empirically supports their claim that NeuralCohort is a strong encoding/feature aggregation method. Methods And Evaluation Criteria: All architectural design considerations are properly introduced with mathematical formulation. While the formulations fundamentally make sense, some of the decisions "Hierarchical Visit Engine" or "PseudoSim Training" are not adequately motivated. It is hard to understand what other possibilities have been tested in related literature and why the authors believe that this constitutes the best and/or most robust method to model the discussed concept. For instance, how would a contrastive learning approach such as SimCLR [1] help or impede the modeling compared to the PseudoSim Training? For instance, it is unclear to me if this architectural design choice is something that works well for the two datasets used in this study or if it is clinically meaningful in other studies, such as Multiple Sclerosis research. I also find it very hard to understand - based on the manuscript and not the codebase - the intermediate steps of the framework and the dimensionality of different feature spaces. This makes it hard to assess if the evaluation of experiments is fair and how baseline algorithms have been tuned or if the experimental design is posed in a way that favors NeuralCohort. [1] Chen T, Kornblith S, Norouzi M, Hinton G. A simple framework for contrastive learning of visual representations. InInternational conference on machine learning 2020 Nov 21 (pp. 1597-1607). PmLR. Theoretical Claims: The manuscript includes no novel proofs but mathematical formulations of architectural design choices. Experimental Designs Or Analyses: The authors provide two experiments on three different datasets with three different backbones, which makes the case that their method works reliably and is adaptable to other backbones. As mentioned previously, it is hard to understand from the main paper/appendix which dimensions feature spaces span, how the authors derive the number of clusters for their experiments, and how architectural design choices (e.g. cluster number) affect the baseline methods. I have read the interesting ablation study in the Appendix. Still, to me, it is not ultimately clear how the baseline methods were tuned (if they were tuned) and how robust the baselines are across a parameter set. While the paper claims to provide a method for cohort generation, it is validated on two downstream segmentation tasks that serve as a proxy for this problem. While I am unaware of a better experiment/task to demonstrate it, I believe this is a bit suboptimal to support the claims. Supplementary Material: I have read the entire supplementary material. Relation To Broader Scientific Literature: The authors claim that NeuralCohort is (one of the) first methods to look into cohort selection apart from traditional methods used by clinicians and in clinical studies. They correctly set their work into the context of neural clustering algorithms, which they also use as baselines. I feel the methods section could explain more about why the authors have decided to model certain relationships the way they have decided to do and how they ground this in prior work. Essential References Not Discussed: I have not found any relevant papers that the authors have missed. Other Strengths And Weaknesses: Strengths: - I would like to highlight that the authors have already shared their code in the reviewing phase. Weaknesses: - To me this paper lacks details regarding how to use NeuralCohorts for other datasets and the intended use case - the formation and selection of cohorts in studies. Other Comments Or Suggestions: N/A Questions For Authors: - How do you typically select hyperparameters such as a positive number of pairs for PseudoSIM for Neural Cohorts? - How were they selected for this paper's experiments? Given the variability of the ablation study in the appendix, are the results in the reported tables the best-case scenario? - Were the number of clusters empirically selected for Figure 8, Supplementary Material? How do the plots look for a different number of clusters ? Given that the performance of NeuralCohort in your experiments is better than baselines but not always by a high margin, I am surprised to see such distinct cluster in comparison. - Did you assess features in the neural cohort clusters? Are they medically meaningful, which would be significant considering that it should be used in medical cohorts? Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We appreciate your insightful comments. This is the link to our supplemented results: https://anonymous.4open.science/r/ICML2025-93F9. Q1: The possibilities of techniques. How would SimCLR help? Key components like reverse-time attention and mutual information have been validated in prior work (e.g., RETAIN[1], FASTDeepHit[2]). While other architectures are possible, our choice achieves SOTA performance, generalization, and interpretability. Many of the components are orthogonal to our primary contribution so NeuralCohort can readily incorporate more advanced alternatives as they become available. SimCLR, where we randomly mask EHR to construct positive pairs, degrades performance as shown in Tables D and E. The reason lies in SimCLR is designed for image data, where augmentations like cropping retain semantic meaning. In EHR, creating label-preserving augmentations is more challenging considering the complex medical semantics of EHR. Q2: Method only works well for the two datasets? How to use NeuralCohorts for other datasets? NeuralCohort is tailored for EHR data and suitable for domains where subpopulation patterns are important, such as diabetes or Multiple Sclerosis. We evaluate NeuralCohort on Diabetes130 dataset (Appx. I), with clinical insights detailed in Q2 of Reviewer 6GpW. We have done the clinical application on Multiple Sclerosis dataset. The distinctive features are listed in Table B. Cohort #1 shows early neurological abnormalities. They should be prioritized for early initiation of DMTs and placed on close clinical surveillance schedules. Hospitals and neurology departments should ensure these patients have expedited access to high-resolution neuroimaging, neurologist consultations, and structured follow-up. Cohort #2 shows slower progression and may follow atypical paths. A conservative management approach with lifestyle interventions is suitable. Operationally, they can be monitored in outpatient settings with less frequent MRI, reserving resources for higher-risk patients. Patients in Cohort #3 display minimal abnormalities, indicating a stable, low-risk, or non-converting group. The optimal strategy for managing this cohort involves conservative care focused on patient reassurance, symptom education, and minimal intervention unless clinical deterioration is observed. Cohort #4 includes younger patients with positive LLSSEP and VEP, suggesting early subclinical neurological involvement despite low EDSS scores. This profile signals elevated risk for MS conversion. Clinical strategies should focus on prevention through lifestyle counseling, low-risk DMTs, and regular monitoring. Besides, this group warrants access to early neurology resources and is well-suited for clinical trials aimed at delaying progression before disability develops. Q3: Which dimensions feature span, how to derive the number of clusters, the number of pairs, and how the baselines were tuned? The dimensions of embedding for diagnosis, medication and laboratory test, visit and patient are 128, 64, 64, 128 and 128. The dimensions of $\mathcal{R} _ 0$, $\mathcal{R} _ L$, $\mathcal{R} _ G$, $\mathcal{R} _ {final}$ are the same dimension as the setting of the backbone. We use Student's t-distribution as a soft assignment function to map patient to cohort, computing similarity via a t-kernel to produce normalized soft assignments. The number of clusters determines the number of centroids and is initialized using KMeans. A sensitivity study on cohort number and pair numbers is provided in Appx. H. All experiments are repeated five times, and the average results are reported. The following protocol is used to ensure fair comparisons. We followed the original papers' recommended hyperparameters or adopted defaults from the official implementation when tuning details were unavailable. To ensure fairness, shared hyperparameters—such as the number of cohorts or clusters—were kept consistent across all methods. Q4: It is a bit suboptimal to support the claims. We explicitly address four key aspects: improved task performance (Sec. 4.2, Appx. I), CH-score for similarity evaluation (Sec. 4.5), t-SNE visualizations of cohort (Sec. 4.5), and clinical validation on MIMIC-III (Appx. K) and Diabetes130 (Q2, Reviewer 6GpW), which could validate the generated cohorts. Q5: How does Figure 8 look for a different number of clusters? The number of clusters is chosen to support clear visualization. Below, we present results for 6 and 10 clusters in Figure A and Figure B. While some baselines form clusters, they lack clear boundaries, whereas NeuralCohort produces more distinct groupings. [1] Choi, Edward, et al. "Retain: An interpretable predictive model for healthcare using reverse time attention mechanism." Advances in neural information processing systems 29 (2016). [2] Do, Hyungrok, et al. "Fair survival time prediction via mutual information minimization." Machine Learning for Healthcare Conference. PMLR, 2023.	Summary: This paper proposes NeuralCohort, a cohort-aware neural representation learning method for healthcare analytics. The approach segments patients into fine-grained cohorts and captures both intra- and inter-cohort information through a two-module paradigm. Claims And Evidence: The paper presents a well-supported evaluation of its method using multiple EHR datasets, demonstrating performance improvements. However, it lacks clear evidence on how cohort insights translate into clinical interventions. Methods And Evaluation Criteria: The methodology integrates existing techniques (hierarchical modeling, GNNs, contrastive learning) without introducing fundamentally new innovations. Theoretical Claims: NA Experimental Designs Or Analyses: The experimental setup has no significant methodological flaws identified. However, the study would benefit from demonstrating practical applications beyond the MIMIC dataset. Supplementary Material: I have read the appendix. Relation To Broader Scientific Literature: NA Essential References Not Discussed: NA Other Strengths And Weaknesses: The paper's strength lies in its comprehensive evaluation across multiple EHR datasets, demonstrating consistent performance improvements when integrated with existing backbone models. I do not find significant methodological or experimental flaws in the study. However, my primary concern is the novelty of the approach. The method appears to be an integration of existing techniques—hierarchical modeling, graph neural networks, and contrastive learning—rather than introducing fundamentally new methodological innovations. Both the core idea and the task itself are not particularly novel compared to existing work, especially given the extensive exploration of similar tasks on the MIMIC dataset. Additionally, it remains unclear how the proposed work and the insights derived from cohort segmentation translate into tangible clinical interventions or improved patient management strategies. I suggest that the authors clearly articulate what is conceptually novel beyond the integration of existing techniques. Moreover, providing concrete examples of how the identified cohorts could inform specific clinical decisions or extending the application beyond standard prediction tasks—already well-studied on MIMIC datasets—would strengthen the contribution of this work. Other Comments Or Suggestions: NA Questions For Authors: NA Code Of Conduct: Affirmed. Overall Recommendation: 2	Rebuttal 1: Rebuttal: Thanks for your constructive feedback. This is the link to our supplemented results: https://anonymous.4open.science/r/ICML2025-93F9. Q1: Lack clear evidence on how cohort insights translate into clinical interventions. Please refer to Appx. K for detailed analysis. To be more specific, Cohort #1 includes patients with cardiovascular conditions and is at high risk for acute cardiac events and extended hospital stays[1]. Early identification enables the prioritization of telemetry beds, cardiology consults, and monitoring. Clinically, this enables timely diuretics, echocardiography, and discharge planning with heart failure follow-up. Cohort #2 features patients with chronic metabolic and hematologic conditions that often co-occur and need interdisciplinary care. Identifying this cohort allows hospitals to mobilize diabetes educators, lipid clinics, and anticoagulation monitoring services. Clinically, it enables insulin titration, lipid therapy, and bleeding risk management to reduce complications and improve outcomes. Cohort #3 is characterized by renal and urological issues requiring frequent labs, fluid monitoring, and nephrology support. Early identification allows hospitals to allocate renal panels, schedule imaging for uropathy, and prepare dialysis resources—helping manage AKI risk and avoid care escalation. Cohort #4 presents complex chronic and acute conditions, requiring coordination across pulmonology, nephrology, endocrinology, and infectious disease. Identifying this cohort supports planning for respiratory support, hormone therapy, infection control, and opioid withdrawal. Operationally, it enables resource allocation for respiratory teams, isolation rooms, and endocrine/renal labs. Q2: Practical applications beyond the MIMIC dataset We evaluated NeuralCohort on a real-world Diabetes130 dataset, which is shown in Appx. I. We also analyze the practical application, similar to Appx. K but on the readmission task. The distinctive features are shown in Table A. Cohort #1 is characterized by longer hospital stays, insulin use, and frequent prior outpatient visits, indicating complex or unstable diabetes requiring intensive inpatient care. These patients often need time to stabilize their glucose levels, adjust medications, and manage comorbid conditions. They benefit from diabetes management plans, glucose monitoring, and endocrinology support. Hospitals should allocate extended-stay beds, involve diabetes educators, and initiate early discharge coordination. Close follow-up via outpatient care or telemedicine helps reduce readmission risk. Cohort #2 comprises low-acuity patients. Likely admitted for scheduled care or monitoring, they benefit from preventive care, education, and routine screening. Hospitals can streamline care using standardized protocols, fast-track discharge workflows, and minimal specialty consults, optimizing resource use for this stable cohort. Defined by a high rate of emergency admissions, younger age, and few prior inpatient visits, cohort #3 likely represents underserved or poorly engaged patients who rely on the ER for primary care needs. They may face social or behavioral health challenges. Interventions should focus on screening for social determinants, community referrals, and behavioral health support. Hospitals can prioritize care navigation and ER diversion efforts to reduce unnecessary admissions and alleviate emergency departments burden. Cohort #4 consists of high-risk, high-utilization patients. Tailored interventions should focus on intensive transitional care management, including medication reconciliation, post-discharge follow-ups within 48–72 hours, and multidisciplinary care planning. Hospitals can assign care managers, enroll patients in chronic care programs, and coordinate outpatient services to reduce readmissions and enhance long-term outcomes. Q3: Novelty of the approach. It should be noted that NeuralCohort is an application-driven ML submission targeting practical healthcare applications, where originality could mean "a novel combination of existing methods to solve the task at hand so as to match the needs of the user" rather than wholly novel methods[2]. Our key innovation lies in the cohort-aware representation learning framework, which explicitly disentangles and models both local intra-cohort and global inter-cohort structures — a perspective not addressed in prior work. Moreover, NeuralCohort not only enhances predictive performance but also yields clinically interpretable embeddings that align with real-world needs, such as intervention planning and resource optimization. [1] Tigabe Tekle, Masho, Abaynesh Fentahun Bekalu, and Yonas Getaye Tefera. "Length of hospital stay and associated factors among heart failure patients admitted to the University Hospital in Northwest Ethiopia." Plos one 17.7 (2022): e0270809. [2] https://icml.cc/Conferences/2025/ReviewerInstructions --- Rebuttal Comment 1.1: Comment: Thanks to the authors for their reply. I would stand for my score due to the limited novelty of the clinical tasks and insights. --- Reply to Comment 1.1.1: Comment: We sincerely thank the reviewer for further feedback. Below, we provide evidence and results to further clarify the insights derived from the cohorts. The observed differences in average length of stay (LOS) across cohorts, along with statistically significant p-values, support the presence of meaningful distinctions among them. A clinical specialist was consulted to provide guidance from a clinical research perspective, and has validated the distinctive cohort features, the associated intervention strategies, and the implications for resource optimization in Q1 on MIMIC-III dataset and Q2 on Diabetes130 dataset and Q2 of reviewer 8wHJ on Multiple Sclerosis dataset. \| Cohort Index \| Avg. LOS (days) \| Distinctive Features \|p-value\| \| ------------ \| --------------- \| ------------------------------- \|-\| \| Cohort #1 \| 11.2 \| HF, Arrhythmia, CHD, Angina \|<0.001\| \| Cohort #2 \| 6.4 \| Diabetes, DLM, CD, Obesity \|<0.001\| \| Cohort #3 \| 8.9 \| OUA, PSL, UF, F&E Disorders \|0.0012\| \| Cohort #4 \| 5.1 \| OPI, CKD, Thyroiditis, Flu \|<0.001\| Thanks for the feedback on the novelty. We would like to provide the following clarification to better highlight the novel contributions of our work. - We propose a general cohort-aware neural representation learning method, NeuralCohort to address the overlook of fine-grained cohorts and comprehensive cohort information exploitation. - To the best of our knowledge, we are the first to explicitly model both intra-cohort and inter-cohort information based on pseudo-medical-similarity semantics and encode them into augmented representations for downstream prediction tasks. - NeuralCohort is designed to be a flexible and modular plug-in that can be seamlessly integrated with various backbone models, enhancing their ability to capture cohort-specific insights and improve predictive performance. - We evaluate NeuralCohort on three real-world EHR datasets across two tasks and analyze the clinical insights for the generated cohorts. The experimental results demonstrate its effectiveness, and the cohort insights—validated by a clinical specialist—highlight its clinical interpretability and significance.	Summary: The paper proposes NeuralCohort -- a cohort-aware neural representation learning method designed to improve electronic health record (EHR) analysis. It addresses the challenges of fine-grained cohort segmentation and effectively utilizes both intra- and inter-cohort information. By incorporating the Pre-context Cohort Synthesis for pseudo patient similarity prediction task, and Biscale Cohort Learning modules to learn the intra- and inter- cohort interactions, NeuralCohort enhances existing models, boosting their performance. Its approach not only improves predictive accuracy but also provides valuable medical insights for EHR studies. Claims And Evidence: Yes Methods And Evaluation Criteria: Yes, the methods had been extensively tested on popular MIMIC-III, MIMIC-IV and Diabates130 datasets which are benchmarks for the EHR domain. Theoretical Claims: Yes mostly, did not go into details. Experimental Designs Or Analyses: The experiments are well designed to showcase the effectiveness of the approach. The suuplementary material has more addendum experiments. Supplementary Material: Yes, all. Relation To Broader Scientific Literature: Prior works have not sufficiently explored the cohort formulation for EHR tasks. Patient similarity has been tackled based on expert labellings and more recently cosine similarity between embeddings from EHR data. This work models patient's visit level representation to then model cohort interactions. It shows the worth of cohort studies. This could be useful for most downstream healthcare analysis tasks. Essential References Not Discussed: n/a Other Strengths And Weaknesses: Strengths - The ideas of modeling in 2 stage manner - first visit level then modeling the intra- and inter- cohort signals are novel. - The method is clearly effective and also interpretible which is a key consideration for healthcare domain. 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 thoughtful and encouraging review. We sincerely appreciate your recognition of NeuralCohort as a cohort-aware neural representation learning framework that effectively addresses the challenges of fine-grained cohort segmentation and the modeling of both intra- and inter-cohort relationships. We are especially pleased that you found the two-stage design — modeling at the patient visit level followed by biscale cohort learning — to be both novel and interpretable. Our goal is to not only improve predictive performance across benchmark EHR datasets such as MIMIC-III, MIMIC-IV, and Diabetes130, but also to provide clinically meaningful insights through interpretable cohort structures. Your support affirms the value of our approach for advancing cohort-based analysis in real-world healthcare applications. --- Rebuttal Comment 1.1: Comment: n/a	null	null	null	null	null	null
An in depth look at the Procrustes-Wasserstein distance: properties and barycenters	Accept (poster)	Summary: This paper defines a quotient space of discrtete measures over which PW is a distance and provides an estimation algorithm for the PW barycenter. This paper then shows that one of the main advantages of PW is its capability to produce very faithful barycenters in particular conditions. Experiments have verified its effectiveness in point cloud alignment and shape analysis, and its application in archaeological data shows the practical significance of the proposed method. ## update after rebuttal I appreciate the response provided in the rebuttal, which addresses some of my concerns, and I maintain the score. Claims And Evidence: yes Methods And Evaluation Criteria: yes Theoretical Claims: Yes, I don’t find any issues with the proofs for theoretical claims. Experimental Designs Or Analyses: The archaeological application experiment only shows the interpolation results. Are there some quantitative indicators to evaluate the results? Supplementary Material: I reviewed all parts of the supplementary material. Relation To Broader Scientific Literature: Procrustes Wasserstein (PW) was introduced in the literature as an optimal transport (OT) distance, alternative to Wasserstein and more suited to tasks such as the alignment and comparison of point clouds. This paper builds a space of discrete probability measures and shows that over that space PW actually is a distance. Essential References Not Discussed: No Other Strengths And Weaknesses: Strengths 1. This paper proves the distance property of PW distance on discrete measure quotient space. 2. This paper introduces the notion of PW barycenter. Weaknesses 1. Figure 1 lacks more explanation. The caption shows: OT barycenters using (a) Free Wasserstein (b) Gromov-Wasserstein with MDS (c) Gromov-Wasserstein with TSNE. However, (a-c) is not introduced in the paper. In addition, the caption should introduce what task this is, such as a matching task or another. 2. MDS and TSNE only have abbreviations, no references or full names are provided. 3. The archaeological application experiment only shows the interpolation results. Are there some quantitative indicators to evaluate the results? Other Comments Or Suggestions: As above Questions For Authors: As above Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: First of all, thanks for the kind remarks and for reviewing the paper and checking the supplementary. We provide in the following the answer to the specific questions. > 1-2. Figure 1 lacks more explanation. The caption shows: OT barycenters using (a) Free Wasserstein (b) Gromov-Wasserstein with MDS (c) Gromov-Wasserstein with TSNE. However, (a-c) is not introduced in the paper. In addition, the caption should introduce what task this is, such as a matching task or another. MDS and TSNE only have abbreviations, no references or full names are provided. We apologize for the lack of clarity regarding Figure 1. Below, we provide additional details about the experiment and include references to the MDS and TSNE methods, which were indeed missing from the text. Here is the new caption for Figure 1, which will be updated in the final version of the paper: “(Top) Two point clouds representing a bird shape in different positions. OT barycenters using (a) Exact Free Wasserstein [1] (b) Gromov-Wasserstein [2] with MDS [3] (c) Gromov-Wasserstein with TSNE [4] (d) Procrustes-Wasserstein.” In this motivational example, we compare different OT techniques for computing barycenters. The two point clouds at the top represent the input measures (depicting a bird shape, without and with noise, and in different positions). The techniques used in panels (a-d) are, respectively: exact Wasserstein barycenters [1], Gromov-Wasserstein barycenters [2] with two different visualization techniques, Multidimensional Scaling (MDS, [3]) and t-distributed Stochastic Neighbor Embedding (TSNE, [4]), and finally, the proposed PW method. The results highlight how the PW barycenter provides the clearest and most precise representation, even for local geometric structures. Additionally, the barycenters are colored by transporting the color of the first bird (top left) onto the computed barycenter. > 3. The archaeological application experiment only shows the interpolation results. Are there some quantitative indicators to evaluate the results? Thank you for this central question. Quantitative methods are available for the quantification of morphological deformations based on simplified morphological patterns in archaeology (e.g. geometric morphometric methods). However, no quantitative method exists that can be used with the entire 3D bone. Ensuring that the observed morphological deformations on the barycentre correspond to a biological reality based on archaeological data is a significant challenge. While acknowledging these challenges, we firmly believe that this preliminary approach signifies a significant opportunity for interdisciplinary research. References: [1] Cuturi, Marco, and Arnaud Doucet. "Fast computation of Wasserstein barycenters." International conference on machine learning. PMLR, 2014. [2] Peyré, Gabriel, Marco Cuturi, and Justin Solomon. "Gromov-wasserstein averaging of kernel and distance matrices." International conference on machine learning. PMLR, 2016. [3] Borg, Ingwer, and Patrick JF Groenen. Modern multidimensional scaling: Theory and applications. Springer Science & Business Media, 2007. [4] Maaten, Laurens van der, and Geoffrey Hinton. "Visualizing data using t-SNE." Journal of machine learning research 9.Nov (2008): 2579-2605. [5] Cuturi, Marco. "Sinkhorn distances: Lightspeed computation of optimal transport." Advances in neural information processing systems 26 (2013).	Summary: The paper proposes a method for aligning and matching point clouds based on Optimal Transport using the Procrustes-Wasserstein distance (PW), allowing the alignment to be calculated by also taking pose transformations into account. The paper shows that PW is indeed a distance in the space of discrete probability measures. It also introduces an algorithm to calculate the barycentres of the measures with respect to PW. The contribution is validated by showing how to initialise optimal transport, testing four main approaches on a synthetic dataset. The method is then tested for clustering on a subset of MNIST and compared with other Optimal Transport metrics. A final application shows how the method was crucial for tracing the morphological evolution of sheep based on astragalus alignments from the Chalcolithic period up to the modern age. Claims And Evidence: The claims of the article are: 1) Using PW, it is possible to encompass geometric transformations. Other articles have already proved this claim (we discuss this in another section). 2) The Procrustes-Wasserstein distance is a distance on the space of discrete probability measures, and this claim is proven in the supplementary. This claim is used to define the barycentres. 3) The calculation of the barycentres is relevant for obtaining clusters that take geometric transformations into account. The algorithm is as precise as the derivations that lead to its optimisation. I'm unsure if it is the first algorithm (as claimed in the introduction). The Frechet mean can actually be considered a barycentre of a discrete measure, and its computation was introduced by Zemel et Al. [1], referring to the OT (the authors do not cite the article). The last claim concerns the initialisation of $\Gamma_{0}$ or admissible transport plans. From the two pictures in Figure 2 and the comments in the text, it appears that only the Fiedler vector ensures convergence. However, it should be noted that the Fiedler vector only works if the Laplacian matrix is noise-free, as in the case studied, which is defined by a synthetic set. Thus, the problem of the initialisation of $\Gamma\_{0}$ remains open for real cases. [1] Zemel, Y. and Panaretos, V.M., 2019. Fréchet means and Procrustes analysis in Wasserstein space. Methods And Evaluation Criteria: Regarding the experiments, the article follows the literature somewhat (see, for example, Cuturi and Doucet) with no tables (here, only Table 1 to compare with other OT metrics) and only pictures without showing measures of similarities and failure values. Even for the main application, there is only one image. However, this is partly justified by the fact that the pictures serve as proof of concept, and the work is not experimental but more theory-oriented. Theoretical Claims: I checked. Experimental Designs Or Analyses: As specified above, I am critical about the initialisation of $\Gamma_{0}$. As shown in the paper, only with the Fiedler vector is convergence obtained at the minimum distance detecting $\Gamma_{0}$. However, the test was carried out on synthetic data and, thus, without noise. In the presence of noise, the Fiedler Vector does not separate the components correctly. Furthermore, the presupposition on the space of measures is very strong. As noted in Zemel [1] an optimal transport map may fail to exist, and instead, one may need to solve the relaxed Monge problem. Supplementary Material: Yes, I reviewed all the supplementary parts. Relation To Broader Scientific Literature: The article is well placed, it is definitely a contribution. However, the paper Aligning Embeddings and Geometric Random Graphs: Informational Results and Computational Approaches for the Procrustes-Wasserstein Problem' by Even et Al., appeared at Neurips 2024, which deals with the problem in a very general way. Although the authors limit their method to discrete measures, they should have mentioned this and, therefore, related their findings to the more general ones of Even et Al.* [2]. Indeed, this should be done in the revised version. Another limitation is perhaps not looking at the Frechet mean (e.g. Zemel's [1]). [2] Even, M., Ganassali, L., Maier, J. and Massoulié, L., 2024. Aligning Embeddings and Geometric Random Graphs: Informational Results and Computational Approaches for the Procrustes-Wasserstein Problem Essential References Not Discussed: Essential references not discussed have been highlighted in the previous paragraph. Other Strengths And Weaknesses: The article makes a simple and useful contribution but has to be compared with the works mentioned above. It has many limitations: 1. It is not well written; there are many spelling mistakes, which I point out in the next paragraph. 2. It is limited in its experiments. Perhaps it should have reduced the space for describing the application and compared the results better with the literature, see, for example, [3]. 3. The initialisation of $\Gamma0_{0}$ should have been analysed more deeply and with real examples. [3] Jin, K., Liu, C., and Xia, C. Two-sided Wasserstein Procrustes analysis. In IJCAI, pp. 3515–3521, 2021. (this paper was cited) Other Comments Or Suggestions: Some spelling errors (line:column) “062:1 the repeated twice" “96:2 discrtete” “112:1 matchin” “113: applicaton” “123:1 the the” “210:2 interative” “289:1 space.Morover” “325:2 calstering” “325:2 provide” “348:1 cluetsring” Questions For Authors: Please look into both Even's and Zemel's papers. You never mention algorithms for computing OT. For example, Cuturi & Doucet refer, in their Algorithm 3 Cuturi fast algorithm [Cuturi 2013] Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: First of all, thank you very much for the careful reading of the paper, as well as for the analysis and comments, they are truly appreciated. We have addressed all the grammatical errors identified in the text, and the corrections will be included in the final version of the paper. We also appreciate the suggestions regarding [Zemel et al., 2019] and [Even et al., 2024], which are now references in the main paper. However, while both studies align with the general problems discussed in our paper, they differ from the specific contributions presented in our work. Below, we provide a detailed discussion on the connections between our work and these references, along with responses to the specific points raised in the review. > 1. Relation to [Zemel et al., 2019]: It is true that the barycenter problem is, by definition, equivalent to computing the Fréchet mean. However, the work of [Zemel et al., 2019] aims to highlight the analogy between the Fréchet mean computation, i.e. barycenters, computed in the Wasserstein space and Procrustes analysis as methods for the “registration” of distributions. Unlike our work, [Zemel et al., 2019] does not minimize a Procrustes-Wasserstein cost, but rather a classical Wasserstein one. Specifically, is it worth to note that Algorithm 1 in [Zemel et al., 2019] consists of N pairwise OT computations, followed by a barycenter update performed directly in the Wasserstein space. We apologize if this distinction was not sufficiently clear in our manuscript. Our work directly addresses the PW problem, introducing the first formalization of PW barycenters along with a practical and efficient algorithm for their computation (Alg. 2). This approach is fundamentally different from [Zemel et al., 2019]. > 2. Relation to [Even et al., 2024]: The problem addressed in [Even et al., 2024] tackles the matching of pairs of distributions from a theoretical perspective, providing thorough results about the convergence of their ML estimates. However, it represents a special case of the more general Procrustes-Wasserstein problem which is approached in the current work. Indeed [Even et al., 2024] specifically considers distributions (pairs of point clouds) that have the same number of points; in their model, the signal only differs from the dependent point cloud by a permutation of the points plus an isometry, then Gaussian noise is added to each point. The OT problem they address corresponds thus to the Monge formulation of OT. In contrast, the problem approached in the current work generalizes to cases where the distributions may have different numbers of points (as can be also observed in the experiments we propose) thereby corresponding to the more general Kantorovich formulation of OT. We look for doubly stochastic solutions (i.e. transport plans), they look for permutation matrices. > 3. Initialization of $\Gamma_0$ We agree with you, the initialization of the Procrustes-Wasserstein matching in real-world scenarios remains an open challenge and addressing it is not the primary goal of our work. However, it is important to note that, differently from what you state, in the matching problem we tackled, noise is present in the Laplacian (although at a level such that the global geometric structure of the shape remains visible). As detailed in our section, the generated clouds $X^i_2$ (meant to be matched to the pivot $X$) also include Gaussian noise applied to each point of the pivot cloud and thus represent a perturbation of the pivot thus adding noise to the corresponding Laplacian matrices. We emphasize that the perturbations applied to the clouds $X^i_2$ are designed to simulate real data scenarios. However, the Wasserstein distance between Fiedler vectors can still find a good and sufficient matching, which can then be used as the initial $\Gamma_0$ for solving Alg. 1. > 4. “You never mention algorithms for computing OT.” We apologize for any lack of clarity in the text. Please refer to responses 2 and 3 to reviewer 6RWS for details. References : [1] Cuturi, Marco, and Arnaud Doucet. "Fast computation of Wasserstein barycenters." International conference on machine learning. PMLR, 2014. [2] Peyré, Gabriel, Marco Cuturi, and Justin Solomon. "Gromov-wasserstein averaging of kernel and distance matrices." International conference on machine learning. PMLR, 2016. [3] Borg, Ingwer, and Patrick JF Groenen. Modern multidimensional scaling: Theory and applications. Springer Science & Business Media, 2007. [4] Maaten, Laurens van der, and Geoffrey Hinton. "Visualizing data using t-SNE." Journal of machine learning research 9.Nov (2008): 2579-2605. [5] Cuturi, Marco. "Sinkhorn distances: Lightspeed computation of optimal transport." Advances in neural information processing systems 26 (2013).	Summary: This paper extends the Wasserstein barycenter to the Procrustes-Wasserstein (PW) barycenter, offering a novel approach to computing representative shapes from a collection of point clouds. Additionally, it provides a proof that the Procrustes-Wasserstein distance satisfies the properties of a valid distance metric. Claims And Evidence: The claims made in the submission are supported by clear and convincing evidence. Methods And Evaluation Criteria: Yes Theoretical Claims: I have checked the correctness that the Procrustes-Wasserstein distance satisfies the properties of a metric. Experimental Designs Or Analyses: Yes, it is soundness. Supplementary Material: It provides the code, and I have check otkmeans.py Relation To Broader Scientific Literature: Procrustes-Wasserstein (PW) barycenter is simple and interesting. Essential References Not Discussed: No Other Strengths And Weaknesses: The paper does not provide any convergence proof for the Procrustes-Wasserstein barycenter, which raises concerns about the theoretical guarantees of the proposed method. Additionally, it lacks an analysis of the computational complexity, which is crucial for understanding the feasibility and scalability of the approach. A detailed complexity analysis would help clarify the efficiency of the algorithm, especially in large-scale point cloud applications. Other Comments Or Suggestions: None Questions For Authors: 1. What is the convergence behavior of the proposed Procrustes-Wasserstein (PW) barycenter? 2. How does the performance change when replacing EMD with the Sinkhorn algorithm? 3. How does the computational complexity of PW barycenters compare to Gromov-Wasserstein (GW) barycenters in theory? 4. How about the performance in partial overlapping shape matching Ethics Expertise Needed: ['Other expertise'] Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Thanks for your kind remarks as well as for reviewing the paper and checking the correctness of the main proof. > 1. What is the convergence behavior of the proposed Procrustes-Wasserstein (PW) barycenter? Inspecting the convergence properties of the PW barycenters is a crucial homework and a very important topic. We are currently working on it, but we honestly believe that having introduced the PW barycenters might be enough for one paper. Moreover, we respectfully point out that the convergence behavior of OT barycenters is not reported in related papers such as (for instance) [1] and [2], both accepted at this conference. > 2. How does the performance change when replacing EMD with the Sinkhorn algorithm? The relevance of the proposed method for computing the barycenter also lies in the quality of the obtained solution, specifically in terms of local geometric details. However, as common in OT, an entropic penalisation can be introduced in the objective function to stabilize the solution and speed up computations. To this end, we conducted new experiments adopting the Sinkhorn algorithm in place of EMD for the pairwise OT computations (line 8 of Alg. 1) and denoted the corresponding barycenter method as Procrustes-Sinkhorn barycenter (PSb). In the camera ready version of the paper, we might dedicate an additional section to provide the formal definition of the regularized problem and the derivation of the update formulas. We exactly observed what is known from the literature: the entropic penalty can be used to stabilize the solution and speed up computations but it comes at a price. A higher $\epsilon$ (the strength of the penalty term) is required to have a faster convergence (see Table here after) but leads to less accurate, deformed barycenters. However, for ML pipelines where there is no need for such a high level of barycentric detail, PSb certainly represents a valuable option. \| \| PWb with EMD (Alg. 1) \| PSb ($\epsilon=10$) \| PSb ($\epsilon=1$) \| PSb ($\epsilon=0.01$) \| \|----------\|:-------------:\|:------------:\|:------------:\|:------------:\| \| Mean time & std. (s) \| 1.91 ± 0.14 \| 1.18 ± 0.26 \| 5.69 ± 1.73 \| 13.74 ± 1.12 Results over 10 barycenter computations (10 runs) considering two input measures of nearly 500 points (as in Figure 1). > 3. How does the computational complexity of PW barycenters compare to Gromov-Wasserstein (GW) barycenters in theory? Thanks for this question. In practical applications, the PW algorithm (Alg. 1) is dominated by the OT computation. Since the Procrustes update has an explicit formula and the dimension D is small (in our case 2 or 3), the cost of the Procrustes step is negligible. Thus, the main computational bottleneck remains the EMD computations, which scales as O(n3 log(n)) (or O(n^2) if one adopts Sinkhorn divergences) according to [3]. The algorithmic complexity of computing PW is thus O(Kn3(log(n)), where K is the number of iterations between the Wasserstein and the Procrustes optimisation (also the number of Ping-Pong steps in [Even et al. 24], with reference to answer to Review GNtQ). By direct analogy with Alg. 2 in [1], the computational complexity of the PW barycenter algorithm follows the same structure as that of Wasserstein barycenters, with the key difference that each Wasserstein update is replaced by a PW computation. The theoretical complexity of a PW barycenter in Alg. 2 is O(TNKn3log(n)) (respectively O(TNKn^2) with Sinkhorn divergences) where N is the number of input measures, n is the maximal number of points in the input clouds and T is the number of barycenter’s updates (line 7, Alg. 2) which are essentially equivalent to the ones of a Wassersetin barycenter and so negligible with respect to the PW updates. Noting that in all our experiments we set the maximum value of K to 100 and assuming this value as a constant << N, which is reasonable when working with real point clouds (thousands of points) the computational complexity of a PW barycenter is the same as the one of a Wassesrtain barycenter, obviously up to a constant. That complexity is smaller than those of GW barycenters (the simple evaluation of the GW$_2$ cost function, without considering the network flow algorithms to solve it, is at least cubic). References: [1] Cuturi, Marco, and Arnaud Doucet. "Fast computation of Wasserstein barycenters." International conference on machine learning. PMLR, 2014. [2] Peyré, Gabriel, Marco Cuturi, and Justin Solomon. "Gromov-wasserstein averaging of kernel and distance matrices." International conference on machine learning. PMLR, 2016. [3] Cuturi, Marco. "Sinkhorn distances: Lightspeed computation of optimal transport." Advances in neural information processing systems 26 (2013).	Summary: The authors propose that in the quotient space of the discrete measures over the rigid transformation equivalence, the Procrustes Wasserstein is a metric. To calculate the Procrustes Wasserstein distance, they introduce several initialization methods, i.e. Euc-GW, Geo-GW, Fiedler-W and UPCA-W. The barycenter problem and algorithms are also provided. Claims And Evidence: The claims are supported by evidence. Methods And Evaluation Criteria: Although the authors show the application of barycenter in tracking the morphological evolution of domestic animals, no comparisons are made with other existing methods, can you show the results by the baselines for morphological interpolations? Theoretical Claims: The proof for Theorem 2.1 and Corollary 2.2 are correct. Experimental Designs Or Analyses: Details of the experimental setup are provided. It would be better if the authors could provide the comparisons with baselines for morphological evolution applications, especially with the Gromov-Wasserstein methods. Supplementary Material: I checked the proof in appendix A and the additional experiments. Relation To Broader Scientific Literature: The proposed method could be applied to point cloud analysis where rigid transformations are prevalent but should not affect the comparisons. Essential References Not Discussed: N/A Other Strengths And Weaknesses: My main concern is the novelty of this work. The quotient space and metric properties are very incremental, and the methods for calculating the initial plan are based on previous methods. Other Comments Or Suggestions: N/A Questions For Authors: In Figure 1, can the authors comment on the gromov-Wasserestein results? Why would there be some outlier points? Code Of Conduct: Affirmed. Overall Recommendation: 1	Rebuttal 1: Rebuttal: Thanks for reviewing the paper and checking the proofs. We are quite disappointed by the gap between the assigned score (reject) and a review which sounds quite positive. We would appreciate further explanations on the concerns raised about lack of novelty: PW barycenters are new. However, we provide in the following detailed responses to the specific questions mentioned. > 1. Lack of comparisons with other methods The purpose of the archaeological section (S5) is not to propose a new morphological interpolation technique that outperforms the state of the art, but rather to demonstrate that in the OT univers, PW offers significant advantages compared with existing alternatives. In our archaeological application, the point clouds $X$ and $Y$ are approximately made of 10k points. At this scale, GW barycenters cannot be computed (well-known computational limitations). Nonetheless, we have conducted additional experiments by computing Wasserstein barycenters using the free support barycenters (FBS) method from the POT library, allowing for a comparison with the PW results shown in Figure 4. We will include these additional experiments in the appendix of the camera ready version of the paper. The computed Wasserstein barycenters can clearly be seen to be of lower quality, similarly to what is observed in Figure 1. Furthermore, we report below the corresponding objective functional values: Eq. (6) from our paper for PW barycenters, and Eq. (5) from [1] for the Wasserstein barycenters. The values for, respectively, the four interpolation steps are as follows: - Wasserstein (FBS): [0.00943, 0.01499, 0.01496, 0.00917] - PW: [0.00092, 0.00155, 0.00155, 0.00091] Our method achieves the lowest barycenter functional value for each interpolation step. > 2. In Figure 1, can the authors comment on the Gromov-Wasserstein results? Why would there be some outlier points? The GW barycenter is computed from pairwise distance matrices of size $N\times N$ and $M\times M$, where $N$ and $M$ correspond to the number of points in $X$ and $Y$, respectively. The barycenter itself is a $K\times K$ matrix (with $K$ fixed a priori) and must then be projected back into the original Euclidean space $\mathbb{R}^D$. In case of Figure 1, $D$ is set to 2. Dimensionality reduction techniques such as Multi-Dimensional Scaling (MDS, [3]) and t-Distributed Stochastic Neighbor Embedding (TSNE, [4]) can be used for this projection. However, this step can lead to suboptimal representations of the GW barycenter, even in simple cases such as the introductory example presented in Figure 1. We have made the caption of Figure 1 clearer in the final version of the paper (for more details please refer to the answer of Q1 for Reviewer HyoR). References: [1] Cuturi, Marco, and Arnaud Doucet. "Fast computation of Wasserstein barycenters." International conference on machine learning. PMLR, 2014. [2] Peyré, Gabriel, Marco Cuturi, and Justin Solomon. "Gromov-wasserstein averaging of kernel and distance matrices." International conference on machine learning. PMLR, 2016. [3] Borg, Ingwer, and Patrick JF Groenen. Modern multidimensional scaling: Theory and applications. Springer Science & Business Media, 2007. [4] Maaten, Laurens van der, and Geoffrey Hinton. "Visualizing data using t-SNE." Journal of machine learning research 9.Nov (2008): 2579-2605. [5] Cuturi, Marco. "Sinkhorn distances: Lightspeed computation of optimal transport." Advances in neural information processing systems 26 (2013). --- Rebuttal Comment 1.1: Comment: I appreciate the authors explaining the GW results in Figure 1, and acknowledge the contribution of propsing PW barycenter and algorithm. For comparisons in archaeological experiments, can the authors show the additional figure? Also, even when restricted to the OT universe, efficient alternatives include (but not limited to) the sliced Wasserstein barycenter [1,2], and the regularized Wasserstein Barycenter [3], deep Wasserstein embedding [4], sliced gromov Wasserstein [5], entropic gromov Wasserstein [6], and the low-rank arroximations [7]. I understand that it is not feasible to compare with all methods, but only one baseline is not enough. [1] Bonneel, Nicolas, et al. “Sliced and radon wasserstein barycenters of measures.” Journal of Mathematical Imaging and Vision 51.1 (2015): 22-45 [2] Liutkus, A., Simsekli, U., Majewski, S., Durmus, A., & Stöter, F. R. (2019, May). Sliced-Wasserstein flows: Nonparametric generative modeling via optimal transport and diffusions. In International Conference on Machine Learning (pp. 4104-4113). PMLR. [3] Iterative Bregman projections for regularized transportation problems. SIAM Journal on Scientific Computing, 37(2), A1111-A1138. [4] Courty, Nicolas, Rémi Flamary, and Mélanie Ducoffe. "Learning wasserstein embeddings." arXiv preprint arXiv:1710.07457 (2017). [5] Titouan, Vayer, et al. "Sliced gromov-wasserstein." Advances in Neural Information Processing Systems 32 (2019). [6] Justin Solomon, Gabriel Peyr´ e, Vladimir G. Kim, and Suvrit Sra. Entropic metric alignment for correspondence problems. ACM Transactions on Graphics (TOG), 35(4):72:1–72:13, 2016. [7] Scetbon, Meyer, Gabriel Peyré, and Marco Cuturi. "Linear-time gromov wasserstein distances using low rank couplings and costs." International Conference on Machine Learning. PMLR, 2022. --- Reply to Comment 1.1.1: Comment: Thank you for your comments. Please find here the figure showing the Wasserstein barycenters computed for the archaeological section: https://pasteboard.co/LIjfirL63O7T.png > _“only one baseline is not enough”_ We would like to emphasize that the main contributions of this paper lie in the new theoretical properties established for the PW distance, as well as in the novel barycenter formulation. As highlighted by Reviewer GNtQ, our experimental approach follows the OT barycenter literature. See for instance [8] with Wasserstein barycenters, and [9] introducing Gromov-Wasserstein barycenters, which focuses on qualitative evaluation through visual comparisons, without benchmarking. Nonetheless, we included Example 4.2 specifically to compare our barycenter with other state-of-the-art OT barycenters in a clustering scenario. > Barycenter comparisons Regarding the suggested references for the barycenter comparison, we would like to clarify that many of them are not directly applicable to the context of our application. Section 5 aims at finding barycentres and not at applying OT metrics for alignment, matching, etc. In order to present comparisons with other OT barycentres, we have computed (in the previous answer and shown in the above figure) the Wasserstein barycenters (Wb), which, however, do not represent a coherent bone structure. This follows naturally from the fact that the traditional Wasserstein problem is not invariant w.r.t. isometries in Euclidean space. Wb are thus unfit in cases of rotated and/or reflected distributions (bones in our application). [1] and [2] represent sliced variants (sWb) of the Wasserstein barycenter, which are again not invariant under isometries. sWb proved to be more computationally efficient than classical Wb, but often at the cost of geometric quality, particularly in local details. This effect can be seen also in Figure 6 of [1] with toy clouds. [3] involves entropic regularization via Sinkhorn iterations (regularized Wb), which indeed improves numerical stability but compromises the quality. In this regard, please also refer to our response to Question 2 of Review 6RWS for the formulation of Procrustes-Sinkhorn barycenters. [4] focuses on learning Wasserstein embeddings. The provided barycenters in [4] (e.g., mean of MNIST digits) are obtained via Euclidean averaging in a learned embedding space trained to approximate the Wasserstein distance. Furthermore, this embedding is not isometry-invariant. [5] introduces the sliced Gromov-Wasserstein distance (sGW). To the best of our knowledge sGW barycenters are not yet implemented in standard OT libraries such as POT, making comparisons nontrivial. However, it should be noticed that even in very simple scenarios such as the introductory example with birds, GW barycenters are subject to distortion. We clarified this in the previous answer. [6] focuses on non-rigid shape matching and [7] on the efficient calculation of GW distances. Both works do not define or study a notion of barycenter, which makes them less directly relevant to our analysis. To conclude and summarize, we respectfully point out that the list of references provided is almost entirely not relevant in terms of BARYCENTER comparison. We hope this clarifies. References: [1] Bonneel, Nicolas, et al. “Sliced and radon wasserstein barycenters of measures.” Journal of Mathematical Imaging and Vision 51.1 (2015): 22-45 [2] Liutkus, A., Simsekli, U., Majewski, S., Durmus, A., & Stöter, F. R. (2019, May). Sliced-Wasserstein flows: Nonparametric generative modeling via optimal transport and diffusions. In International Conference on Machine Learning (pp. 4104-4113). PMLR. [3] Iterative Bregman projections for regularized transportation problems. SIAM Journal on Scientific Computing, 37(2), A1111-A1138. [4] Courty, Nicolas, Rémi Flamary, and Mélanie Ducoffe. "Learning wasserstein embeddings." arXiv preprint arXiv:1710.07457 (2017). [5] Titouan, Vayer, et al. "Sliced gromov-wasserstein." Advances in Neural Information Processing Systems 32 (2019). [6] Justin Solomon, Gabriel Peyr´ e, Vladimir G. Kim, and Suvrit Sra. Entropic metric alignment for correspondence problems. ACM Transactions on Graphics (TOG), 35(4):72:1–72:13, 2016. [7] Scetbon, Meyer, Gabriel Peyré, and Marco Cuturi. "Linear-time gromov wasserstein distances using low rank couplings and costs." International Conference on Machine Learning. PMLR, 2022. [8] Cuturi, Marco, and Arnaud Doucet. "Fast computation of Wasserstein barycenters." International conference on machine learning. PMLR, 2014. [9] Peyré, Gabriel, Marco Cuturi, and Justin Solomon. "Gromov-wasserstein averaging of kernel and distance matrices." International conference on machine learning. PMLR, 2016.	null	null	null	null	null	null
Organize the Web: Constructing Domains Enhances Pre-Training Data Curation	Accept (poster)	Summary: This paper presents WebOrganizer, a method to construct, and annotate two sets of explainable and orthogonal domains (24 topics and 24 formats) with LLMs (e.g., Llama-3.1-405B-Instruct). The annotations are then approximated by a smaller (140M) model, making it scale efficiently to large corpora. It then employs the technique from RegMix to find the optimal domain mixture to optimize target performance by treating MMLU and HellaSwag as reference tasks. Experiment results show that the annotated domains can curate the pretraining data better than semantic clustering, and also augment quality-based filters to further improve the data curation outcome. Additionally, topic and format domains are basically orthogonal and complement each other. Analyses provide further insights into how quality-based filters implicitly change the domain mixture. Claims And Evidence: Claims are supported by clear evidence, but some experimental and evaluation drawbacks below may make the claims about the improvements over baseline methods less convincing: - The cluster baselines only group the data into 24 clusters, which is far away from the optimal cluster number (~10k) in previous works [1][2]. I don't think the number of clusters needs to be strictly the same as the number of domains in their comparison. - The improvements on OLMES (Table 1) may not smoothly transfer to DCLM Core (which is more informative and comprehensive from my perspective). For example, the topic × format one cannot outperform a single topic or format in DCLM Core. [1]: Abbas, Amro, et al. "Semdedup: Data-efficient learning at web-scale through semantic deduplication." arXiv preprint arXiv:2303.09540 (2023). [2]: Zhang, Chi, et al. "Harnessing Diversity for Important Data Selection in Pretraining Large Language Models." arXiv preprint arXiv:2409.16986 (2024). Methods And Evaluation Criteria: Their methods to construct, and annotate two sets of explainable and orthogonal domains, and optimize their mixtures to improve target performance overall make sense. It would be better to make the domain construction more automated with fewer human efforts. In terms of the evaluation criteria, I do have some different opinions. The authors mention in the Appendix that given the symbolic nature of some tasks, e.g., dyck sequence completion, MMLU, and HellaSwag are likely not good proxies for finding the best domain mixture., while I think it is a better practice for this research to adopt better proxy data that can generalize better than MMLU and HellaSwag (e.g., some instruction data), rather than limit the main evaluation to the tasks more related to the chosen proxies. In other words, it is more convincing to choose DCLM Core as the main evaluation rather than OLMES since the main setup of this work is based on DCLM. Theoretical Claims: This paper does not make theoretical claims and focuses mostly on the empirical part. Experimental Designs Or Analyses: The experiment and analysis design is overall sound and self-consistent, except for the cluster baseline/evaluation issues I mentioned above, which I feel are important for my judgment. Supplementary Material: No supplementary material provided. Relation To Broader Scientific Literature: This paper is related to previous domain mixing work in pretraining scenarios but extends the concepts of domains from simple web URLs to more fine-grained and explainable topics/formats identified by LLMs, which can provide a new perspective to pretraining data curation. However, the key technical contributions seem a little bit limited due to the existence of similar previous research [1]. [1] Bai, Tianyi, et al. "Multi-Agent Collaborative Data Selection for Efficient LLM Pretraining." arXiv preprint arXiv:2410.08102 (2024). Essential References Not Discussed: I think [1] is a paper that has similar contributions to this one, which leverages GPT-4o as a topic annotator and trains a BERT-based model as the topic classifier. Its data selection pipeline also considers both domain, topic, and quality dimensions. I have not found the citation to [1] in this paper and I think the contribution of WebOrganizer seems a little bit limited given the similarity to prior works. It also publicly releases its BERT topic classifier, which could serve as a direct comparison to the topic classifiers in this paper. [1] Bai, Tianyi, et al. "Multi-Agent Collaborative Data Selection for Efficient LLM Pretraining." arXiv preprint arXiv:2410.08102 (2024). Other Strengths And Weaknesses: Strengths - This paper provides an explainable technique to analyze the inherent composition of pretraining data and the behavior of quality filters. - WebOrganizer has the potential to improve over current individual quality-based filters by identifying the optimal domain weights. - The writing is clear. Weaknesses - The proposed method to identify and annotate topic domains, technically, does not significantly vary from prior works (please refer to Essential References Not Discussed). - The choice of the domain taxonomies (topic and format) and the number of used domains (24) are somehow intuitively set (or found) by humans. A more fundamental question would be how to identify the taxonomy and granularity of domain classifications more automatically. - The experiment setups can be polished as well. (1) the full potential of the clustering baseline has not been thoroughly presented; (2) the improvements over a more holistic evaluation set (DCLM Core in Table 10) are not as significant as in Table 1. DCLM is meant to be a standardized benchmark to evaluate the pretraining curation outcome and it is better to follow their evaluation setup. Specifically, the DCLM Core set consists of more than 20 tasks while the 9 evaluation tasks in OLMES seem to favor too much knowledge and commonsense abilities. Furthermore, the authors use the MMLU training sets as the target tasks, which already have the in-domain data from ARC-e, ARC-c, and OBQA. Other Comments Or Suggestions: I would also suggest the authors try out different (maybe larger) DCLM setups to show the generalization abilities of their method, but the feasibility definitely depends on the available computational resources the authors have because pretraining is always costly. Questions For Authors: 1. What is the clustering performance if we scale the number of clusters from 24 to 10k-level following the best practices in prior works [1][2]? 2. What if we combine clusters x format in the data selection because clusters mostly align with topics in terms of both characteristics and evaluation results? Will it match the performance of the topic × format? Also, do you have some insights on why a single topic or format classifier cannot outperform clusters too much? 3. Can you provide a comparison of your topic classifier with the one released by [3]? 4. What is the detailed cost (preferred specific numbers) to adopt RegMix to find the optimal domain mixtures, i.e., training 512 models of 50M parameters for 1B tokens? 5. In Lines 142-143, could you provide more details on how humans and LLM (Llama-3.1-405B-Instruct) work together to refine the topic and format definitions? 6. How do you extract 75% confidence from LLM annotation? 7. This is just out of curiosity: will different annotation LLMs (like DeepSeek) have different behaviors in terms of classifying domains? [1]: Abbas, Amro, et al. "Semdedup: Data-efficient learning at web-scale through semantic deduplication." arXiv preprint arXiv:2303.09540 (2023). [2]: Zhang, Chi, et al. "Harnessing Diversity for Important Data Selection in Pretraining Large Language Models." arXiv preprint arXiv:2409.16986 (2024). [3] Bai, Tianyi, et al. "Multi-Agent Collaborative Data Selection for Efficient LLM Pretraining." arXiv preprint arXiv:2410.08102 (2024). Code Of Conduct: Affirmed. Overall Recommendation: 2	Rebuttal 1: Rebuttal: Thank you for your review and for engaging closely with our work! We are glad you found that our methodology is overall sound and that our claims are supported by clear evidence. However, you raised several points with respect to evaluation and novelty, which we hope to address below. > Comparing to greater number of clusters in SemDeDup and Quad The central premise of our paper revolves around the question of how to partition a monolithic dataset into meaningful subsets for data mixing. Therefore, we consider different ways of structuring the data into an equal number of partitions and apply a fixed domain mixture optimization algorithm (for which we use RegMix). We believe this is a fair experimental setting given our paper’s goals. However, the reviewer correctly points out interesting future extensions, such as studying the effect of domain granularity. The two mentioned papers, SemDeDup [1] and Quad [2], are fantastic related works, but neither of them perform k-means clustering with the goal of learning a data mixture. Instead, SemDeDup [1] performs clustering to compute “prototypicality” scores and select data points that are least similar to the cluster center — therefore performing sample-level filtering — and the DCLM paper finds that it performs worse than the RefinedWeb baseline (Table 4). Quad [2] employs fine-grained clustering to obtain robust and efficient influence estimates across groups and then employs binary thresholding to select groups of similar data points from a corpus. Their proposed algorithm is designed for fine-grained group selection instead of data mixture optimization and requires careful tuning of the alpha and gamma hyperparameters. We agree with the reviewer that it would be interesting to add Quad to the experiments, but we would not think of it as a baseline for domain mixing, but rather compare it to FineWeb-Edu and DCLM-fasttext and see whether Quad would also benefit from reweighting domains. We hope to add these experiments in the final version of the paper. > DCLM Core is more informative and comprehensive than OLMES DCLM Core may contain a more comprehensive range of tasks, but in our experiments, we noticed substantial variance with the DCLM Core tasks at the 1B parameter scale (up to 1 point) and many tasks were close to random guessing performance. In fact, the DCLM paper acknowledges that other evaluation frameworks such as LightEval may be more suitable for evaluating small models. We also note that data mixing is a more subtle intervention on the training data than quality filtering, requiring more stable evaluations to reveal small differences between models. Ultimately, we found OLMES to be more reliable and informative. We also note that DCLM Core does not include MMLU, although MMLU is undoubtedly one of the most popular benchmarks for LLMs. We agree with the reviewer that it would be an interesting avenue for future work to investigate better and more diverse proxy data for domain optimization, but this was ultimately not the focus of our work. Instead, we chose MMLU and HellaSwag as they are widely known in the research community and used in almost all previous data selection works. > It would be better to make domain construction more automated with less human effort Since pre-training data curation is so crucial in shaping the behavior of a model that may potentially be used by millions of people, we argue that there is some value in retaining human oversight in the data curation process! Nevertheless, we expect future methods to automate the process of taxonomizing and structuring the web with much finer granularity. > Relation to Bai et al. Thank you for bringing this interesting paper to our attention! We agree that there are similarities with our work and we will definitely highlight them in the next version of our paper. Most notably, Bai et al. [3] also contribute a topic classifier of 13 topics derived by summarizing k-means clusters, which we will compare to our 24 topics. From our analysis in Section 2.4, we would expect k-means clusters to reflect topic information, whereas it would be harder to obtain format domains this way. Besides contributing a high-quality set of format domains, we believe our work makes several independent contributions: (1) We show that topic and formats are approximately orthogonal and their distributions can be combined, (2) We propose a new, simple and effective way of combining data mixing with quality-based data selection, (3) We study the implicit domain biases of two popular quality filters. Questions: Unfortunately, we have reached the rebuttal space limit and cannot respond to the interesting questions here [1] Abbas et al. "SemDeDup: Data-efficient learning at web-scale through semantic deduplication" [2] Zhang et al. "Harnessing Diversity for Important Data Selection in Pretraining Large Language Models" [3] Bai et al. "Multi-Agent Collaborative Data Selection for Efficient LLM Pretraining"	Summary: The paper introduces WebOrganizer, a framework to categorize pre-training data for LMs using topics and formats. The labels are annotated by a pretrained LM. Experiments show that (1) reorganizing data according to these domain classifications significantly improves downstream performance, (2) integrating WebOrganizer with existing quality-based data filtering methods further boosts model performance, (3) existing quality filters are implicitly doing filtering based on topics and formats. Claims And Evidence: Most claims made in this paper are generally clear and supported by convincing experiments. One assumption I don't understand is Sec 4.2 "we make the assumption that we can select topics and formats independently", an analysis on a smaller subset of pretraining data could be interesting. Methods And Evaluation Criteria: Most methods and evaluation are adopted from existing works (e.g., pretraining data, domain importance estimation methods, benchmarks). They are pretty standard and make sense for the problem. Theoretical Claims: The paper does not include significant theoretical claims or formal proofs. I don't fully understand the assumption in Sec 4.2 "we make the assumption that we can select topics and formats independently". Experimental Designs Or Analyses: The pretraining and evaluation designs (for both domain mixing and its combination with quality filters) sound valid to me. Supplementary Material: I reviewed the supplementary material Relation To Broader Scientific Literature: The paper is clearly related to existing literature on pre-training data selection and quality filtering. It shows that (1) a simple domain-based filtering is more effective than quality-based filtering, (2) domain-based selection can improve quality-based filtering. 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: 4	Rebuttal 1: Rebuttal: Thank you for your kind review! We are glad you found the claims in the paper clear and supported by convincing experiments! > Assumption of selecting topics and formats independently We don’t mean to make an assumption in the theoretical sense, but we simply propose to form a mixture distribution of p(topic, format) = p(topic) p(format) given individual mixture distributions p(topic) and p(format). This is motivated by Section 2.3, where we find that topics and formats often have close to zero pointwise mutual information, i.e., they co-occur almost as though they were independently distributed.	Summary: This paper tackles two main challenges: first is to separate the huge pre-training corpus into groups of domains and styles, and the second part is to compute the optimum mixing/reweighting strategy to combine these datasets to achieve targeted improvements in few specific metrics like MMLU and HellsSwag. They also demonstrate that this approach is potentially to quality filtering with complementary gains using both. Experiments further validate the hypothesis. Claims And Evidence: Yes. both the issues claimed have supporting evidence in the form of ample experiments and analysis. Methods And Evaluation Criteria: Yes. the paper targets improvement in evaluation datasets MMLU and HellaSwag, so the use of them and the resulting improvements are totally valid. Theoretical Claims: No theoretical claims. Experimental Designs Or Analyses: Yes. the paper targets improvement in evaluation datasets MMLU and HellaSwag, so the use of them and the resulting improvements are totally valid. Supplementary Material: No. Did not review the supplementary material. Relation To Broader Scientific Literature: The paper provides a thorough comparison with the existing literature. It also includes comparison and contrast with respect to the quality filter literature, making it comprehensively clear the advantages in the paper. Essential References Not Discussed: Not an expert in the field, so not sure. Other Strengths And Weaknesses: Strengths - The paper addresses a very important problem of making sense of billion-scale training data for LLMs, by suggesting to group them into domains and styles along with an effective mixture technique. - The method is easily scalable to bigger datasets, and the choice to run experiments with smaller models and extrapolate observations to bigger models is effective. - The gains are complementary to quality metrics, so there is room for further improvement. Weaknesses - The whole technique to extract the mixture using RegMix is directly derived from a prior work RegMix, so the new ideas in that part are limited. - The paper only focuses on improving two metrics, and scalability to improve multiple evaluation metrics seems unclear from the paper. Other Comments Or Suggestions: Please refer above. Questions For Authors: Please refer to the weaknesses section above and answer the questions. Ethical Review Concerns: None. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Thank you for your review of our paper! We are glad that you highlighted our extensive experiments and analyses, as well as the scalability and practical value of our proposed approach. We would like to briefly address two of your points. > Reliance on RegMix In the paper, we clearly acknowledge that we use RegMix as an existing technique, since our focus is not on contributing another method for optimizing domain ratios given a set of data sources. Instead, we believe that the greater novelty of our work is to shift attention to defining the subsets for effective and large-scale data mixing. Nevertheless, we still extend RegMix to a novel setting, where we directly optimize the task loss of two downstream benchmarks (the bits-per-byte of the correct answers), instead of the perplexity on a corpus such as C4. In Appendix C, we also discuss several new modifications to RegMix that facilitate this, including fitting multiple per-task regression models and employing an iterative search method. > Scalability to improve multiple evaluation metrics is unclear We will make predictions of the topic and format mixtures for additional target tasks (the existing RegMix checkpoint only need to be evaluated on new tasks) and include these in the appendix in the final version of the paper. In our current draft, we focus on only two target tasks, MMLU and HellaSwag, since (a) these tasks are well known in the community and are commonly used for evaluating data selection due to their relevance and low variance (b) we can more easily associate characteristics of the combined mixture with one of the two tasks (c) it was not clear to us how many tasks should be averaged (e.g., should we assign a higher weight to MMLU than one of multiple commonsense tasks?) (d) we reserve more tasks to be used for evaluating generalization to “unseen” tasks. In fact, we find that mixtures for MMLU and HellaSwag generalize well across many popular benchmark tasks. However, we agree with the reviewer that finding the “right” target tasks will remain a question for future research.	Summary: The authors propose a framework for organizing domains from unstructured web corpora along dimensions of topic and format. They use a human-in-the-loop procedure to design domain taxonomies and train a small language model to automatically categorize documents in a pre-training corpus, a 200B token subset of CommonCrawl. Empirical experiments show that using their proposed notions of domain along both topic and format helps improve downstream task performance when combined with quality filters and domain reweighting, though reweighting data domains alone is shown not to match the benefits of filtering alone. Claims And Evidence: Claims supported Methods And Evaluation Criteria: Yes Theoretical Claims: N/A Experimental Designs Or Analyses: Sound experimentation Supplementary Material: N/A. Read parts of appendix Relation To Broader Scientific Literature: Well-grounded in broader scientific literature. Very solid contribution, substantial enough but not groundbreaking to the point of being controversial Essential References Not Discussed: See other Comments for additional reference suggestions -- I would consider them relevant but not "essential" Other Strengths And Weaknesses: Strengths: 1. Well-written -- a sincere pleasure to read overall 2. Strong empirical results 3. Compelling proposed domain taxonomy that may be useful to a broad audience 4. Interesting explorations across a broad set of ablations, including a k-means clustering baseline and a framing of quality filters as implicit domain reweighting 5. Overall high quality reproducibility efforts for established dataset filtering Weaknesses: 1. Some clarity issues. In particular it is at times difficult to follow the reasoning for including the Section 5 experiment in the paper 2. Domain mixing results for only two downstream tasks are included, MMLU and HellaSwag (+ their combination), though the respective mixtures found are evaluated on a larger set of downstream tasks. I feel the paper would be stronger with more than just two domain mixing experiments, though I do not feel the current claims are necessarily undersupported as is. A skeptical reader may feel the results veer towards anecdotal 3. I would have liked to see more explicit discussion of limitations of the present study Other Comments Or Suggestions: Clarity issues and typos: 1. 2.2, "fine-tuning a small classifier model 2. I found the choice of wording in line 300 confusing ("Domain mixing is broadly effective" paragraph in 4.4). Unsure what exactly is meant by the "Despite the target task accuracy" sentence. In any case it does not seem essential to the paragraph, but I wonder if it might be more clear if the authors framed it as tasks being in-domain vs out-of-domain (if a matter of which tasks the domain mixture was geared towards), or simply mentioned the lower performance on HellaSwag specifically (if a matter of the underperformance on that single task) 3. Clarify what the "random sampling baseline" is referring to in 4.4's "Domain Mixtures improve quality filters" paragraph 4. I had trouble following the "Approximating quality filters by domains" paragraph in general, partially due to the density of typos (see below). More detail in the associated Table 2 caption could help. It is difficult to understand exactly what the "Baseline corpus" is out of context, and why perplexity score is expected to be lowest on it (see Q6 below). Explicitly framing the experiment as an ablation could help prevent misunderstandings as well: "document-level quality filtering is a far stronger intervention on the pre-training distribution than rebalancing domains or topics" feels possibly irrelevant to the key points of the paper. I would rather see a discussion of e.g. expected % values in Table 2 given particular hypotheses, or some kind of counterfactual reasoning about the results 5. Line 365, "In this case, the implicit Topic x Format mixture" 6. Line 370, "this classifier could be better suited" 7. Line 372, "values for domain mixing are substantially lower Additional related work the authors may be interested in citing 1. [Chronopoulou et al., 2022](https://aclanthology.org/2022.naacl-main.96/) and [Reid et al., 2022](https://aclanthology.org/2022.emnlp-main.63/) propose two different hierarchical domain taxonomies. [Chronopoulou et al., 2022](https://aclanthology.org/2022.naacl-main.96/) propose a provenance-based taxonomy where leaf domains are from the top 100 URL domains from C4, and resulting domains may span both topic and format. [Reid et al., 2022](https://aclanthology.org/2022.emnlp-main.63/) propose two hierarchical levels of fine-grained and higher level topical domains. Relevant since the authors mention potential future work further breaking down their proposed domains into hierarchical taxonomies. 2. [Na et al., 2024](https://aclanthology.org/2024.emnlp-main.1176/) is another data mixing methodology paper, though "optimizing" data mixtures is not proposed as explicitly (no proportion reweighting experiments, only speculation of the method's extensibility towards reweighting). Relevant since the current submission's authors mention efficiency concerns from selecting a training mixture over the entire cross product of topic x format domains proposed and Na et al. propose a way to efficiently approximate fine-grained data ablations over many possible data mixtures with model merging instead of additional training. At the very least probably a Related Work citation (probably either Data mixture optimization or Analysis of pre-training data) 3. [Held et al., 2025](https://arxiv.org/abs/2501.11747) is very recent and only a pre-print but also feels pretty relevant as another data mixing methodology paper. I am not familiar enough with RegMix or UtiliMax to know whether UtiliMax is expected to be a promising alternative over RegMix for the current submission and/or any follow-up experiments, but I felt it is at the very least a related works citation (Data mixture optimization) 4. More influence functions literature for "Analysis of pre-training data": [Choe et al., 2024](https://arxiv.org/abs/2405.13954), [Yu et al., 2024](https://proceedings.neurips.cc/paper_files/paper/2024/hash/c4bec0d2fd217e6c2c3eafeced432582-Abstract-Conference.html) I do not consider any of these to be "essential" references, necessarily, but I do feel engagement with these works could improve the overall quality of the paper Questions For Authors: 1. Is the proposed taxonomy expected to be applicable out of the box to more general LLM corpora (including e.g. synthetic data, proprietary data, and other content not typically found readily on the web)? If there are limitations, how feasible or compute intensive would it be to adapt the proposed taxonomy to fit a new web corpus e.g. adding just one more topical domain or one more format domain? 2. In general, I am curious to know what the work for 2.2 (Training domain classifiers for scaling annotations) and the related appendix section required in terms of GPU hours, and in particular how it compares to the projected cost of annotating documents with Llama 405b 3. Why was `gte-base-en-v1.5` chosen to compute document embeddings (as opposed to e.g. tf-idf embeddings used by [Gururangan et al](https://arxiv.org/abs/2303.14177), whom the authors cite as an exemplary baseline for k-means clustering of documents? 4. I had trouble following a detail of Target Tasks in Section 3: "To avoid contamination, we use the training and validation set of [MMLU and HellaSwag], respectively." How is this expected to help avoid contamination? 5. What are the key takeaways of Figure 4? 6. Are perplexity scores reported in Table 2 with respect to the baseline corpus's held-out data, or is there a different held-out set for each row? Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: Thank you for your detailed review and for regarding our paper as a solid contribution to the field with strong empirical results. We are especially grateful for the detailed suggestions with respect to the typos and clarity in Section 5, and the many interesting and relevant citations. We will improve the paper with your feedback and discuss these references in the related works section. We will also use the extra page of the final version to add a clear limitations section before the impact statement! > Domain mixing results for only two downstream tasks We focus on MMLU and HellaSwag, since these tasks exhibit interesting qualitative differences, are widely known in the community and are used by most prior works as stable and relevant metrics for data selection. However, we will include topic and format predictions for additional tasks in the appendix of the next version. Training additional models on many target task mixtures is unfortunately beyond our current computational resources and we believe that is equally important to hold out a set of tasks for measuring generalization to “unseen” tasks. Questions: 1. Applicable to more general LLM corpora? While we specifically designed our taxonomy with the goal of structuring many terabytes of web data, our domain classifiers can be applied to any text domain (we will also release a classifier that does not require an URL) and we would expect our models to produce reasonable results. Adapting the taxonomy is more complicated and computationally expensive — one would need to annotate additional data and retrain the domain classifiers — but our open-sourced scripts should make these operations run smoothly! 2. GPU time for training domain classifier? Great question! Fine-tuning the domain classifier is relatively cheap. The first stage of training takes less than 8 H100 hours and the second stage less than 1 H100 hour. By far the most extensive stage is annotating 100k web pages with Llama-3.1-405B, which takes approximately 600 H100 hours. 3. Why gte-base-en-v1.5? gte-base-en-v1.5 is the best small-scale embedding model on MTEB at the time of writing with support for longer documents (up to 8192 tokens). Unlike bag-of-word representations (like tf-idf), the neural encoder can produce embeddings which also reflect semantic and conceptual aspects of the source document. 4. Avoiding contamination The task examples for fitting RegMix and evaluating our final models are from completely disjoint sets, and we never use final test examples for fitting domains. Since our domain mixtures are very low-dimensional, it is unlikely to leak substantial information from the test sets, but it is still best practice to use a different split for mixture optimization. 5. Takeaways from Figure 4 DCLM-fasttext and FineWeb-Edu are currently used to create some of the most widely used pre-training datasets and Figure 4 reflects the composition of these datasets. By comparing to the RegMix predictions, it also visualizes how the pre-training distributions change in the final four rows of Table 1, giving us some indication of which types of content are either “overlooked” or “overvalued” by the quality classifier. For example, we observe that FinWeb-edu has a strong inherent topic bias for Science, Health, and History, but overly filters out more diverse topics. Meanwhile, DCLM-fasttext uniquely has strong preferences for the formats Comment Sections and Creative Writing. We will expand on this discussion in the next version of the paper. 6. Perplexity scores in Table 2 These are computed on the same held-out data of the baseline corpus! We will add this for clarification. --- Rebuttal Comment 1.1: Comment: Thank you for the detailed response to my review! In general, I happily reaffirm my score of 4, as I feel strongly that this paper should be accepted. Responding to some more specific points below: - I do feel domain mixing for tasks beyond just MMLU and HellaSwag would strengthen the paper, so I look forward to seeing additional results in the appendix of the camera ready. However, I find the central claims satisfactory overall because I personally view the core contributions of the paper as those more closely tied to the proposed domain taxonomy. The domain mixing result is nice empirical evidence that the proposed domain taxonomy is a good and useful one that can help towards increasing performance on downstream tasks, but in my opinion there is utility in the inherent characteristics and construction of the taxonomy itself. - It seems to me that the ordeal of adapting the existing proposed domain taxonomy to include new domains would be worth the compute costs to some parties. On the other hand, many would deem it infeasible or too expensive to redo the authors' annotation with Llama 405b themselves (and therefore appreciate the open release of the smaller trained annotation model). (I forgot to ask initially, but I think many would find it useful to understand the costs of performing inference with the smaller annotation model over the corpus as well). I encourage the authors to include these details of compute requirements in their revisions. I look forward to seeing the answers to my questions and concerns incorporated into the revisions. Additionally, I read the other reviews and rebuttals, and I found none of the other concerns to be major enough to influence my score downwards. In particular, the essential related work mentioned by Reviewer suAs seems to be a very recent, lesser known pre-print that has not yet passed peer review, so I do not believe it is [appropriate](https://icml.cc/Conferences/2025/ReviewerInstructions) to hold it against the authors of the present work for missing it (though I would encourage them to engage with it in any future revisions).	null	null	null	null	null	null
Robust Multi-Agent Reinforcement Learning with Stochastic Adversary	Accept (poster)	Summary: This paper proposes a soft-policy-based MARL observation adversary consisting of a director module and an attack generator. The convergence guarantee of the director module is provided. Experiments on SMAC and CAV benchmarks demonstrate the effectiveness of the proposed method. ## update after rebuttal My concerns are largely addressed. I raise my score from 2 to 3. Thank you to the authors for their response and the additional experiments. It is good to see the improvements made to the manuscript. Please make sure the improvements are integrated in the next version. Claims And Evidence: Yes Methods And Evaluation Criteria: Yes Theoretical Claims: Yes, I checked Theorem 3.4 and 3.5. Experimental Designs Or Analyses: Yes. I checked Section 4. Experiments. Supplementary Material: Yes, I reviewed most parts of the appendix and a small part of the source code. Relation To Broader Scientific Literature: The key contributions extend and refine ideas from MARL, robustness in machine learning, and open-environment learning. By addressing the challenge of robustness in MARL, this paper advances these fields and provides a framework for developing more robustly collaborative AI systems. Essential References Not Discussed: The purterbation of observations in MARL is an open-MARL problem, where the key factors of the learning process change. A survey of this problem [1] should be discussed. Also, the idea of learning an adversary and proving its optimality is similar with [2], which should be discussed and compared as a baseline. [1] A Survey of Progress on Cooperative Multi-agent Reinforcement Learning in Open Environment. Lei Yuan, et al. 2023. [2] Robust Multi-agent Coordination via Evolutionary Generation of Auxiliary Adversarial Attackers. Lei Yuan, Ziqian Zhang, et al. 2023. Other Strengths And Weaknesses: ## Strengths 1. Rigorous Theoretical Foundation: The paper provides a thorough theoretical analysis of adversary optimality, including formal proofs for convergence on the adversary's optimal policy. This strengthens the methodological grounding of the approach. 2. Comprehensive Empirical Evaluation: The experiments span diverse multi-agent benchmarks and demonstrate consistent improvements over strong baselines. ## Weaknesses 1. Incremental Algorithmic Contribution: While the integration of stochastic adversaries is technically sound, the core idea of training robust agents via adversaries is well-explored in prior work. The novelty lies primarily in the specific instantiation rather than a conceptual leap. 2. Underdeveloped Justification for Stochasticity: The claim that stochastic adversaries mitigate overfitting is not sufficiently substantiated. Population-based methods like RAP [1] and ROMANCE [2] explicitly address this via diverse adversary ensembles, whereas the paper's stochastic policy approach lacks a direct comparison or analysis to validate this advantage. 3. Overly Complex Formalisms with Limited Clarity: The OD-POMDP/PD-POMDP formulations introduce heavy notation without commensurate payoff in insight. Figure 1 occupies too much space but is not clearly explained. [1] Robust Reinforcement Learning Using Adversarial Populations. Eugene Vinitsky, et al. 2020. [2] Robust Multi-agent Coordination via Evolutionary Generation of Auxiliary Adversarial Attackers. Lei Yuan, Ziqian Zhang, et al. 2023. Other Comments Or Suggestions: None. Questions For Authors: See Weaknesses. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Thank you for your insightful suggestion. We have added RAP and ROMANCE as benchmark methods in the 8m VDN-based setting, as shown in Table 7 (https://anonymous.4open.science/r/icml25-9974-8E33/9974.pdf). Q1: Essential References Not Discussed We plan to include a discussion of the references in the introduction and incorporate ROMANCE as a baseline method in our experiments to enable a more comprehensive comparison. Q2: Incremental algorithmic contribution Although the core idea of training robust agents via adversaries has been explored in prior work, there are still some open and challenging problems, such as overfitting, which has been highlighted in recent papers and is a central focus of our study. Certainly, the concept of stochastic adversaries is not new, as it has been studied in the context of policy robustness in several works, including ROMANCE and RAP. However, there are significant differences between policy robustness and state robustness in terms of both formulation and motivation. Formally, policy robustness involves perturbing agents' actions to evaluate their robustness, whereas state robustness involves perturbing the agent's input states without directly altering its actions. ROMANCE, as a policy robustness method, requires constraints on adversarial agents, i.e., introducing a sparse action attack budget to limit the number of adversarial interventions, in order to preserve training stability. These constraints are not applicable to our state robustness training method. If our method takes these constraints, only some agents might become robust, while others would remain sensitive to state perturbation. Our experiments also show this phenomenon. RAP, as another policy robustness method, does not use these constraints, and it takes a population of adversaries to deal with overfitting. However, if our state robustness learning method adopts a similar approach to address overfitting, it generates numerous out-of-distribution states (resulting in destabilization of the training process) and significantly increases memory costs. Therefore, although stochastic adversaries have been used for policy robustness, they do not translate well to the setting of state robustness. In contrast, our paper provides a feasible way. We’ll add this discussion in the future version. Q3: Underdeveloped justification for stochastic adversaries. We have added both RAP and ROMANCE as baselines in our experiments for comparison. To fairly compare with RAP, we have adopted its core idea of promoting adversary diversity by selecting from the population of deterministic adversaries and applied it within the PAAD framework. Experimental results show that our method achieves better performance across diverse adversarial scenarios, while being more memory-efficient by noting that RAP requires training and maintaining multiple adversaries in parallel. For ROMANCE, we have conducted two sets of experiments: ROMANCE-p, using the original ROMANCE policy adversary, and ROMANCE-s, where our SDor module is replaced with ROMANCE adversaries. Results indicate that ROMANCE does not effectively help the protagonist learn state-robust policies. Q4: Overly complex formalisms with limited clarity In the definitions, we have used superscripts $p$ and $a$ to distinguish between the states, actions, and policies of the protagonist and the adversary, respectively. We agree that Figure 1 is overly large and under-explained, and we plan to replace it with the linked Figure 2 in the final version.	Summary: The paper proposes replacing workst-case adversary to stochastic adversary to improve robustness in multi-agent reinforcement learning (MARL). The proposed adversary model consists of a director and an actor where the former predicts a direction of manipulation and the latter translates this action into a manipulated observation. The paper proves the convergence and optimality of the training dynamics. It also conducts experiments on StarCraft II and autonomous driving datasets that the proposed model effectively address the issues of adversarial overfitting and director-actor misalignment, which are commonly seen in the adversarial MARL literature. Claims And Evidence: Most claims are supported by clear and convincing evidence, with one perhaps unclear statement: - The sentence in line 431 starting with "However..." says the proposed ATSA method achieves the best attack performance, but Fig. 3(a) PAAD(VDN) seems to imply the ATSA attacker cannot degrade the agent performance as much as the PAAD attacker, right? Methods And Evaluation Criteria: Both StarCraft II and Autonomous Driving problems are valid and common problems in MARL. The evaluation metrics are the cumulative rewards and win rate (resp. crash rate) for StarCraft II (resp. Autonomous Driving). The metrics are reasonable. Benchmarks are a list of other adversarially trained MARL models, as well as the case where the adversay is absent. These benchmarks are also reasonable. Theoretical Claims: I checked all proofs and theoretical claims and not spotted any issues, provided that the cited results are correct. Experimental Designs Or Analyses: I checked the experiments on metric comparisons, ablation tests, attacker performance, and the perturbation effect. The experiment design is valid and the results support their claim on the proposed advantages. - Some details on the training parameters is missing, such as epochs, learning rate, horizon, etc., which may influence the reproducibility of the results. - Some ablation tests on $\alpha$ could make the experiments more complete. Supplementary Material: I reviewed supplementary matrials on proofs, extended experiments, and result analysis. The sentence on line 1096 starting with "However..." says that PPAD is instable because it achieves higher performance when the perturbation is large than when it is small. I feel probably a clearer definition of instability is missing here since the same tendency also exists for the proposed model ATSA, despite a smaller magnitude. Relation To Broader Scientific Literature: This work belongs to the multi-agent reinforcement learning and adversarial learning literature. The key finding advances the state-of-the-art performance in the robust MARL area. Essential References Not Discussed: No missing essential references recognized. However, the Related Work section only contains discussions with different robust reinforcement learning algorithms. Perhaps some discussions on adversarial learning would help understand the context more. The idea of using randomization to simultaneously detering attacks and maintaining naive-case performance should exist somewhere in the literature. Other Strengths And Weaknesses: This paper is strong both in originality and technical contents. It innovatively proposed a training approach with stochastic adversaries. This method is itself novel and original and proved effective in ensuring high RL model performance under different types of adversaries. Both theory and experiments are rich enough to support the claimed superiority of the proposed model. The weakness is in the discrete and finite environment setting. The applicability of ATSA to continuous control (e.g., MADDPG) remains undiscussed. Other Comments Or Suggestions: The last sentence of section 2.2: The notations are a little confusing. Do the authors mean $\hat{o}\sim v(\cdot\|\tau)$ instead of $\tilde{o}\sim v(\cdot\|\tau)$ as $v$ is $\mathcal{M}$-dimensional (line 120) and $\tilde{o}$ is $\mathcal{N}$-dimensional (line 128). Also, is it the "joint policy of the protagonist agent" or the joint policy of the adversary? Questions For Authors: No. Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: Thank you for your question. Based on your suggestion, we have provided additional experimental results, including ablation studies on $\alpha$ (Fig. 1) and continuous control tasks (Table 1), available at the following link: https://anonymous.4open.science/r/icml25-9974-8E33/9974.pdf Q1: Some unclear statement The sentence in line 431: You are correct. We have corrected it. The sentence on line 1096: We define instability as the variation in performance under different perturbation levels. Although ATSA shows a similar trend in this specific figure, the overall results across all eight evaluation plots indicate that ATSA is more stable than PAAD, with consistently smaller performance fluctuations under varying perturbation levels. The last sentence of section 2.2: Yes, the correct notation should be $\hat o \sim v(\cdot\|\tau)$, where $v$ is the joint policy of the adversary. Q2: Training parameters We run 4,000,000 environment steps across all environments and methods. For SDor, both actor and critic use a learning rate of 0.0005. The target networks are updated every 200 episodes. In SMAC, we use the default episode horizon provided by each environment. For the CAV environment, the horizon is set to 100 timesteps. Q3: Some ablation tests on $\alpha$. We have added ablation experiments on the temperature parameter $\alpha$. The results show that when $\alpha$ approaches 0, it leads to a decline in robustness. In this case, the policy becomes deterministic, which results in performance similar to that of PAAD—showing good results under PAAD attacks but poor performance under FGSM attacks. Q4: Essential References We plan to add relevant references on adversarial learning and the use of randomization techniques to balance robustness and nominal performance. Q5: The applicability of ATSA to continuous control (e.g., MADDPG) remains undiscussed. We have conducted experiments based on MADDPG and FACMAC in the MPE environment to demonstrate the potential applicability of ATSA to continuous control tasks. Our method under the MADDPG framework shows some improvement compared to existing baselines such as FGSM, PAAD, and ATLA. However, the performance under the FACMAC framework is not particularly strong under both clean and adversarial conditions. This indicates that our method has limitations in continuous action spaces and needs further improvement. We suspect that this is due to two main reasons: 1) In multi-agent environments, inducing coordinated worst-case behaviors via gradient-based attacks is challenging. 2) For step-wise adversaries like PAAD and ATSA, it is difficult to generate compound perturbations that follow the intended direction of policy disruption. We plan to include this discussion in Section 4 of the future version.	Summary: This paper proposes Adversarial Training with Stochastic Adversary (ATSA) to fortify the robustness of models trained by multi-agent reinforcement learning. It addresses the overfitting problem of existing methods by training the proposed adversary online alongside the protagonist agent. ATSA implements an SDor-STor structure that performs policy perturbation and uses a loss function that leverages the protagonist agent's policy information when training the adversary policies. Claims And Evidence: The 1st claim is the mathematical proof proving the SDor’s soft policy converges to a global optimum according to factorized maximum-entropy MARL and leads to the optimal adversary. It is generally supported by the theoretical proof. The 2nd claim is that the proposed ATSA demonstrates robustness against diverse perturbations of observation while maintaining outstanding performance in environments without perturbation. This is generally supported by the experiments whereas several questions remain, please see below. Methods And Evaluation Criteria: The proposed method is reasonable considering the adversarial training in MARL. The evaluation is conducted on 2 common benchmarks for MARL the StarCraft and the connected autonomous vehicles, 2 MARL methods (value decomposition network and Q-MIXing network), and 6 baseline agent training methods. Theoretical Claims: Read through, but not carefully verify them Experimental Designs Or Analyses: The experimental design and soundness will be better if more benchmarks are included such as Multi-Agent Particle Environment (MPE). The MARL methods used can be more powerful such as QTRAN. Supplementary Material: I have read the appendix. Relation To Broader Scientific Literature: This paper related to adversarial robustness and multi-agent reinforcement learning. Essential References Not Discussed: This is reference is not discussed in the paper. Robust Multi-Agent Reinforcement Learning via Adversarial Regularization: Theoretical Foundation and Stable Algorithms. NeurIPS 2023 Other Strengths And Weaknesses: One of the weakness is the time complexity and the issue of scalability of the proposed method. The introduction of adversarial agents will lead to higher time complexity and limited scalability. Other Comments Or Suggestions: There is a typo in Table 1's "NoAdv" column - it should be labeled "WR" instead. Is it necessary for each agent to have an adversarial policy? For example, in a system with 3 agents, could we use only 2 adversarial agent policies that rotate between different combinations of agents? Would such an approach be effective? Questions For Authors: How does the stochastic adversary specifically help prevent destabilization of the protagonist agent's training and overfitting to extreme adversarial perturbations? Are the perturbations from the stochastic adversary less extreme compared to other approaches? In Table 2, under the VDN row and ATLA column, why is the performance (61.10) significantly lower than RN and PR when using the same agent training method and ATLA adversarial attack? Additionally, what explains the large standard deviations in Table 2? Line 221 states that the considered case involves a deterministic and discrete protagonist agent policy. Given evaluation tasks like StarCraft, how practical is this setting? What are the implications when the policy is non-deterministic? What specific deep neural network architectures and parameters are used to learn the soft Q-functions and soft policies for SDor? What performance trade-offs exist between non-adversarial settings and adversarial training when using ATSA? Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We have added additional experiments on the MPE environment (Table 1), the QTRAN (Table 4) and non-deterministic policy (Table 2), ERNIE (Table 5), and results for Q5 (Table 6). Please refer to https://anonymous.4open.science/r/icml25-9974-8E33/9974.pdf Q1: MPE and QTRAN. As suggested, we have extended our evaluation to include additional benchmarks. The analysis of the MPE experimental results can be found in our response to Reviewer 5nJY, Q5. QTRAN achieves better performance than other methods in the 8m scenario. Q2: Essential References Not Discussed. In the final version, we plan to include a discussion of ERNIE in Section 1 and add it as a benchmark method in Section 4. We have conducted a preliminary experiment with ERNIE under the 3m scenario (VDN-based). As seen, although ERNIE performs well in clean and random noise settings, ATSA outperforms ERNIE in average win rate under different types of perturbations. Q3: Time complexity and scalability The additional time complexity introduced by adversarial training is indeed inevitable. In the 8m scenario, training VDN with ATSA for 4M steps takes approximately 14 hrs 9 mins, while training with PAAD takes around 13 hrs and 38 mins. This indicates that ATSA incurs a comparable training cost to other adversarial training methods such as PAAD. Regarding scalability, it should be noted that our method is designed within the CTDE framework, which has inherent scalability limitations. We suspect that challenges remain in both the theoretical convergence of entropy-based Mean-Field RL to the Nash Q-value and in the practical implementation of such methods, which require further investigation. Q4: Typo We will correct it in the final version. Q5: Is it necessary for every agent to have a dedicated adversarial policy? Yes, it is necessary for each agent to have its own adversarial policy. To test this, we have trained ATSA-based (QMIX) protagonists in the 3m and 8m environments with only two adversarial policies that rotate among different agent combinations at each timestep. We have compared these with settings where all agents are adversarial (i.e., fully coordinated). The results show that using only two adversarial agents in rotation (i.e., ATSA-2) does not consistently improve the robustness of the protagonist. Q6: How does a stochastic adversary promote stable and generalizable training, and are its perturbations less extreme than those from other methods? Our method introduces an entropy term with a temperature coefficient $\alpha$ to encourage diverse adversarial behaviors. Early in training, a higher $\alpha$ promotes broader exploration, preventing overly disruptive perturbations and stabilizing learning. As $\alpha$ decays, the adversary focuses more on reward optimization. This controlled exploration leads to less extreme, more varied perturbations, reducing overfitting and training collapse—making our method more stable than others. Hence yes, compared to other approaches, the perturbations are indeed less extreme. Q7: VDN+ATLA performance and large standard deviations. ATLA struggles to learn effective adversarial policies in high-dimensional state spaces, often behaving like random noise. This results in weak protagonist training and degraded performance, even without attacks. The large standard deviations in Table 2 stem from the CAV reward design, where severe penalties for collisions cause high return variance, especially under unstable or adversarial conditions. Q8: How practical is assuming a deterministic discrete policy in StarCraft, and what if the policy is stochastic? This setting is widely adopted in the CTDE framework, where many classic multi-agent methods—such as VDN, QMIX, and QTRAN—are also based on discrete action spaces with deterministic policies. Moreover, these methods are commonly evaluated on benchmarks like SMAC/StarCraft, which naturally align with this assumption. To further explore the applicability in stochastic policy settings, we have also conducted experiments under the non-deterministic policy (i.e., FOP). The preliminary results indicate that our method is also applicable to non-deterministic policies. Q9: SDor architectures and parameters. The actor and critic networks of SDor are composed of two MLP layers with a GRU (hidden size 64) inserted between two layers. RMSprop is used to optimize all parameters. Q10: What performance trade-offs exist between non-adversarial settings and adversarial training when using ATSA? In our eight experimental settings, ATSA does not achieve the best performance in three cases under the NoAdv condition. However, it outperforms other methods in most settings and achieves the highest average performance across both clean and adversarial conditions.	Summary: This paper proposes Adversarial Training with Stochastic Adversary (ATSA) for training Multi-Agent Reinforcement Learning (MARL) models, where the adversary is trained simultaneously with the protagonist agent. ATSA reduces the models' sensitivity to perturbations in observations, while addressing issues with existing adversarial training methods (such as FGSM and PAAD), which tend to overfit to their own perturbations, resulting in models that perform poorly in a no-adversary (clean) setting. This is achieved via a Stochastic Director (SDor) that performs policy perturbations, and a SDor-guided generator (STor) that generates observation perturbations given SDor's suggestion. SDor is then trained to both minimize the protagonist's reward and maximize the entropy of its policy, with the latter encouraging exploration. The authors also introduce a SDor-STor loss function to quantify and penalize deviations between SDor-suggested perturbations and those produced by STor, thereby aligning STor's perturbations with SDor's intention. Theoretical proofs show that under factorized maximum-entropy MARL, SDor's soft policy achieves a global optimum, resulting in an optimal observation adversary. Experimental results using an extensive set of baseline techniques (no adversary, random noise, FGSM, ATLA, PR, and PAAD) show that ATSA is robust in a variety of settings. Overall, ATSA achieves the best average performance among all baseline methods, while existing methods such as FGSM and PAAD perform poorly in clean scenarios or against different adversaries. A number of ablation studies are also performed, demonstrating the contribution of the SDor-STor loss function to ATSA's performance. Claims And Evidence: The paper's claim that ATSA improves robustness is supported by the experimental results, achieving the highest average performance in all the examined scenarios. The claim that existing methods such as FGSM and PAAD overfit to their own perturbations and therefore perform poorly in clean environment and also against other adversarial methods (such as ATSA itself) is also supported by the experimental results. The authors also theoretically prove the optimality of SDor. Ablation studies further justify the use of the SDor-STor loss function and how it leads to higher performance. The only claims that are somewhat unclear to me are claims 2 and 4 in Section 4.2, please see the relevant question below. Methods And Evaluation Criteria: The authors compare against multiple benchmark RL environments, MARL methods, and adversarial/clean settings. The experiments are therefore sound/comprehensive and support the authors' claims. Theoretical Claims: I did not check theoretical proofs. Experimental Designs Or Analyses: The experimental design and setup are appropriate for the problem being studied. I have one clarifying question regarding the configuration of different adversaries and training methods, which I've included below. Supplementary Material: I did not review supplementary material. Relation To Broader Scientific Literature: The paper adds to existing literature by designing a novel method that incorporates information about the policy of protagonist agents, addressing a limitation of prior techniques that do not perform well in scenarios other than their own. This ultimately results in more robust MARL models that perform optimally in a more diverse set of conditions. Essential References Not Discussed: None. Other Strengths And Weaknesses: This is a great paper with a good mixture of novelty, theoretical proofs, and experimental results. I particularly appreciate the depth/diversity of the experimental results, and the ablation study at the end. The overall motivation behind ATSA is insightful and the authors provide a sufficient amount of evidence that their proposed method outperforms state-of-the-art methods. One limitation of the proposed method is the assumption that the protagonist's policy is deterministic and discrete. However this still covers a large set of problems, and the continuous setting is left for future work. A slight weakness of the experimental results is that the performance metrics tends to be noisy in some cases, especially for the Connected and Autonomous Vehicles (CAV) environment. This can undermine the statistical significance of the results. However, the fact that ATSA achieves the best average performance across all settings is a strong justification. Other Comments Or Suggestions: 1. I suggest the authors perform a statistical test on results in the average columns of Tables 1 and 2, to determine rows where the lower average performance is statistically significant. This could strengthen the paper's claim that ATSA achieves a better "across-the-board" performance. 2. It would also be helpful to clearly state in the introduction that the approach assumes a discrete policy. Questions For Authors: 1. Could you elaborate on how the experiments were conducted for Tables 1 and 2, particularly when pitching one adversary algorithm against a different training method for the protagonist agent? Are models retrained for each cell in the tables (i.e., the protagonist's policy in each cell is trained using the training method specified by the row, but in an environment where the adversary specified by the column is present)? 2. In Tables 1 and 2, are the confidence intervals standard deviations? How many episodes were they computed over? 3. Could you provide more details/justification regarding the following claims in Section 4.2: "PR faces challenges in balancing adversarial and standard losses" and "ATLA struggles with large action spaces, reducing its effectiveness". For the latter, why is ATLA (and not other methods) specifically called out for struggling with large action spaces? Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: Thank you for the suggestion. Additional results—including continuous (Table 1), non-deterministic (Table 2) cases, and further details for Q5 (Tables 1 and 3)—are available at the following link: https://anonymous.4open.science/r/icml25-9974-8E33/9974.pdf Q1: Deterministic and discrete protagonist policy limits its applicability. We have now added experiments on continuous action spaces and non-deterministic policies. In continuous action space tasks, ATSA demonstrates a certain level of effectiveness, but there is room for improvement. Please refer to the response to Reviewer 5nJY, Q5 for more details. In the non-deterministic setting (i.e., FOP), our method outperforms baselines. However, our theoretical analysis assumes a deterministic and discrete policy, and extensions to other settings remain future work. We plan to explicitly state this assumption in the introduction and provide further discussion in the future work section. Q2: Statistical significance tests. We have conducted Wilcoxon Signed-Rank Tests to assess the statistical significance of ATSA's performance. In Table 1, ATSA shows significant improvement in 24 out of 36 baseline comparisons. In Table 2, ATSA significantly outperforms baselines in 10 out of 12 cases for Reward and 9 out of 12 for CR. We plan to mark significant results (p < 0.05) with an asterisk (*) in the AVG columns of Tables 1 and 2 in the final version. Q3: Are the protagonist models retrained for each cell in Tables 1 and 2 based on the specified training method and adversary, or is a shared model used across settings? The protagonist model in each cell is trained by using the method specified by the row, while the adversary is trained by using the method specified by the column. Importantly, no retraining is performed for each cell, i.e., the adversary is not retrained specifically to target each protagonist. For example, when evaluating PAAD (as the protagonist) against ATSA (as the adversary), the PAAD model is trained independently using its own adversarial training procedure, and the ATSA adversary is also trained independently using its own procedure—not against the PAAD-trained policy specifically. Similarly, the PAAD protagonist is not trained using the ATSA adversary. We will clarify this setup in Section 4.1.2 of the future version. Q4: Do the confidence intervals in Tables 1 and 2 represent standard deviations, and over how many episodes are they computed? Yes, the values are standard deviations computed over 500 evaluation episodes. Q5: More justification for the claims that (1) PR struggles to balance adversarial and standard losses, and that (2) ATLA is less effective in large action spaces. (1) PR formulates the policy loss as $\mathcal L = \mathcal L_{regular} + \mu \mathcal L_{adv}$, where $\mu$ controls the trade-off between standard and adversarial performance. Following [1], we set $\mu=0$ for the first 2M steps and $\mu=0.1$ thereafter (denoted PR-0.1). To further investigate this trade-off, we have run two additional experiments: PR-0.05, where $\mu=0.05$ in the final 2M steps and Rep-PR [2], where $\mu$ is repeatedly increased from 0 to 0.1 three times during training. Results on the 3m (QMIX-based) setting are available at the provided link. These results show that small changes in $\mu$ have notable impacts. While Rep-PR helps on clean inputs, it is less robust under attack. This illustrates the difficulty PR faces in balancing clean and adversarial performance. We plan to include Rep-PR as a benchmark method and report full results in the future version. (2) ATLA models the adversary as an RL agent that learns to perturb the environment state. This means the adversary's action space is tied to the dimensionality of the state space. As stated in [3]: “If the original state space is high-dimensional, learning a good policy in the adversary’s MDP (i.e., ATLA) may become computationally intractable.” To illustrate this, we have conducted an experiment in the MPE environment, where the state dimensionality is relatively small (16). Based on FACMAC, the results of ATLA and PAAD-trained protagonists against PAAD are 175.35 and 155.76. These results show that ATLA performs well in low-dimensional settings. However, in our main experimental environments, the state dimension ranges from 30 to 80, which significantly increases the adversary's action space and training complexity. As a result, ATLA becomes less effective. This supports our claim that ATLA struggles with large state spaces, reducing its effectiveness in high-dimensional environments. [1] Enhancing the robustness of QMIX against state-adversarial attacks, 2024 [2] A Robust Mean-Field Actor-Critic Reinforcement Learning Against Adversarial Perturbations on Agent States, 2024 [3] Who is the strongest enemy? Towards optimal and efficient evasion attacks in deep RL, 2022	null	null	null	null	null	null
Test-Time Training Provably Improves Transformers as In-context Learners	Accept (poster)	Summary: The paper investigates the theoretical and empirical advantages of Test-Time Training (TTT) for improving transformers as in-context learners. Authors develop a theoretical framework to characterize how a single-step gradient update at test time enhances in-context learning. The authors provide a rigorous theoretical proof. The analysis covers the role of alignment between pretraining distribution and target tasks, the ability of TTT to mitigate distribution shift, and its sample complexity benefits. Empirical evaluations support the theoretical findings and demonstrate that TTT significantly reduces required sample sizes while maintaining performance. Claims And Evidence: The paper provides sound theoretical backing and empirical results to support the claims. However, the reliance on linear transformers may limit generalizability to more complex architectures. Methods And Evaluation Criteria: Yes. Theoretical Claims: Yes, the paper presents sound and rigorous theoretical derivations. I've read and checked the Analysis for Isotropic Covariances and Analysis for General Covariance parts for the theoretical claims and there's no obvious issues. Experimental Designs Or Analyses: Yes, the experimental design is valid and directly supports the theoretical claims, including the experiments on TabPFN (demonstrating efficiency improvements and sample size reductions) and the simulations with GPT-2 (showing TTT for handling distribution shift). Potential limitations are the narrow focus on TabPFN and the need for additional benchmarks to validate broader applicability. Supplementary Material: I've read part of the supplementary material, as it contains too much detailed proofs. I did not find obvious problems. Relation To Broader Scientific Literature: Yes, I think this paper can help the broad community to understand TTT better and provide new insights for utilizing TTT. Also, the experiments on TabPFN shows new opportunities to reduce test time scaling cost (when using ICL). Essential References Not Discussed: No Other Strengths And Weaknesses: Strength: Very novel and natural theoretical explanation for TTT and ICL. Weaknesses: Limited to simple or toy linear transformer architectures and basic TabPFN tasks, restricting broader applicability. Other Comments Or Suggestions: No. Questions For Authors: 1. Would it be necessary to analyze the effects of different optimizers separately? 2. Do you know about work that explains in-context learning using gradient updates? Since TTT also relies on gradient updates, what are the deeper differences and connections between the two when viewed from the perspective of gradient updates? Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: We thank the reviewer for their favorable evaluation of our work and for the helpful feedback. We now reply to each of the points raised below. > Experimental Designs Or Analyses. Yes, the experimental design is valid ... Potential limitations are the narrow focus on TabPFN and the need for additional benchmarks to validate broader applicability. Response: Thank you for your feedback. We chose to conduct our experiments with the TabPFN model because it's well-aligned with our theoretical setting with similar token encodings but different prior distributions. This favorable agreement made TabPFN a particularly good setting to conduct large-scale experiments on how TTT reduces the context length needed. For the benchmarks used while evaluating TabPFN, we realized that we did not provide enough contextual information in the paper for our choice of the T4 dataset (Gardner et al., 2024), which is an extensive collection of public benchmarks containing diverse real tabular tasks. In the revision, we will include how we filtered the datasets in T4 according to the requirements of TabPFN and our problem setup, as well as how we constructed the experimental pipeline. Still, we agree that additional domains beyond tabular data would help demonstrate the broader applicability of our theoretical claims. > Weakness. Limited to simple or toy linear transformer architectures and basic TabPFN tasks, restricting broader applicability. We thank the reviewer for the feedback. The TabPFN v2 model itself has been pre-trained on a wide range of tabular distributions, and we evaluate it on the T4 dataset (Gardner et al., 2024) through many diverse real-life tabular tasks. So, we actually demonstrate how TTT reduces the number of in-context examples across a broad range of realistic classification tasks by plotting the average performance across all tasks in T4. This extensive coverage enables us to. For the discussion on model architecture, we refer the reviewer to our related response for the weakness mentioned by Reviewer StUH. > Q1. Would it be necessary to analyze the effects of different optimizers separately? Response: We appreciate this question. In our TabPFN experiments, we initially used AdamW as the optimizer, as it's known to work well with transformer architectures. Based on your question, we tried the same experiment using the standard SGD with momentum and observed minimal differences in final performance. The results are available [here](https://anonymous.4open.science/r/TestTimeTrainingProvablyImprovesTransformersAsInContextLearners-F845/TabPFN_SGD.pdf). > Q2. Do you know about work that explains in-context learning using gradient updates? Since TTT also relies on gradient updates, what are the deeper differences and connections between the two when viewed from the perspective of gradient updates? Response: Thank you for highlighting this connection. The existing works (e.g., Ahn et al., 2023; Mahankali et al., 2023; Zhang et al., 2023; Li et al., 2024) show that in-context learning can be viewed as implicit gradient descent within a transformer's forward pass which effectively simulates a preconditioned GD governed by the task prior. In contrast, our TTT approach explicitly updates the model parameters at inference and provides task-specific adaptation rather than one governed only by the prior. In ICL, any gradient descent occurs internally without updating the weights; as a result, the model can only implement the preconditioned GD it meta‐learned from pretraining. Instead, TTT uses a real gradient step on test data and handles the distribution shift with a low computational cost. Finally, while most ICL analyses operate at the population level (i.e., with infinite samples), our setting provides finite‐sample guarantees on performance improvements on how a single‐step update can reduce the needed context length. Ahn, K., Cheng, X., Daneshmand, H., and Sra, S. Transformers learn to implement preconditioned gradient descent for in‐context learning, 2023. URL https://arxiv.org/abs/2306.00297 Zhang, R., Frei, S., and Bartlett, P. L. Trained transformers learn linear models in-context, 2023. URL https://arxiv.org/abs/2306.09927. Li, Y., Rawat, and Oymak, S. Fine-grained analysis of in-context linear estimation: Data, architecture, and beyond, 2024. URL https://arxiv.org/abs/2407.10005. Mahankali, A. V., Hashimoto, T., and Ma, T. One step of gradient descent is provably the optimal in-context learner with one layer of linear self-attention, 2024. URL https://arxiv.org/abs/2307.03576 --- Rebuttal Comment 1.1: Comment: Thanks for answering my questions and addressing my concern, I'll keep my score.	Summary: This paper examines the impact of test-time training (TTT) on the performance of a single-layer linear attention model (without an MLP) after a single gradient step during test-time fine-tuning. The authors focus on the problem of in-context linear regression and characterize the performance improvement achieved through one step of gradient descent for a linear attention model in terms of the context length ($n$) and the ambient dimension ($d$). Claims And Evidence: Yes, the claim well supported with empirical experiment on synthetic data. Methods And Evaluation Criteria: Yes, they all make sense. Theoretical Claims: The theoretical framework is sound; however, it is highly limited to a single attention layer (without an MLP) and applies only to the linear regression problem. Experimental Designs Or Analyses: The experiments are reasonable; however, to support the claim that this theory provides insight into broader in-context learning (ICL) problems, it would be beneficial to include additional ICL tasks, such as a two-layer ReLU neural network, or expand the evaluation with more datasets for the TabPFN experiments(currently it is only tested on 1 data set). Supplementary Material: I just skimmed through it. Relation To Broader Scientific Literature: NA Essential References Not Discussed: NA Other Strengths And Weaknesses: I found the paper interesting, and the theoretical insights were valuable. The experiment with real TabPFN was also compelling. The main limitation of the paper is its focus on a single-step gradient descent and a simplified model. However, despite this constraint, the paper still provides meaningful insights. Other Comments Or Suggestions: trying on more data set for TabPFN would be an interesting addition helps with completeness. Questions For Authors: 1. How would performing additional gradient descent steps at test time affect the results? Specifically, how would it impact the loss improvement described in the paper's theorem? 2. Can this approach be extended to a one-layer transformer with softmax attention and an MLP? How challenging would this extension be, and what factors contribute to the difficulty? Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We thank the reviewer for the detailed feedback and positive evaluation of our work. We address the weaknesses and questions brought up below. > Experimental Designs Or Analyses. The experiments are reasonable; however, to support the claim that this theory provides insight into broader in-context learning (ICL) problems, it would be beneficial to include additional ICL tasks, such as a two-layer ReLU neural network, or expand the evaluation with more datasets for the TabPFN experiments (currently it is only tested on 1 data set). Response: Thank you for highlighting this important detail. In lines 379–381, we mistakenly referred to a “single dataset,” but we intended to say “each dataset” in the The Tremendous TabLib Trawl (T4) benchmark (Gardner et al., 2024). T4 is a large-scale, high-quality collection of public tabular benchmarks containing approximately 4 million tables. Our choice to use T4 was indeed to make evaluations more comprehensive by covering a broad range of data. As stated in lines 412-413, we report the average performance across all datasets in T4 with sufficient samples in Figure 3-a. > Weakness. The main limitation of the paper is its focus on a single-step gradient descent and a simplified model. Response: Thank you for your feedback. We want to highlight that we focus on single‐step gradient descent because it is both practically motivated due to its efficiency and theoretically interesting. The TTT update can be implemented in a single forward-backward pass with appropriate masking, as described by the Remark in Section 3, which makes it a meaningful choice with minimal test-time compute overhead. Moreover, our theory and experiments demonstrate that single-step gradient descent can be sufficient, which aligns with the existing practical works (Akyürek et al., 2024) that just a few gradient steps offer significant test-time improvements. Also, even with the linear attention model, the analysis poses significant technical challenges: we must calculate the 8th moments of matrices, and since this is practically intractable, we rely on Gaussian approximation techniques presented in Lemma B.1 in Appendix B. > Q1. How would performing additional gradient descent steps at test time affect the results? Specifically, how would it impact the loss improvement described in the paper's theorem? Response: Thank you for your thoughtful question. Theoretically, there are technical difficulties in analyzing multiple steps of gradient descent as each subsequent update introduces higher-order dependencies and makes it hard to compute the expectation $\mathbb{E}[\mathbf{W}^\top \mathbf{W}]$. However, as we discussed in our multi-gradient step experiment in Figure 2c, one would expect the improvement obtained from the next steps to diminish. This can also be intuitively seen in Section 5, as the improvement is given by $A^2/(A+B)$ where $A$ is the misalignment and $B$ is the magnitude term. Each gradient step reduces $A$ as we decrease the misalignment between $\mathbf{W}$ and $\boldsymbol{\beta}_{TT}$, and that $B$ remains relatively stable with the updates. Then, it can be argued that the loss improvement decreases in the next gradient steps. > Q2. Can this approach be extended to a one-layer transformer with softmax attention and an MLP? How challenging would this extension be, and what factors contribute to the difficulty? Response: We thank the reviewer for raising this point. For a single-layer transformer with softmax attention and possibly an MLP layer at the end, the gradient involves calculating terms like $\nabla_{\mathbf{W} } \mathrm{softmax}(\mathbf{X} \mathbf{W} \mathbf{X}^\top)$ where $\mathbf{W}_Q \mathbf{W}_K^\top = \mathbf{W}$. For example, considering one row of this resulting matrix $\mathbf{s} = \begin{bmatrix} s_1 ~ \cdots ~ s_n \end{bmatrix}^\top = \mathrm{softmax}(\mathbf{X}\mathbf{W}\mathbf{z}) \in \mathbb{R}^{n}$ and taking its derivative w.r.t $\mathbf{W}$ gives the following form: $$ \qquad \frac{\partial s_i}{\partial \mathbf{W}} = s_i (\mathbf{x_i} - \sum_{j} s_j \mathbf{x_j}) \mathbf{z}^{\top}. $$ As we analyze the performance of the model after the gradient descent update, we encounter expressions involving high-order moments of data matrices while calculating $\mathbb{E}[\mathbf{W}^\top \mathbf{W}]$. With this much complicated gradient form, analyzing the update and especially calculating high-order moments of the data matrix $\mathbf{X}$ becomes far more challenging and intractable. Also, adding an MLP layer might further complicate the backward pass by adding another layer of non-linear transformation.	Summary: This paper investigates how Test-Time Training (TTT) affects transformer models' in-context learning capabilities. The authors formulate this as a two-stage problem: a model is first trained on a pre-training dataset, then further trained on test data using single-step gradient descent. They provide theoretical proofs for performance gains through TTT, analyze the relationship between context length and test data size, and compare TTT with direct training on test data from scratch. Experimental results validate their theoretical findings. Claims And Evidence: Yes. The claims are supported by theoretical proofs and experimental validation. Methods And Evaluation Criteria: The paper presents a simplified version of TTT compared to practical implementations. Their approach fixes the context and uses k different mini-batch data with MSE loss to train the model, testing it using the same context as training. This simplification differs significantly from TTT used in practice such as [1],[2], potentially limiting the practical insights this work can provide. [1] Akyürek, E., et al. "The surprising effectiveness of test-time training for abstract reasoning."  [2] Sun, Y., et al. "Learning to (learn at test time): RNNs with expressive hidden states." Theoretical Claims: The mathematical proofs contain imprecise statements, particularly in the use of approximation symbols ($\approx$) without specifying error bounds. For a paper focused on rigorous theoretical analysis, such imprecision is problematic, as seen in Theorem 4.2 and Corollary 4.5. Experimental Designs Or Analyses: While the theoretical validation experiments are sound, the real-world experiments in Section 6.2 have methodological issues. The comparison between TabPFN and TabPFN+TTT should account for the additional 1000 samples used in TTT as part of the context length. The comparison in Figure 3a is therefore problematic. Additionally, for the T4 benchmark experiments, more detailed information about test dataset size and sampling methodology would be beneficial. Supplementary Material: No supplementary material was included in the submission. Relation To Broader Scientific Literature: The paper's main contribution lies in proving that fine-tuning on labeled test data can improve performance. However, this empirical result is somewhat expected, limiting the paper's potential impact. Essential References Not Discussed: NA Other Strengths And Weaknesses: Strengths: 1. Comprehensive comparison of TTT performance with different initialization strategies (pre-trained vs. zero initialization) 2. Thorough analysis of performance gains relative to context and test example numbers, with experimental results supporting theoretical findings Weaknesses: 1. The paper's oversimplified TTT procedure. The main comparison between randomly initialized models and pretrained models lacks practical insights due to this oversimplified framework. 2. The experiments in Section 6.2 need more detailed analysis and better clarification of the methodological choices. 3. The expressions and claims in propositions and theorems are unclear and could be better formulated. Other Comments Or Suggestions: If there are any misunderstandings on my part, please point them out, and I will reconsider my evaluation of this work. Questions For Authors: please refer to the weakness part in Other Strengths And Weaknesses, I don’t have more question, my main concern is the oversimplified problem setting. This simplification makes the approach significantly diverge from practical TTT applications. Ethical Review Concerns: NA Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We thank the reviewer for their detailed evaluation. We reply to each of the points below. > Theoretical claims. The mathematical proofs contain imprecise statements. ... Response: Thank you for pointing this out. The approximations in Theorems 4.2, 5.3, and Corollary 4.5 stem from ignoring lower order terms and using Gaussian Approximation in Lemma B.1, which rigorously bounds the error term. In the proportional regime ($n/d = \Theta(1)$), all approximations yield an error on the order of $n^{-1}$, while the main loss terms are in the constant order. Consequently, any approximation error is small, which is evident in the close match between theoretical and empirical curves in Figures 1-2. We also wanted to kindly note that after Theorems 4.2 and 5.3 in lines 190-192 and 290-291, we refer readers to Remark B.5 in Appendix B for discussion on the validity of the approximations. We appreciate your feedback, and to clarify these points, we plan to move Remark B.5 into the main body. > Methods And Evaluation Criteria. Their approach fixes the context and uses k different mini-batch data ..., testing it using the same context as training. > Weakness 1. The paper's oversimplified TTT procedure. ... comparison between randomly initialized models and pretrained models lacks practical insights due to this oversimplified framework. Response: Thank you for your question. While our single-step TTT setup may not capture every real-world scenario, it's both theoretically interesting and practically informative. The main reason behind using the same context is to make gradient update tractable. For testing, however, we do not reuse the same context as in training but instead evaluate the model over any new context–query pairs by taking expectations (lines 140–142). Even under the current setup, there are major technical challenges, such as computing $\mathbb{E}[\mathbf{W}^\top \mathbf{W}]$, which requires the Gaussian Approximation technique and a rigorous error analysis. Without fixing the context in the training, it's practically infeasible to obtain a closed-form update (Proposition 3.1) and compute this expectation. Still, we believe that our framework presents two clear, theoretically verified practical insights: 1) We characterize how alignment between the pre-trained model and target task affects TTT improvements and phase-transition points, which is illustrated in Figures 2a-2b and practically verified by GPT-2 experiments of Figure 2c. 2) Both our theory and experiments indicate that one-step TTT can be sufficient, which complements the existing practical findings (Akyürek et al., 2024) that a few gradient steps yield significant test-time improvements. Overall, we believe our framework offers useful practical insights and can serve as a baseline theoretical reference for future research on TTT-ICL interactions. > Experimental Designs Or Analyses. .... the real-world experiments in Section 6.2 have methodological issues. ... > > Weakness 2. The experiments in Section 6.2 need more detailed analysis and better clarification of the methodological choices. Response: Thank you for your feedback. While TabPFN+TTT indeed uses an extra $1000$ samples, our main goal is to demonstrate how TTT reduces the needed sample complexity for each query from the new task, not just one. The TTT update is performed only once per task to adapt the model, which helps improve the inference time efficiency as each subsequent evaluation needs much fewer in-context examples. We want to highlight that this is more evident near the zero-shot regime as TTT helps the model "memorize" new task dynamics and improves accuracy from 0.2 to 0.45. Akyürek et al. (2024) also argue that during TTT, for each task, the model is evaluated on a batch of test points after a small number of gradient steps on a test-time training set, specifically in Section 5 for BBH tasks. Regarding the dataset, we use the T4 benchmark from Gardner et al. (2024), which is a large set of real-world tabular tasks and consists of four million tables. Following the official TabPFN v2 implementation and our own setup, we select the datasets with at least 1,250 samples (1,000 for training, using an 80–20 split), at most 10 classes (selecting the 10 most frequent), and a 100-feature limit (chosen randomly). We also convert regression tasks into 10-class classifications based on quartiles to maintain consistency in training and evaluation. We appreciate your feedback and plan to detail our dataset choice and experimental methodology both in the main text and appendix. > Weakness 3. ... propositions and theorems are unclear and could be better formulated Response: We are planning to do a pass over the statements and relocate Remark B.5. into the main text for clarity and completeness of the approximations in the theorem statements. We welcome any additional suggestions to clarify our statements.	Summary: In-context learning and Test-time Training (TTT) are two ways of enhancing the predictive power of pretrained models on new tasks at test time. In-context learning involves incorporating demonstrations from the task into the prompt context. TTT involves light finetuning of the model on data related to the test task. Recent work has shown that TTT can naturally integrate with in-context learning: one can lightly finetune the model on provided demonstrations and subsequently use them as an in-context prompt with the finetuned model. This paper develops a theoretical understanding of TTT to enhance the in-context learning ability of a model for a given task. Specifically, given a model trained for in-context learning of linear functions, the model is test-time trained on in-context prompts from a target linear function. The analysis focuses on single-layer linear attention models where a single gradient step is used for TTT. The paper characterizes the performance of the test-time trained model as a function of context length, the number of TTT samples, and the alignment between the pretrained model and the target task. High-level takeaways from the analysis include: - With TTT, one can reduce the number of in-context learning examples needed to perform well on a given task. Of course, this comes at the cost of additional training samples and extra time during the TTT phase. - Comparison of TTT from scratch vs. TTT on a model pretrained for in-context learning: (i) The relative advantage of TTT on top of a pretrained in-context learning model depends on how "aligned" the target task is with the tasks the model was trained on. (ii) As the number of TTT samples increases, the relative advantage of TTT on a pretrained model diminishes. Simulations demonstrate the theory, and some findings are also empirically validated on multi-layer non-linear Transformers. Finally, the paper takes a model pretrained for in-context learning of tabular data and shows that with TTT, one can substantially reduce the number of in-context examples needed to perform well on given tasks. This leads to efficient inference, especially given the quadratically growing cost of softmax attention. ### update after rebuttal I thank the authors for their detailed response and answering my clarifying questions. My general view of strengths and weaknesses of the paper remains the same. Hence, I would stick to my original rating. Claims And Evidence: Yes, the claims made in the submission are supported by clear evidence. Methods And Evaluation Criteria: Yes, the proposed methods and evaluation criteria make sense for the problem. Theoretical Claims: I did not verify the proofs but the claims made intuitive sense and were also corroborated with simulations. Experimental Designs Or Analyses: The experimental design and analysis seems sound. Supplementary Material: I did not go through the supplementary material. Relation To Broader Scientific Literature: Discussed in summary and strengths and weaknesses sections. Essential References Not Discussed: Prior work has been adequately discussed. Other Strengths And Weaknesses: Strengths: The intersection of TTT and in-context learning provides a valuable framework for understanding the interplay between in-context learning and in-weights learning. This paper advances this understanding by formally exploring the role of factors such as alignment between target and pretraining tasks, the number of TTT samples, and context length. I also liked the experiment with tabular data. Recently, Transformer models pretrained for in-context learning of tabular data have proven highly effective. However, inference with these models can be expensive for large tabular datasets due to the cost increasing qudratically with the sequence length. This work demonstrates that such costs can be significantly reduced using TTT, though at the expense of additional training time. Overall, I enjoyed reading the paper. It is clearly written, with simulations accompanying most theoretical results, making it easy to absorb the main claims. Weaknesses: While the theory presented concretely highlights the effect of various factors on TTT, most results do not seem particularly surprising. A possible criticism is that the theory does not provide new insights that significantly change existing perspectives on TTT or in-context learning. Other Comments Or Suggestions: Minor typo: The gradient seems to be missing from the gradient descent update equation in line 134. Questions For Authors: Q1. What is the intuition behind non-monotonic trends in Figure 1a? This was probably the most non-intuitive result for me. It would be great if the authors could discuss the intuion and practical relevance of this result. Q2. Are there any insights from your theoretical analysis that you think would hold generally and add to existing perspectives on TTT or in-context learning? I know this question is a bit subjective but I would love to hear authors' thoughts on this. Q3. The experiment with GPT-2 is not on top of a pretrained GPT-2 model but using a randomly initialized GPT-2 style architecture? It would be good to clarify this to avoid confusion. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We appreciate the reviewer’s positive assessment of our work and their detailed feedback. We now address each point below. > Weakness. While the theory presented concretely highlights the effect of various factors on TTT, most results do not seem particularly surprising. ... theory does not provide new insights that significantly change existing perspectives on TTT or in-context learning. Response: The main goal of our paper is to provide a rigorous theoretical framework that precisely quantifies the improvement by single-step gradient descent with TTT for in-context learning tasks. While it may seem intuitive that TTT would help or that transition points might emerge, to our knowledge, our work is the first formal analysis revealing why and how these phenomena occur. Achieving this required overcoming significant technical challenges, including computing high-order matrix moments using Gaussian approximations with a rigorous error analysis. Particularly, we characterize the improvement by TTT in terms of context length $(n)$, embedding dimension $(d)$, test-time training set size $(k)$, and the alignment between the pre-trained model and target task. This characterization allows us to show how the transition points depend on different regimes of test-time training set size $(k)$ and alignment between the model and target task, and we reveal the resulting non-monotonicities after TTT. Moreover, our theory and experiments show that one step of TTT is sufficient, which complements the existing practical research (Akyürek et al., 2024) stating that a few gradient steps offer significant test-time improvements. We hope that our results will serve as a foundation for future research on the interaction of TTT and ICL methods. We've provided a further discussion of insights in Q2. > Minor typo: The gradient seems to be missing from the gradient descent update equation in line 134. Response: Thanks; we will edit the revision accordingly. > Q1. What is the intuition behind non-monotonic trends in Figure 1a? Response: The non-monotonic behavior is observed as the result of two opposing effects, which are the initial loss and the improvement by TTT. * As $n$ grows against $d$ (i.e. $\alpha$ increases), the pre-trained model does better initially and already has a lower loss before TTT, which makes it harder to be further reduced by TTT as the rank-1 update is unable to correct all directions. * On the other hand, when $d$ grows against $n$ ($\alpha$ decreases), the initial loss is high, and there's more room (error) to be corrected by rank-1 update, and thus, the improvement by TTT is larger. This intuitively aligns with Theorem 4.2, which states that the TTT improvement scales as $(\frac{d}{n+d})^3$. Together, these two trends cause the non-monotonic behavior. Practically, this tells us that TTT through single-step gradient descent is more likely to be useful when $d = \Omega (n)$. > Q2. Are there any insights from your theoretical analysis that you think would hold generally and add to existing perspectives on TTT or in-context learning? Response: We thank the reviewer for the valuable question. A key insight from our paper is that test-time training can serve as a lightweight, supervised complement to ICL. When TTT is combined with ICL, one might benefit from the examples at test time in a supervised fashion and do a quick parameter update by treating a subset of them as training data instead of simply using them all as context. Accordingly, we analyze the single-step gradient descent as it has minimal test-time compute overhead (which makes it close to realistic settings). This way, the TTT update can be done only in a single forward-backward pass with appropriate masking, as discussed in the Remark in Section 3. Through our experiments, we also observe that a single gradient step of TTT captures a large part of the benefit compared to multiple steps, and might be an appealing method for practical scenarios. This observation also holds in practice as Akyürek et al. (2024) find that only a small number of gradient steps on test-time training data is enough to achieve strong performance. We believe that our work might inspire future integrations of TTT with ICL. > Q3. The experiment with GPT-2 is not on top of a pretrained GPT-2 model but using a randomly initialized GPT-2 style architecture? Response: We thank the reviewer for bringing this detail. Between lines 428-431, we discuss how we obtain the pre-trained and scratch models. The scratch model is just initialized randomly with the GPT-2 architecture before the TTT process. For the pre-trained model, we obtain it by training it until convergence with the tasks sampled from the task covariance $\boldsymbol{\Sigma}_{\boldsymbol{\beta}}$, and before the training, it's also initialized randomly using the GPT-2 style architecture. We will add this missing detail and clarify the related paragraph further.	null	null	null	null	null	null
On the Resilience of LLM-Based Multi-Agent Collaboration with Faulty Agents	Accept (poster)	Summary: The paper explores how well multi-agent systems based on large language models (LLMs) can handle errors introduced by faulty agents. It specifically looks at resilience across tasks like writing code, solving math problems, translating text, and evaluating written text. To test this, it uses two methods: AUTOTRANSFORM, which alters agent behaviors, and AUTOINJECT, which directly introduces errors into agent communications. Findings show that hierarchical system structures cope best with faults, outperforming flat and linear setups. Interestingly, linear structures were the least resilient. The authors recommend hierarchical models for designing robust multi-agent collaborations using LLMs. Claims And Evidence: Yes. Methods And Evaluation Criteria: Yes. Theoretical Claims: There are not many theoretical claims in this paper. Experimental Designs Or Analyses: I examined the experimental design and analyses conducted in this paper. The experiments utilized two well-defined error simulation methods, AUTOTRANSFORM and AUTOINJECT, across three clearly differentiated multi-agent system structures (linear, flat, and hierarchical).The metrics used (accuracy and specific task-related metrics such as Pass@1 and BLEURT) were appropriate and clearly presented. Overall, the experimental design and analyses are sound and rigorous. The only concern here is the author only use several baseline like Self-Collab and CAMEL which cannot fully reflect the current advanced methods. Suggest to add more discussion about Graph-based framework (LangGraph, GPTSwarm), and most popular industrial practice ones like Dify, etc. Supplementary Material: I reviewed the supplementary materials; they contain code without additional analyses and do not influence my review. Relation To Broader Scientific Literature: The paper's key contributions connect closely with broader scientific literature on multi-agent systems, resilience, and safety in AI collaborations. Essential References Not Discussed: Need to supplement more discussions about published in 2024 and 2025, for example, the automated evaluation methods. Besides, in the introduction, I suggest the author could move the core claim at the very beginning. Since some of the basic claims are not so attractive recently but I like the basic idea. Other Strengths And Weaknesses: - It would be beneficial if the authors could include additional experiments to demonstrate whether the observed issues persist across other frameworks. - The idea of this paper is not brand-new but I appreciate the solid writing in this paper. Other Comments Or Suggestions: See my previous comments. Questions For Authors: See my previous comments. Ethical Review Concerns: No ethical concerns. Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: We deeply appreciate reviewer 3cYX’s time for reviewing and your insightful comments. We are particularly encouraged that you find that the experiments and analyses are sound and rigorous. We address your concerns one by one: ## [Design & Analysis] [W1] Advanced methods like Graph-based frameworks. Inspired by GPTSwarm and MacNet, we design two advanced graph-based multi-agent frameworks using four agents: 1. Complete graph (a flat structure): each agent generates their own answers. After receiving all others’ answers in the next run, they re-generate the answers after thinking. The final answer is the majority one. 2. Star (a hierarchical structure): one leader proposes three approaches and distributes them to the three agents. After receiving the solutions, the leader gives its evaluation and generates the final answer. We evaluate GPT-3.5 using the Math task. The performance is shown in the table below. We can conclude that our methods and analyses are applicable to diverse frameworks. Flat structure still has a lower performance since there is no leader coordinating the work. \| System Type \| Vanilla \| AutoTransform \| AutoInject \| \|---\|---\|---\|---\| \| Graph \| 28.00 \| 20.00 \| 16.00 \| \| Star \| 36.00 \| 30.00 \| 28.00 \| ## [Reference 1] More related work in 2024-2025. We have thoroughly cited and compared relevant papers in 2024-2025 [1-9] in our paper, according to all reviewers’ suggestions. In short, the NetSafe is the most relevant. While they provide amazing findings about the impact of different numbers of faulty agents, they do not investigate more subjective tasks like translation and text evaluation. We include code generation task, enabling us to study the impact of error types. Additionally, our proposed AutoTransform and AutoInject methods can be viewed as automated evaluation tools for simulating failure scenarios and systematically measuring the robustness of multi-agent systems. This aligns with recent trends in automatic evaluation techniques (e.g., Zhang et al., 2024; Ju et al., 2024) where LLMs are used to both generate perturbations and evaluate outcomes. [1] Zhang et al., Multi-agent Architecture Search via Agentic Supernet. 2025. [2] Yu et al., A Survey on Trustworthy LLM Agents: Threats and Countermeasures. 2025. [3] Mao et al., AgentSafe: Safeguarding Large Language Model-based Multi-agent Systems via Hierarchical Data Management. 2025. [4] Zhou et al., CORBA: Contagious Recursive Blocking Attacks on Multi-Agent Systems Based on Large Language Models. 2025. [5] Wang et al., G-Safeguard: A Topology-Guided Security Lens and Treatment on LLM-based Multi-agent Systems. 2025. [6] Yu et al., LLM-Virus: Evolutionary Jailbreak Attack on Large Language Models. 2025. [7] Zhang et al., G-Designer: Architecting Multi-agent Communication Topologies via Graph Neural Networks. 2024. [8] Yu et al., NetSafe: Exploring the Topological Safety of Multi-agent Network. 2024. [9 Tran et al., Multi-Agent Collaboration Mechanisms: A Survey of LLMs. 2025. [Zhang et al. (already in our paper)] PsySafe: A Comprehensive Framework for Psychological-based Attack, Defense, and Evaluation of Multi-agent System Safety. [Ju et al. (already in our paper)] Flooding Spread of Manipulated Knowledge in LLM-Based Multi-Agent Communities. ## [Reference 2] Improving the introduction section. We appreciate that you like our basic ideas. We have moved the core claims to the beginning of our introduction section. The text is shown below: > Just as human organizations rely on resilient structures to function despite internal errors, multi-agent systems built on large language models (LLMs) must also withstand faulty participants to remain effective. In this paper, we argue that the resilience of LLM-based multi-agent collaboration critically depends on the system’s structural design. As these agents increasingly take on complex, collaborative tasks, their decentralized nature makes them vulnerable to clumsy or even malicious agents—those that degrade performance or disrupt workflows. Drawing a parallel to organizational theory, we find that hierarchical structures—common in robust human institutions—offer superior resilience over flat or linear ones. To rigorously test this hypothesis, we propose two methods for simulating faulty agents, and demonstrate that structural design, combined with simple defensive strategies, can significantly mitigate performance degradation.	Summary: The paper investigates the resilience of different multi-agent architectures to faulty agents. Two approaches, autotransform, which transforms the system prompt of the agent into a malicious one, and autoinject, which takes the outputs of other agents and intentionally injects specific errors, have been proposed to create faulty agents for the evaluation. The experiments involve four different tasks and six agents. The results show that hierarchical design of the multi-agent system is more resilient to faulty agents. Claims And Evidence: "We are the first to examine how different structures of multi-agent systems affect resilience when faulty agents exist and disrupt collaboration." There are other works a few months ahead studying the same problem, with similar results. "The hierarchical structure has a higher resilience than the other two, exhibiting the smallest accuracy drop." Intuitively, I tend to believe this is correct. However, beyond the structure, how the agents communicate with each other also influences the robustness. The results in Figure 3 involve two agents per type, but without the distinction of the communication scheme, which weakens the conclusion. Methods And Evaluation Criteria: I am concerned about the design of autotransform, which assumes that the single agent functions with one piece of system prompt. In fact, the agent can interact with the environment and use tools in various ways. The system prompts can be diverse and involve multihop interaction with either the user or the environment. It is unclear whether the approach can be generalized to more general agent settings. Also, the evaluation focuses on code generation, math problems, translation, and text evaluation. All these tasks can be achieved using an agent or just a model. Tasks not achievable by a standalone model should be considered. Theoretical Claims: There are no theoretical results in this work. Experimental Designs Or Analyses: See Methods And Evaluation Criteria Supplementary Material: I reviewed the D. Propmt details. Relation To Broader Scientific Literature: Zhang et al, G-Designer: Architecting Multi-agent Communication Topologies via Graph Neural Networks, Oct 2024. This paper studied different topologies of multi-agent systems. Yu et al, NetSafe: Exploring the Topological Safety of Multi-agent Network, Oct 2024. This paper studies which topology of multi-agent system is safer, which is highly related to the current work. Essential References Not Discussed: [1] Zhang et al, G-Designer: Architecting Multi-agent Communication Topologies via Graph Neural Networks, Oct 2024. [2] Yu et al, NetSafe: Exploring the Topological Safety of Multi-agent Network, Oct 2024. These two papers are highly relevant and were posted three months before the submission deadline. Especially in [2], there are similar conclusions regarding the relation between safety and agent topology. Other Strengths And Weaknesses: The paper is well-written, and the motivation is well-explained. However, the scope of the work needs to be expanded. Comparison with previous works should be included. Other Comments Or Suggestions: n.a. Questions For Authors: When the core LLM of one of the agent is changed to large reasoning models with a lot of (perhaps redundant) reasoning outputs, will the performance be affected? Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We deeply thank reviewer iwu4 for reviewing and appreciate the suggestions. We are encouraged that you find our paper well-written and sufficiently motivated! We address your concerns one by one: ## [Claim & Evidence 1] [Broader Literature] [Reference] [W1] Missing papers. Thanks for providing the missing references. We have thoroughly cited and compared the works of Zhang and Yu in our Related Work section. Additionally, we have included discussions about other relevant papers [1-6]. In short, the NetSafe is the most relevant. While they provide amazing findings about the impact of different numbers of faulty agents, they do not investigate more subjective tasks like translation and text evaluation. We include code generation task, enabling us to study the impact of error types. Additionally, according to ICML 2025 Reviewer Instructions (icml.cc/Conferences/2025/ReviewerInstructions), “Authors cannot expect to discuss other papers that have only been made publicly available within four months of the submission deadline.” Thus the two papers submitted in October are concurrent work of our submission. [1] Zhang et al., Multi-agent Architecture Search via Agentic Supernet. [2] Yu et al., A Survey on Trustworthy LLM Agents: Threats and Countermeasures. [3] Mao et al., AgentSafe: Safeguarding Large Language Model-based Multi-agent Systems via Hierarchical Data Management. [4] Zhou et al., CORBA: Contagious Recursive Blocking Attacks on Multi-Agent Systems Based on Large Language Models. [5] Wang et al., G-Safeguard: A Topology-Guided Security Lens and Treatment on LLM-based Multi-agent Systems. [6] Yu et al., LLM-Virus: Evolutionary Jailbreak Attack on Large Language Models. ## [Claim & Evidence 2] The communication scheme of agents. In our experiment, all of our selected models adopt a communication scheme of direct messaging, meaning that only the recipient agent will be able to see the message and no other message processing schemes such as summarizing or broadcasting is involved in the process. Therefore, the communication scheme is a controlled variable in our experiment, and does not influence our conclusion on the system structures. ## [Method & Evaluation 1] Whether AutoTransform can be generalized to more general agent settings (tool uses). AutoTransform takes the whole agent profiles as the subject of our transformation. While system prompts can be diverse (for multiple tool uses), an agent’s profile is usually consistent, since it includes the main goals, task descriptions and constraints of an agent. Therefore, our method can work with agents equipped with tools that can interact with the environment. Moreover, some of our selected systems are already equipped with external tools. For instance, Self-collab equipped agents with a python interpreter for code testing, and MetaGPT’s agents have access to a message pool from which to retrieve history messages when performing tasks. This ensures our method is still valid in the more general settings. We also compute the performance on code tasks of different systems by whether or not they have tool modules. As is shown below, the performance of AutoTransform is consistent with these two types of agent systems. \| System Type \| Vanilla \| AutoTransform \| \|---\|---\|---\| \| w/o Tool Use \| 63.20 \| 47.00 \| \| w/ Tool Use \| 66.27 \| 42.70 \| ## [Method & Evaluation 2] Other tasks. We acknowledge the need for evaluating more complex, real-world tasks hard to complete by a standalone model, such as making complete, executable software. For example, generate a snake game with pygame. Using a single GPT-3.5, the code is incomplete and the snake cannot be controlled. Using CAMEL, we achieve an executable game, with extensive features. When using AutoTransform, the code is still executable but the snake's speed is too fast and the mapping between arrow key and snake's movement is mixed (e.g., pressing "left" will make the snake move upward). When using AutoInject, the game is totally unexecutable due to multiple errors injected. Our method is still effective in such real-world scenarios. Additionally, though the tasks can be completed by single agents, from the results of single agents vs. multi-agents in Figure 4 on page 6 we can see that multi-agent systems can improve the performance over single agents. ## [Q1] CoT models. We explore the impact of CoT using a reasoning model, o1-mini, on the Math task due to budget limits. The results are presented in the tables below. For models using CoT, the performance is largely improved. However, we can still observe the performance decrease caused by faulty agents. Hierarchical structures still outperform the other two. \| o1-mini (Math) \| Linear \| Flat \| Hierarchical \| \|---\|---\|---\|---\| \| No Attack \| 78.00 \| 80.00 \| 81.00 \| \| AutoTransform \| 14.00 \| 18.00 \| 63.00 \| \| AutoInject \| 70.00 \| 74.00 \| 77.00 \|	Summary: This paper investigates the resilience of large language model (LLM)-based multi-agent systems against faulty or malicious agents. It compares different system architectures—Linear, Flat, and Hierarchical—across tasks like code generation, math problem-solving, translation, and text evaluation, finding hierarchical structures most resilient. Additionally, it introduces methods to simulate agent errors (AUTOTRANSFORM, AUTOINJECT) and proposes defense strategies (Challenger, Inspector) that significantly enhance system robustness. Claims And Evidence: Overall, the paper's claims are well-supported by clear experimental results and analyses. Key findings—such as hierarchical structures offering better resilience, semantic errors causing greater impact than syntactic ones, and certain error injections even improving performance—are convincingly demonstrated. However, the explanation for why AUTOTRANSFORM errors have less impact than AUTOINJECT in GPT-3.5 contexts may need further empirical validation or deeper analysis. Methods And Evaluation Criteria: In general sense the methods make sense. When you specify the reasons at the line 261-268, you should specify proofs of those such as citations, or giving examples, similarly from line 247 to 253, you should give more proof instead of just giving a reason with out proof. Theoretical Claims: N/A Experimental Designs Or Analyses: In your experiment, you using different multiagent framework for those structure, metagpt, camel etc, how do you make sure it is gonna be a fair comparison of those structures then, since they all use different system prompt and some special design, so I would question the fairness when you using 6 different code base for the test to represent for different structures. Supplementary Material: Yes Prompt and case study Relation To Broader Scientific Literature: The paper related to prompt attack agent attack, agent system roboustness Essential References Not Discussed: N/A Other Strengths And Weaknesses: Strengths: 1. The paper addresses an important and timely research topic. 2. It represents the first systematic exploration within this specific area. Weaknesses: 1. The graphical presentation could be improved for better readability and clarity. Some explanations require refinement; for example, on line 19, clearly define what agents A, B, and C represent, ideally adopting a more formal mathematical notation. 2. The explanations provided between lines 261–268 and 247–253 lack sufficient empirical support or citations. The authors should strengthen their claims by providing concrete examples or referencing relevant prior studies. 3. When presenting results and findings, explicitly include numerical data and specific evidence to substantiate conclusions clearly. Other Comments Or Suggestions: Suggestion: 1. I would like to see some other communication topologies can be considered such as Tree, star, graph, in Scaling Large Language Model-based Multi-Agent Collaboration 2. I would like to see how your method will affect single agent, then you can. Compare with how multiagent can handle it better or worse Questions For Authors: N/A Ethical Review Flag: Flag this paper for an ethics review. Ethics Expertise Needed: ['Privacy and Security'] Ethical Review Concerns: Since this research is about multiagent attack and defense, ethical review is required Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We deeply thank reviewer xvqz for your time and effort in reviewing our work, and your invaluable comments that further enrich our paper. We are particularly encouraged that you find our claims well-supported, our methods & evaluations reasonable, and by your recognition of the importance and novelty of our work. We address your concerns here: ## [Claim & Evidence] AutoTransform is harder to control than AutoInject. The reason why faulty agents produced by AutoTransform have less impact than directly injecting errors (AutoInject) is because GPT-3.5-Turbo is weaker in terms of the precise control of generated errors. We conduct an analysis using AutoTransform to instruct agents to introduce syntax errors in 20% and 40% of the code lines. The results are summarized below: \| Error Rate \| Avg \| Std \| Min \| Max \| \|---\|---\|---\|---\|---\| \| Instruct 20% \| 1.56 \| 3.65 \| 0.00 \| 14.30 \| \| Instruct 40% \| 9.49 \| 26.70 \| 0.00 \| 90.10 \| These results indicate significant variability, with agents struggling to consistently achieve the precise error rates of 20% or 40%. This underscores the necessity and robustness of our AutoInject method. ## [Method & Evaluation] [W2 & W3] Inclusion numerical data and specific evidence to support our claims. We have added numbers at (1) Left-column: Line 248, 251, 261, 274 and (2) Right-column: Line 251, 253, 257, 263, 292, 308, from the results in Table 5, 6, 7, and 8 in Appendix C on page 13. ## [Design & Analysis] Fair comparison using the 6 different code bases. Different structures have various role designs. For example, a flat system may not have a leader, where the other two systems have. There is not a set of profiles applicable to all multi-agent systems. Therefore, instead of manually writing profiles, we use the code bases from published studies which have been optimized by the authors for the specific structures. To offer fairer comparison, i.e., to mitigate the impact of using different prompts, we have included two systems per structure. ## [W1] Math definition on agent collaborations. A multi-agent system can be defined as a graph: $G = (V, E)$, where $V$ represents agents and $E \subseteq V \times V$ is a set of directed edges. Each $(u, v) \in E$ denotes agent $u$ reports to agent $v$. - Linear systems are: directed path graphs, where $\forall v \in V, v \neq s, v \neq t$, we have: $\deg^+(v) = \deg^-(v) = 1$; for the endpoints, $\deg^-(s) = 0$, $\deg^+(s) = 1$, $\deg^+(t) = 0$, and $\deg^-(t) = 1$. Agents in this structure form a chain from $s$ to $t$. - Flat systems are: directed complete graphs with bidirectional edges, where $\forall u, v \in V, u \neq v$, both $(u, v) \in E$ and $(v, u) \in E$. This represents a fully connected, non-hierarchical structure. - Hierarchical systems are: rooted directed trees, where there exists a unique root agent $r \in V$ such that $\deg^-(r) = 0$, and $\forall v \in V \setminus {r}$, $\deg^-(v) = 1$. The structure is acyclic and forms a strict top-down hierarchy. ## [Q1] Other communication topologies. Inspired by MacNet and GPTSwarm, we design two advanced graph-based multi-agent frameworks using four agents: 1. Complete graph (a flat structure): each agent generates their own answers. After receiving all others’ answers in the next run, they re-generate the answers after thinking. The final answer is the majority one. 2. Star (a hierarchical structure): one leader proposes three approaches and distributes them to the three agents. After receiving the solutions, the leader gives its evaluation and generates the final answer. We evaluate GPT-3.5 using the Math task. The performance is shown in the table below. We can conclude that our methods and analyses are applicable to diverse frameworks. Flat structure still has a lower performance since there is no leader coordinating the work. \| System Type \| Vanilla \| AutoTransform \| AutoInject \| \|---\|---\|---\|---\| \| Graph \| 28 \| 20 \| 16 \| \| Star \| 36 \| 30 \| 28 \| ## [Q2] Impact on single agents. We conduct experiments on applying the two error-introducing methods on a single agent based on GPT-3.5-Turbo across all four tasks. The performance is shown below: \| Tasks \| Vanilla \| AutoInject \| AutoTransform \| \|---\|---\|---\|---\| \| Code \| 58.41 \| 15.24 \| 3.92 \| \| Math \| 24.00 \| 18.00 \| 8.00 \| \| Translate \| 68.42 \| 61.08 \| 68.42 \| \| Text Eval \| 41.25 \| 32.50 \| 18.75 \| Compared to the performance of other multi-agent systems (the table below), we conclude that all three types of systems have better resilience against both methods compared to a single agent. This is because the systems have other “good” agents for reviewing and testing, which can identify the errors made by the faulty agent. \| Systems \| Vanilla \| AutoInject \| AutoTransform \| \|---\|---\|---\|---\| \| Single Agent \| 48.02 \| 31.71 \| 21.66 \| \| Linear \| 55.62 \| 38.27 \| 38.24 \| \| Flat \| 54.37 \| 40.25 \| 43.93 \| \| Hierarchical \| 53.00 \| 48.12 \| 46.57 \|	Summary: This paper explores the resilience of multi-agent collaboration by introducing faulty agents and errors. It embarks on an empirical approach to examine performance drops in different scenarios / multi-agent system structures. The authors introduce AUTOTRANSFORM and AUTOINJECT algorithms for creating faulty agents with the evaluation based on error types, quantities, and frequencies. The work provides some insights on the impact of faulty agents across different tasks, including code generation, translation, math and text evaluation. Claims And Evidence: The paper provides comprehensive empirical experiments with multiple tasks (code generation, math solving, translation and text evaluation), system structures (linear, flat and hierarchical) and error types (semantic and synaptic). The impacts of faulty agents are observed in various settings and illustrated in different figures. Methods And Evaluation Criteria: The proposed methods are reasonable for investigating the resilience of multi-agent AI system with two algorithms: AUTOTRANSFORM and AUTOINJECT. It also provide a number of tasks, including coding, math solving, translation and text evaluation for better generalizability of its findings. Theoretical Claims: The paper does not have mathematical proofs. Experimental Designs Or Analyses: The experimental design of the paper is reasonably well-executed, with multiple experiments across different multi-agent systems and diverse tasks. The authors also provide various ways of controlling errors to investigate the performance impacts. Supplementary Material: Yes Relation To Broader Scientific Literature: - The paper broadly relates to LLM-based multi-agent collaboration, building on existing literature work, such as MetaGPT, AgentVerse, etc. The authors investigate the concept of resilience in these multi-agent systems by introducing faulty agents. - It also provides a theoretical basis for understanding multi-agent collaboration topology, demonstrating certain structures perform better. - The key contributions of the paper extend the broad areas of AI safety and trustworthiness. Essential References Not Discussed: Some missing references: - Perez, E., Huang, S., Song, F., Cai, T., Ring, R., Aslanides, J., ... & Irving, G. (2022). Red teaming language models with language models. arXiv preprint arXiv:2202.03286. - vulnerabilities in LLMs. - Tan, S., Joty, S., Baxter, K., Taeihagh, A., Bennett, G. A., & Kan, M. Y. (2021). Reliability testing for natural language processing systems. arXiv preprint arXiv:2105.02590. - reliability testing for NLP systems - Tran, K. T., Dao, D., Nguyen, M. D., Pham, Q. V., O'Sullivan, B., & Nguyen, H. D. (2025). Multi-Agent Collaboration Mechanisms: A Survey of LLMs. arXiv preprint arXiv:2501.06322. - multi-agent collaboration Other Strengths And Weaknesses: Strengths: - Comprehensive evaluations across multiple dimensions: tasks, structures, error types and rates, providing the understanding and benchmarks of resilience in mult-agent AI systems. - Clear implications for designing robust MAS with findings on various multi-agent structures. - Clear explanations of observations and findings, relating the performance impacts to collaboration mechanisms. Weaknesses: - Lack of theoretical analyses/formal proofs and deeper investigations on collaboration mechanisms. - Faulty agents in the world might be more complicated with dynamic scenarios among multiple agents. - Only GPT models were investigated without the use of chain-of-thought abilities (which might be useful in improving resilience) - The insights of multi-agent structures are limited as there should be mechanisms to improve existing structures. Other Comments Or Suggestions: Nil Questions For Authors: - Can the authors explore dynamic scenarios with multiple faulty agents? There should be a way to control the number of agents and the functionality-to-errors ratio in each agent to be more realistic. - Can you explain why certain structures are more resilient, thereby leading to better configurations or optimization of the agent systems? - Noises can also lead to better performance, can the authors explore further the key mechanisms behind these observations? - What are the practical implications and broad impacts of your paper? Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We deeply appreciate reviewer LJmt’s time for reviewing and providing valuable suggestions. We are encouraged that you find our experiments comprehensive and well-executed, methods reasonable, and conclusions helpful for the community. We address your concerns here: ## [W1] Math definition on agent collaborations. A multi-agent system: $G = (V, E)$, where $V$: agents and $E \subseteq V \times V$: each $(u, v) \in E$ denotes agent $u$ reports to agent $v$. - Linear systems are: directed path graphs, where $\forall v \in V, v \neq s, v \neq t$, we have: $\deg^+(v) = \deg^-(v) = 1$; for the endpoints, $\deg^-(s) = 0$, $\deg^+(s) = 1$, $\deg^+(t) = 0$, and $\deg^-(t) = 1$. - Flat systems are: directed complete graphs, where $\forall u, v \in V, u \neq v$, both $(u, v) \in E$ and $(v, u) \in E$. - Hierarchical systems are: rooted directed trees, where there exists a unique root agent $r \in V$ such that $\deg^-(r) = 0$, and $\forall v \in V \setminus {r}$, $\deg^-(v) = 1$. ## [W2] Real-world complicated scenario. To generate a snake game with pygame. Using a single GPT-3.5, the code is incomplete and the snake cannot be controlled. Using CAMEL, we achieve an executable game. When using AutoTransform, the code is still executable but the mapping between arrow key and snake's movement is mixed. When using AutoInject, the game is totally unexecutable. Our method is still effective in such real-world scenarios. ## [W3] Other models & CoT. We conduct experiments using the LLaMA-3.1-70B-Instruct model on all the four tasks and a reasoning model, o1-mini, on the Math task. The results are presented in the tables below. The hierarchical structures perform the best still hold for non-GPT-based models. The performance is largely improved with CoT (o1), while we can still observe the impact of faulty agents. Hierarchical structures still outperform the other two. \| LLaMA \| Linear \| Flat \| Hierarchical \| \|---\|---\|---\|---\| \| No Attack \| 73.78 \| 76.83 \| 76.15 \| \| AT \| 11.90 \| 39.03 \| 66.96 \| \| AI \| 38.72 \| 36.59 \| 55.64 \| \| o1 \| Linear \| Flat \| Hierarchical \| \|---\|---\|---\|---\| \| No Attack \| 78 \| 80 \| 81 \| \| AT \| 14 \| 18 \| 63 \| \| AI \| 70 \| 74 \| 77 \| ## [W4] Advanced structures. Inspired by MacNet and GPTSwarm, we design two advanced graph-based multi-agent frameworks using four agents: 1. Complete graph (a flat structure): each agent generates their own answers. In the next run, they re-generate the answers after thinking on others' results. 2. Star (a hierarchical structure): one leader proposes three approaches and distributes them to the three agents and generates the final answer. We evaluate GPT-3.5 using the Math task. Our methods and analyses are applicable to diverse frameworks. Flat structure still has a lower performance. \| System Type \| Vanilla \| AT \| AI \| \|---\|---\|---\|---\| \| Graph \| 28 \| 20 \| 16 \| \| Star \| 36 \| 30 \| 28 \| ## [Q1] Multiple faulty agents. We explore the scenario of two faulty agents in AgentVerse on the Math task using GPT-3.5. AgentVerse has 4 agents, with Solver faulty by default. Here, we make an additional one, either Critic or Planner, faulty. Our methods are still valid. The Planner, who decides the high-level direction, plays a more important role. Its faults cause a greater performance decrease. \| Faulty Agents \| Error Method \| Performance \| \|---\|---\|---\| \| None \| None \| 28 \| \| Solver \| AI \| 20 \| \| S + Critic \| AI \| 14 \| \| S + Planner \| AI \| 12 \| \| S \| AT \| 16 \| \| S + Critic \| AT \| 14 \| \| S + Planner \| AT \| 2 \| ## [Q2] Explanation on performance of different structures. We can have an analogy with real-world human organization structure. A hierarchical structure enables centralized decision-making, where a top-level role gathers information and efficiently distributes decisions through clear chains of command. In contrast, a flat structure often lacks clear leadership, leading to decision paralysis and coordination issues. A linear structure has a defined chain of command, but communication is slower, and top leaders have limited oversight of lower levels. ## [Q3] Explanation on how noises improve performance. (1) Double Checking: Injecting obvious errors prompts agents to respond with corrections, which often fix both the injected and existing issues. (2) Divergent Thinking: Systems can stagnate due to repetitive reasoning from identical LLMs. Introducing major errors shifts the discussion, promoting fresh insights. ## [Q4] Practical implications. (1) designing hierarchical multi-agent systems help, which reflects a prevalent collaboration mode in real-world human society. (2) Agents can have questions or suggestions on others' results, boosting fault recovery. ## [References] Missing papers. We have cited and compared the works of Perez, Tan, and Tran in our paper. In short, we consider a new scenario where the vulnerability comes from weaker agents in a multi-agent system. --- Rebuttal Comment 1.1: Comment: Thanks for addressing my comments. I have updated my score. --- Reply to Comment 1.1.1: Comment: We deeply thank reviewer LJmt for checking our response! We are glad that your concerns are addressed. Your comments are important for further improving this work. Thanks once again for re-considering your rating!	null	null	null	null	null	null
Privacy Amplification by Structured Subsampling for Deep Differentially Private Time Series Forecasting	Accept (spotlight poster)	Summary: This paper studies privacy amplification with structured subsampling, for applications in DP-SGD training on forecasting models. The sampling considered works by first selecting a subset of time series (top-level sample), then one or more contiguous subsequences per sample (bottom-level sample), and finally splitting each subsequence into a context window and ground-truth forecast. The authors derive event- and user-level privacy guarantees for sampling contiguous subsequences. They also study the tradeoffs between the choice of parameters for the top or bottom level sampling, and show that composing batches of many top-level sequences is optimal for the privacy guarantees. To handle the privacy of the context/forecast windows, the authors propose data augmentation with Gaussian noise. Claims And Evidence: Yes. Methods And Evaluation Criteria: - It might be good to include results on a wider range of epsilon in Table 1, or to include a plot. Theoretical Claims: I did not check the proofs in the appendix. Experimental Designs Or Analyses: - The authors mainly study the theoretical privacy guarantees of the different subsampling parameters. However, it would also be informative to empirically compare how the subsampling affects the utility of the model, independent of the privacy guarantees, so that we can know whether improvements are due to the privacy analysis or the choice of subsampling parameters. This would be a useful baseline to know how much the new privacy analysis improves on the results. - It might be good to compare against a baseline using DP-SGD in a black-box manner, to better demonstrate the improvements from the new analysis. Supplementary Material: No. Relation To Broader Scientific Literature: The authors are the first to study the privacy analysis for this particular type of structured subsampling used in forecasting, though the techniques used are not new. Essential References Not Discussed: N/A Other Strengths And Weaknesses: Strengths: - Privacy analysis is thorough and the tradeoffs between the subsampling parameters are studied in detail. Weaknesses: - The analysis seems very specific to the application in forecasting models, and it is unclear whether their results will be useful in other applications. - The techniques used are not novel, and the main novelty is applying existing techniques to a new application. - It would be good to have more experimental baselines to determine the impact of the new analysis. Other Comments Or Suggestions: N/A Questions For Authors: - How do the subsampling parameters affect the model utility, independent of the privacy analysis? Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: Thank you for your review and great suggestions for further expanding our experimental evaluation! Please note that we cannot update the manuscript during this phase, but will integrate your suggestions as soon as possible. ## Additional experiments/baselines ### Effect of subsampling parameters on utility, independent of privacy There are three key parameters: How we select sequences ("top-level"), how many subsequences $\lambda$ we sample per sequence, and batch size $\Lambda$. In the following, we first let $\lambda=1$ (like in our other experiments), and vary the top-level scheme and $\Lambda$: https://figshare.com/s/490812bd1b089d5c1dc5 Larger batch sizes $\Lambda$ improve utility on `solar_10_minutes` for some models, potentially due to its sparsity. However, the top-level scheme has no significant effect on utility. Based on this observation, we choose large batch sizes $\Lambda=128$ and vary $\lambda$: https://figshare.com/s/c4068a78b2d4f06aee25 There is no significant difference between $\lambda=1$ and $\lambda=16$, and no top-level scheme consistently outperforms any other. We will add these results to Appendix C.2 and reference them from 5.2 to motivate our parameter choices for DP training. ### Black-Box DP-SGD Baseline Thank you for this suggestion, which will let us better explain to readers why structured subsampling is preferable to standard DP-SGD. With standard fixed-batchsize DP-SGD, we would directly sample a batch of size $\Lambda$ from the $N_\mathrm{total} = N \cdot (L-L_F+1)$ subsequences of which $L_C+L_F$ contain sensitive information, with $L_C$ and $L_F$ being the context and forecast length. For $L_C+L_F=1$, one can use known tight bounds in a black-box manner (see Theorem 11.2 from Zhu et al. (2022)). However, they assume that only $1$ sensitive subsequence can appear in a batch, which makes them invalid when there are multiple sensitive subsequences ($L_C+L_F>1$) Like in our Theorem 4.3, we know that with $L_C + L_F > 1$ the privacy of standard DP-SGD is in fact optimistically lower-bounded by $H_{e^\varepsilon}(\sum_{i=0}^{L_C+L_F} \gamma_i \cdot N(2i, \sigma)\|\|N(0,\sigma))$, where $\gamma_i$ is the probability of sampling $i$ substituted subsequences, i.e., there is a risk of multiple leakage. The following compares this lower bound to our upper bound for structured subsampling with $\lambda=1$ under $N_\mathrm{total}=10^6$ and varying $\Lambda,L_C+L_F$: https://figshare.com/s/c061340645d5132c4a7e Standard DP-SGD is equally private for $L_C+L_F=1$ and less private for $L_C+L_F>1$, precisely because it cannot prevent multiple leakage. We will include this discussion and reference it from ll.90-92 in Section 1.1: "This risk of multiple leakage is underestimated if we apply guarantees for standard DP-SGD in a black-box manner (see Appendix C.3), [...]". ### Wider range of $\varepsilon$ in Table 1 Thank you! We expanded the set of $\varepsilon$: https://figshare.com/s/bbef7e6e8ad6ce500bf1 --- ## Novelty of Techniques Since our work is the first to analyze multi-level subsampling and privacy amplification for sequential data, we assume that you are referring to the fact that we use couplings to bound divergences in our derivations (please let us know if we misunderstood you). Please note that defining couplings only makes up a part of our overall proof strategy. For example, of our derivations for bottom-level sampling in on pp. 28-37, only Appendices E.1.3 and E.2.0 on pp.31-32;35 make use of this technique, whereas the remaining proofs introduce novel techniques and results (e.g. adaptive parallel composition for dominating pairs in E.1.1). Furthermore, applying couplings still requires non-trivial efforts (defining partitionings, proving validity of couplings, identifying distance constraints, deriving worst-case components given constraints,...) ## Applications Beyond Forecasting While we focus on forecasting, the underlying approach generalizes to multiple domains: 1. Our method can be directly applied to private self-supervised training for language models, where one also predicts "ground truth sequences" from a "context window" (see Section 4.5). 2. Our bounds directly apply to user-level privacy for arbitrary data, where $K$ records from one of $N$ data holders are substituted (see ll. 709-711). 3. Our novel amplification-by-augmentation method from Section 4.3 applies to any neighboring relations that enforces a bounded $\ell_2$ distance between datasets (e.g. privacy for patches in images). Based on your feedback, we will mention all applications at the end of Section 4.5 so that the broader impact of our work is highlighted in one specific paragraph and not scattered over the manuscript. --- Thank you again for your efforts! Please let us know if you have any additional questions during the discussion period. --- Zhu et al. Optimal Accounting of Differential Privacy via Characteristic Function. AISTATS 2022 --- Rebuttal Comment 1.1: Comment: Thank you for all the clarifications! I have increased my score accordingly.	Summary: This paper investigates the problem of training forecasting models (specifically those that leverage the temporal structure directly in their architecture) on both univariate and multivariate time series data. As is present most prior work on DP-SGD, amplificaton is a key result necessary for achieving realistic privacy-utility tradeoffs on deep learning tasks. The authors focus their work in this paper on deriving a structured subsampling procedure that provides similar amplificaton guarantees for these forecasting models. Finally, they demonstrate the new privacy utility tradeoffs when using this subsampling procedure. ### Update after rebuttal ### The authors have addressed my concerns and provided sufficient detail about how the accounting was implemented. Thus I feel confident about this utility of this new subsampling mechanism for practice. Thus, I have maintained my score at Accept. Claims And Evidence: The claims in the submission are supported with theoretical analysis, which is necessary for amplifcation results. Their empirical results are less focused on the main claim of the paper and an investigation of the impact of the main contribution of the paper. Methods And Evaluation Criteria: The proposed methods are well motivated for the forecasting problem, especially compared to assumptions placed by prior work that would lead to worse privacy-utility tradeoffs. Structured subsampling of the time sequences in a novel way that results in new amplification results is directly applicable to the forecastijng domain. Theoretical Claims: I checked the correctness of the proofs in Section 4. While it is possible I may have missed minor details, from my current understanding these proofs are sound. Experimental Designs Or Analyses: Yes, I checked the soundness and validity of the experimental designs. I have no issues for the choices made. Supplementary Material: Yes, I reviewed the supplementary material for the theoretical analysis. Relation To Broader Scientific Literature: This paper combines existing techniques in randomization to achieve privacy amplification in a new way for time series data. This builds upon a recent set of work by Li et al. and Kogi et al. to provide amplifcation results in the time series domain. Additionally, it provides a new way to train deep learning time series models with differential privacy. This is especially important for privacy-sensitive domains such as healthcare and finance where time series data is abundant. Essential References Not Discussed: None. Other Strengths And Weaknesses: Strengths: - Novel amplification theory for time series data - Well-written theoretical section - Widely applicable result to enable better DP learning of time series data Weaknesses: - Section 5.2 could benefit from improved writing and detail for clarity and motivation Other Comments Or Suggestions: None. Questions For Authors: 1. In the appendix the authors state that they use the `dp_accounting` library in their experiments. I'd like to understand how the amplification result presented in the paper was implemented with that library. Since it doesn't support this new result how was it incorporated? (i.e. how should I think about this result as an analogy to the q parameter that represents the sampling probability of batch) 2. The bi-level sampling seemed primarily motivated by LLMs but there are no natural language results? What do you see as the obstacles for adapting the method for that original motivation? Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: Thank you for your review! Please note that we cannot update the manuscript during the current rebuttal phase, but will integrate your feedback as soon as possible. ### Motivation for Section 5.2 Upon re-reading the section, we agree that we could have done a better job of explaining what exactly we intend to demonstrate by evaluating the CRPS of different models at different $\epsilon$, especially because our paper may also be read by forecasting practitioners outside the differential privacy community. Based on your feedback, we will replace the first paragraph of Section 5.2 with the following: "Our previous experiments show how different parameterizations of the considered subsampling scheme affect the privacy of DP-SGD applied to time series. However, altering how batches are sampled will affect the training dynamics of forecasting models. Parameterizations that offer strong privacy (small $\epsilon$ and $\delta$) could potentially result in low model utility. The following experiments serve to show that we can in fact train neural forecasting models with strong privacy guarantees while retaining better utility than non-neural methods, i.e., DP-SGD for time series offers a good privacy--utility trade-off." Please let us know if there are other parts of Section 5.2 that you think should be improved. ### Implementation of Bounds For reference, the bounds for $\lambda=1$ in Theorems 4.2, 4.4, and 4.5 are of the form $\begin{cases} H_\alpha((1-q) \cdot N(0, \sigma) + q \cdot N(2, \sigma)\|\| N(0,\sigma) ) & \text{if } \alpha \geq 1\\\\ H_\alpha(N(0,\sigma) \|\| (1-q) \cdot N(0, \sigma) + q \cdot N(2, \sigma) ) & \text{if } \alpha < 1 \end{cases}$ where $q$ depends on the neighboring relation, top-level scheme, bottom-level scheme, and amount of Gaussian data augmentation. The first case is equivalent to a `GaussianPrivacyLoss` with `sensitivity=2`, `sampling_prob=q` and `AdjacencyType.REMOVE`. The second case is equivalent to `sensitivity=2`, `sampling_prob=q` and `AdjacencyType.ADD`. We implement the case distinction through a class `SwitchingPrivacyLoss` that overrides `get_delta_for_epsilon` and evaluates one of the two `PrivacyLoss` objects, depending on the value of $\varepsilon$ (see `src/dp_timeseries/privacy/pld.py` in the supplementary material). For $\lambda > 1$ and our optimistic bounds (e.g. Theorem 4.3), we need to consider a mixture with more than two components. For this, we can apply the same approach to the existing `MixtureGaussianPrivacyLoss` with `AdjacencyType.REMOVE` and `AdjacencyType.ADD`. For $\lambda > 1$ and our pessimistic bounds (e.g. Theorem F.2), we need pairs of Gaussian mixtures and weighted sums of privacy profiles. These cannot be implemented via existing child classes and require custom classes (see `DoubleMixtureGaussianPrivacyLoss` and `WeightedSumPrivacyLoss` in `src/dp_timeseries/privacy/pld.py` in the supplementary material) ### Motivation for Bi-Level Subsampling (LLMs?) The bi-level approach is actually not motivated by LLMs, although your comment made us realize that a reader may get this impression from the "Bi-Level Subsampling for LLMs" paragraph in Section 2. Instead, our goal is to analyze the privacy implications of combining DP-SGD with a batching approach that has already been used to train forecasting models before the advent of LLMs. For example, in GluonTS, top-level sampling is implemented by a [TrainDataLoader](https://ts.gluon.ai/stable/api/gluonts/gluonts.dataset.loader.html) and bottom-level sampling is implemented by an [InstanceSampler](https://ts.gluon.ai/stable/api/gluonts/gluonts.transform.sampler.html). Based on your feedback, we will replace the first sentence of Section 4.2 with the following: "Recall from Section 1.1 that typical approaches for training forecasting models may also randomize which sequences $x_n$ contribute to a batch (e.g. by shuffling). As is standard with DP-SGD, we replace this shuffling operation with an independent sampling operation per batch to simplify privacy accounting". ### Application to LLMs There is in fact nothing that would prevent the direct application to token/sentence-level private self-supervised training with teacher forcing. Just like in forecasting, one samples a finite "context window" from which a "ground truth sequence" is predicted. One would just need to replace the data loader in existing LLM implementations. The main limitation is that this method may be less optimized for memory access in distributed training than the highly refined data loaders that are likely being used to train commercial models on large clusters. Based on your comment, we will replace the last sentence of Section 4.5 with the above paragraph, since "the connection [... to ...] language modeling is immediate" is somewhat ambiguous. --- We hope that we addressed all your comments to your satisfaction. Please let us know if you have any additional questions during the discussion period.	Summary: This paper studies privacy amplification under subsampling when working with forecasting models on time series data. In these cases, the dataset usually consists of sequences, and subsampling occurs on multiple levels: top-level sampling chooses a subset of sequences, bottom-level sampling chooses a subsequence from each of these layers, and then the subsequences are split into context and forecast (after which a model is trained on this data via Noisy SGD w Gaussian noise). The paper studies thoroughly how these various sampling choices impact privacy amplification by subsampling both analytically and empirically, making the following observations (among some others): a) They show that as one would expect, when the top-level sampling scheme is deterministic, and the bottom-level sampling is sampling $\lambda$ sequences without replacement, for a fixed batch size, $\lambda=1$ corresponds to the most per-epoch privacy. They also tightly characterize the privacy profile in this case. Next, they consider that when $\lambda > 1$, fewer epochs are needed for the same number of training steps, and hence ask whether $\lambda=1$ is still an optimal choice when you hold the number of training steps fixed (as opposed to a per epoch type guarantee). They numerically show that this is the case, by showing a lower bound on the per epoch privacy profile for $\lambda > 1$ and compare that to the tight profile for $\lambda=1$. Applying composition, they show that in many ranges of $\epsilon$ (and for various settings of other parameters), $\lambda=1$ continues to be an optimal choice. b) Next, they consider the effect of using sampling wor for top-level sampling and bottom-level sampling. In this case, they analytically show that per-step privacy profile is indeed additionally amplified roughly by the probability of sampling a sequence in the top-level. They also numerically show that this scheme gives amplification over deterministic top-level sampling at a per-epoch level (by applying composition on their per-step guarantee). c) Finally, in cases where the values in neighboring datasets can change in bounded ways ($+v$ or $-v$) they consider randomizing the context and forecast by adding Gaussian noise (in addition to top and bottom level sampling wor), and show that this further amplifies the privacy (the quantitative guarantee depends on the variance of the noise added). They also carry out some experiments to measure whether utility can be maintained while training on common benchmarks using many models of interest. They use tools built in prior work on privacy amplification by subsampling (couplings and dominating pairs) in their theoretical analyses. Claims And Evidence: Most of the claims (described in the summary) are supported with convincing evidence. The claim about utility (CPRS) not being significantly compromised when training models with privacy was confusing to me- I wasn't able to find in the section a detailed overview of the sampling choices that were made when training these models. Methods And Evaluation Criteria: Yes, the proposed methods and evaluation criteria make sense for the problem at hand- one additional evaluation critera that would have been useful when comparing the sampling schemes is not just the privacy level but the utility obtained for the same privacy parameters with different sampling schemes (for e.g. when using sampling wor at the top level, you'd expect to see the same data point more frequently, which may result in worse utility than the deterministic scheme for the same number of epochs, even though you have better privacy). Theoretical Claims: I skimmed the proofs of the theoretical claims in the supplementary material and they seemed reasonable. I did not check all the proofs in detail. Experimental Designs Or Analyses: Yes, I checked the soundness of all the experimental designs for the claims described in the summary. One question I had was re the sampling scheme used in the utility experiments (see methods and evaluation criteria), but the experimental design seemed largely reasonable. Supplementary Material: I reviewed the experiments section in detail, and skimmed the theoretical proofs. Relation To Broader Scientific Literature: This paper studies privacy amplification via subsampling for more complex multi-level subsampling schemes frequently used in forecasting models with time series data. It fits into a long line of work on privacy amplification via subsampling, but most prior work has been on subsampling for static datasets. The relatively sparse literature on bi-level sampling schemes for private deep-learning has not considered the interplay of privacy amplification effects of applying sampling to multiple levels. Essential References Not Discussed: Most essential references are discussed. In the intro, when referencing graph data, a number of key early citations on privatizing graph properties are missed and other citations are given instead (see the full version of 'Analyzing Graphs With node Differential Privacy' by Kasivishwanathan Nissim Raskhhodnikova Smith in 2015 and the citations therein). However, this is a relatively tangential set of citations and not as relevant to the paper so I don't think it a big omission. Other Strengths And Weaknesses: The main strength of the paper is its thoroughness; the privacy profiles of many combinations of top-level and bottom-level sampling schemes are explored in detail, both analytically and experimentally and natural choices there-in and how to make them are discussed. I don't see any major weaknesses to discuss other than clarifications about the utility experiments that would be useful. I do think comparing the utilities of the various sampling choices (as opposed to purely the privacy amplification obtained) would have made the paper even more impactful, but that's a natural point for future work. Other Comments Or Suggestions: 1) In the 'other guarantees' section on page 5 I was confused about the point regarding dominating pairs for substitution relations- shouldn't dominating pairs for addition/removal yield ones for substitution (since substitution corresponds to a removal as well as an addition)? 2) On page 6, some more reasoning about why the epoch-level guarantees are better when using subsampling at both the top and bottom levels would be useful (since on the epoch level one might expect that the benefits of top-level subsampling without replacement vanish). 3) I did not understand the explanation on page 7 for why composing many $\lambda>1$ steps results in larger privacy loss than $\lambda =1$ for a wider range of $\epsilon$ than for a single step, shouldn't the individual $\delta(\epsilon)$ for each step add resulting in similar effects in the many-step case? More explanation here would be very helpful. 4) On page 16 the authors say "In all cases, we observe that λ = 1 improves its privacy relative to other λ > 1 after 100 training steps"- but this claim seems untrue in figure 5 so a more nuanced claim needs to be made (however, it is true in figures 6 and 7). 5) On page 20, the interpolation of the graphs makes them a lot more confusing, for a while I thought $\lambda=16$ was the best in figure 10a until I read the text in detail. Might be worth presenting without interpolation. Questions For Authors: No further questions. Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: Thank you for your review and great questions! Please note that we cannot update the manuscript during the current rebuttal phase, but will integrate your feedback as soon as possible. ### Sampling choices/parameters for model training Thank you for pointing out this ommission. We will of course specify these additional parameters in Section 5.2. Our models were trained using top-level sampling without replacement, bottom-level sampling with replacement, and $\lambda=1$, i.e., one subsequence per sequence. For the datasets (`electricity`, `solar`, `traffic`) we used batch sizes $\Lambda=(128, 128, 256)$, noise multipliers $\sigma=(2.0, 4.0, 4.0)$, clipping constants $C=(10^{-4}, 10^{-4},10^{-4})$, and relative context lengths $L_C \mathbin{/} L_F = (1, 4, 8)$. The remaining parameters are already specified in Appendix B.2. ### Effect of Sampling Choices on Utility Based on your comment and a suggestion from Reviewer 3, we investigated the effect of different sampling choices on model utility, which we will include in our revised manuscript. Due to the character limit on rebuttals, please see our response to Reviewer 3 for details. ### Prior Work on Graph DP Thank you for pointing us to the work by Kasivishwanathan et al (2015). We will reference their work - as well as Nissim et al. (2007), who first studied edge privacy - in Section 1. ### 1 - Dominating Pairs for Substitution You are right, any dominating pair for $K$ insertions and $K$ removals is also dominating for $K$ substitutions. We erroneously assumed that the "insert-$K$-remove-$K$" neighboring relation admitted more pairs of datasets, which would have made the statement for Poisson sampling. But this is of course not the case, thank you. Please note that this was not intended to be a core contribution, but just a corollary of our more general, novel results for multiple sequences/users. Our Theorem E.1 (sampling with replacement under group substitution) also remains novel, since no prior work has analyzed WR sampling under group insertion/removal either. We will update ll. 264-266 of the "Other Guarantees" paragraph to: "Thus far, dominating pairs for sampling with replacement have only been known for individual substitutions. Thus, these guarantees are of interest beyond forecasting". ### 3 - Why a Single Subsequence is Preferable Under Composition You are right. If we were to use pointwise addition of the $\delta(\epsilon,\lambda)$, then the ordering w.r.t. number of subsequences $\lambda$ would stay the same. However, tight composition works by (1) determining the privacy loss distribution corresponding to the entire privacy profile $\delta : \mathbb{R} \rightarrow [0,1]$, (2) self-convolving the PLD, and (3) converting back to privacy profiles. Unlike pointwise addition, this is a non-linear functional operating on entire privacy profiles and may thus change their ordering. We posit that $\lambda=1$ is better because $\lambda > 1$ allows more catastrophic failures of privacy (sampling multiple sensitive subsequences), whose probability accumulates under composition (see ll.381-387). We believe that this effect could be better understood by studying the infinite limit of composition using central limit theorems for DP, which provide a simple formula in terms of privacy loss moments. To make this clearer to readers, we will update Section 4.5 as follows: "[...], future work may also want to investigate them analytically, e.g., via central limit theorems (Sommer et al. 2019), in particular to understand why $\lambda=1$ offers better privacy under composition." ### 2 - Why Top-Level Sampling is Preferable As with the previous point, tight composition does not have a nice analytical expression that could be used to answer this question. Again, we believe that considering the infinite limit of composition (here: epoch length) could be a promising direction towards understanding why top-level subsampling offers better privacy despite requiring more compositions. ### 4 - Relative Improvement under Composition Thank you for pointing out this inconsistency. We will use the following formulation instead: "We observe that, after 100 training steps, $\lambda=1$ offers better privacy than $\lambda \in \{2,4\}$. It also offers better privacy than $\lambda \in \{8,16\}$ for small top- and bottom-level sampling probabilitites." We will also include a column for $1000$ steps, where $\lambda=1$ actually outperforms $\lambda=16$ across all $\epsilon$ for the same parameterization as in Fig. 5: https://figshare.com/s/4292ea34e216427a0ded ### 5 - Interpolation on Page 20 We agree that interpolation makes the figures on p. 20 somewhat hard to read, and will remove it: https://figshare.com/s/9a3282037c6d268cd37a --- Thank you again for your review! Please let us know if you have any additional questions during the discussion period. --- Nissim et al. Smooth sensitivity and sampling in private data analysis. STOC 2007.	null	null	null	null	null	null	null	null
How Much Can Transfer? BRIDGE: Bounded Multi-Domain Graph Foundation Model with Generalization Guarantees	Accept (poster)	Summary: The authors argue that while the "pretrain-then-prompt" framework has been extensively studied in other fields, its application in the graph domain remains underexplored, particularly from a theoretical perspective. To address this gap, this paper introduces BRIDGE, a pretraining and prompt learning framework designed for multi-domain graph data, incorporating a theoretically driven regularization loss. During the pre-training phase, BRIDGE performs dimension-wise alignment and semantic-wise feature alignment, inspired by the Independent Causal Mechanism. In the fine-tuning phase, alongside the downstream task loss, BRIDGE introduces an aligner routing network that selectively assembles the pre-trained source domain aligner and proposes a spectral regularizer to minimize the upper bound of generalization error. They conduct experiments in both cross-dataset and cross-domain settings to demonstrate the effectiveness of the proposed framework. ## update after rebuttal As I mentioned in the 'Rebuttal Comment', my concerns have been well addressed; therefore, I have updated my score. Claims And Evidence: I agree with their claim that prompt learning is under-studied in the graph domain from both practical and theoretical perspectives. Moreover, each module in BRIDGE is intuitive, and the proposed regularizer is supported by a strong theoretical foundation, which is a significant advantage of this work. Methods And Evaluation Criteria: The authors' evaluation criteria for cross-dataset and cross-domain settings are valid. However, I suggest incorporating larger datasets (e.g., ogbn-arxiv) for both the source and target domains. This is important for two reasons: 1) assessing whether the model's performance improves as the amount of training data increases, and 2) evaluating the model's ability to effectively perform inference on large datasets. Additionally, while the paper does not report training and inference times, I am concerned that calculating the spectral regularizer could be time-consuming for large datasets. Theoretical Claims: I did not find any issues with the theoretical claims. Experimental Designs Or Analyses: The experimental design is valid, but an ablation analysis comparing the model with and without the prompt is needed. Supplementary Material: I checked Appendix A, B, D, and E. Relation To Broader Scientific Literature: I believe the key contribution of this paper is the proposed theoretical analysis bounding knowledge transfer generation, along with the derived regularization loss, which can serve as a foundation for future work in this field. Essential References Not Discussed: N/A Other Strengths And Weaknesses: A major concern with this paper is the low performance observed in the few-shot case (m=2,3) in Figures 2, 3, E.1, E.3, and E.4. Since pre-training is particularly beneficial when supervision is limited, this represents a critical scenario for the model's effectiveness. Other Comments Or Suggestions: N/A Questions For Authors: 1) It would be helpful if the authors could clarify why BRIDGE performs well in the zero and one-shot settings but not in the two or three-shot cases. 2) I would like to know the training and inference times. 3) Please consider including larger datasets for both the source and target domains. 4) Please show the ablation studies regarding the prompt 5) Please show how the learned 'S' gains significantly more knowledge from the same domain compared to cross-domain sources to validate the selective knowledge assembly. For checking the validity of selective knowledge assembly, showing the learned 'S' that it is truly gains high knowledge from same domain than cross domains. SelectiveKnowledgeAssembly If all of these concerns are addressed, I would be happy to reconsider my score. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We sincerely thank for the positive evaluation regarding its theoretical foundation for constructing GFMs. Response: Q1: Why work well in zero-/one-shot but not in two-/three-shot. A1: Thank you for the insightful question. - 0-shot limited for text-attributed graphs: Knowledge transfer based solely on structural information is inherently challenging in zero-shot scenarios. BRIDGE primarily targets text-free graphs, with experiments (RQ5) integrating an LLM as an enhancer to show effectiveness when textual semantics are available. - Why excels at 1-shot but not 2-/3-shot: BRIDGE’s MoE-based selective knowledge assembly effectively utilizes precise domain-invariant knowledge, providing a principled advantage at extremely sparse supervision (1-shot). At 2-/3-shot, the MoE routing faces increased uncertainty, while simpler alignment strategies (e.g., ProNoG, GCOPE, MDGPT) temporarily gain an advantage with limited additional supervision. When supervision further increases (≥5-shot), BRIDGE’s spectral regularizer dominates by constraining generalization error, restoring its superior performance. --- Q2: The training and inference time. A2: Thanks for bringing up the important issue. - Pre-training Phase: We adopt an early-stopping strategy based on loss, so the maximum training time depends on a preset maximum of 1000 epochs. No explicit inference is conducted during pre-training. Results (s): \| Source \| Time / Epoch \| Total Time \| \| --- \| --- \| --- \| \| CS, PM, Ph, Com \| 1.67 \| 1653.57 \| \| CR, PM, Ph, Com \| 1.53 \| 1624.01 \| \| CR, CS, Ph, Com \| 0.92 \| 938.38 \| \| CR, CS, PM, Com \| 1.20 \| 1147.02 \| \| CR, CS, PM, Ph \| 1.31 \| 1698.75 \| - Fine-tuning Phase: We report time per epoch, total fine-tuning time, and inference time separately. The spectral regularizer (highlighted as potentially time-consuming) is only computed during fine-tuning loss, particularly at small shot numbers ($m$). To reduce computational costs in eigenvalue decomposition, we implemented approximate techniques (lines 969–989). Results (5-shot Node Cls., s): \| Target \| Time / Epoch \| Inference Time \| Total Time \| \| --- \| --- \| --- \| --- \| \| Cora \| 0.13 \| 0.02 \| 142.37 \| \| CiteSeer \| 0.18 \| 0.02 \| 183.15 \| \| PubMed \| 0.82 \| 0.10 \| 1002.62 \| \| Photo \| 0.36 \| 0.09 \| 384.26 \| \| Computers \| 0.69 \| 0.05 \| 755.39 \| \| Reddit \| 6.62 \| 2.30 \| 579.16 \| --- Q3: Including larger datasets (e.g., ogbn-arxiv) for both source and target domains. A3: Thanks for this valuable suggestion. - In source domain: Following your advice, we have now included ogbn-arXiv as an additional dataset for pre-training. Results (Acc. %): \| S → T \| 1-shot Node Cls. \| 1-shot Graph Cls. \| \| --- \| --- \| --- \| \| CS, Ph, arXiv → Cora (cross-dataset) \| MDGPT: 37.21, BRIDGE: 43.62 \| MDGPT: 45.35, BRIDGE: 48.20 \| \| CS, Ph, arXiv → Reddit (cross-domain) \| MDGPT: 58.82, BRIDGE: 64.16 \| MDGPT: 68.22, BRIDGE: 71.74 \| - In target domain: We have already validated BRIDGE on Reddit. Notably, Reddit has 232,965 nodes and 114,615,892 edges (Table D.1), substantially larger than ogbn-arXiv (169,343 nodes and 1,157,799 edges). Therefore, the strong performance on Reddit sufficiently demonstrates BRIDGE’s capability for knowledge transfer on large-scale graphs. --- Q4: The ablation studies regarding the prompt. A4: Thank you for the insightful suggestion. We have conducted an ablation concerning the graph prompts for fine-tuning. Results (Acc. %): \| T: CiteSeer \| 1-shot Node Cls. \| 1-shot Graph Cls. \| 5-shot Node Cls. \| 5-shot Graph Cls. \| \| --- \| --- \| --- \| --- \| --- \| \| BRIDGE \| 42.18 \| 50.49 \| 60.20 \| 59.80 \| \| BRIDGE (w/o prompt) \| 35.23 \| 34.12 \| 50.34 \| 49.17 \| Note that, prompts $\boldsymbol{\mathcal{P}}$ and routing weights $\mathbf{S}$ are the only tunable parameters. Without prompts, only $\mathbf{S}$ is trained, significantly restricting fine-tuning flexibility and degrading performance, highlighting prompts' necessity in BRIDGE. --- Q5: How does 'S' favors same-domain over cross-domain knowledge for selective assembly? A5: We calculate the learned assignment weights for source experts from the same domain versus cross-domain sources. Results (1-shot, Node Cls.): \| S \| T \| Weights \| \| --- \| --- \| --- \| \| CS, PM, Ph, Com \| CR \| [0.5742, 0.2950, 0.0486, 0.0822] \| \| CR, CS, PM, Ph, Com \| Reddit \| [0.3001, 0.2855, 0.0634, 0.1254, 0.2256] \| Analysis: For Cora (CR), Academic experts (CS, PM) receive significantly higher weights (0.5742, 0.2950) compared to E-Commerce sources (Ph, Com: 0.0486, 0.0822). For Reddit, the structurally similar E-Commerce expert (Computers, 0.2256) and Academic experts (CR, 0.3001; CS, 0.2855) dominate. These results validate that BRIDGE effectively favors knowledge transfer from same-domain or structurally similar-domain experts, supporting our selective assembly design. --- Rebuttal Comment 1.1: Comment: Thank you for your thorough response to my concerns. In particular, the detailed experiments addressing question 5 have clarified how the proposed models effectively integrate cross-domain knowledge. I hope these experiments will be included if the paper is published. Based on this, I will be raising my score. --- Reply to Comment 1.1.1: Comment: Thank you for your positive feedback and for raising your score! We’ll make sure to include the experiments from these questions in the camera-ready version.	Summary: BRIDGE is a bounded multi-domain graph pre-training and prompt learning framework that enhances knowledge transfer in graph foundation models. It integrates domain-invariant alignment, a lightweight MoE for selective knowledge transfer, and a graph spectral-based generalization bound. Experiments show state-of-the-art performance in few-shot classification across datasets and domains, with further improvements when combined with LLMs. I consider this paper as a new bench for more generalizable and trustworthy GFMs, as existing works on GFMs lacks theoretical analysis of cross-domain transfer of pre-trained knowledge, to the best of my knowledge. Claims And Evidence: The claims made in this paper are generally supported by clear empirical results and theoretical analysis, while some aspects could be more thoroughly validated. - The well-supported claims include the effectiveness of BRIDGE in few-shot learning, theoretical justification for multi-domain knowledge transferability, effectiveness of key modules or components, etc. - The potentially problematic claim probably lies in the scalability and computational efficiency. BRIDGE claims superior efficiency compared with other baselines in down-prompting, but comparisons only focus on fine-tuning convergence speed rather than end-to-end training costs. But I believe this is not a major issue, as GFMs do not place a strong emphasis on the training cost of the pre-training phase but rather focus on whether they can achieve good performance quickly during the fine-tuning stage. Methods And Evaluation Criteria: I agree that the proposed methods and evaluation criteria align well with multi-domain graph transfer learning under the GFM settings. The “pretrain-then-prompt” paradigm, domain-invariant alignment, and spectral-based generalization bound basically seems to effectively address more generalized and trustworthy knowledge transfer in multi-domain GFMs. The evaluation on few-shot node and graph classification with cross-dataset and cross-domain settings is promising, and comparisons with 15 baselines strengthen credibility. The only concern lies in the computational efficiency are not fully analyzed. A more comprehensive evaluation on larger real-world graphs and detailed cost analysis would further validate BRIDGE’s practicality. Theoretical Claims: I have reviewed the theoretical claims and proofs presented in the paper, particularly focusing on the generalization error bound derivation and its spectral regularization component. - generalization error upper bound: an optimizable upper bound for the generalization error built upon the graph spectral theory and Lipschitz continuity. While the bound is theoretically sound, the paper lacks in-depth theoretical validation of how tight this bound is. Some additional visualization or sensitivity analysis of the bound’s impact on performance would strengthen the authors’ claim. - Lipschitz constant lower bound: relies on the graph eigenvalue decomposition to express the Lipschitz constant in a spectral form. The bound assumes optimal transport-based alignment of graph structures on both sides, but the practical effectiveness of this assumption is somewhat unclear. More discussion on whether real-world graphs under GFM settings satisfy these assumptions would be beneficial. Experimental Designs Or Analyses: I reviewed the experimental design and analyses in the paper, focusing on the few-shot learning setup, baseline comparisons, ablation studies, and efficiency evaluations. Pros: - The few-shot experimental design is well-suited for evaluating multi-domain knowledge transfer under the GFM settings. - Baseline selection is comprehensive and covers multiple paradigm related to the paper scope. - Ablation studies effectively isolate key components, and independently analyze their contributions, respectively. - The LLM integration experiment for the initial feature enhancement is novel and promising. Cons: - Missing comparisons to general domain adaptation baselines, not only resitricted to graph learning. - No full computational cost analysis, including training and inference time, memory for both pre-training and fine-tuning. - LLM feature alignment lacks qualitative validation. Supplementary Material: I reviewed the supplementary material, focusing on the proofs, experimental setups, hyperparameter tuning, and additional results. In summary, the appendices provide a thorough theoretical and experimental foundation for the paper’s claims. The proofs for generalization bounds and domain alignment are well-structured, and the experimental setup, hyperparameter analysis, and additional results reinforce BRIDGE’s effectiveness. However, several areas require further validation: - The practical impact of the generalization bound is not empirically tested. - Statistical significance tests are missing in ablation studies. Addressing these issues would strengthen the robustness of the findings. Relation To Broader Scientific Literature: The key contributions of this paper build upon and extend several existing areas of multi-domain graph pre-training, prompt learning for graphs, generalization bounds, and LLMs for GFM understanding. - multi-domain graph pre-training: BRIDGE introduces a domain-invariant alignment strategy that aligns both dimensions and semantics across domains, addressing the cross-domain generalization challenge more explicitly than prior work. Unlike prior works relying on textual metadata for alignment, BRIDGE is agnostic to text attributes, making it applicable to a wider range of graphs. - prompt learning for graphs: BRIDGE extends prompt learning to multi-domain graph settings, introducing a lightweight MoE network to selectively transfer domain-specific knowledge, which prior graph prompt methods lack. Unlike GraphPrompt and GraphPrompt+, which manually design prompts, BRIDGE learns self-supervised prompt initializations, making it more adaptive. - generalization bounds: BRIDGE integrates generalization bounds into its optimization, providing an explicit, optimizable spectral regularizer that controls transferability constraints. Unlike past works that assume smooth transfer functions, BRIDGE derives an explicit bound in the graph spectral space, which is novel in the filed of GFMs. - LLMs for graph understanding: BRIDGE incorporates LLM-generated node descriptions as a feature alignment mechanism, demonstrating improved multi-domain adaptation. Unlike MDGPT, BRIDGE’s graph-specific prompting enables more efficient knowledge transfer without relying on extensive LLM augmentation. Essential References Not Discussed: I believe that the related work section and other parts of the paper have included the necessary references, allowing me to understand the current state of research in the relevant field and to objectively evaluate the contribution of this paper. Other Strengths And Weaknesses: Strengths: - The pretrain-then-prompt approach for multi-domain graph learning is an promising extension of prior works that primarily focused on either pretraining or prompting separately. - The graph spectral-based generalization bound provides a new theoretical perspective on quantifying transferable knowledge, which is not commonly explored in existing works. - The integration of domain-invariant alignment with a lightweight MoE for selective knowledge transfer is a novel contribution that improves adaptability across domains. Weakness: - The paper does not analyze how minimizing the bound directly affects transfer performance, making it unclear how well the bound correlates with real-world generalization. - The MoE mechanism is a key component of BRIDGE, facilitating selective knowledge transfer, but the paper does not compare different MoE architectures. It is unclear why this specific MoE design was chosen over alternatives such as soft attention-based routing or adaptive gating mechanisms. - Multi-domain learning can suffer from negative transfer, where knowledge from one domain hurts rather than helps performance in another. The paper assumes all knowledge is beneficial, but does not analyze whether certain source domains degrade performance in the target domain. Other Comments Or Suggestions: Typos and Grammars: - The symbol “≜” (Eq. (12) and Eq. (13)) is not commonly used. - “The graph learner compound of the encoder …” should be “The graph learner is composed of the encoder …” - “We consider as benefiting from the spectral regularizer …” should be “We attribute this improvement to the spectral regularizer …” - “between domains introduces graph pre-training variations …” should be “between domains introduces variational inference in graph pre-training …” Questions For Authors: - Can you provide an empirical analysis or more easy-to-follow understanding demonstrating whether minimizing the generalization upper bound directly improves transfer performance? - Did you conduct any experiments to quantify negative transfer? Are there cases where knowledge from one domain degrades performance in another? - How does BRIDGE compare against full fine-tuning methods (e.g., LoRA, Adapter-based fine-tuning) in terms of performance vs. computational cost? - Other questions, please refer to the aforementioned weaknesses. Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: Thank you for your thoughtful review and positive feedback. We appreciate your recognition of BRIDGE’s contributions and address your comments and suggestions point by point below. Q1: The scalability and computational efficiency. A1: Thank you. For scalability, we address this in Reviewer Efax (Q3) with new results on ogbn-arXiv (source) and analysis on Reddit (target). For efficiency, see Reviewer Efax (Q2), where we provide end-to-end training and fine-tuning time comparisons. --- Q2: Theoretical validation of the generalization error bound tightness. A2: The bound tightness primarily depends on: (1) how accurately the Wasserstein distance $d_W$ captures true domain divergence, and (2) how precisely the Lipschitz constants ($L_f$, $L_g$) reflect actual smoothness of the learned graph representations. Lower $d_W$, tighter estimates of $L_f$ and $L_g$ yield a tighter bound, more closely approximating empirical generalization errors. We will explicitly evaluate these factors empirically in future revisions. --- Q3: The practical impact of the generalization bound. A3: The generalization bound indicates how effectively BRIDGE transfers knowledge across domains. A smaller bound means better transfer (e.g., between similar graphs like Cora and PubMed), whereas a larger bound signals difficulty (e.g., between citation networks and social graphs), guiding practical adjustments like additional fine-tuning. --- Q4: How minimizing the bound directly affects transfer performance. A4: Directly minimizing the bound improves BRIDGE’s transfer by explicitly constraining domain divergence ($d_W$) and smoothness ($L_f$, $L_g$). Practically, this means representations from different domains become closer and smoother, significantly enhancing generalization to unseen graphs. Experiments (Section 5.3, Figure 4) confirm that optimizing this bound via the spectral regularizer consistently leads to higher accuracy on downstream tasks. --- Q5: Whether real-world graphs satisfy optimal transport-based alignment assumption. A5: The optimal transport-based alignment assumption has been widely adopted in prior studies, and our work follows this common practice. The underlying reason is that real-world graphs often share intrinsic structural similarities (e.g., similar community or connectivity patterns across social or citation graphs), allowing optimal transport methods to meaningfully measure domain divergence. --- Q6: Missing comparisons to general domain adaptation baselines. A6: Since BRIDGE targets graph-structured data, we compare with strong graph-specific adaptation baselines (e.g., GCOPE, MDGPT). General domain adaptation methods lack structure-aware design, making them less relevant for fair comparison. --- Q7: LLM feature alignment lacks qualitative validation. A7: Thank you for this valuable comment. We clarify that the LLM-enhanced alignment is not part of BRIDGE's core contributions. Rather, it serves as an auxiliary experiment to demonstrate BRIDGE’s applicability to text-attributed graphs, highlighting BRIDGE’s broad adaptability. We agree qualitative validation would further support this applicability and will consider it in future extensions. --- Q8: Statistical significance tests for ablations. A8: Thank you for raising this point. Explicit statistical significance tests (e.g., t-tests) for ablation studies are relatively uncommon for papers in AI research communities. Ablations generally aim to intuitively illustrate each component’s individual contribution rather than establish statistical differences rigorously. Consistent with common practice, our ablations provide results averaged over multiple runs (with std), clearly showing reliable performance differences. --- Q9: Compare different MoE architectures. A9: Our MoE is a lightweight internal module of BRIDGE. Rather than comparing MoE variants in isolation, we focus on end-to-end comparisons with full graph adaptation methods (e.g., MDGPT, GCOPE) to reflect overall effectiveness. --- Q10: Compare against full fine-tuning methods. A11: BRIDGE focuses on efficient prompt-based tuning, not full model updates. We compare with strong graph prompt baselines (e.g., ProNoG, GraphPrompt), which align better with our design and goals. --- Q11: Negative transfer issues for multi-domain learning. A11: Negative transfer is a key challenge in multi-domain learning. BRIDGE addresses this via expert assignment weights ($\mathbf{S}$), which down-weight less relevant domains. As shown in our response to Reviewer Efax (Q5), $\mathbf{S}$ effectively favors helpful sources. We acknowledge BRIDGE doesn’t explicitly handle extreme cases where all source domains are harmful, which will be explored in future work. --- Q12: Typos and Grammars. A12: We will carefully proofread the manuscript.	Summary: This paper introduces BRIDGE, a graph foundation model framework designed for multi-domain knowledge transfer using domain-invariant feature aligners, a MoE prompt initialization, and a theoretical generalization bound. It addresses feature heterogeneity across domains, efficient adaptation via prompt tuning, and theoretical quantification of transferability. The framework is validated on 6 diverse graph datasets with convincing empirical results. Claims And Evidence: Most of the claims are clearly supported with some minor problems. - Multi-domain feature alignment: the authors propose a two-stage aligner that unifies domain features. Though no direct alignment metric is provided, performance gains over baselines support this claim. - Prompt-based fine-tuning with MoE: ablations confirm MoE improves low-shot learning, and BRIDGE outperforms 15 baselines in few-shot settings. - Generalization bound informs model design: the bound integrates Wasserstein distance and Lipschitz constraints, operationalized via a spectral regularizer that improves transfer performance. The claim is theoretically sound, though empirical validation of the bound’s direct impact would strengthen it. Methods And Evaluation Criteria: Technical contributions: BRIDGE is proposed by combining prompt learning, domain adaptation, and spectral regularization. - Baselines & benchmarks: evaluated against 15 baselines across 6 datasets in three domains (academic, e-commerce, social), covering node and graph classification. - Ablation & sensitivity studies: component-wise analysis, showing MoE and spectral regularizer are critical. Theoretical Claims: - Domain adaptation bound for graph transfer: extends Wasserstein distance-based domain adaptation theory to graph learning, where the bound depends on the Lipschitz constant of the GNN encoder. - Spectral analysis for transferability: derives a lower bound on the Lipschitz constant using graph spectral properties. Uses this to construct $R_{spec}$, penalizing over-sensitive representations. - Mathematical correctness: the proofs follow graph domain adaptation theory, adapting results from Mohri (2018) and Gama (2020). However, empirical verification of Lipschitz behavior reduction should be included. Experimental Designs Or Analyses: -BRIDGE achieves SOTA performance on all tasks: outperforms all 15 baselines in one-shot and five-shot classification. Cross-domain generalization (e.g., social graphs) is improved over existing pre-training methods. MoE prompting performs better in extremely low-shot settings, confirming its role in knowledge transfer. -Ablation studies validate each component: removing the feature aligner, MoE, or spectral regularizer significantly reduces accuracy. Faster convergence than standard fine-tuning. -Hyperparameter sensitivity: performance varies with aligner strength ($\alpha$), MoE routing entropy ($\beta$), and spectral regularization ($\gamma$). Some tuning is needed, but trends remain consistent across datasets. Supplementary Material: Yes. -Theoretical proofs are solid, but empirical validation of theoretical insights (e.g., tracking Lipschitz behavior) should be further included. -Additional experiments reinforce claims, showing BRIDGE’s effectiveness across multiple datasets and ablations. -LLM-based text augmentation helps slightly, but BRIDGE still requires at least one labeled example for good performance. -Complexity analysis is well-documented, though spectral regularization may add some computational overhead. Overall, the supplementary material strengthens the credibility of the paper, providing extensive proofs, extra experiments, and implementation details. Relation To Broader Scientific Literature: This paper contributes to multiple areas in graph representation learning, domain adaptation, few-shot learning, and graph foundation models. It integrates ideas from these domains into a novel framework that enhances transferability across graph datasets. Essential References Not Discussed: There are no critical missing references in the paper. The authors provide a comprehensive review of related work, covering graph pre-training, domain adaptation, prompt learning, and theoretical generalization bounds. They cite relevant prior works. The citations potentially sufficiently contextualize BRIDGE’s contributions, and nearly no essential prior work appears to be missing. Other Strengths And Weaknesses: Strength: - Combines multi-domain learning, prompt-based transfer, and theoretical regularization into a unified framework. - Outperforms all baselines across 6 datasets and multiple domains, with robust few-shot generalization. - First work to derive a domain adaptation bound for prompt-based graph transfer, integrating Lipschitz constraints. - Includes full proofs, hyperparameter details, and additional experiments, enhancing transparency. Weakness: - Many moving parts (aligners, MoE, spectral regularizer) and multiple hyperparameters, making tuning challenging. - Performance drops significantly when no labeled target examples are available (m=0 setting). A true zero-shot graph foundation model remains an open challenge. - Eigen-decomposition for $R_{spec}$ could be expensive on large graphs. A runtime analysis would be helpful. Other Comments Or Suggestions: See Weakness. Questions For Authors: During the pre-training stage, what is the difference between training all graphs together versus training them separately one by one? How do their performances compare? (Considering that training all graphs together poses a significant memory challenge.) - Given limited labeled data, how were hyperparameters optimized? Are there default recommendations? - Did $R_{spec}$ actually reduce domain divergence or Lipschitz constants? Can you show this empirically? Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: Thank you for your insightful and constructive review, and for recognizing the contributions of BRIDGE. We address your questions briefly below. Q1: The empirical validation of the generalization bound. A1: To empirically validate the effectiveness of the bound, we conducted specific ablation studies by removing the spectral regularizer (Section 5.3). Removing the spectral regularizer resulted in a clear performance drop: specifically, accuracy decreased from 42.18% to 41.33% (−0.85%) for 1-shot node classification, and more significantly from 60.20% to 54.51% (−5.69%) for 5-shot node classification on the CiteSeer dataset. This substantial performance degradation empirically demonstrates the effectiveness of our generalization bound in improving transferability. These findings explicitly confirm the bound’s role in guiding practical model design. --- Q2: Empirical verification of Lipschitz behavior reduction should be included. A2: Thank you for raising this important point. While our experiments clearly show that including the spectral regularizer improves transfer performance (Section 5.3), the original submission did not explicitly measure the Lipschitz constant's empirical evolution. Theoretically, the spectral regularizer is specifically designed to constrain the Lipschitz constant by penalizing large variations in learned representations. Given your valuable suggestion, we plan to explicitly measure and report the evolution of the empirical Lipschitz constant in future version, to more clearly demonstrate how our method reduces the representation sensitivity across domains. --- Q3: Still requires at least one labeled example for good performance. A3: Indeed, BRIDGE is specifically designed for text-free graphs, where zero-shot knowledge transfer based solely on structural information is inherently limited, which is a fact well-supported by prior works. Pure structural information lacks sufficient semantic cues, leading to poor zero-shot performance, as extensively confirmed in the literature. To demonstrate that BRIDGE can also effectively leverage textual semantics when available, we conducted additional experiments integrating textual information generated by an LLM as an enhancement strategy (Section 5.6, Table 3). Results clearly showed notable improvements: e.g., node classification accuracy on Reddit improved from 55.72% (structure-only) to 57.16% (structure + LLM) under zero-shot conditions. These experiments indicate that BRIDGE, though originally targeted for text-free scenarios, can effectively incorporate textual semantics, significantly improving zero-shot transfer performance when such information is available. We will explicitly clarify BRIDGE’s intended scope (text-free graphs) and discuss the potential benefits of textual augmentation thoroughly in the revision. --- Q4: Spectral regularization may be expensive. Runtime analysis. A4: Thanks for bringing up this important issue. We reply the same concerns for [Reviewer Efax (Q2)](https://openreview.net/forum?id=bjDKZ3Roax&noteId=e2XOFb3spO). To explicitly address this, we adopted efficient approximation techniques (lines 969–989) based on truncated eigenvalue decomposition and eigenvalue approximations. --- Q5: Tuning challenging. A5: Your point regarding the complexity of hyperparameter tuning due to multiple moving parts is valid. Recognizing this issue, we provided a detailed sensitivity analysis of key hyperparameters (Figure 6, Section 5.5), covering: $K$, $\alpha$, $\beta$, and $\gamma$. These clearly presented sensitivity analyses significantly simplify practical hyperparameter tuning by offering explicit recommendations and robust ranges. We also have provided the suggested hyperparameter settings in Appendix F.1 and the configuration files. --- Q6: Difference between training all graphs together versus one by one. A6: Thank you for this insightful question. In BRIDGE, all graphs from different domains were trained simultaneously in the pre-training phase, explicitly enabling cross-domain alignment and knowledge transfer. This approach encourages the model to learn shared domain-invariant features across multiple domains simultaneously, resulting in enhanced transfer performance. However, we recognize that training all graphs jointly can pose substantial memory overhead. Training graphs separately (one domain at a time) reduces memory consumption significantly but sacrifices explicit cross-domain feature alignment, potentially weakening transferability. While this sequential training strategy was not explicitly investigated in the original submission, we acknowledge your point and will explicitly clarify our current training strategy and discuss potential trade-offs in the revision. Detailed empirical comparisons of joint vs. sequential training strategies will be included in future work to thoroughly address this important point.	null	null	null	null	null	null	null	null
What Do Learning Dynamics Reveal About Generalization in LLM Mathematical Reasoning?	Accept (poster)	Summary: The paper introduces a novel metric called "pre-memorization train accuracy" that predicts how well large language models will generalize during reasoning tasks. The key insight is examining model performance on training examples before they are memorized verbatim. The authors show this metric strongly correlates with test accuracy (R² ≥ 0.9) across different models, datasets, and training configurations. They leverage this finding to improve data curation, achieving 1.5-2x better data efficiency compared to standard approaches. Claims And Evidence: From my experience, it would be better to add more ablation studies testing different definitions of memorization beyond perplexity thresholds. Methods And Evaluation Criteria: The methodology is sound, with careful experimental design. The authors evaluate their metric through multiple lenses: aggregate test performance prediction, per-example robustness analysis, and practical data curation improvements. The evaluation on both mathematical (GSM8k) and general reasoning tasks demonstrates broad applicability. Theoretical Claims: I have verified the proofs in Section 2 and Appendix E. The formalization of language-thought modeling gap and the derivations of Propositions 2.4 and 2.7 are mathematically rigorous. The assumptions and conditions are clearly stated. Experimental Designs Or Analyses: The experiments are thorough and well-designed. The authors control for multiple variables like learning rate, dataset size, and model architecture. From my experience, it would be better to add experiments testing the metric's sensitivity to different random seeds. Supplementary Material: I reviewed Appendices A-D which provide essential details about threshold selection, training configurations, implementation details, and prior generalization metrics. The supplementary material effectively supports the main findings. Relation To Broader Scientific Literature: The paper effectively positions itself within relevant literature on memorization, generalization, and LLM reasoning. It builds upon and advances prior work on measuring memorization (Feldman & Zhang 2020) and understanding Chain-of-Thought reasoning (Wei et al. 2022). Essential References Not Discussed: In my view, it would be better to add recent works on emergent abilities in LLMs and how they relate to memorization versus generalization. The discussion would benefit from incorporating recent papers on phase transitions in LLM learning. Other Strengths And Weaknesses: A key strength is the practical utility of the findings - the metric provides actionable insights for improving training efficiency. One weakness is the reliance on perplexity thresholds for defining memorization, which may not capture all forms of memorization. Other Comments Or Suggestions: NA Questions For Authors: 1) How sensitive is the pre-memorization accuracy metric to the choice of memorization threshold? 2) Does the correlation with test accuracy hold for much larger models (>70B parameters)? 3) How does the metric behave during few-shot learning versus full fine-tuning? Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: We thank the reviewer for the nice feedback! We answer the questions below. > How sensitive is the pre-memorization accuracy metric to the choice of memorization threshold? In Fig, 9, we provide some some analysis on the sensitivity of the predictive power (R^2) of our metric to the choice of the memorization threshold. We found that R^2 degrades smoothly with respect to p, which makes it is relatively easy to find a good value of p by sweeping a range of values. > Does the correlation with test accuracy hold for much larger models (>70B parameters)? Unfortunately, we do not have the compute to test this right now, though we believe this would be an interesting direction for future work > How does the metric behave during few-shot learning versus full fine-tuning? Our metric cannot be directly applied in the few-shot learning setting. However, we believe understanding the relationship between the few-shot data and downstream generalization would be a very interesting direction for future study.	Summary: This paper focuses on LLM reasoning tasks and proposes a metric called per-memorization train accuracy, which is the accuracy of model samples on training queries before they begin to copy the exact reasoning steps from the training set. The authors show that the proposed metric is predictive of the test accuracy in dataset level, as well as model robustness to perturbation at a sample level. They further use this metric to improve sample efficiency by prioritize training on samples with low pre-memorization accuracy. ## update after rebuttal I thank the authors for the clarifications. I increased my score to 3 (provided that they make the title and scope of their claims clearer as math reasoning) Claims And Evidence: Evidence 1: while it is always annoying to be asked for results on more datasets, I think it is needed here. The paper is purely empirical and there are quite a few other datasets (besides the 2 math-only datasets) that authors could have evaluated to further strengthen their conclusion. Methods And Evaluation Criteria: Most of the evaluation criteria makes sense to me, and I have a following question: Method 1: If I understand correctly, the pre-memorization accuracy for a single sample can only be either 0 or 1 (correct or wrong)? If so, why the accuracy in Figure 7 is continuous? Theoretical Claims: The paper is mostly empirical and there are no theoretical results. However, this is not considered as a weakness. Experimental Designs Or Analyses: Experimental design 1: In terms of writing, I think the paper lacks necessary details here and there. For example, - The experimental setup of Section 4.1 is not mentioned, the models used in Figure 3 are not mentioned) - Similar for Figure 6, the model used to train is not mentioned. - In section 5.2 (L369 right), how and which GPT is used to rephrase examples in the original dataset? The author mentioned that they followed a similar procedure in Setlur et al. 2024, but it is important to briefly summarize (or give examples) how it is done. Overall, adding these details will help the reader in developing a more concrete idea and therefore make the reading much smoother. Supplementary Material: I have checked the appendix. There is no other supplementary material except for the appendix. Relation To Broader Scientific Literature: - Broader literature 1: the idea of relying on the correlation of a prosed metric and the test accuracy to predict test accuracy broadly relates to works trying to predict out-of-distribution (OOD) performance in a similar manner. The reason is that there is need to estimate how the model at hand will perform on target domain when labeled OOD target data is hard to obtain. - Broader literature 2: the idea of using the proposed metric to expand the training dataset broadly relates to synthetic data and data selection. For the latter, many works try to reduce the training dataset by removing noisy or redundant ones and only keep the informative ones, which is a concept called Coreset in the relevant literature. Essential References Not Discussed: The paper reminds me of Miller et al. 2021, where they show in-distribution accuracy correlates with OOD accuracy in many cases. Maybe worth discussing in related work. Reference: Accuracy on the Line: On the Strong Correlation Between Out-of-Distribution and In-Distribution Generalization. Miller et al. 2021 Other Strengths And Weaknesses: Strength: the paper is generally well-organized and the idea is easy to understand. Understanding memorization and generalization is timely and important, and the proposed Pre-Memorization Train Accuracy shows storng correlation with the test accuracy on unseen samples. Weakness: my concern is on the actionable point and implication of this paper. - In Appendix A (Figure 9), the correlation between the proposed metric and test accuracy varies a lot with differnet threshold $p$, and the optmal $p$ is different for different datasets. For an unseen dataset, how would you predict test accuracy without calibrating the $p$ w.r.t. true test accuracy? Can you clarify how the metric can be used in practice? Other Comments Or Suggestions: Minor: L298 right side, it should be Fig. 7 instead of 6? Questions For Authors: I would be happy to increase my score if the authors could address my questions in Weakness, Evidence 1, Method 1, Experimental design 1, especially the first two. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We thank the reviewer for the feedback! In the following rebuttal, we first provide a detailed description of how our metric is calculated and used in practice. Next, we address the concerns about the scope of our experiments. Finally, we provide clarifications for our experimental setup. We will update the final version of our submission to include these additional details. > Weakness: my concern is on the actionable point and implication of this paper. In Appendix A (Figure 9), the correlation between the proposed metric and test accuracy varies a lot with differnet threshold p, and the optmal p is different for different datasets. For an unseen dataset, how would you predict test accuracy without calibrating the p w.r.t. true test accuracy? Can you clarify how the metric can be used in practice? We would like to clarify that the main goal of our work is not to predict test accuracy using the model’s training behavior, since test accuracy can be measured relatively easily with a holdout dataset. Instead our goal is to 1) better understand aspects of a model’s learning dynamics which govern their downstream generalization, and 2) use our findings to improve model generalization. Towards goal 1, we analyze the model’s behavior through training, and find that models tend to have 2 modes of optimizing the learning objective: one which leads to downstream generalization and one which doesn’t (learning progression 1 vs 2 in Fig. 2). Train accuracy conflates the two models of learning. In contrast, pre-memorization train accuracy allows us to delineate between the two, and identify the examples that are learned in a “generalizable” manner and the examples that are not. Towards goal 2, we study how pre-memorization train accuracy can be used to improve data curation. While test accuracy measures a model’s generalization in aggregate, pre-memorization train accuracy can measure generalization for individual train examples. This allows us to determine which train examples are “hard” for the model, which can better inform the kinds of examples to collect that would most improve model performance. The exact workflow for our data curation experiments is as follows. We assume access to a dataset split into a train/test set, using which we can calibrate p with a few (<3) training runs using test accuracy. We measure the pre-memorization train accuracy of the train examples. Using this information, we curate new data that is drawn from the same distribution as training examples with low pre-memorization train accuracy in the current iteration. > Evidence 1: while it is always annoying to be asked for results on more datasets, I think it is needed here. The paper is purely empirical and there are quite a few other datasets (besides the 2 math-only datasets) that authors could have evaluated to further strengthen their conclusion. The experiments in our paper include more than 60 training runs across different models, tasks, dataset scale, and training settings. While we focused on two mathematical datasets, we believe the depth and comprehensiveness of our analysis is comparable if not exceeds the standards for empirical conference papers. We unfortunately do not currently have the compute to perform experiments on additional datasets. However, we believe this should not be the reason for rejection, as many reasoning papers have been accepted at similar-tier conferences with comparable or even more limited dataset coverage. For instance: [1] RL on Incorrect Synthetic Data Scales the Efficiency of LLM Math Reasoning by Eight-Fold (Neurips) - Experiments: GSM8k, MATH [2] Scaling LLM Test-Time Compute Optimally Can Be More Effective Than Scaling Parameters for Reasoning (ICLR) - Experiments: MATH > Method 1: If I understand correctly, the pre-memorization accuracy for a single sample can only be either 0 or 1 (correct or wrong)? If so, why the accuracy in Figure 7 is continuous? We take multiple samples of outputs for every input, and calculate the average accuracy > Experimental design 1: In terms of writing, I think the paper lacks necessary details here and there. For example, > The experimental setup of Section 4.1 is not mentioned, the models used in Figure 3 are not mentioned) The models are trained using llama 2 8B on the full dataset with 6 epochs, and peak learning rates as described in the figure > Similar for Figure 6, the model used to train is not mentioned. We used llama2 8b >In section 5.2 (L369 right), how and which GPT is used to rephrase examples in the original dataset? The author mentioned that they followed a similar procedure in Setlur et al. 2024, but it is important to briefly summarize (or give examples) how it is done. The data used in our work was generated using the exact procedure as described in Appendix E of Setlur et al. 2024, which details the model, system prompt, and approximate cost. We are happy to add or clarify any more details needed. --- Rebuttal Comment 1.1: Comment: I appreciate the author's response. Some of my questions are addressed but my main concerns remain: - Regarding $p$, its value directly connects to the definition of memorization. For different datasets, you use different $p$, how can memorization be defined differently for different data? - Regarding datasets, I agree that there are papers published with few datasets, but here you are trying to conclude a general correlation, so the number of datasets are more important in your case (this is also raised by other reviewers). If adding more datasets is prohibitive, I think maybe it's better to revise 'LLM reasoning' -> 'LLM math reasoning' in the title, to avoid over-claiming. --- Reply to Comment 1.1.1: Comment: We thank the reviewer for the quick response! > Regarding p, its value directly connects to the definition of memorization. For different datasets, you use different p, how can memorization be defined differently for different data? Different datasets exhibit different levels of inherent stochasticity, which influences the perplexity of model samples. For example, consider the following 2 datasets: Dataset 1 contains 2 training examples of the form (input, target): Example1: (“input”, “A”) Example 2: (“input”, “B”) Dataset 2 also contains 2 training examples: Example1: (“input1”, “A”) Example2: (“input2”, “B”) A model which perfectly minimizes the training loss on dataset 1 has perplexity 2 when presented with training inputs. In comparison, a model which perfectly minimizes the training loss on dataset 2 has perplexity 1 when presented with training inputs. This example illustrates how different datasets, which may exhibit different inherent levels of stochasticity, might lead to different perplexity thresholds for memorization. > Regarding datasets, I agree that there are papers published with few datasets, but here you are trying to conclude a general correlation, so the number of datasets are more important in your case (this is also raised by other reviewers). If adding more datasets is prohibitive, I think maybe it’s better to revise ‘LLM reasoning’ -> ‘LLM math reasoning’ in the title, to avoid over-claiming. We are happy to revise the title of our work to ‘LLM math reasoning’ and make it clear in our paper that the scope of our claims is for math reasoning.	Summary: The paper studies how LLMs generalize in reasoning tasks and introduces "pre-memorization train accuracy" as a metric that predicts test accuracy. The key idea is that models first learn correct reasoning patterns before they start memorizing training examples, and this early accuracy is strongly correlated with final test performance. The authors show that this metric is predictive across different models and datasets. They also propose using this metric for data selection. The results suggest that tracking model performance before memorization kicks in can be useful for better training strategies. Claims And Evidence: The claims are mostly well supported by experiments. The paper shows strong correlations between pre-memorization accuracy and test accuracy, and the data curation experiments give good evidence that this metric can be useful for improving sample efficiency. One possible concern is that models in real-world fine-tuning setups often only train for one epoch, meaning they may not actually go through a clear pre-memorization and memorization phase. So it's not clear how well this metric would apply outside of multi-epoch settings. Methods And Evaluation Criteria: The methods seem reasonable for studying generalization in reasoning tasks. The authors use standard reasoning datasets GSM8K and MATH which are a good fit since they allow distinguishing between correct reasoning and memorization. The main metric (pre-memorization train accuracy) is well defined. The evaluation is thorough, with different models, learning rates, and dataset sizes. That said, since most practical LLM fine-tuning is done in a one-pass setting, it might be more useful to measure pre-memorization accuracy over early batches instead of epochs. Theoretical Claims: There aren't any formal theoretical results in the paper. Experimental Designs Or Analyses: The experiments are generally sound, with strong empirical results. The authors systematically vary learning rates, dataset sizes, and models to validate their claims. However, the multi-epoch training setup is a bit unrealistic. Most LLM fine-tuning is done in a single pass, so it’s unclear if the metric holds in that scenario. Supplementary Material: I did note review the supplementary material section. Relation To Broader Scientific Literature: The paper is closely related to research on memorization and generalization in deep learning. It connects well with past work on leave-one-out memorization metrics (Feldman & Zhang, 2020) and discussions on whether memorization helps or hurts generalization. Essential References Not Discussed: Nothing that I am aware of. Other Strengths And Weaknesses: Strengths: - Novel and well-motivated metric for understanding generalization. - Strong empirical results with high correlation to test accuracy. - Practical applications for data curation and improving sample efficiency. Weaknesses: - Limited model and dataset diversity (only two models, only math reasoning). - No theoretical justification for why pre-memorization accuracy is predictive. - The multi-epoch training assumption might limit applicability to real-world LLM fine-tuning. Other Comments Or Suggestions: - Would be interesting to test if pre-memorization accuracy helps detect spurious correlations in training data. - The p-selection process still raised concerns about leakage. Maybe an alternative selection method would be more robust. - Typo: "acheived" -> "achieved" Questions For Authors: 1. How does pre-memorization accuracy behave in one-epoch fine-tuning? Many LLMs are fine-tuned in a single pass. Does the metric still hold if computed over early training steps? 2. Could this work for non-math reasoning tasks? 3. Does this method work when models are weaker? 4. Could pre-memorization accuracy be used to predict how well a model generalizes OOD? Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: We thank the reviewer for the nice feedback! We answer the questions below: > How does pre-memorization accuracy behave in one-epoch fine-tuning? Many LLMs are fine-tuned in a single pass. Does the metric still hold if computed over early training steps? Reasoning data tend to be rare, so it is common in prior work to do multiple passes on these datasets. For instance, [1] does some analysis on model performance and number of epochs of training, and found that pass@1 performance on the test set continues to increase for 50 epochs Our work also does analysis on both the one-epoch finetuning setting, as well as early-epochs in longer training runs (Fig. 4). We found that pre-memorization train accuracy is still highly predictive of test accuracy in these settings. [1] Training Verifiers to Solve Math Word Problems > Could this work for non-math reasoning tasks? We believe our findings are likely to hold in problem settings where the target label includes both chain-of-thought reasoning (not uniquely correct) and a final answer (uniquely correct and unlikely to be guessed correctly) > Does this method work when models are weaker? We have not tested. Weaker models (e.g. GPT 2) tend to perform very poorly on reasoning tasks, which is likely to make the analysis largely uninformative > Could pre-memorization accuracy be used to predict how well a model generalizes OOD? We have not tested our work in the OOD setting, though we believe this would be an interesting direction for future study!	Summary: This paper investigates how the learning dynamics of large language models (LLMs) during finetuning influence their generalization on reasoning tasks. The key contribution is the introduction of pre-memorization train accuracy, defined as the highest accuracy a model achieves on a training example before it begins to replicate the exact reasoning steps (memorization) from the training data. The authors demonstrate that this metric strongly correlates with test accuracy across models (Llama3 8B, Gemma2 9B), datasets (GSM8k, MATH), and training configurations (learning rates, epochs, dataset sizes), achieving coefficients of determination bigger than 0.9. Furthermore, this paper discusses the relationship between pre-memorization accuracy and the model prediction robustness, finding that at the per-example level, low pre-memorization accuracy indicates fragile model predictions. Perturbations to such examples (e.g., altering prompts) significantly degrade accuracy, whereas high pre-memorization examples remain robust. Additionally, this paper proposes a data curation algorithm based on the pre-memorization accuracy, which could yield 1.5-2 gains in data efficiency over i.i.d. sampling and outperforms heuristic-based and optimization-based data selection methods. ## update after rebuttal I raised my score to 3 (boardline) since the authors' detailed response to me and other reviewers. However, some of my questions were not addressed and I still regard authors should take a deeper exploration about this very interesting phenomenon, standardize their method's detail and implement the pre-mem accuracy on additional datasets. Claims And Evidence: See Other Strengths And Weaknesses and Questions Methods And Evaluation Criteria: See Other Strengths And Weaknesses and Questions Theoretical Claims: There isn’t any theoretical analysis. Experimental Designs Or Analyses: See Other Strengths And Weaknesses and Questions Supplementary Material: No Relation To Broader Scientific Literature: This paper advances the understanding of LLM generalization in reasoning tasks by introducing pre-memorization train accuracy—a metric capturing model accuracy before memorizing training solution traces—and bridges gaps across multiple research areas. Essential References Not Discussed: No Other Strengths And Weaknesses: Strengths: 1. The introduction of pre-memorization training accuracy is a fresh idea. It focuses on model performance before memorizing exact solutions, which hasn't been explored much before. 2. The paper shows high $R^2$ values (≥0.9) across different models and datasets, which is impressive. 3. The data curation method using pre-memorization accuracy improves sample efficiency, which is useful for real-world training scenarios. Weakness: 1. The authors need a deeper analysis and discussion of pre-memorization accuracy. The robustness and data curation sections lack sufficient insight beyond stating the relationship between pre-memorization accuracy and test accuracy, especially since test samples could be interpreted as a form of perturbation on the training dataset. 2. The process for choosing the perplexity threshold p lacks explanation and analysis. The reasons why p is strongly dependent on the task/model remain unclear. 3. The experiments are restricted to mathematical datasets. Additional experiments with diverse datasets (e.g., logical reasoning or commonsense QA) are necessary to validate generalizability. 4. The perturbations used (like adding "First") are minor and may not test true robustness against more complex or semantic changes. 5. The explanation of the data curation process lacks detail. The rationale for hyperparameter choices (e.g., thresholds and iterations) is insufficiently explained or discussed. 6. The authors categorize training samples into two types based on learning dynamics but fail to explain the underlying reasons why some samples exhibit one training pattern while others show another. Other Comments Or Suggestions: See Other Strengths And Weaknesses and Questions Questions For Authors: 1. The authors categorize samples with high perplexity (ppl) and high accuracy as well-generalized. However, it is possible the model simply memorizes the final answer rather than learning reasoning steps. Is there any analysis or experiment addressing this concern? 2. The perplexity threshold p is selected by sweeping values, but the chosen p seems disproportionately large relative to the task/model. Is there an explanation for why such high thresholds are necessary? 3. In Figure 1 (left), the curve for the learning rate 5e−7 closely aligns with y=x, suggesting a strong train-test accuracy correlation. Is pre-memorization accuracy effectively equivalent to accuracy under very small learning rates since it is measured early in training? 4. Figure 4 uses Llama3 8B and Gemma2 9B, but Figure 8 (right) substitutes Gemma2 9B with DeepSeekMath 7B. What motivated this inconsistency in model selection? 5. In the data curation experiments, only levels 1–3 of the MATH dataset are used for training. Why was only a subset of MATH employed instead of the full dataset? Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We thank the reviewer for the feedback! In this rebuttal we provide a more detailed discussion of the implications of our experimental findings, and provide additional explanations for our experimental design. > The authors need a deeper analysis and discussion of pre-memorization accuracy. In the following response, we will summarize the main motivation and findings of our paper, and provide new discussion regarding the implications of these findings and how they relate to the motivation. We acknowledge that our paper currently lacks discussion with regards to the implications of our work, and we will update it to include this in more detail. Motivation: Our work is motivated by the following phenomenon: models derived from the same pretrained model and finetuned on the same finetuning dataset can have vastly different test performance, even when their train accuracies are nearly perfect. Here, the optimization of the training loss is not the issue, which suggests that something about the models’ learning dynamics is causing the difference in models’ generalization. The goal of our work is to better understand the relationship between a model’s learning dynamics and generalization. Findings: The main finding of our work is that pre-memorization train accuracy (a metric of a model’s learning dynamics) is a good predictor of a model’s downstream generalization. We provide experiments showing this both in aggregate and on a per-example basis. Implications: Our findings suggest that models exhibit two different modes of optimizing the training objective: one which leads to downstream generalization and one which doesn’t (learning progression 1 vs 2 in Fig. 2). Train accuracy conflates the two models of learning. In contrast, pre-memorization train accuracy allows us to delineate between the two, and identify the examples that are learned in a “generalizable” manner and the examples that are not. This analysis sheds lights on the aspects of a model’s learning dynamics that lead to the differences in downstream generalization, and provides us with a tool that enables more nuanced interventions to the training recipe (e.g. via data curation) to improve generalization. > The authors categorize samples with high perplexity (ppl) and high accuracy as well-generalized. However, it is possible the model simply memorizes the final answer rather than learning reasoning steps. Is there any analysis or experiment addressing this concern? Yes, in Sec 5.2, we present experiments where we perturb the prompt of the training examples, and measure how much the model’s predictions degrade from these perturbations. We find that model predictions for examples with high pre-memorization train accuracy tend to maintain high accuracy, while predictions for low pre-memorization train accuracy tend to degrade much more significantly. This experiment addresses the reviewer’s concern, as it shows that examples with low pre-memorization train accuracy actually do not generally maintain the ability to produce correct final answers for perturbed prompts. > Is pre-memorization accuracy effectively equivalent to accuracy under very small learning rates since it is measured early in training? No, we do not believe that pre-mem accuracy will always be equivalent to train accuracy under very low learning rates, because prior works have found that smaller learning rates can lead to more memorization (see [1]). So in the general case, we don't think our experiments can be used to imply any relationship between learning rate and memorization. [1] Fitting Larger Datasets by Learning with Small Batch Sizes and Regularized Initialization > Figure 4 uses Llama3 8B and Gemma2 9B, but Figure 8 (right) substitutes Gemma2 9B with DeepSeekMath 7B. What motivated this inconsistency in model selection? Different authors contributed to different parts of the paper’s experiments. Due to a lack of communication at the time, we ended up choosing different models to use for our experiments. > In the data curation experiments, only levels 1–3 of the MATH dataset are used for training. Why was only a subset of MATH employed instead of the full dataset? MATH is hard for models at the scale we are looking at, so most examples end up being in the “hard” regime, and all data curation approaches end up selecting from the same data distribution. In order to highlight the difference between the different approaches, we focused on a subset of the dataset where a larger ratio of examples are in not the “hard” regime. > The process for choosing the perplexity threshold p lacks explanation and analysis... The explanation of the data curation process lacks detail. We provide a detailed explanation of the process we use to select p in Appendix A, and the process for data curation in Appendix D. Please let us know if there are any additional questions you have regarding the processes. --- Rebuttal Comment 1.1: Comment: I sincerely appreciate the author's response. Most of my concerns are addressed and I will update my score. However, I still have some suggestions for this paper: 1. Test the effectiveness of pre-mem accuracy on additional reasoning datasets. 2. Since the threshold $p$ is different across different tasks/models, choosing the $x_i$ with ppl from the top $k%$ of dataset may be more reasonable.	null	null	null	null	null	null
On the Dynamic Regret of Following the Regularized Leader: Optimism with History Pruning	Accept (poster)	Summary: The paper presents a FTRL variant for dynamic regret with optimism in a compact domain. The paper relies on an adaptive correction $g_t^I$ to correct stored gradient states $\sum_t g_t$, similar as an ``adaptive restart'' of FTRL whenever is desired. This general development yields to regret bound when path length $P_T$ is known or unknown a priori, which are mimax optimal. The bound also automatically recovers optimal static data dependent regret. Claims And Evidence: Yes. The paper claims investigating FTRL variants for dynamic regret, which is supported by their results in section 3. Methods And Evaluation Criteria: The paper use classical regret as evaluation criterion. Theoretical Claims: main text was checked Experimental Designs Or Analyses: Included in appendix F, most case works well support the hypothesis of the need of FTRL based dynamic regret. The author was also very open to discuss the worst case and give explanation. Supplementary Material: Reviewed Appendix A, B, C3.1, Relation To Broader Scientific Literature: As claimed, fill the gap of FTRL based data dependent dynamic regret. Essential References Not Discussed: Well referenced. Other Strengths And Weaknesses: Strength: The paper is well written and easy to follow. The remarks under each theorem are very helpful to compare results to previous literature. Weakness: It is in general questionable the need of FTRL based data dependent dynamic regret, as there are already other algorithms can achieve the same bound. Especially seeing the development in this paper are still fragile in scenario 5. Other Comments Or Suggestions: with potential typo in line 395, should be <= Questions For Authors: None Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Thank you for taking the time to read the paper and providing the feedback Weaknesses. We appreciate the reviewer’s recognition of the clarity of the FTRL-based analysis for dynamic comparators. We understand the concern regarding its broader impact, given that the minimax dynamic regret bounds are known and achieved by other algorithms. Our motivation for introducing a new FTRL variant and analyzing it in this setting is as follows: $\bullet$ Flexible regularization. A key strength of FTRL is its ability to use general regularizers that can vary arbitrarily between iterations. For instance, proximal regularizers centered around different points in the domain allow the algorithm to incorporate prior knowledge about potentially good points, $\boldsymbol{\tilde{x}}_t$, as centers. This flexibility contrasts OMD, whose stability term is a scaled version of a fixed mirror map. $\bullet$ Flexible pruning: Our framework supports flexible pruning, enabling algorithmic variants between lazy and greedy methods. To see this point perhaps more clearly, the reviewer is kindly invited to take a look at the Dual interpretation asked by reviewer ecer. While the framework of Jacobsen and Cutkosky (2022) could, in principle, do that, we present here FTRL-native theoretical insights (Lemmas $4.1$\&$4.3$). These results provide explicit trade-offs and open avenues for adaptively choosing pruning frequency based on iterate-stability preferences. $\bullet$ Further insights on OMD/FTRL connections. The importance of further understanding the FTRL framework was recently highlighted by Ahn et al. (2024), who showed that the widely used Adam optimizer is essentially a form of FTRL with an exponentially decaying dual-space state. This motivates revisiting FTRL with potential modifications to how it retains this state. We see our work as a contribution in this direction, identifying when and why FTRL fails under dynamic comparators, and proposing selective pruning as a principled solution. Overall, we note that when one departs from the original versions of FTRL and OMD, it is not difficult to create variants of one algorithm that resemble (in formulas or bounds) the other. Independent of naming and definitions, our work shows that pruning the history of gradients enables dynamic regret bounds with desirable properties. It also opens new directions for exploring interpolation between laziness and greediness, which lies at the core of this very interesting FTRL vs OMD discussion. Other comments. $\bullet$ 395: it is indeed an inequality and not equality. Thanks for pointing out the typo.	Summary: This paper investigates the Follow-the-Regularized-Leader method (FTRL) under the Online Convex Optimization (OCO) framework for dynamic regret minimization. Specifically, the authors propose a series of FTRL-based methods, deliver novel analysis and establish new dynamic regret bound, which can recover existing known results. Overall, the topic is crucial for OCO community, and the theoretical guarantees are interesting. Claims And Evidence: Yes, there are experiments to verify the proposed theoretical results. Methods And Evaluation Criteria: Yes. Theoretical Claims: I review the overall proof framework, and its analysis follows some existing analytical tools. Experimental Designs Or Analyses: There are experimental studies in the appendix to support theoretical findings. Supplementary Material: No Relation To Broader Scientific Literature: This work bridges the gap between dynamic regret minimization and FTRL-based methods, a topic that has been explored in several related studies (Jacobsen & Cutkosky, 2022). Essential References Not Discussed: This work primarily investigates dynamic regret optimization, a highly active topic in the online learning community. I suggest that the authors include the following studies in the related work section to better illustrate the development of dynamic regret optimization. * Optimal Dynamic Regret in Exp-Concave Online Learning. 2021. * Optimal Dynamic Regret in Proper Online Learning with Strongly Convex Losses and Beyond. 2022. * Non-stationary Projection-Free Online Learning with Dynamic and Adaptive Regret Guarantees. 2024. Additionally, I noticed that the authors mention the SEA model but only discuss the work of Chen et al. (2024), overlooking other important milestones. I suggest that the authors incorporate discussions of the following works in their introduction about the SEA model. * Between stochastic and adversarial online convex optimization: Improved regret bounds via smoothness. 2022. * Online Composite Optimization Between Stochastic and Adversarial Environments. 2024. Finally, since the topic of this paper is highly significant, I suggest that the authors use a table to systematically compare previous works with the contributions of this paper. Other Strengths And Weaknesses: Strengths * This paper is well-organized, clearly written, and easy to follow. * This paper presents an insightful understanding for the literature. The authors provide a comprehensive explanation on the motivation behind the proposed method. Weakness * See in the following parts. Other Comments Or Suggestions: * In Line 084, there appears to be a citation error. In Chen et al. (2024), Remark 11 does not seem to discuss dynamic regret optimization for FTRL-based methods. * In Line 181, typos: JC22 => Jacobsen & Cutkosky, 2022 * In Line 265, typos: $E'_T=O(T^)$ => $E'_T=O(T)$ Below are some formatting suggestions: * I recommend avoiding the multiple use of footnotes. * The authors place the experimental section in the appendix. I suggest considering its inclusion in the main part instead. Questions For Authors: * In Line 302, what is the meaning of $1+ \beta - 1\leq 1/2+\beta/2$？In addition, I suggest explicitly stating that $P_T=O(T^{\beta})$ at this point for clarity. * In my view, the construction of $g_t^I $ in (5) is crucial for the analysis. The authors could further elaborate on the motivation behind this design—whether it arises from analytical requirements or is inspired by existing works. Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: Many thanks for your review and feedback. References. We selected Chen et al. (2024) from the SEA thread as it was the first to study SEA under the dynamic regret metric. That said, we will update the related work with the suggested background references (SEA \& others) so as to better reflect the development of dynamic regret, and include a tabular summary of bounds. Other comments. $\bullet$ Line 84: You are right, the discussion appears after Remark (8); Remark (11) was from their conference version. We will correct this in the revision. Questions. $\bullet$ Regarding the inequality, this should be just $\beta\leq1/2+\beta/2$ to highlight that the $H_T \doteq \sum_t \epsilon_t \lVert \boldsymbol u_t - \boldsymbol u_{t+1} \rVert$ term does not dominate the $\sqrt{P_TE_T}$ term in worst case prediction error $E_T=c E'_T= O(T)$. Note that in light of the discussion with reviewer 2ZjR (in the Remark), we will update the remark by mentioning that $H_T$ is $\mathcal{O}\sqrt{P_TE_T}$ Design choice. Below, we outline the rationale behind our pruning design from three complementary perspectives: preliminary intuition, analytical basis, and suggestive related work. $\bullet$ Intuition. The pruning rule is motivated by the primal-dual view in online learning over compact sets. While primal iterates stay within the compact domain $\mathcal{X}$, dual variables (e.g., cumulative gradients) can grow unbounded in $\mathbb{R}^n$. If projections repeatedly return the iterate to the same region, why keep accumulating dual information that no longer influences decisions? Pruning addresses this by trimming dual history when appropriate. The pruning cone adds flexibility, enabling partial or delayed resets to control stale information in the dual space. Of course, choosing to prune at each time makes the update equivalent to OMD (see related work below). $\bullet$ Analytical basis. If we wish to manipulate the update $\boldsymbol{x}_t$ to offset accumulated gradients, the natural starting point is the linearization of $f_t(\cdot)$, as it directly shapes the update. Ideally, we seek predictions $\tilde f_t(\cdot)$ whose subgradients can cancel or reduce the influence of past gradients. This is precisely what the pruning cone captures: it characterizes the directions in which the update can afford to remove history, and the composition with the indicator function formalizes this capability. $\bullet$ Related work. As discussed in the paper, a key inspiration comes from the equivalence between OMD and FTRL, first articulated in McMahan’s survey, for unbounded domains, and for bounded domains under fixed learning rates. This equivalence was further explored by Fang et al. (2022) [Online Mirror Descent and Dual Averaging…], who extended the analysis to time-adaptive learning rates. Both works focus on non-optimistic static regret. Additionally, the comprehensive work of Jacobsen \& Cutkosky (2022) introduced the centered mirror descent family, capturing both lazy and greedy updates by composing the indicator with either their $\psi_t$ or $\varphi_t$ terms. This naturally raises the question of how varying this choice across time may influence the algorithm’s behavior, and what roles predictions play in this.	Summary: This work revisits the Follow-The-Regularized-Leader (FTRL) framework and explores how to utilize FTRL to derive dynamic regret bounds. The key finding in this paper is to predict with the modified loss $f_t(x) + I_{X}(x)$ rather than $f_t(x)$, where $I_X(x)$ is the indicator function. When the unprojected decision $x_t^{uc}$ in the FTRL framework deviates from the domain $X$, the introduction of the indicator function $I_X$ serves as a "corrective mechanism", thus enabling the derivation of dynamic regret bounds. This paper considers two cases: when the path length $P_T$ is known and when $P_T$ is unknown in previous but the comparator $u_t$ at each round can be perceived. For the former case, an $O((1+P_T)\sqrt{E_T})$ bound is established, where $E_T$ is a data-dependent factor. As for the latter case, the authors achieve an $O((1+\sqrt{P_T})\sqrt{E_T} + A + \min\{P_T + E_T^\prime\})$ bound, where $A$ could be $O((1+P_T)\sqrt{E_T})$ at the worst case. Claims And Evidence: In Line 105, the authors claim "As for FTRL, to the best of our knowledge, no dynamic regret guarantees, whether problem-dependent or not, have been established in the existing literature". While in the paper "Understanding Adam Optimizer via Online Learning of Updates: Adam is FTRL in Disguise" published in ICML’24, this paper shows that dynamic bounds can be obtained through the FTRL framework by adding discounted factors to the losses. Conducting a more comprehensive survey and provide a more detailed comparison with the metioned approach is necessary. Methods And Evaluation Criteria: The authors present a toy numerical experiment to support their findings, which is acceptable given that this paper primarily emphasizes the theoretical understanding of the FTRL framework. Theoretical Claims: I checked the key proof highlighted in the main text. Experimental Designs Or Analyses: I checked the experimental designs, which is acceptable to support their findings. Supplementary Material: I reviewed the parameter tuning in the code. This work performs a fair comparison among mentioned methods. Relation To Broader Scientific Literature: The similar ideas of forgetting or pruning some information of the FTRL algorithm to derive dynamic regret bounds have been proposed by [Understanding Adam Optimizer via Online Learning of Updates: Adam is FTRL in Disguise, ICML’24] through adding discounted factors to the losses. This paper considers an another approach by adding indicator functions to the loss functions. Essential References Not Discussed: An essential reference missing from this paper is [Understanding Adam Optimizer via Online Learning of Updates: Adam is FTRL in Disguise, ICML’24], which is the pioneering work to establish dynamic regret bounds under the FTRL framework. Other Strengths And Weaknesses: Strengths: - The structure of this paper is well-organized and it is easy-to-follow. - This paper explores an interesting direction, as the relationship and differences between FTRL and OMD is crucial to realize two fundamental online learning algorithmic designs. Weakness: - The assumption of knowning $u_t$ at each round is too strong at least for me, and optimizing the exact values of $u_t$ may lead to overfitting to the online loss functions. - Theorem 3.3 is not optimal at the worst case, making it less competitive to existing results. - The obtained results are not guaranteed to hold for any comparators. Overall, this work presents interesting views to the FTRL framework. However, I believe it could be further refined by considering more general cases of dynamic regret bounds, which would help enhance its impact. Other Comments Or Suggestions: - Is $\partial$ missed in Line 100 when recalling $g_t$? - Is the definition of V_T on line 109 missing a squared term? - There is a typo ($O(T)$) at the right column in Line 266. - I am confused about the definition of $A$ at the right column in Line 276. Are there any typos? Questions For Authors: - Can the introduction of indicator functions be understood from a primal-dual perspective? From this viewpoint, OMD performs a non-projected update in the dual space and only applies projection when transitioning back to the primal space. Could a similar perspective be applied to FTRL? - Is it possible to modify the proposed algorithm so that it can guarantee dynamic regret bounds for arbitrary comparators? Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Thank you for reading the paper and providing feedback. Claims \& missing reference. We agree that it is important to discuss carefully Ahn et al. “Adam is FTRL in …”; we indeed cite this paper and mention that it uses an FTRL variant that attenuates history to obtain discounted regret bounds. That said, their paper also introduces a reduction from discounted to dynamic regret, which we did not discuss in detail in the current draft. Thanks for pointing this out. Here is a brief clarification: $\bullet$ In the bounded domain setting, their bound is $P_T^{1/3} T^{2/3}$ (From their Corollary 3.4, assuming knowledge of $P_T$), which is suboptimal due to its super-$\sqrt{T}$ dependence. $\bullet$ In contrast, our bounds, which also assumes $P_T$ knowledge, achieve $\sqrt{P_T T}$ in the worst case and further establish a refined $\sqrt{P_T E_T}$, which is data-dependent. This is not a limitation of their work, but rather a natural outcome of their goal: explaining ADAM via FTRL. To clarify this, we will: $(i)$ explicitly attribute the first sublinear-in-T dynamic regret bound for FTRL to Ahn et al. (2024), and $(ii)$ revise the sentence in our paper to read: “…As for FTRL, no dynamic regret guarantees, data-dependent or otherwise, with $\sqrt{T}$ rate have been established ...” We note that their Cor. 3.5 improves the bound to $\sqrt{P_T T}$ but only in the unbounded setting. Weakness 1\&3: Note that Theorems $3.1$,$3.2$, and $3.4$, do in fact hold for all comparators (i.e., without knowing $\boldsymbol{u}_t$). This is because in Thm. $3.1$ and $3.4$, no information on $P_T$ is used (and the price is paid accordingly). As for Thm. $3.2$, knowing $P_T$ in advance does not necessarily mean that we know all the comparators, but rather that we compete with sequences whose path length is at most $P_T$. Here, we followed the standard notation from the literature, but indeed, a better notation would be fixing any $B$. Then, we compete with any sequence whose $P_T\leq B$ to get $\sqrt{BE_T}$. It is only Thm. $3.3$ that assumes observability of $\boldsymbol u_t$ online. Yet, these need not be the minimizers of each corresponding $f_t$ (i.e., not necessarily overfitting). Weakness 2: For observable comparators, estimating $\sqrt{E_T / P_T}$ online is infeasible due to non-monotonicity. Our data-dependent approach recovers the $\sqrt{E_T P_T}$ bound when $\sqrt{P_t/E_t}$ changes direction $O(\sqrt{P_T})$ times (i.e., mostly monotone). The method performs no worse than tuning strategy $1$, while offering improvements when this structure is present. In all cases, the doubling trick of Jadbabaie et al. remains applicable. Other comments Thanks for spotting the typos. For the def. of $A$, it is more convenient to keep it but update the proof accordingly to have $2R\sigma A$ instead of $A/2$. Questions. Dual perspective. To provide a dual view, we look at the update step via the lens of dual maps. Recall the standard FTRL update: $ \boldsymbol x_{t+1}^{\text {RL}} = \arg\min_x \langle \boldsymbol g_{1:t}, \boldsymbol x\rangle + r_{0:t}(\boldsymbol x) =\nabla r_{0:t}^(-\boldsymbol g_{1:t})$, where $r_{0:t}^(\cdot)$ is the conjugate of the dual map $\nabla r_{1:t}(\cdot)$, restricted to $\mathcal{X}$ via $r_0 = I_\mathcal{X}$. From this viewpoint, FTRL maintains the state as cumulative gradients in dual space. In contrast, the OMD update, as you noted, is expressed as: $\boldsymbol x_{t+1}^{\text{MD}} = \nabla r_{0:t}^(\nabla r_{1:t-1}(\boldsymbol x_t) - \boldsymbol g_t)$. Our selective pruning update can be simply interpreted as: $\boldsymbol x_{t+1} = \arg\min_x \langle \boldsymbol p_{1:t}, \boldsymbol x \rangle + r_{0:t}(\boldsymbol x) = \nabla r_{0:t}^(-\boldsymbol p_{1:t}) = \nabla r_{0:t}^(\nabla r_{1:t-k-1}(\boldsymbol x_{t-k})-\boldsymbol g_{t-k:t})$, where $k$ denotes the most recent step at which we chose to prune. The last equality holds by the definition of $\boldsymbol g_k^{I}$ (assuming no predictions). Intuitively, we retain explicit gradient history only since the last pruning step $t-k$, while summarizing earlier history implicitly via the dual mapping of $\boldsymbol{x}_{t-k}$. The crux of the paper is showing that the way history is split (explicitly tracked after pruning, and implicitly captured before) is what controls dynamic regret. Guaranteeing* $\sqrt{P_TE_T}, \forall u_t$. One can ``modify" OptFPRL with the second tuning strategy (that competes with comparators of at most $P_T$ switches); we can instantiate a set of $\Theta(\log T)$ sub-learners, each with a halving $\sigma$ starting from $1/\sqrt{T}$. Then, using the meta-learner of Zhao et al. (2020), the minimax bound can be recovered. The gist of this approach is that eventually $\exists$ an expert $i$ such that $\forall P_T, \sigma^{(i)} \geq 1/\sqrt{P_T}\geq 1/2\sigma^{(i)}$. This will be added to the paper as part of the discussion. --- Rebuttal Comment 1.1: Comment: I thank the authors for their responses, which address my concerns. Accordingly, I have decided to raise my score to 3. However, I believe that, to enhance the impact of the results, the paper should provide a more thorough discussion on how to use the meta-learner proposed by Zhao et al. (2020) to achieve the $\sqrt{P_T E_T}$ result. I hope the authors will revise the manuscript accordingly. --- Reply to Comment 1.1.1: Comment: Thank you for taking the time to engage with our response and for updating the score. We appreciate your feedback and will ensure that the points raised in our exchange are incorporated into the final version to further strengthen the paper.	Summary: The paper presents a new optimistic algorithm, Follow-The-Pruned-Leader (FPRL) that aims to achieve dynamic regret in $O(\sqrt{P_TE_T})$, where $E_T$ measures the prediction error. The key insight is to avoid simply stacking previous gradients as they make the standard Follow-the-Regularized-Leader (FTRL) less adaptive to dynamic environments. It is done by "pruning" past gradients when their updates become too "large". They achieve $O(\sqrt{P_T E_T})$ when $P_T$ is known in advance or the comparison sequence is observable, but also universal regret (i.e for all sequences simultaneously). Finally, all the terms in the regret scale with the prediction error, meaning that, compared to previous work who had an incompressible dependence on $P_T$, the dynamic regret of FPRL can be constant for perfect predictions. ## update after rebuttal I decided to maintain my score Claims And Evidence: Yes, They provide proofs for all their claims along with simulation experiments the improvement of their method. However, the claims regarding the remark 258R-270R is not detailed in appendix contrary to the authors claims. Methods And Evaluation Criteria: They use dynamic regret as a criteria which is standard. Theoretical Claims: I checked all proofs, all except the proof of Theorem 3.3 that I did not read. I skimmed through the one of Theorem 3.4. No issues on what I read in terms of proof, but there is some comments that must be addressed, notably on the cyclic dependency (See weaknesses). Experimental Designs Or Analyses: Yes, the experimental design makes sense and highlight the strength and weaknesses of their method. It would have been good to also have experiments showing how the regret converges for perfect predictions while other methods that have a linear dependency on $P_T$ keep increasing. This would be in a very dynamic environment, like scenario 4 of Appendix F Supplementary Material: Yes. All except C.3 Relation To Broader Scientific Literature: - The algorithm builds on previous FTRL / OptFTRL work but contribute a new idea of choose smartly a subgradient from $I_\mathcal{X}$ (indicator function of the set) to have a more adaptive algorithm. Their update has some similarity with (McMahan, 2017) - Their dynamic regret guarantee improves the current best ones, i.e Zhao et al., 2024 by having a regret that goes to a constant when the predictions are perfect. Essential References Not Discussed: None that I can think of. Other Strengths And Weaknesses: Strengths: - The experiments really highlight the benefit of their method - The regret derivation is easy to follow and the main body explain the core ideas pretty well Weaknesses: - Some math equations are hard to follow because of typos and alignments. - Computation cost (see next weakness) - The authors mention avoiding the circular dependency, but I am unsure (if we want to stay computationally efficent). OOMD linearize first in order to minimize computation cost, and since $x_t$ is unknown, the linearization is often done around $\tilde x_t$ (an intermediate value that does not depend on $f_t$). Here $x_t$ depends on $\tilde f_t$, thus we cannot linearize around $x_t$ to make the computation. So, if we wanted to stay computationally efficient and linearize the prediction, it will be around $x_{t-1}$ leading to the same issue noted by Scroccaro et al. (2023). Other Comments Or Suggestions: A bit too many typos and math alignments that are wrong: (I use L for the left column and R for the right) 1. the notation $z_{1:t} := \sum_{\tau=1}^t z_\tau $ where $z$ is any sequence is never formally introduced. (yes it appears in line 72R but not as a definition). 2. The function $h$ is used in line 307R-310R before being introduced in line 367L). 3. Appendix 180: I think it should be $x_t = \arg\min_{x\in\mathcal{X_t}}$ instead of for any $x_t \in \mathcal{X}, \dots$. As the condition (5) in line 185 is true only if $x_t$ is the minimizer of $\mathcal{X}$, but I might be wrong 4. Math Alignment issues ( the equal or inequality signs appear mid lines, making it hard to read): - Appendix 324-326 - 385R-389R - Appendix 165 . That $\tilde f_{T+1}$ term is too isolated 5. Typos - 265R ($E(T^)$ (missing the power and the parenthesis is raised - Appendix 638 $\delta_t$ appears in its own upper bound - Appendix 660 $<p_t, x> \to <p_t, x_t>$ - 421L . "we have $R_T$" followed by equations. Maybe it should be "$R_T$ is upper bounded by:" or $R_T$ should be in the equation below. Questions For Authors: 1. What is the difference in computation time between this method and OMD. Does the method benefits from using an optimization on $\tilde f_{t+1}$ when OOMD focuses on the linear approximations. 2. (Repeat on the experiment) Does the regret converges for perfect predictions while other methods that have a linear dependency on $P_T$ keep increasing. (The regret, not the average regret). 3. See third weakness. Any comment ? 4. In appendix 103, you say, when $\sigma_{1:t} = 0$ but it does not seem to be used in that proof. Is that a typo? Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: Thanks for taking the time to read the paper and provide the feedback. Claims \& evidence $258R$: Indeed, these details were omitted from the main text due to space constraints and accidentally left out of the appendix. We apologize for this oversight. Briefly, the claim is that the term $H_T \doteq \sum_t \epsilon_t \lVert\boldsymbol u_{t+1} - \boldsymbol u_t\rVert $ is $\mathcal{O}(\sqrt{P_TE_T})$, and therefore never dominates the bounds in Theorems $1$-$4$, since those are $\Omega(\sqrt{P_TE_T})$. We state the remark below. Remark: Let $\epsilon_t^2$ scale as ${1}/{t^{1-\alpha}}, \alpha \in (0,1]$ so that $E_T = \Theta(T^{\alpha})$. Similarly, let $\lVert \boldsymbol{u}_{t+1} - \boldsymbol u_t \rVert$ scale as $\frac{1}{t^{1-\beta}}, \beta \in (0,1]$ so that $P_T = \Theta(T^{\beta})$. Then, we get that $H_T = \sum_t {1}/{t^{(1-\alpha)/2\ +1-\beta}} = \Theta(T^{\beta +\ \alpha/2\ -1/2})$ and it holds $ {\beta +\ \alpha/2\ -1/2}\ \leq\ (\alpha+\beta)/{2},\quad \forall \alpha, \beta \in [0,1).$ The RHS is the growth rate of $\sqrt{P_TE_T}$. Weaknesses. On the circular dependency. Incorporating non-linearized $\tilde f_t(\cdot)$ is offered as an option to avoid circular dependencies, but it is not required for the update to be well-defined. When efficiency is a priority, linearized FTRL, like OOMD, can follow the standard practice by setting $\tilde {\boldsymbol g_t} = \nabla \tilde f_t(\boldsymbol x_{t-1}) $ (i.e., linearizing the predicted function around the previous iterate), as done in prior work (e.g., see $\tilde{\boldsymbol g_t}$ Flaspohler et al., 2021). Hence, we maintain linearized forms and computational efficiency at the cost of having the somewhat less-informed quantity $\sum_t \lVert \nabla f_t(\boldsymbol x_t) - \nabla \tilde f_t(\boldsymbol x_{t-1})\rVert^2$ instead of $E_T$, as you correctly note. Moreover, in many cases, avoiding non-linearization does not compromise efficiency (see Questions) Questions. Linearization \& Efficiency. In fact, including $\tilde f_t(\cdot)$ does not always compromise efficiency. For example, when $\tilde f_t(\cdot)$ are weighted $\ell_2$-norms, the complexity remains the same as OMD (i.e., closed form in $\mathbb R^n$ + Bregman projection). Nonetheless, for general convex predictions, solving a convex subproblem is indeed required. In such cases, practitioners retain the option to linearize (around the previous iterate). on $\sigma_{1:t}=0$. This condition addresses the situation when $\boldsymbol x^{\text{uc}}_t$ does not exist. In other words, we simply specify that if such a point does not exist, it is treated as lying outside $\mathcal{X}$, ensuring the update step formula remains well-defined. Recommended experiment. We repeat Scenario 4 from the paper, but now comparing the optimistic variants of OGD, FTRL, and our proposed OptFPRL. We plot the regret $R_T$ under predictions constructed as the original functions plus adversarial noise. Specifically, the adversarial noise is set as the negative of the original cost functions, with magnitude decaying quickly as $1/(0.1t)$, becoming negligible by $t \approx 100$. The resulting figure, along with algorithm implementations and the full code to reproduce these results, is available at the doubly-anonymized link: https://anonymous.4open.science/r/11679-3538. As noted in the paper, standard FTRL can be easily “trapped,” accumulating redundant gradients and failing to track the comparators. Optimistic OGD and our OptFPRL react immediately when losses change direction. Indeed, achieving constant regret under perfect predictions primarily serves as a sanity check for scale-freeness, rather than the central advantage. This objective was set to preserve the scale-freeness property observed in OMD while developing FPRL. The main benefit of FTRL-based formulation lies in its flexibility to arbitrarily choose and, potentially center differently, regularizers, enabling a ``compressible" dependence on $P_T$, as opposed to having fixed mirror maps that time varying weights (i.e., learning rates). Other comments. Thank you for the careful reading, we will make sure to fix the typos. $\bullet$ Appendix $180$. True, the minimizer in $\mathcal{X}$ ($h_0=I_{\mathcal{X}}$). $\bullet$ Appendix $638$. $\delta_t \rightarrow \epsilon_t$. $\bullet$ $421$L. $R_T \rightarrow R_T\leq$.	null	null	null	null	null	null
Be Confident: Uncovering Overfitting in MLLM Multi-Task Tuning	Accept (poster)	Summary: This paper proposes Noise Resilient Confidence Alignment (NRCA) to reduce overfitting in open-response tasks during multi-task fine-tuning of Multimodal Large Language Models NRCA enhances performance on tasks like image captioning and visual question answering, outperforming traditional fine-tuning methods. Experiments and comparisons validate its effectiveness and compatibility with other optimization strategies. Claims And Evidence: The claims are well-supported by clear and convincing evidence. Methods And Evaluation Criteria: The authors respectively measure the multi downstream tasks performance and further utilize the average performance to evaluate the overall performance. Authors conducts experiments on four downstream datasets into two task types: image captioning (open-response) and visual question-answering (fixed-choice) to formulate the multi-task setting. Theoretical Claims: The authors analyze token prediction confidence in Eq.7 and argue that open-response tasks tend to reach overly confident predictions due to an overreliance on inherent memorization. Experimental Designs Or Analyses: The experimental results are thorough and well-rounded, as the authors conduct a variety of experiments comparing different methods across multiple downstream tasks. Supplementary Material: The supplementary material includes additional experiments with varying batch sizes and training loss analysis for different tasks, addressing potential questions. The pseudo-algorithm is clear and easy to understand. Relation To Broader Scientific Literature: This paper presents a simple yet effective approach to alleviate the overfitting issue of the open-response task during the multi-task tuning process. It addresses a novel research problem within the field of MLLM fine-tuning. Essential References Not Discussed: Authors could add the discussion with the multi-task learning which shares the similar research objective with this paper. Other Strengths And Weaknesses: For strengths: 1. Novel Problem Focus: Identifies the under - explored issue of open - response overfitting in MLLM multi - task tuning, which is crucial as MLLMs are increasingly used for diverse tasks. 2. Effective Solution: Proposes NRCA, a method that uses Gaussian - perturbed visual inputs and confidence alignment. It effectively reduces overfitting and improves performance, as shown by experiments on multiple datasets and MLLM architectures. 3. Comprehensive Testing: Conducts wide-ranging experiments with two MLLM architectures LLaVA and VILA and four downstream datasets across open-response and fixed-choice tasks. Ablation studies further analyze the method's components. 4. Proposed method is relatively resource-efficient. It doesn't need to store pre - trained MLLM weights, reducing computational burden. Furthermore, the method's hyper-parameters work well across different MLLM models For weakness: 1. Application Limitation NRCA is designed for alleviate open-response overfitting and when there are only the fixed-choice tasks, its effectiveness is less obvious, restricting its universal application. It encourages the further discussion on limitation. 2. Typos Errors. In Table 3, not retaining two decimal places. Please carefully check for grammar and markup issues 3. The rationale for Eq.5 to detach the normal branch lacks the explanation. The authors should discuss the reason behind it. Other Comments Or Suggestions: The paper is written in a complicated manner with many key words such as open-response and fixed choice. Provide the clear definition would be better for paper readability. Questions For Authors: The authors should add more detailed limitation discussion and check the typo error. The rationale behind the proposed operation should add relative discussion. Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: Dear Reviewer XwCL: Thank you very much for your valuable comments and constructive feedback. Below, we carefully address each of your concerns point-by-point, providing detailed explanations and additional evidence to clarify our approach and validate its effectiveness. Q1: Limitation Discussion (Other Strengths And Weaknesses & Questions For Authors) A1: Open-response and fixed-choice tasks reflect two complementary aspects of Multimodal Large Language Model (MLLM) capabilities: the ability to generate free-form responses to open-ended questions, and the ability to select correct answers from predefined options. These two task types are widely recognized and are also included in the pre-training datasets construction. Solely tuning on fixed-choice tasks would degrade into the single task optimization and limits model application scope. In contrast, open-response tasks are crucial for unlocking MLLM ability to generate free-form expressions, which go beyond the limitations of traditional classification. We have provided a discussion in Page 5. We will provide a detailed limitation discussion in our revised manuscript. Thanks for your valuable suggestions! Q2: Typos Errors (Other Strengths And Weaknesses & Questions For Authors) A2: Thanks for your tips. We will fix the typos and check grammar and markup issues in our revised manuscript！ Q3: Rationale for Normal Branch Detach (Other Strengths And Weaknesses & Questions For Authors) A3: In Eq. 5, we aim to enhance the visual behavioral effect to improve prediction robustness and reduce reliance on language priors. To achieve this, we encourage the noisy prediction confidence $\tilde{\mathcal{I}}$ to align with the normal prediction confidence $\mathcal{I}$, enforcing a one-way alignment constraint. Therefore, we detach the normal branch to prevent it from being influenced by the noisy branch during optimization. We will provide a detailed rationale discussion in our paper. Thanks. Q4: Clear Keyword Definition (Other Comments Or Suggestions) A4: Open-Response task means the task of generating a response to a given question such as image captioning dataset. Fixed-Choice task denotes the task of selecting one of several options from the candidate list, e.g., visual question-answering dataset. We will clarify the definition in our revised manuscript. Thanks for your suggestion!	Summary: In this work, the author focuses on Multimodal Large Language Models tuning. Specifically, the authors propose a method called Noise Resilient Confidence Alignment (NRCA) that aims to alleviate the issue of overfitting, particularly in open-response tasks during multi-tasks tuning. approach emphasizes maintaining consistent prediction patterns in MLLMs by enhancing the integration of visual cues alongside language priors. Through experimental evaluations, they show that their method improves model robustness by aligning token prediction confidence towards the normal visual branch and reduces the over-reliance on language priors. The authors conduct extensive experiments on popular model architectures, validating the effectiveness of their approach across various multi-task downstream settings, including tasks like image captioning and visual question answering . Claims And Evidence: Yes. The claims and evidence are clear and convincing. Methods And Evaluation Criteria: The NRCA method is designed to alleviate open-response overfitting during MLLM fine-tuning by encouraging prediction consistency between distorted and normal visual patterns. CIDER and Top-1 Accuracy are used to evaluate performance on downstream tasks. Comparisons with baseline methods and ablation studies further validate NRCA’s effectiveness. Theoretical Claims: N/A. Experimental Designs Or Analyses: Yes. The authors use common evaluation metrics such as CIDER and Top-1 Accuracy, depending on the task. They perform experiments on popular Multimodal Large Language Models (LLaVA and VILA) using datasets like Flickr30k, COCO-Cap, ScienceQA, and IconQA. Supplementary Material: The authors provide a notation table and algorithm description in the supplementary material, along with a theoretical analysis for both open-response and fixed-choice tasks, addressing behavioral discrepancies. Relation To Broader Scientific Literature: The author introduces an interesting problem that during multi-task tuning, open-response tasks exhibit overfitting behavior, a phenomenon that has not been thoroughly explored in existing research. Proposed method consider encourage prediction consistency to alleviate the reliance on language prior. Essential References Not Discussed: None. Other Strengths And Weaknesses: Pros: - The paper introduces an innovative problem of overfitting in open-response tasks during multi-task fine-tuning, a gap not previously explored in existing research. This adds a valuable contribution to the field. - The paper includes a thorough set of experiments across a range of datasets and downstream tasks, such as image captioning and visual question answering, demonstrating the effectiveness of NRCA. The use of popular benchmark datasets like Flickr30k and COCO-Cap strengthens the reliability and generalizability of the results. - The NRCA method is a unique approach to controlling overfitting. By encouraging prediction consistency between distorted and normal visual patterns, NRCA offers a more interpretable mechanism for preventing overfitting, compared to traditional fine-tuning methods. - The paper includes a notation table and algorithm description in the supplementary material, making it easier for other researchers to reproduce the results and understand the underlying methodology. Cons: - Conceptual Discussion: The authors should further claim the different for your methods with existing methods. Why they can not solve the problem mentioned in the paper to highlight the contribution. - The explanation for Figure 3 is unclear. Does it means your method alleviat the reliance on language prior? - Dataset Construction. As for the MLLM tasks, the authors should report the textual prompt for different tasks for better illustration. Other Comments Or Suggestions: Refer to weakness. Questions For Authors: Please refer to Other Strengths And Weaknesses parts. Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: Dear Reviewer SJh5: Thank you for your thoughtful review and for raising key concerns regarding our work. We aim to address your concerns in our detailed responses below, hoping to provide clarity and demonstrate the effectiveness of our proposed approach. Q1: Conceptual Discussion (Other Strengths And Weaknesses) A1: In the context of Multimodal Large Language Model (MLLM) tuning on downstream tasks, empirical evidence shows a tendency toward overfitting on the target distribution. This is primarily due to the mismatch between the model large-scale capacity and the limited size of domain-specific samples. Existing investigations either introduce stiff penalty regularization terms or design partial update masks. However, such approaches typically focus on single-task adaptation and apply uniform anti-overfitting objectives across all examples, without accounting for task-specific differences. Under multi-task settings, different task types often exhibit inconsistent fitting behaviors. Our analysis reveals that open-response tasks are particularly prone to overfitting, largely due to their heightened dependence on textual modalities. To address this, we propose a novel approach that mitigates overfitting on the target distribution by enforcing confidence alignment from noisy visual inputs to their corresponding clean visual patterns. We will provide a detailed conceptual explanation for the proposed approach in our revised manuscript to highlight our novelty. Thanks for your valuable suggestions! Q2: Figure 3 Explanation (Other Strengths And Weaknesses) A2: Figure 3 illustrates the performance under both normal and noisy visual input for different methods. Existing methods show minimal performance gap regarding visual quality, which reflects the restricted affect from the visual branch and presents a high reliance on the textual prior information to generate the corresponding output response. We will provide a detailed explanation for Figure 3 in our revised manuscript. Thank you for your helpful suggestion. Q3: Dataset Construction (Other Strengths And Weaknesses) A3: For fixed-choice tasks (ScienceQA and IconQA), we use the textual prompt: “Answer with the option’s letter from the given choices directly.” For open-response tasks (Flickr30k and COCO-Cap), we collect five manually written instructions and randomly sample one as the prompt for each caption, as follows: - "Describe the image as simply as possible with a sentence or phrase" - "Give a brief summary of what you see" - "Provide a short description of the image" - "Write a short description for the image" - "Briefly describe the content of the image" We will provide a clear description of the dataset construction procedure in our revised manuscript. We will release the corresponding training and test JSON files in the final version. Thank you for your valuable suggestions!	Summary: This paper introduces "Noise Resilient Confidence Alignment" (NRCA), a method to address overfitting in multi-task fine-tuning of Multimodal Large Language Models (MLLMs). The authors observe that while fine-tuning MLLMs on multiple tasks, performance on open-response tasks (like image captioning) degrades over time, whereas fixed-choice tasks remain stable. They attribute this to MLLMs over-relying on language priors rather than visual information. The proposed solution injects Gaussian noise into visual inputs and enforces alignment between prediction confidence on noisy and clean inputs, thereby enhancing visual representation in the model. Experiments across multiple benchmarks (Flickr30k, COCO-Cap, ScienceQA, IconQA) with different MLLM architectures (VILA, LLaVA) show NRCA consistently outperforms baseline methods and other fine-tuning approaches. Claims And Evidence: The paper's primary claim that open-response tasks degrade during multi-task fine-tuning is well-supported by empirical evidence in Figure 1, showing performance drops on Flickr30k while ScienceQA remains stable. The claim that NRCA alleviates this issue is supported by extensive experiments across different datasets, model architectures, and fine-tuning parameters. However, the claim that language priors are the root cause of this degradation is less convincingly established. While the authors observe that models produce similar outputs for normal and noisy images (Figure 3), this could have other explanations besides language prior reliance. The connection between confidence alignment and reduced language prior dependency lacks a strong theoretical foundation. The empirical results are strong and consistent across various settings Update: the last part was clarified during the rebuttal period. Methods And Evaluation Criteria: The proposed method is well-motivated from the problem observation and appropriate for addressing multi-task fine-tuning challenges. The evaluation across multiple benchmarks like COCO-CAP and IconQA, and , with both open-response and fixed-choice tasks, provides a comprehensive assessment of the approach. Theoretical Claims: The paper doesn't present formal theoretical proofs but offers explanations for why NRCA should work. The rationale connecting confidence alignment to improved visual representation is reasonable but would benefit from a more rigorous formulation. Update: The author rebuttal addressed my concern. Experimental Designs Or Analyses: The experimental design is sound and comprehensive. The authors test across: Multiple MLLM architectures (VILA, LLaVA) Different model sizes (3B, 7B) Various fine-tuning epochs (E=3, E=5) Different batch sizes (B=16, B=24, B=32) Multiple benchmark datasets The ablation studies isolate contributions of key components. The authors also demonstrate robustness to hyperparameter settings and analyze the method's resource efficiency compared to alternatives. Supplementary Material: Yes, I reviewed the training code attached in the supplementary materials. Relation To Broader Scientific Literature: The work builds effectively on existing literature in MLLM fine-tuning, particularly addressing overfitting challenges. The authors appropriately contextualize their work within related methods like parameter-efficient fine-tuning and regularization approaches. Essential References Not Discussed: Some important references that might improve the paper's contextualization: Literature on modality bias in multimodal models that could provide alternative explanations for their observations Other recent work specifically on vision-language alignment during fine-tuning that could offer complementary insights on overfitting prevention Update: the author responded during the rebuttal period and cited meaningful comparable literature in the field. Other Strengths And Weaknesses: Strengths: Novel identification of the open-response overfitting problem in multi-task MLLM fine-tuning Simple yet effective confidence alignment approach that's architecture-agnostic Comprehensive empirical evaluation across diverse settings Practical resource efficiency compared to alternative methods Weaknesses: The theoretical connection between language priors and open-response overfitting needs stronger justification Surprising effectiveness of random mask tuning (which achieves competitive results) isn't thoroughly analyzed Other Comments Or Suggestions: - Consider expanding the analysis of why random mask tuning performs so well The paper would benefit from more explicit evaluation of visual attention patterns before and after applying NRCA Questions For Authors: How do you explain the strong performance of random mask tuning as it relates to language prior issue with open-ended q-a geneartion? Does this suggest the problem might not be specifically about language priors but perhaps more general optimization challenges? The gains on fixed-choice tasks are sometimes modest or even negative. Could you explain why enforcing confidence alignment might occasionally harm performance on these tasks? Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Dear Reviewer ELAr: We sincerely thank you for your valuable feedback and hope our responses adequately address your concerns and merit a score revision. Q1: Theoretical Claims of NRCA and Its Connection to Visual Representation A1: Denote $I$ and $\tilde{I}$ as the average confidence over ground-truth tokens under clean and perturbed visual inputs (see Eq 4). Let $\tilde{z}_t$ and $z_t$ be the predicted logits at position $t$, and let $\sigma(\cdot)$ denote the softmax function. The confidence alignment objective of $\mathcal{L}_{\text{NRCA}}$ is: $$ \min \left\| 1 - \frac{\tilde{I}}{I} \right\| = \min \left\| \frac{1}{T} \sum_{t=1}^T \frac{\sigma _{y_t}(z_t)-\sigma _{y_t}(\tilde{z}_t)}{I} \right\|. $$ Since $I$ is detached from the computational graph, the optimization reduces to: $$ \min\left\| \sum_{t=1}^T \sigma _{y_t}(z_t)-\sigma _{y_t}(\tilde{z}_t) \right\|. $$ Assuming $\sigma _{y_t}(z_t) \geq \sigma _{y_t}(\tilde{z}_t)$ for all $t$ (a natural assumption since clean inputs typically yield higher confidence), the objective becomes: $$ \min \sum_{t=1}^T \left( \sigma _{y_t}(z_t)-\sigma _{y_t}(\tilde{z}_t) \right). $$ This encourages the ground-truth token probabilities under perturbed inputs to approach those under clean inputs, i.e. $$ \sigma _{y_t}(\tilde{z}_t) \to \sigma _{y_t}(z_t). $$ Since $\tilde{z}_t=g(\phi(f(\tilde{x}_v)),h_t)$, the loss encourages the learnable modules ($\phi$ and $g$) to produce robust visual features that preserve confidence on ground-truth tokens under perturbations, thereby improving visual representation quality. Q2: Theoretical Connection Between Language Priors and Open-Response A2: We consider token-level prediction in autoregressive multimodal generation, where the model learns the probability of a target sequence $y=(y_1, \dots, y_T)$ given a visual input $x^v$ and textual prompt $x^t$. The objective is to minimize the negative log-likelihood $L_{\text{CE}}.$ In open-response tasks such as image captioning (eg Flickr), the output is a multi-token sentence of length $T=k$, with autoregressive factorization: $$ p(y \mid x^v, x^t)=\prod_{t=1}^k p(y_t \mid y_{\lt t}, x^v, x^t). $$ Due to the richness and uniqueness of each output, the model may overfit by memorizing input-output mappings and relying on linguistic priors in $y_{\lt t}$ rather than visual cues. In contrast, fixed-choice tasks (e.g., IconQA) involve single-token outputs ($T=1$) from a small label set: $$ p(y \mid x^v, x^t)=p(y_1 \mid x^v, x^t), $$ where prefix conditioning is absent and language priors are less effective. The model must therefore rely more on visual input, reducing overfitting. This analysis complements Appendix C and the observations in Fig 6, further clarifying the connection between language priors and overfitting in open-ended tasks. Q3: Essential References Discussion A3: Prior work on modality bias shows that MLLMs often over-rely on textual priors, causing visually misaligned hallucinations[1]. Contrastive decoding compares token distributions across views but adds inference cost[2]. Our method aligns token-level confidence during fine-tuning to improve understanding. For vision-language alignment, existing methods either build diverse instruction data or use reinforcement learning with designed reward signals, both requiring costly annotation or tuning[3]. Our method avoids these overheads and integrates directly into standard fine-tuning. [1] Multi-modal hallucination control by visual information grounding,CVPR2024 [2] Mitigating Object Hallucinations in LVLMs through Visual Contrastive Decoding,CVPR2024 [3] Visual-RFT: Visual Reinforcement Fine-Tuning,arXiv2025 Q4: Random Mask Tuning Effectiveness Discussion A4: Random Mask Tuning applies stochastic masks to parameters, injecting noise to reduce reliance on specific subnetworks and implicitly regularize by limiting parameter co-adaptation. While effective on smaller models (VILA3B), its performance drops on larger ones (LLaVA7B), as shown in Tab 4, suggesting its effect comes from constrained optimization rather than addressing language prior dominance. In contrast, our method perturbs visual inputs and aligns token-level confidence with the clean visual branch, enhancing visual grounding and ensuring consistent performance across model scales. We will include a detailed analysis in the manuscript. Q5: Visual Attention Patterns A5: Due to limited space, please refer to Q2 in Response to Reviewer H4RG. Q6: Fixed-Choice Tasks Performance A6: The phenomenon of modest gain in fix-choice task is also present in several counterparts designed to alleviate overfitting. Though some of them perform marginally better on fixed-choice tasks, they tend to incur trade-offs and underperform on open-response tasks. By enhancing visual robustness through confidence alignment, our method achieves a better trade-off and consistently surpasses all baselines in overall multi-task performance.	Summary: In the reviewed paper, the authors identify overfitting in open-response tasks as a significant challenge in multi-task multimodal large language model (MLLM) fine-tuning. They propose a novel method called NRCA, which aligns prediction confidences between noisy and normal visual inputs to improve visual representation learning. The paper presents comprehensive empirical evaluations that demonstrate the effectiveness of the NRCA approach in addressing the identified issue. Claims And Evidence: The following claims are not well supported `We argue that leveraging MLLM to achieve multi-task specialization is a more efficient approach than the conventional one-to-one fine-tuning paradigm.` How to define the multi-task specialization? The original MLLM training itself is somehow a `multi-task specialization`. Is this method applicable to MLLM training itself? Methods And Evaluation Criteria: Yes. Theoretical Claims: None Experimental Designs Or Analyses: Partially. Although the author asserts that NRCA addresses the issue of relying on the language prior, the supporting experiments and analysis unconvincing in demonstrating that the final improvement stems from resolving this problem. Including a visualization could aid readers in better understanding the proposed method and its effectiveness. Supplementary Material: Yes, code. Relation To Broader Scientific Literature: A common method for reducing hallucinations in multimodal large language models (MLLMs) involves adjusting the next-token logits contrastively based on the standard prediction distribution. This paper primarily distinguishes itself through its unique approach to loss design. Essential References Not Discussed: No Other Strengths And Weaknesses: The paper discusses its limitations, which is commendable. It also provides the code, enhancing transparency and reproducibility. Additionally, the design of the NRCA loss function is cleverly crafted, showcasing an innovative approach. The limitation comes from the additional forward/backward pass. Other Comments Or Suggestions: Table 2 is a bit confusing without checking main text. Questions For Authors: Could you design experiments to confirm that the observed improvement genuinely results from addressing the issue of reliance on the language prior? Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Dear Reviewer H4RG: Thank you very much for your affirmation of our work, as well as the insightful concerns and questions you have raised. We have carefully considered each comment and provided responses. Q1: Multi-Task Specialization Definition (Claims And Evidence) A1: Multi-Task Specialization refers to fine-tuning a pre-trained model for a specific downstream application, which normally has a limited amount of data, compared with the pre-training data scale. For example, the authors of LLaVA claim that it involves $150k$ unique language-image instruction-following samples. However, the specialization application samples are much more limited, i.e., $10k$ for target task. Thus, tuning on the downstream distribution tends to lead to overfitting on the specialization task. And we point out that open-response tasks easily appear the overfitting behavior within the multi-task specialization. We attribute this degradation to language prior reliance and propose Noise Resilient Confidence Alignment to enhance the effect of visual cues in the token prediction. Therefore, our method is applicable to Multimodal Large Language Model (MLLM) training itself but benefits more in the specialization tuning process. We will provide a detailed multi-task specialization definition in our revised manuscript. Thanks for your valuable suggestions! Q2: Language Prior Reliance Visualization Analysis (Experimental Designs Or Analyses & Questions For Authors) We assume that for Multimodal Large Language Model (MLLM), input tokens include System Tokens, Prompt Tokens and Visual Tokens and appear different contribution for the prediction output. Thus, we utilize the attention map between the first output token and the input token under the noisy visual input to visualize the contribution of different input token. Besides, recent works [1,2,3] have shown that the MLLM tend to extract object information from the image at the middle layers. Thus, we plot the all layers and middle layers attention allocation for the first output token in the following Table. The results reveal that our method allocates more attention weights on the visual cue. Besides, in Figure 3 (on Page 5), Full Fine-Tuning shows a limited performance gap between noisy and normal visual signals, revealing the reliance on language prior rather than understanding the visual information. Therefore, both the attention allocation analysis and performance comparison demonstrate that our method effectively reduces reliance on language priors and enhances the overall performance of the model. Table: Attention allocation and performance comparison with relative methods. We conduct the evaluation on the Flickr30k with noisy visual input. We tuning on the Flickr30k+ScienceQA datasets based on LLaVA architecture. \|Metric \|Full-FT \| Rand Mask \| Mag Mask \| Grafting \| L2-Reg \| Ours \| \|----\|---\|---\|---\|---\|---\|---\| \| System (All) \| 0.6837 \| 0.6966 \| 0.6927 \| 0.6673 \| 0.6791 \| 0.6677 \| \| Prompt (All) \| 0.1229 \| 0.1297 \| 0.1280 \| 0.1241 \| 0.1181 \| 0.1225 \| \| Visual (All) \| 0.1933 \| 0.1737 \| 0.1793 \| 0.2084 \| 0.2029 \| 0.2098 \| \| System (Mid) \| 0.5865 \| 0.5874 \| 0.5859 \| 0.5726 \| 0.5826 \| 0.5574 \| \| Prompt (Mid) \| 0.1733 \| 0.1843 \| 0.1832 \|0.1664 \| 0.1623 \| 0.1576 \| \| Visual (Mid)\| 0.2402 \| 0.2282 \| 0.2309 \| 0.2609 \| 0.2552 \| 0.2850\| \| Accuracy\| 62.25 \|57.00 \| 60.07\| 60.26 \| 59.78 \| 67.89 \| Attributed to rebuttal format constraints, we will include attention map in our final version. Thanks for valuable suggestions! [1] EAZY: Eliminating Hallucinations in LVLMs by Zeroing out Hallucinatory Image Tokens, arXiv, 2025 [2] From Redundancy to Relevance: Information Flow in LVLMs Across Reasoning Tasks, NAACL, 2025 [3] Cross-modal Information Flow in Multimodal Large Language Models, CVPR, 2025 Q3: Table Design (Other Comments Or Suggestions) Thank you for your suggestion. We will reorganize the formulation of Table 2 to make it clear and easy to understand!	null	null	null	null	null	null
Benchmarking Abstract and Reasoning Abilities Through A Theoretical Perspective	Accept (poster)	Summary: This paper introduces a rigorously designed and theoretically grounded benchmark for a crucial yet underexplored area: the evaluation of abstract reasoning in Large Language Models (LLMs). The work establishes a clear mathematical framework that defines abstract reasoning as the ability to extract invariant patterns and consistently apply rules, independent of superficial representations. Central to the contribution are two novel, complementary metrics: the Abstract Reasoning Score (Γ) to quantify baseline accuracy and the Memory Dependence Score (Δ), a diagnostic metric innovatively designed to reveal the degree to which models rely on memorization versus genuine abstraction. Through systematic symbol remapping in carefully designed rule-based tasks, the benchmark compels models to demonstrate true pattern recognition. Extensive empirical evaluations across a diverse suite of LLMs, encompassing varying scales and prompting strategies, convincingly demonstrate the limitations of current models in abstract reasoning, particularly in symbolic manipulation and generalization. The paper's findings powerfully advocate for the use of this benchmark to guide future progress in AI systems capable of robust abstract thought, representing a significant step forward in LLM evaluation. Claims And Evidence: The paper’s core claim, asserting that contemporary LLMs exhibit significant deficits in abstract reasoning and are demonstrably prone to memorization—especially when confronted with novel symbolic representations—is convincingly and thoroughly substantiated. The experimental results are particularly compelling: the stark performance decline observed in Number Base Reasoning (NBR) tasks, even for the largest models, alongside the insightful diagnostic capabilities of the Memory Dependence Score (Δ), provide robust empirical support. For example, the consistent increase in Δ observed across models highlights a clear reliance on specific symbol tokens. The benchmark's innovative design, based on systematic symbol remapping within rule-based tasks, is demonstrably effective in isolating and measuring abstract reasoning, moving beyond superficial pattern matching or simple statistical correlations. The comprehensive evaluations, spanning a wide array of models, from 7B to 70B scale, and diverse prompting techniques, further reinforce the strength of the evidence presented. The paper effectively and persuasively argues against the sufficiency of relying solely on standard accuracy metrics for a nuanced assessment of genuine reasoning capacity in LLMs. Methods And Evaluation Criteria: The methodology employed in this work stands as a significant strength. The benchmark design itself, particularly the ingenious incorporation of systematic symbol remapping, represents a valuable methodological contribution to the field of LLM evaluation. The proposed metrics, Γ and Δ, offer a well-defined and crucially, complementary framework for rigorous evaluation. The Memory Dependence Score (Δ) is particularly noteworthy as it provides a diagnostic measure capable of differentiating between genuine abstract reasoning and mere memorization – a vital distinction frequently overlooked in many LLM evaluations. The deliberate use of rule-based tasks, thoughtfully categorized into Basic Computation (BC), Extended Calculation (EC), Number Base Reasoning (NBR), Math Application (MA), Symbolic Math Abstraction (SMA), and Symbolic Reasoning (SR), provides a structured and scalable approach to evaluating diverse facets of abstract reasoning. The experimental setup, meticulously encompassing a diverse range of models, prompting strategies (including both Direct Prompting and Chain-of-Thought), and computational resources, demonstrates appropriate rigor and careful consideration of experimental controls. Theoretical Claims: The paper's rigorously developed theoretical framework represents a substantial strength and a defining characteristic of this work. It provides precise formal definitions for key concepts including abstraction mapping, reasoning functions, and composite reasoning functions, offering a solid and mathematically sound conceptual grounding for the benchmark. The theorems presented (3.7, 3.8, 3.9) are not merely assertions but are theoretically validated, demonstrating the validity of Γ for assessing Rule-Given potential and, importantly, Δ as a robust measure for evaluating Rule-Inductive Abstraction capabilities. This level of theoretical rigor significantly distinguishes the paper from purely empirical evaluations and provides a robust foundation for both the empirical findings and the proposed evaluation methodology, enhancing the paper’s overall impact and credibility. Experimental Designs Or Analyses: The experimental design is not only well-executed but also remarkably comprehensive in its scope and depth. The authors have systematically and meticulously evaluated a diverse range of LLMs, thoughtfully spanning different model scales (from 7B to 70B), varying architectures, and distinct access methods (encompassing both open-source and API-based models). The deliberate inclusion of different prompting strategies, namely Direct Prompting and Chain-of-Thought (CoT), allows for a nuanced and granular analysis of model behavior and reasoning capabilities under varying conditions and input formats. The detailed and transparent reporting of results across all defined task categories, and particularly the fine-grained analysis of the Memory Dependence Score (Δ) at the level of both operand and operator symbols, provides exceptionally valuable and granular insights into the inherent limitations of current LLMs in abstract reasoning. The automated evaluation process, which incorporates gpt-40-mini for parsing responses and ensuring objective answer correctness assessment, further enhances the objectivity, reliability, and overall rigor of the study. Supplementary Material: Yes, I reviewed the supplementary material, specifically the Appendix located after the main text which includes detailed performance tables (Tables 2 and 3), additional figures (Figure 6), and expanded proofs of the theorems. Relation To Broader Scientific Literature: This paper is exceptionally well-contextualized within the broader and highly relevant scientific literature concerning abstract reasoning in both cognitive science and artificial intelligence. The related work section is particularly effective in its detailed discussion of existing benchmarks designed to assess AI reasoning, clearly articulating their limitations in the context of rigorously evaluating abstract reasoning within LLMs, and, crucially, in effectively differentiating between genuine abstraction and superficial memorization. The paper thoughtfully builds upon established theoretical perspectives from cognitive science and clearly and persuasively articulates the specific advancements and novel contributions offered by the proposed benchmark and evaluation metrics. The grounding of the work in established cognitive science literature, particularly regarding the distinction between Rule-Given and Rule-Inductive reasoning, is entirely appropriate and significantly strengthens the paper's scholarly context and theoretical underpinnings. Essential References Not Discussed: While the literature review is demonstrably thorough and highly relevant to contemporary LLM research, one could argue for the inclusion of more foundational key works from the pre-LLM era in the field of symbolic AI and rule-based reasoning. For instance, seminal works on production systems, knowledge representation, and early symbolic reasoning architectures, while not strictly essential for grasping the paper’s core contributions in the context of modern LLM evaluation, could provide a more complete and historically nuanced perspective on the evolution of AI reasoning research. However, the current literature review is highly focused and effectively addresses the most pertinent prior work directly relevant to the paper's contributions within the current landscape of LLM research. Other Strengths And Weaknesses: Strengths: - Novel and Theoretically Grounded Benchmark: The paper introduces a genuinely novel and exceptionally well-theoretically motivated benchmark that directly addresses a critical gap in the rigorous evaluation of abstract reasoning capabilities in LLMs. - Diagnostic Memory Dependence Score (Δ): The innovative introduction of the Memory Dependence Score (Δ) stands out as a significant strength, providing a uniquely valuable and diagnostic tool for disentangling genuine abstraction from mere memorization. - Comprehensive and Rigorous Empirical Evaluation: The empirical evaluation is remarkably comprehensive, covering a wide and diverse range of models and prompting strategies, providing exceptionally robust and generalizable results. - Clear Identification of Critical Research Gaps: The paper effectively and persuasively identifies fundamental limitations in current LLMs' abstract reasoning capabilities and clearly points towards valuable and impactful future research directions, advancing the field. - Well-Defined Task Categories and Dataset: The structured categorization of tasks (BC, EC, NBR, MA, SMA, SR) and the creation of a well-documented dataset contribute significantly to the reproducibility and usability of the benchmark. Weaknesses: - Potential for Further Task Complexity: While already comprehensive, the scope of the benchmark tasks could be further expanded in future iterations to incorporate even more complex and nuanced reasoning scenarios, particularly those involving multi-step inference and more intricate rule structures, to maintain its leading-edge utility as LLMs continue to advance. - Depth of Rule-Inductive Reasoning Exploration: While the benchmark addresses rule-inductive reasoning, further and deeper exploration of model performance specifically in the domain of rule induction from genuinely novel data – data designed to minimize any reliance on pre-existing patterns or biases learned during pre-training – could potentially provide even richer and more granular insights into this challenging aspect of abstract reasoning for LLMs. Other Comments Or Suggestions: - Future Benchmark Development and Maintenance: To maximize long-term impact, consider explicitly emphasizing the ongoing development, community engagement, and potential expansions of the benchmark in future publications and releases. Establishing a clear roadmap for incorporating increasingly complex reasoning tasks and adapting to advancements in LLM technology will be crucial for maintaining its continued relevance and utility to the research community. - Elaborate on Rule-Inductive Reasoning Challenges: Further elaboration, perhaps incorporating more concrete and illustrative examples, specifically detailing the nuanced challenges LLMs demonstrably face when engaging in rule-inductive reasoning tasks, would be highly beneficial for readers less familiar with the intricacies of this cognitive process. - Dataset Accessibility, Documentation, and Community Building: Ensuring open and easily accessible access to the meticulously curated dataset, coupled with providing exceptionally thorough and user-friendly documentation of its structure, generation process, and intended usage, is absolutely crucial for maximizing reproducibility, fostering broader community adoption, and ensuring the long-term impact of this valuable benchmark. Consider creating a dedicated project website or repository to facilitate access and community contributions. Questions For Authors: - Benchmark Evolution Roadmap: Could the authors outline their specific plans and roadmap for the continued evolution and expansion of the benchmark? Specifically, what types of increasingly complex reasoning tasks are envisioned for future iterations, and how will the benchmark be adapted to remain effective and challenging as LLMs continue to advance in capabilities? Understanding this long-term vision would further solidify the benchmark's value as a lasting contribution. - Deep Dive into Rule Induction Failure Modes: To enhance practical understanding for researchers seeking to improve LLM rule induction, could the authors provide more specific, illustrative examples and a more detailed analysis of the typical failure modes observed in LLMs when tackling rule induction tasks? Focusing on concrete examples, particularly from the SMA and SR task categories, would offer valuable insights into the precise nature of the limitations and guide targeted improvement efforts. - Dataset Access and Community Engagement Strategy: What is the authors' strategy for ensuring broad and sustainable access to the benchmark dataset and fostering community engagement around its use and potential expansion? Clearly articulating plans for dataset accessibility, comprehensive documentation, and community contribution mechanisms would maximize the impact and utility of this valuable resource for the wider AI research community. Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: ### 1. Task Complexity Expansion We agree that further expanding task complexity is essential. In future work, we will: - Introduce multi-step reasoning tasks that require chaining hypotheses, intermediate conclusions, and final integration. - Incorporate hierarchical rules with nested, conditional, and conflict resolution components. - Implement dynamic difficulty adjustment using parameters (e.g., reasoning steps, rule density, interference factors) to generate tasks that evolve with model proficiency. --- ### 2. Enhancing Rule-Inductive Reasoning We plan to deepen our investigation into rule induction by: - Increasing test difficulty—e.g., training with 8-bit binary data and testing with 16-bit numbers—to challenge the model’s generalization. - Recording and validating the reasoning steps, not just the final answer; automated tools will assess the plausibility of the reasoning chain. - Including detailed error case analyses, primarily in the Symbolic Math Abstraction (SMA) and Symbolic Reasoning (SR) categories, to illuminate common failure modes. --- ### 3. Benchmark Evolution and Maintenance We have a three-stage plan to keep the benchmark state‑of‑the‑art: - Short-term: Open-source the evaluation framework with detailed examples and error analysis. - Mid-term: Develop a dynamic task difficulty system through parameterization of reasoning steps and rule complexity. - Long-term: Build an adaptive challenge mechanism that auto-generates advanced tasks as models improve. We will also create robust feedback channels and community platforms to encourage continuous improvement. --- ### 4. Detailed Examples and Error Analysis for Rule Induction We will add: - Inclusion of Detailed Case Studies: We will include a dedicated section in our open-source GitHub repository that presents detailed case studies, particularly focusing on SMA and SR tasks. - Error Pattern Analysis: Along with concrete examples, we will provide analyses of common error patterns, explaining the underlying causes and typical failure modes in rule-induced tasks. We thank you for emphasizing the need for more specific examples and error analyses. We agree that these enhancements will provide immediate, valuable insights into model limitations and help guide future improvements. --- ### 5. Dataset Openness and Community Engagement To maximize community impact, we will: - Open-source the complete project on GitHub, including data generation code, symbol mapping, the full dataset, and all evaluation scripts. - Provide thorough documentation and user guides. --- We appreciate your detailed feedback. Your recommendations have pinpointed vital areas for improvement. In response, we have developed clear and actionable measures to refine task complexity, enhance rule induction analysis, and ensure the benchmark remains dynamic and accessible. These improvements will help us advance robust abstract reasoning evaluation in LLMs. Sincerely, The Author Team	Summary: This work build a benchmark of arithmetic computation tasks that targets at the abstract reasoning abilities of large language models, and finds out that the power existing large language models relies on the task domains. Claims And Evidence: See below Methods And Evaluation Criteria: The benchmark provides signal that demonstrates the limitation of the reasoning abilities of existing large language models, but not sufficient in supporting the abstract reasoning abilities. Theoretical Claims: The theorems are very brief and not placed in a well-described framework with all the concepts well explained. Experimental Designs Or Analyses: The benchmark consists of basic arithmetic tasks, where the areas where abstract reasoning are more broadly discussed (e.g. more complex logical reasoning, commonsense reasoning) is not discussed. Supplementary Material: N/A Relation To Broader Scientific Literature: The topic would raise interest to the broader scope of audience. Essential References Not Discussed: N/A Other Strengths And Weaknesses: There are several places worth mentioning in Section 3. - For Definition 3.1, the key difference between concrete instances and abstract features is not explained. In other words, what makes a string concrete instances instead of abstract features. What is the difference between the mapping C->A and A->C? - For Definition 3.2, the 'x' operation in 'AxR' is not explained. Meanwhile, the example is confusing as the conclusion applied here is 'This dog is likely to bark' without introducing the origin of the uncertainty here. Does this also apply to all the reasoning functions? - Theorem 3.7 is hard to understand, the foundation of the validity is not explained. - For theorem 3.9, the score range interpretation can be irrelevant to \gamma is w1=w2 according to the definition. Other Comments Or Suggestions: N/A Questions For Authors: N/A Code Of Conduct: Affirmed. Overall Recommendation: 1	Rebuttal 1: Rebuttal: ## 1. Concrete Instances vs. Abstract Features Our paper distinguishes concrete instances (C)—detailed input strings containing surface-level information—from abstract features (A), which capture only the essential properties required for reasoning. For example, a concrete description of a dog may include breed and color, whereas its abstract feature reduces these details to “dog.” Our mapping f: C->A is designed to force models to look beyond token memorization; an inverse mapping (from A->C) is unnecessary for our task. --- ## 2. Notation and Example in Definition 3.2 ### (a) Notation "$A \times R$" In Definition 3.2, the notation $A \times R$ indicates the set of all ordered pairs `(a, r)`, where each `a` belongs to the abstract feature set `A` (Section 3.1) and each `r` belongs to the rule set `R` (Section 3.2). The reasoning function `Re` is defined as Re: $A \times R$→Q, which means that for any input pair `(a, r)`, the function produces a corresponding conclusion `q` in `Q`. This formulation follows standard mathematical conventions (e.g., see [Cormen et al., 2009]) for combining elements from two previously defined sets. ### (b) The Example Involving Uncertainty The phrase “This dog is likely to bark” illustrates that typical human reasoning can involve uncertainty. However, in strictly symbolic or arithmetic tasks, the reasoning outcome is deterministic. The example is meant only to show how abstract features and rules combine, with the particular uncertainty reflecting context rather than a general property of all reasoning functions. --- ## 3. Theoretical Foundation of Theorem 3.7 Theorem 3.7 states that if a large language model achieves an abstract reasoning score Γ on our test set T that meets or exceeds a threshold γ, then for every task (c, r, q) in T the probability of correctly outputting q (via the abstraction mapping f and the reasoning function Re) is at least γ. In essence, a high Γ confirms the model’s robust ability to perform abstract reasoning across T. This theorem is grounded in our rigorous definitions of f and Re, which provide a clear correspondence among the inputs, the applied rules, and the correct outputs. Although the main text offers only a brief proof, more detailed proofs and explanations are available in the Appendix. --- ## 4. Score Range Interpretation (Theorem 3.9) For Theorem 3.9, we define the combined score as F(Γ, Δ) = w₁·Γ + w₂·(1 − Δ) and, according to Theorem 3.8, a higher threshold γ implies a higher Γ. The weights w1 and w2 are chosen based on task requirements. Even when w1 = w2, the two components remain distinct: Γ measures the reasoning accuracy, while (1 − Δ) reflects the model's robustness against dependence on specific tokens. Thus, the score range interpretation stays relevant as each component captures a distinct aspect of performance. --- ## Additional Responses ### 1. On Supporting Abstract Reasoning Abilities Our task design is not limited to simple arithmetic operations. Instead, we adopt a symbol remapping strategy that forces models to abandon reliance on surface-level patterns and requires them to extract and apply the underlying abstract rules. For example, in a date calculation task (e.g., `days between dates([2024, 07, 29], [2021, 10, 31]) = ?`), the model is required not only to perform numerical computations but also to understand the intrinsic logic between time and dates, which manifests a higher demand for abstract reasoning. Even large-scale models did not achieve above 60% accuracy on these tasks, which shows that our benchmark is sufficiently challenging for current models’ abstract reasoning abilities. ### 2. On the Conciseness of Theorems and Theoretical Framework We acknowledge that our current exposition of definitions and theorems is brief. The definitions of the abstraction mapping (f) and the reasoning function (Re) serve as the foundational building blocks of our mathematical model, and the corresponding theorems (e.g., Theorem 3.7 and Theorem 3.9) follow standard analytical approaches. Detailed proofs and clarifications are provided in the Appendix. ### 3. On the Benchmark’s Focus on Arithmetic Tasks While our benchmark primarily features arithmetic and related symbolic tasks, it is not confined to simple calculations. In addition to basic arithmetic, our benchmark incorporates extended calculation tasks, operations in various number bases, and date calculations. Most tasks are designed using symbol remapping techniques to destabilize simple memorization, thereby revealing models’ inability to generalize abstract rules beyond familiar forms. --- Because your review was relatively brief, we hope you will raise more questions or concerns to help us further improve the quality of our paper. Your additional feedback will be invaluable as we continue to refine our theoretical framework and experimental design. Thank you for your review. Sincerely, The Author Team	Summary: This paper presents a theoretically grounded benchmark to evaluate abstract reasoning in Large Language Models (LLMs). It defines abstract reasoning as extracting essential patterns and applying consistent rules to these patterns. Two metrics, Γ (Abstract Reasoning Score) and ∆ (Memory Dependence Score), are introduced to measure reasoning ability and distinguish abstraction from memorization. Evaluations across various LLMs reveal limitations in non-decimal arithmetic and symbolic reasoning, as well as significant memory dependence. The findings highlight the need for improved abstract reasoning capabilities in LLMs. Claims And Evidence: The claims are well-supported by the evidence presented. The authors provide a rigorous theoretical framework, introduce novel metrics, and conduct evaluations to demonstrate the limitations of current LLMs in abstract reasoning. The findings somewhat highlight key areas for future research. Methods And Evaluation Criteria: The methods and evaluation criteria in the paper are well-suited for assessing abstract reasoning in LLMs. The theoretical framework and metrics measure abstraction versus memorization. The benchmark, with systematic symbol remapping and diverse tasks, rigorously evaluates reasoning abilities. Overall, the proposed methods offer valuable insights for advancing abstract reasoning in LLMs. Theoretical Claims: The paper presents several theoretical claims supported by formal proofs, including Theorem 3.7 (validity of Γ for Rule-Given potential), Theorem 3.8 (validity of ∆ for Rule-Inductive abstraction), and Theorem 3.9 (score range interpretation). These proofs aim to establish the mathematical soundness of the proposed metrics. The proofs appear to be correctly formulated and logically consistent, providing a rigorous foundation for the metrics. The Law of Large Numbers is appropriately invoked in Theorem 3.7, and the invariance properties are well-argued in Theorem 3.8. The score interpretation in Theorem 3.9 is also logically structured. Experimental Designs Or Analyses: The experimental designs and analyses in the paper are sound and valid. The authors evaluated various LLMs using a comprehensive benchmark with both Direct Prompting and Chain-of-Thought strategies. The results reveal some limitations in abstract reasoning and memory dependence. The findings may be helpful for improvement in LLMs. Supplementary Material: No Supp. Relation To Broader Scientific Literature: The paper integrates cognitive science theories of abstraction and reasoning into a novel framework, extending prior work on generalization and reasoning evaluation. Its metrics and benchmark design address some limitations of existing methods, focusing on symbolic tasks and diverse reasoning facets. Empirical findings align with known challenges in LLMs' generalization and highlight the need for improved reasoning capabilities, advancing the discourse on AI abstract reasoning. Essential References Not Discussed: The paper provides a good review of related work in abstract reasoning and evaluation of large language models (LLMs). However, there are a few works that could further enrich the context and provide additional depth to the discussion: 1. The integration of neural networks with symbolic reasoning is an active area of research. The paper could reference Neuro-Symbolic AI: The Third Wave by [Artur d'Avila Garcez, 2020], which discusses the combination of neural and symbolic approaches to improve reasoning capabilities. 2. The paper's focus on benchmarking abstract reasoning could be complemented by citing classic cognitive science benchmarks. For example, the Raven's Progressive Matrices have long been used to evaluate human abstract reasoning. Including such benchmarks would provide a broader perspective on the challenges and methods used in evaluating reasoning. (Using the text-based RPM problem in [Taylor Webb, Nature Human Behaviour, 2023]) 3. This paper could cite "The Measure of Intelligence by [Chollet'19]", which provides a comprehensive framework for evaluating intelligence in AI systems. This work offers valuable context for the theoretical underpinnings of the paper's approach to abstract reasoning. Other Strengths And Weaknesses: +: 1. The benchmark is designed to cover a wide range of tasks. This allows for a good view of different facets of abstract reasoning. 2. This paper introduces both "Abstract Reasoning Score" and "Memory Dependence Score" to provide a nuanced evaluation of model performance 3. The paper provides a strong theoretical foundation for abstract reasoning by formalizing the processes of abstraction and reasoning. 4. The paper includes extensive evaluations across various LLMs (7B-70B scale, API-based models, and agent frameworks). -: 1. The paper acknowledges the influence of training data on model performance but does not provide a detailed analysis of how different training data configurations might affect abstract reasoning capabilities. 2. The paper does not provide a direct comparison of LLM performance to human-level reasoning. 3. The paper could provide more detailed implementation details for the benchmark tasks, such as specific examples of symbol remapping and task configurations. Other Comments Or Suggestions: N/A Questions For Authors: See Strengths And Weaknesses Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: ## 1. Relevant References Thank you for highlighting these references. Chollet (2019) is already cited (see Introduction). In the revised version, we have added: - *Garcez (2020), Neurosymbolic AI: The 3rd Wave* This work highlights the limits of connectionist methods and supports our discussion on transitioning from memorization to true abstraction. - Webb et al. (2023), Emergent Analogical Reasoning in Large Language Models This study provides empirical evidence on zero-shot analogical reasoning and contextualizes our findings on performance drops under symbol remapping. --- ## 2. Analysis of Training Data Configurations ### Experimental Design Overview To further evaluate the influence of different training data configurations on abstract reasoning, we tested two models—Llama-3.1-8B-Instruct (fine-tuned) and GEMINI-2.0-FLASH-THINKING-EXP-01-21—and also tested human participants. Training Data Configuration: - Unmapped () Configuration:* The training data is generated using a random seed to follow the same distribution as the `fixed_len_chat_bit_raw_dataset`. No symbol mapping is applied. - Fully Mapped (†) Configuration: The training data is generated using a random seed to follow the same distribution as the `fixed_len_chat_bit_dataset`. Symbol mapping is applied. Test Benchmarks: - We test on two mapped datasets: - `fixed_len_chat_bit_dataset` - `fixed_len_chat_str_dataset` Training Setup: Training was performed using a single NVIDIA A800 80GB GPU, with 2,000 training samples over 8 epochs, a batch size of 8, cosine learning rate scheduling (with 3% warm-up), and using bfloat16 mixed precision. ### Experimental Results and Analysis Below are our experimental results: \| Model \| Untrained \| Epoch 8 \| \|-\|-\|-\| \| fixed_len_chat_bit_dataset\|\|\| \| Llama-3.1-8B-Instruct\|0.13\|0.18\| \| Llama-3.1-8B-Instruct cot\|0.05 \|0.07\| \| Llama-3.1-8B-Instruct†\|0.13\|0.60\| \| Llama-3.1-8B-Instruct cot†\|0.05\|0.11\| \| gemini-2.0-flash-thinking-exp-01-21\|0.57\|\| \| gemini-2.0-flash-thinking-exp-01-21 cot\|0.46\|\| \| Human\|0.97\|\| \| fixed_len_chat_str_dataset\|\|\| \| Llama-3.1-8B-Instruct\|0.27\|0.27\| \| Llama-3.1-8B-Instruct cot\|0.03\|0.07\| \| Llama-3.1-8B-Instruct\| 0.27\|0.25\| \| Llama-3.1-8B-Instruct cot\| 0.03\|0.02\| \| gemini-2.0-flash-thinking-exp-01-21\| 0.19\|\| \|gemini-2.0-flash-thinking-exp-01-21 cot\|0.17\|\| \| Human\|0.47\|\| Key Observations and Conclusions: - Under the unmapped configuration, the performance improvement is marginal. - For the fully mapped configuration, the Llama-3.1-8B-Instruct model shows significant improvement on the bit dataset (from 0.13 untrained to 0.60 by Epoch 8). In contrast, the Llama-3.1-8B-Instruct cot† shows improvements from 0.05 to 0.11. Analysis of the Chain-of-Thought outputs indicates that the model still largely imitates the training examples rather than explicitly inferring and applying abstract rules.However, the improvement on the string dataset is limited, suggesting that the rules learned under remapping do not generalize well across different symbolic representations. - Human performance exceeds that of the models, further underscoring that current LLMs heavily rely on memorized associations rather than fully extracting and applying abstract rules. --- ## 3. Comparison with Human-Level Abstract Reasoning We conducted a supplementary experiment with four undergraduate computer science students who evaluated the same tasks: - Bit Dataset: Human participants achieved an accuracy of 0.97. - String Dataset: The overall human accuracy was 0.47. This direct comparison clearly demonstrates that even with extensive training, LLMs continue to underperform relative to human abstract reasoning capabilities, reinforcing the need for further improvements in model design and training. --- ## 4. Detailed Benchmark Implementation We agree with this recommendation and will revise Appendix A.7 in a future version to include detailed examples demonstrating the symbol remapping process and specific task configurations. Furthermore, we commit to releasing the complete source code, which will comprise: - A dynamic symbol mapping tool with customizable remapping rules. - Code templates for generating custom datasets across all six defined task categories. - An automated evaluation pipeline that computes both Abstract Reasoning Score (Γ) and Memory Dependence Score (∆), ensuring consistent answer matching. --- Once again, we thank the reviewers for their highly constructive feedback and for helping us identify areas for clarification and improvement. We believe that the revisions and additional experiments described above have significantly strengthened our work, and we appreciate your careful consideration of our manuscript. Sincerely, The Author Team --- Rebuttal Comment 1.1: Comment: I sincerely appreciate the authors' responses. Most of my concerns have been addressed. I also hope the authors can incorporate the related studies and the analysis into the paper and discuss them. Considering that this work has some innovation and provides appropriate analysis, I am happy to maintain my original score. --- Reply to Comment 1.1.1: Comment: Dear Reviewer, Thank you very much for your careful review and valuable comments. We are delighted that you appreciate the innovations and analytical insights presented in our work, as well as our rigorous theoretical framework, experimental methodology, and overall benchmark design. In our revised manuscript, we have incorporated additional references on neurosymbolic integration and classical cognitive benchmarks—as mentioned in our previous rebuttal—and introduced new citations such as Neural-Symbolic Learning and Reasoning: A Survey and Interpretation. We have also added a new experimental section, as outlined in our rebuttal, to compare unmapped versus fully mapped training data configurations, including human performance comparisons. This new section includes both a table and a line chart to clearly illustrate our findings. We have released the complete source code on GitHub. Once again, we sincerely thank you for your constructive feedback and for recognizing the value of our benchmark. Your positive remarks have been a great encouragement to our team, and we are confident that the revisions and additional experiments have further reinforced our theoretical contributions and research findings, as well as provided valuable insights for advancing abstract reasoning capabilities in LLMs. Sincerely, The Author Team	Summary: The goal of the paper is to evaluate the abstract reasoning capabilities of LLMs. The paper points out flaws with two existing benchmarking paradigms: The symbolic reasoning benchmarks like GSM8K risk memorization since the models could be (inadvertently) trained on these benchmarks. The visual abstract benchmarks like ARC are not well suited for LLMs due to their visual nature. The paper first lays out what it means by reasoning: abstraction, where the model identifies patterns from various inputs, followed by reasoning, where the model applies consistent rules to these abstractions to arrive at some outputs. The paper builds a symbolic benchmark and shows gaps in reasoning abilities of LLMs. Claims And Evidence: Yes. The main claim of the paper is the design of a formal setup for measuring abstract reasoning abilities of LLMs. The paper does a fairly good job of building this setup. The paper also does quite well in grounding this setup in existing literature in cognitive sciences. Methods And Evaluation Criteria: Yes. The benchmarks are math related but do provide coverage across a large number of mathematical operations (Appendix 6). Theoretical Claims: I went over the proofs in Appendix 2. While the proofs algebraically seem correct, I think they need some work in connecting the algebra to the application. The paper should specify what exactly the probability distributions in these proofs are, how we sample from them, and what the properties like validity in Eq. 9 are. Experimental Designs Or Analyses: I looked at the dataset design in Appendix A6. The datasets are relevant. However, the paper should add details and examples from these datasets. For instance, just by reading the name `var_len_chat_bitop_raw_dataset`, it is difficult for a reader to infer exactly what this dataset is and what the precise prompts used here were. Supplementary Material: Yes. I went over A2, A6 and some parts of A7. Relation To Broader Scientific Literature: The paper does a good job of framing itself w.r.t. the existing literature on LLM benchmarking. Essential References Not Discussed: Not that I could tell. Other Strengths And Weaknesses: ## Strengths 1. The fact that the paper formally defines the basic building blocks, e.g., concepts, abstraction and reasoning is quite useful and could lay a strong foundation for follow ups in this area. 2. The paper is quite well-written. Formalism (e.g., Definitions in Section 3.1) is followed up with concrete examples. ## Weaknesses 1. Definition 3.5: The paper should explicitly mention the probability distribution the test set T is samples from. Is it sampled from some task based distribution in the real world (e.g., SAT problems)? Could it contains duplicates that are the same problem but phrased differently? 2. Line 233: The paper should spend some more time on the validity of these alterations. Should we expect the same performance after altering 0/1 to A/B? One could argue both ways. For instance, humans can perform arithmetic in base 10 much more easily than in base, say 89. Does this different make humans poor abstract reasoners? 3. Theorem 3 proof in Appendix 2 needs some work. The proof verifies the properties for some extreme cases and shows some monotonicity. How does adherence to these properties make the metric in Eq. 9 a “valid” metric. What properties do we want in a valid metric anyway? Other Comments Or Suggestions: None Questions For Authors: 1. ARC doesn’t work for LLMs, but would it work with multi-modal LLMs? Why not test multi-modal LLMs given that they are becoming quite ubiquitous. Also, humans learn from both language and vision. So why not consider multimodal datasets? 2. Line 113: “However, these often lack direct application to LLM abstract reasoning evaluation”. How does ConceptARC lack application to LLM abstract reasoning? 3. The same concept could be described in many different words. For instance, “four-legged”, “having four legs”, etc. Does the paper enforce some kind of minimality constraints on the concepts, e.g., all equivalent expressions of a concept should be mapped to a single word pr phrase. 4. Line 146, second column: On “For instance, with the abstract concept, …”. The example mentions that “dog is likely to bark”. The word “likely” here implies some form of uncertainty in the behavior, e.g., the dog might bark in 80% of cases upon seeing another dog. How does the framework plan to quantify this uncertainty. Should this quantification be a part of the rules? 5. Theorem 3.7: What is the probability in Eq. 7 computed over? 6. Line 913: The strings here like “JJJQQQQQ” seem quite challenging for a LLM tokenizer, and will lead to a large number of tokens as compared to natural language. Given the tokenization issues, should we expect LLMs to be able to solve the resulting problems? Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: ### 1. Test Set Sampling and Duplicates 1. Test Set Distribution: Uniform distribution. 2. Real-World Distribution and Correlation: No, it is not sampled from a real-world task-based distribution such as SAT problems. However, our benchmark shows strong correlation with other benchmarks. For example, if we only consider the models tested in our paper (excluding agents): gemini-2.0-flash-thinking-exp-01-21* achieved rank 1 with the highest Γ score in our benchmark, and on LiveBench its average reasoning score reached 78.17, outperforming all other models. qwq-32B-preview* achieved scores comparable to 72B and API models in our benchmark, with a LiveBench average reasoning score of 57.71. Qwen2.5-72B-Instruct consistently outperforms competing models both in our benchmark and on the Korean SAT LLM Leaderboard baseline. 3. Elimination of Duplicates: No, duplicate phrasings have been strictly eliminated. --- ### 2. Symbol Remapping and Its Rationale 1. Performance Consistency After Remapping: Yes. A truly abstract model should maintain comparable performance post-remapping. For instance, GEMINI-2.0-FLASH-THINKING-EXP-01-21 drops by 0.40 on the `fixed_len_chat_bit_dataset` after remapping, indicating sensitivity to symbolic changes. In contrast, four computer science undergraduates scored nearly identically (1.00 and 0.97). 2. Humans and Non-Decimal Arithmetic: No. Although non-decimal bases may pose challenges, humans can perform arithmetic in various numeral systems once abstract rules are applied. In our test of 16 samples from the `add_base3_raw_dataset`, undergraduates achieved 0.87 accuracy, while GEMINI-2.0-FLASH-THINKING-EXP reached 0.75. --- ### 3. Validity of the Metric F(Γ, ∆) 1. Properties of a Valid Metric: A valid metric should be monotonic (increasing with higher Γ and decreasing with higher ∆, sensitive (proportional to changes), continuous, and normalized within [0, 1]. 2. Our Metric: Defined as F(Γ, ∆) = w1Γ + w2(1 − ∆) it satisfies these properties. 3. Justification: Our metric inherits the desirable mathematical properties documented in the literature (e.g., Sokolova and Lapalme). --- ### 4. Multimodal Considerations 1. ARC work for multi-modal LLMs Yes. While ARC is designed for 2D visual inputs and can potentially benefit multimodal LLMs. For example, Align-DS-V—an experimental vision-language model derived from DeepSeek-R1-Distill-Llama-8B—achieved a score of 40.5 on the ARC-Challenge (5-shot), compared to 21.4 from DeepSeek-R1-Distill-Llama-8B. 2. Consider multimodal datasets Our work complements ARC by isolating the text modality to evaluate abstract reasoning in LLMs. While multimodal LLMs are emerging and humans naturally integrate visual and linguistic cues, most LLMs excel at language processing. Focusing exclusively on text allows us to establish a clear baseline for abstract reasoning without the added complexity of visual data. --- ### 5. Applicability of ConceptARC to LLMs LLMs are optimized for one-dimensional text, not two-dimensional spatial data. Our experiments show that even when Arabic numerals and simple graphics are array-formatted, LLMs struggle with 2D spatial properties, making ConceptARC less suitable for assessing textual reasoning. --- ### 6. Minimality in Concept Representations Our abstraction mapping process as an information compressor that inherently normalizes equivalent expressions without requiring an explicit minimality algorithm. --- ### 7. Addressing Uncertainty in Reasoning The phrase “likely to bark” in our cognitive example was intended solely as an illustrative simplification. Our framework currently outputs deterministic results post-abstraction; future work will integrate probabilistic models to handle inherent uncertainties. --- ### 8. Clarification on Eq. 7's Probability In Theorem 3.7, the probability is computed over the test set T, where each task is independently sampled from a uniform distribution over the task space. --- ### 9. Tokenization and Long Symbolic Strings Sequences like “JJJQQQQQ” may split into multiple tokens by the tokenizer; however, modern LLMs handle these effectively. In our benchmark, the majority of token counts for such symbolic strings are below 5k—well within the 8K-token (or larger) context window of current models. --- ### 10. Clarification of Dataset Names - var_len: Variable operand lengths. - chat: Conversational style prompts. - bitop: Bit manipulation operations. - raw: Original symbols without remapping. Detailed descriptions and examples will be added to Appendix A.6. --- We appreciate the reviewer’s feedback and hope that these clarifications, along with our proposed modifications, demonstrate the robustness of our theoretical framework and benchmarking strategy. Thank you very much for your consideration. Sincerely, The Author Team	null	null	null	null	null	null
Runtime Analysis of Evolutionary NAS for Multiclass Classification	Accept (poster)	Summary: This study presents a theoretical analysis of the runtime of the ENAS algorithm in solving multiclass classification problems. The authors first introduce a benchmark problem and then propose a two-level search space. Based on this design, the authors analyze the upper and lower bounds on the expected runtime and provide empirical results that validate their theoretical findings. The findings indicate that the simple one-bit mutation can achieve similar performance to the commonly used bit-wise mutation of ENAS. Claims And Evidence: All the claims of this study are well supported. Methods And Evaluation Criteria: Both the introduced benchmark problem and the two-level search space can well support the ENAS problem at hand. Theoretical Claims: I have checked the correctness of the proofs for theoretical claims in this work, including the fitness function, the upper bound, and the lower bound, which are well designed and proofed. Experimental Designs Or Analyses: The experiments can justify the claims of this study, but more datasets should be better. Supplementary Material: I reviewed the supplementary materials, including the details of parameter setting, more examples for Mcc tasks, and additional proofs, which can further support the claims of this study. Relation To Broader Scientific Literature: The paper contributes to the theoretical understanding of ENAS by analyzing runtime bounds, which can be regarded as a continual work of Lv et al. This work extended the study from binary classification tasks to multclass classification tasks. Lv Z, Bian C, Qian C, et al. Runtime Analysis of Population-based Evolutionary Neural Architecture Search for a Binary Classification Problem[C]//Proceedings of the Genetic and Evolutionary Computation Conference. 2024: 358-366. Essential References Not Discussed: This study focuses on the runtime analysis of the ENAS algorithm, and the introduction and related works have discussed the more relevant aspects of the topic. Other Strengths And Weaknesses: Strengths 1. The paper provides the important theoretical findings of ENAS. The findings are crucial, especially for the multiclass optimization task for ENAS. 2. The insights of the mutation operations can guide the design of the ENAS algorithms and also can simplify the existing ENAS algorithms. 3. The upper and lower bounds for the runtime of ENAS, which can effectively guide the mutation selection of the ENAS algorithm. 4. The definition of the MCC benchmark problem and the fitness function are good to support the following theoretical proof. 5. The two-level search space aligns well with the application of ENAS algorithms in practice, making the theoretical findings applicable to real-world ENAS settings. 6. All the theorems of the paper, such as runtime bounds and fitness function, are proved correctly. 7. The empirical analysis is designed to verify the effectiveness of the theoretical findings. 8. The paper is well-organized and the presentation is easy to understand. Weaknesses 1. This study analyzes the (1+1)-ENAS algorithm and finds that simple one-bit mutation can achieve similar performance as commonly used bit-wise mutation. However, are the ENAS algorithms widely used in practice are (1+1)-ENAS? In other words, can this finding well support the widely used ENAS algorithms in practice? 2. The differences and the challenges of the multiclass classification and binary classification for ENAS algorithms should be well-defined. Based on this definition, the contribution of this study can be more meaningful. 3. Although the authors justify that one-bit mutation can be a powerful mutation operation for ENAS, they do not provide strong practical guidelines on how practitioners should choose between one-bit and bit-wise mutations in different settings. Do the authors believe that all the bit-wise mutations in ENAS should be replaced with one-bit mutation? Other Comments Or Suggestions: Here are some minor weaknesses of this study: 1. This study focuses only on the mutation operations of the ENAS algorithm, ignoring other important evolutionary operators, e.g., crossover and selection operations, which are commonly used in practical ENAS implementations. The authors should discuss them in the limitation section. 2. The experiments of this study are limited in scope. Including more datasets or SOTA ENAS algorithm could strengthen the findings. Questions For Authors: Please check Other Strengths And Weaknesses and Other Comments Or Suggestion. Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: Many thanks for your valuable comments of our work. Below, we would like to take this opportunity to respond to your concerns. >1. Are the ENAS algorithms widely used in practice are (1+1)-ENAS? In other words, can this finding well support the widely used ENAS algorithms in practice? (1) In practice, most ENAS algorithms are population-based, while (1+1)-ENAS serves as a theoretical foundation for runtime analysis and designing population-based algorithms. (2) Yes. Our finding shows that simple one-bit mutation achieves comparable runtime performance to bit-wise mutation on the MCC problem, validating that the one-bit mutation is not inherently inefficient. This aligns with practical ENAS methods like AmoebaNet (Real et al., 2019) and AE-CNN (Sun et al., 2019b), which utilize single-step mutation (functionally analogous to one-bit mutation) as their core search operator. Thanks to your comment, we will revise to discuss the connection to practical implementation. >2.The differences and the challenges of the multiclass classification and binary classification for ENAS algorithms should be well-defined. Differences: 1) decision regions: multiclass classification divides input space into $M$ decision regions (vs. two in binary classification), increasing neural architectural demands; 2) classification accuracy: multiclass classification aggregates per-class accuracy across all $M$ regions, amplifying the complexity of the fitness evaluation; 3) search space: the neural architecture for solving multiclass classification is a combination of multiple binary classifiers or a more complex architecture (vs. binary classification’s binary classifier), exponentially expanding the search space. Challenges: 1) problem definition: accurately modeling inter-class dependencies and region-specific sample distributions; 2) fitness function: mathematically formulating the fitness (i.e., classification accuracy) of neural architecture from geometric properties; 3) search space partition: partitioning the search space by analyzing the interactions between architectural components (e.g., blocks, cells). Thanks to your suggestion, we will incorporate these clarifications into the revised manuscript. >3. Do the authors believe that all the bit-wise mutations in ENAS should be replaced with one-bit mutation? No. Consistent with the No Free Lunch Theorem, neither operator is universally optimal: bit-wise mutation excels in exploration-heavy scenarios (e.g., topology-based search spaces), while one-bit mutation prioritizes simplicity and serves as a parameter-free alternative (e.g., no need to tune bit-flip probability). As an initial attempt at ENAS runtime analysis, we prioritize foundational cases, while future work will expand comparisons to diverse tasks. We appreciate your support as we advance this work. >4.This study focuses only on mutation, ignoring other important evolutionary operators, which should be noted as a limitation. Our study focuses on mutation as it is a core component of ENAS and many ENAS are limited to mutation only (Real et al., 2017; Real et al., 2019; So et al., 2021). This also aligns with the theory community of evolutionary computation, where initial analyses often start with mutation (Auger & Doerr, 2011; Neumann & Witt, 2010; Zhou et al., 2019; Doerr & Neumann, 2020), thereby providing a stepping stone for further exploration. While advanced operators like crossover and stochastic selection are vital in practice, their runtime analysis remains challenging due to irregular combinatorial interactions and limited theoretical frameworks. We will explicitly discuss this. >5.The experiments of this study are limited in scope. Including more datasets or SOTA ENAS algorithm could strengthen the findings. Our search space is simplified for the MCC problem, which makes it difficult to directly apply the studied ENAS framework to other domains (e.g., image classification) without architectural re-engineering. Future work will expand this framework to diverse tasks. In addition, to further strengthen our finding, we have extended experiments to three SOTA ENAS algorithms: ($\lambda$+$\lambda$)-ENAS with mutation only ($\lambda\in\{2,4,10\}$), which is adopted in methods like LEIC (Real et al., 2017) and AmoebaNet (Real et al., 2019); one-point crossover-based ENAS, which is adopted in CNN-GA (Sun et al., 2019a) and ENAS-kT (Yang et al., 2023); and uniform crossover-based ENAS, which is adopted in Genetic CNN (Xie & Yuille, 2017). All additional experiments are under identical problem settings (Section 5). The results (see anonymous links: [fixed $r=10$, varing $M$](https://anonymous.4open.science/r/5666/rebuttalFigs/a-varing-M.pdf) and [Fixed $M = 20$, varying $r$](https://anonymous.4open.science/r/5666/rebuttalFigs/b-varing-r.pdf)) show that one-bit mutation still performs better. Thanks to your suggestion, we will integrate them into the manuscript.	Summary: This paper introduces a novel runtime analysis framework for evolutionary neural architecture search (ENAS). Compared with the previous studies, which focus on the binary classification problem, the runtime analysis focuses on the multiclass classification problem in this work. Specifically, this study first introduces a multiclass classification benchmark problem called MCC. Then, a more practical search space with two interrelated levels is designed. Based on this, the expected runtime bounds of (1+1)-ENAS are analyzed. ## update after rebuttal Claims And Evidence: All the claims made in this work are well supported by theoretical proofs or experimental results, none of which is problematic. Methods And Evaluation Criteria: The proposed method and evaluation criteria indeed make sense for the problem in this work. The multiclass classification benchmark problem successfully extends the runtime analysis from binary classification to multiclass classification. Theoretical Claims: I have checked the correctness of all proofs and theoretical claims, and believe that they are all correct. Experimental Designs Or Analyses: I have checked the experimental results regarding the different mutation settings in (1+1)-ENAS algorithm. This set of results can well support the claims made in Theorems 4.1 to 4.4. Supplementary Material: I have reviewed all parts in the supplementary material. Relation To Broader Scientific Literature: In terms of the runtime analysis for ENAS, previous studies mainly focus on the binary classification problem, and their representation of the search space limits the application to multiclass classification problem. Different from these studies, this work achieves the analysis for multiclass problem via the proposed multiclass classification benchmark problem and the search space with two inter-related levels. Essential References Not Discussed: None. Other Strengths And Weaknesses: Strengths: + This paper mainly focuses on the runtime analysis of ENAS, which is a very important topic in NAS research. The authors provided several novel viewpoints in this field. + This paper pushes the runtime analysis of ENAS toward the new area regarding the multiclass classification problem. Compared with the previous studies focusing on the binary classification problem, this work achieves significant improvements upon them. + A multiclass classification benchmark problem and a novel fitness function are introduced. The fitness function not only contributes to the theoretical analysis of ENAS, but also can be transferred to other fields in evolutionary computation. + The authors present a practical search space specifically for the multiclass classification problem, pushing the search space design towards a new direction in the field of ENAS. + All the claims in this work are well supported by sufficient theoretical proofs or experimental results. + The expected runtime bounds obtained contribute to the design of ENAS algorithms, especially for the design of the mutation operator. + The paper is very well presented, and the illustrations and visualizations are nicely done. Weaknesses: + The authors state that the expected runtime to find the target solution is $O(rMln(rM))$. However, it is suggested to discuss how this conclusion contributes to ENAS. + I wonder if the theoretical findings are valid when there are infinite classes. Please provide more details regarding this point. + Is there a sequence for the two types of mutations in the two-level mutation process? How does this sequence affect the theoretical analysis in this work? + In lines 223-229 of page 5, the authors state that the definition of classification accuracy is suitable for balanced datasets. I wonder if the distribution of data is imbalanced (e.g., long-tailed data), what impact will it have on the theoretical findings? Other Comments Or Suggestions: None. Questions For Authors: Please refer to the Other Strengths And Weaknesses section. Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: Many thanks for your recognition and comments of our work. Below, we would like to take this opportunity to address your concerns. >1. The authors state that the expected runtime to find the target solution is $O(rM\ln(rM))$. However, it is suggested to discuss how this conclusion contributes to ENAS. This result highlights the relationship between the expected runtime and key problem parameters, i.e., $M$ (the number of classes) and $r$ (which affects the decision regions for each class). The result provides two insights for ENAS: 1) due to the polynomial runtime dependency on classification problem parameters $M$ and $r$, the ENAS generations (iterations) should scale with classification difficulty; 2) since our runtime results (Theorems 4.1 to 4.4) show that one-bit and bit-wise mutation achieve comparable runtime in (1+1)-ENAS solving MCC problem, the one-bit mutation as a simpler and parameter-free operator (e.g., no need to tune bit-flip probability) can be prioritized in ENAS design. >2. I wonder if the theoretical findings are valid when there are infinite classes. Please provide more details regarding this point. Yes. As shown in Theorems 4.1 to 4.4, the expected runtime $\mathbb{E}[T]$ holds with any number $M$ of classes. This finding shows that the architecture search difficulty increases with $M$ due to the finer partitioning of the decision spaces. Moreover, the theoretical framework does not impose any upper limit on the number $M$ of classes, meaning the findings apply regardless of whether $M$ is finite or tends to infinity. However, in extreme cases where $M$ becomes infinitely large, practical considerations such as finite computational resources should be taken into account. >3. Is there a sequence for the two types of mutations in the two-level mutation process? How does this sequence affect the theoretical analysis in this work? Yes, there is a sequence in the two-level mutation process. By first selecting the cell to mutate (outer-level mutation) and then applying the mutation (inner-level mutation) to the selected cell, we can track the expected changes between the parent and offspring, and also can quantify the progress made at each step. However, reversing the sequence would make the algorithm infeasible, as the index of the cell to be mutated would be unknown, making it unclear where the inner-level mutation should be applied. Specifically, given a solution $\pmb{x}$, which is encoded by $M-1$ triplets of integers, i.e., $\pmb{x} =${$(n_A^1, n_B^1, n_C^1),\ldots,(n_A^{M-1}, n_B^{M-1}, n_C^{M-1})$}, the algorithm must first select the cell index $m\in${$1,\ldots,M-1$}, and then apply the inner-level mutation to modify the selected cell $(n_A^m,n_B^m,n_C^m)$. >4. In lines 223-229 of page 5, the authors state that the definition of classification accuracy is suitable for balanced datasets. I wonder if the distribution of data is imbalanced (e.g., long-tailed data), what impact will it have on the theoretical findings? If the data distribution is imbalanced, the formulation of the fitness function (i.e., Eq. (2)) will need to consider the distribution of each class of data, which will introduce new conditions for judging whether each cell reaches the optimal state or not in the ENAS search process, e.g., the conditions $I_{\pmb{x}}^m=2r$ and $J_{\pmb{x}}^m=2r$ for $o^m$ to be 1 (as stated in line 353) will be affected by the distribution of data. Furthermore, a dependency would exist between the number of optimal cells $\|\pmb{o}\|_1$ in Eq. (3) and the distribution of data. Consequently, this affects the computation of expected progress (e.g., Eq. (4)) and the distribution of the optimal cells in the initial solution (e.g., Eq. (6)), ultimately making the theoretical findings (i.e., expected runtime shown in Theorems 4.1– 4.4) dependent on the data distribution.	Summary: This paper investigates the runtime analysis of Evolutionary Neural Architecture Search for multiclass classification problems. The core of the research is the proposal of a multiclass classification benchmark problem and the design of a two-level search space based on this problem. The authors then analyze the expected runtime bounds of the (1+1) ENAS algorithm with one-bit and bit-wise mutations for solving MCC. The results show that both mutation strategies achieve similar performance in terms of expected runtime, which is further verified by empirical studies. This work represents the first theoretical analysis of ENAS for multiclass classification, providing new insights into understanding ENAS. ## update after rebuttal After the rebuttal, I feel my concerns have been well-discussed by the authors, although some of weaknesses are not very easy to modify during a such short period. Therefore, I choose to keep my positive scores, and I believe that all the reviewers are lean towards to accept this submission. Claims And Evidence: The claims made in the submission are generally supported by clear and convincing evidence, particularly in the context of the theoretical analysis and the proposed benchmark problem. Methods And Evaluation Criteria: The proposed methods and evaluation criteria in this paper are well-aligned with the problem of runtime analysis for evolutionary neural architecture search in multiclass classification. Theoretical Claims: The proofs presented in the paper are logically structured and follow established techniques in runtime analysis. Further validation through sensitivity analysis, empirical studies, and exploration of alternative proof techniques would strengthen the theoretical claims and enhance their practical applicability. Experimental Designs Or Analyses: Yes, I reviewed the soundness and validity of the experimental design and analysis presented in the paper, focusing on the empirical evaluation of the (1+1)-ENAS algorithm with different mutation strategies on the proposed MCC problem. Supplementary Material: Yes, I reviewed the Appendix. In details, the supplementary material details the neural architecture's parameters and decision regions, provides examples of solving the MCC problem, and includes rigorous proofs for the theoretical claims. Relation To Broader Scientific Literature: The key contributions of this paper are related to several important areas of the broader scientific literature, particularly in the fields of Evolutionary Computation, Neural Architecture Search, and Runtime Analysis of Evolutionary Algorithms. Essential References Not Discussed: There is no essential references missing. Other Strengths And Weaknesses: Strengths, - This paper is the first to conduct a runtime analysis of ENAS for multiclass classification problems. By proposing the MCC problem and a mathematically formulated fitness function, it provides a benchmark for theoretical research on ENAS. - The authors use rigorous mathematical tools, such as multiplicative drift analysis and fitness-level techniques, to derive upper and lower bounds on the expected runtime. - The findings suggest that simpler mutation strategies like one-bit mutation can be effective in ENAS, which may simplify the design of future ENAS algorithms. Weaknesses, - How does the proposed runtime analysis scale with increasing problem complexity (e.g., higher-dimensional input spaces or larger numbers of classes)? Are there any limitations in extending the analysis to more complex scenarios? - The fitness function assumes optimal parameter tuning for each architecture. How sensitive are the theoretical results to deviations from this assumption? Could the analysis be extended to account for suboptimal parameter tuning? - The paper shows that one-bit and bit-wise mutations achieve similar performance. How do these findings influence the design of future ENAS algorithms? - Can the theoretical framework be extended to analyze more complex ENAS algorithms? If so, what are the key challenges? Other Comments Or Suggestions: Overall, the manuscript is technically sound and well-presented, with some theoretical insights. Please refer to other strengths and weaknesses for drawbacks. Questions For Authors: Please refer to my weaknesses listed above. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Your detailed comments are much appreciated, and we will revise the manuscript accordingly. Below, we address your questions. >1.How does the proposed runtime analysis scale with increasing problem complexity (e.g., higher-dimensional input spaces or larger numbers of classes)? Are there any limitations in extending the analysis to more complex scenarios? (1) We first explain the impact of increasing problem complexity by using larger numbers of classes (i.e., increasing $M$ in the analysis). In this case, the proposed runtime analysis scale will not be changed. This can be found from our theoretical results (Theorems 4.1 to 4.4) that reveal the relationship between runtime $T$ and classes number $M$, i.e., the expected runtime $\mathbb{E}[T]$ of (1+1)-ENAS grows polynomially with $M$. Next, we explain the impact of increasing problem complexity by using higher-dimensional input spaces. In this case, runtime analysis becomes more challenging due to that the fitness function is difficult to express in a mathematically tractable form. This difficulty arises from the fact that the mathematically formulated fitness function is derived by the hypervolume of the decision regions, while the higher-dimensional input spaces result in that the hypervolume of the higher-dimensional decision regions cannot be calculated from the geometric properties of the decision regions (i.e., higher-dimensional spaces make it difficult to provide a geometric interpretation of the neural network’s decision regions). (2) Yes, the main limitation is that the complex decision regions restrict the mathematical formulation of the fitness function. This, in turn, makes it difficult to directly assess the progress of the ENAS search process, which is a crucial step in the runtime analysis. We will revise to add more discussion. Thank you. >2.The fitness function assumes optimal parameter tuning for each architecture. How sensitive are the theoretical results to deviations from this assumption? Could the analysis be extended to account for suboptimal parameter tuning? (1) The theoretical results are robust to small deviations from optimal parameter tuning. Specifically, deviations from optimal parameter tuning will introduce noise into the fitness evaluation process, which could potentially alter the fitness landscape and disrupt the ranking of architectures' fitness values. However, if the fitness values maintain a high correlation with the true performance of the architectures, the impact on the ranking of candidate architectures is likely to be minimal, and thus unlikely to affect the search results in each round. In such cases, the theoretical results may not be notably affected. Overall, if the deviation is very small, the impact on the theoretical results is not significant. (2) To account for suboptimal tuning, the analysis could be extended via (1+$\epsilon$)-approximation or noisy optimization frameworks. We will discuss these directions in the revised manuscript and pursue them in future work. We appreciate your support as we advance this work. >3.The paper shows that one-bit and bit-wise mutations achieve similar performance. How do these findings influence the design of future ENAS algorithms? The design complexity of one-bit and bit-wise mutation–based ENAS algorithms differs: one-bit mutation is a simple and parameter-free operator that applies a single random change per step, while bit-wise mutation requires to tune the bit-flip probability (e.g., setting $p=1/n$ versus $p=0.5$ yields vastly different exploration-exploitation balances, where $n$ is the problem size). Our findings show that the simpler one-bit mutation can be prioritized in ENAS algorithm design. This is particularly effective for block/cell-based search spaces, where one-bit mutation operator could achieve significant changes in neural architecture. Furthermore, this aligns with practical ENAS methods like AE-CNN (Sun et al., 2019b), which utilize single-step mutation (functionally analogous to one-bit mutation) as their core search operator. We thank the reviewer for this comment and will revise to strengthen the discussion on mutation operator selection. >4.Can the theoretical framework be extended to analyze more complex ENAS algorithms? If so, what are the key challenges? Yes, the theoretical framework—including search space partitioning, optimization phase division, distance function definition, and individual transition probability analysis—can be extended to more complex ENAS algorithms. However, this extension faces key challenges: 1) how to calculate the probability of ENAS algorithm making progress in one step; 2) how to derive a tighter expectation of one-step progress (which is related with the progress derived by evolution operators); 3) how to select an appropriate runtime analysis tool based on the relationship between the distance at each generation (iteration) and the expected progress.	Summary: The paper delves into the runtime analysis of ENAS for multiclass classification，It introduces a new benchmark problem, MCC, designed to simulate multiclass classification tasks, and formulates a fitness function to evaluate neural architectures' performance on this problem. The authors also design a two-level search space, support detailed theoretical analysis. Empirical experiments further validate these theoretical results, highlighting the potential for simpler mutation strategies in ENAS design. ## Update after rebuttal The authors' rebuttal looks great to me. My final recommendation is a clear accept. Claims And Evidence: In general, the claims made in the submission are backed by a combination of rigorous mathematical proofs and experimental results. Methods And Evaluation Criteria: The proposed methods and criteria are appropriate for the theoretical analysis. Theoretical Claims: I have checked the correctness of the proofs for the theoretical claims presented in the submission. As follows, Upper/Lower Bound on Expected Runtime for (1+1)-ENAS with One-bit/Bit-wise Mutation. Experimental Designs Or Analyses: Yes, I reviewed the experimental designs and analyses presented in the submission. The experiments focus on evaluating the performance of the (1+1)-ENAS algorithm with different mutation strategies (one-bit and bit-wise mutations) on the proposed MCC benchmark problem. Supplementary Material: Yes, I reviewed the supplementary material provided with the submission -- They are useful. Relation To Broader Scientific Literature: The paper makes several contributions that are well-aligned with the broader scientific literature. Essential References Not Discussed: Yes, there are several related works that provide essential context for the key contributions of the paper. Other Strengths And Weaknesses: Pros as follows, 1.The authors propose a multiclass classification benchmark problem (MCC) with a mathematically formulated fitness function. This is a significant contribution as it provides a standardized problem for analyzing ENAS algorithms. 2.The two-level search space (cells and blocks) is designed to be consistent with common ENAS settings, this design supports the theoretical analysis. 3.The theoretical results are supported by empirical studies, demonstrating the practical relevance of the findings. Cons as follows, 1.The proposed MCC benchmark problem, while theoretically sound, is highly simplified and may not reflect the complexity of real-world multiclass classification tasks. 2.The runtime analysis focuses on the number of generations required to find an optimal solution but does not consider the computational resources (e.g., memory, processing power) needed to evaluate each candidate architecture. 3.The authors do not address how the proposed theoretical bounds scale with increasing problem complexity, which is crucial for understanding their practical feasibility. 4.The analysis assumes a relatively uniform and idealized search space, methods like dropout, batch normalization, or architectural constraints are not accounted for. These techniques can significantly influence the optimization landscape and runtime behavior of ENAS algorithms. Whether these techniques affect the optimization and runtime behavior of ENAS algorithms. Other Comments Or Suggestions: The manuscript makes nice contributions to the theoretical understanding of ENAS for multiclass classification. The work of theoretical analysis is difficult and admire the author's efforts in this direction. More comments refer to weaknesses. Questions For Authors: Refer to weaknesses. Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: Many thanks for your recognition and encouraging comments of our work. Below, we take the opportunity to respond to your concerns. >1.The proposed MCC benchmark problem, while theoretically sound, is highly simplified and may not reflect the complexity of real-world multiclass classification tasks. The MCC benchmark is designed to capture essential properties of real-world multiclass classification tasks, including both linearly and nonlinearly divisible decision regions (e.g., half-space region, unbounded/bounded polyhedra region). Many classification problems can be described as a disjoint union of these decision regions. While real-world tasks may involve additional complexities (e.g., noisy or more complex decision boundaries) that extend beyond the current MCC scope, the MCC benchmark provides a tractable yet representative framework for analyzing ENAS behaviors. This simplified abstraction aligns with conventions in the theory community of evolutionary computation, where unimodal benchmark problems like OneMax and LeadingOnes similarly simplify real-world problems to analyze algorithmic behaviors (Droste et al., 2002; Doerr et al., 2008; Doerr & Goldberg, 2013; Witt, 2013). We will explicitly discuss the limitations of the MCC problem in the manuscript. >2.The runtime analysis focuses on the number of generations required to find an optimal solution but does not consider the computational resources (e.g., memory, processing power) needed to evaluate each candidate architecture. Our runtime analysis focuses on the expected number of fitness evaluations (i.e., the expected number of generations in this work) required to find an optimal solution, which concerns the ENAS search strategy and aligns with the theory community of evolutionary computation (Auger & Doerr, 2011; Neumann & Witt, 2010; Zhou et al., 2019; Doerr & Neumann, 2020). The computational cost (such as memory and processing power) per fitness evaluation is determined by the architecture training and validation process, which remains independent of the ENAS search strategy under analysis and consequently does not impact our runtime analysis. We will clarify this distinction in the manuscript. >3.The authors do not address how the proposed theoretical bounds scale with increasing problem complexity, which is crucial for understanding their practical feasibility. The problem complexity is determined by two parameters: $M$ (the number of classes) and $r$ (which affects the decision regions for each class). As proven in Theorems 4.1 to 4.4, the expected runtime $\mathbb{E}[T]$ of (1+1)-ENAS grows polynomially with $M$ and $r$. We will revise the manuscript to explicitly discuss this. >4.The analysis assumes a relatively uniform and idealized search space, methods like dropout, batch normalization, or architectural constraints are not accounted for. These techniques can significantly influence the optimization landscape and runtime behavior of ENAS algorithms. Whether these techniques affect the optimization and runtime behavior of ENAS algorithms. We fully agree that techniques like dropout, batch normalization, and architectural constraints can affect the optimization and runtime behavior of ENAS algorithms. Specifically, dropout and batch normalization can introduce noise into the fitness evaluation result, thereby effecting the optimization and runtime behavior of ENAS algorithms. Additionally, architectural constraints can reshape the search space, thereby altering the fitness landscape and consequently impacting the optimization and runtime behavior of ENAS algorithms. Current frameworks exclude these components due to unresolved challenges: (1) nonlinear interactions between architectural fitness and the noise introduced by dropout and batch normalization, complicating fitness modeling; (2) architecture constraints (e.g., parameter/resource limits) will introduce multi-objective optimization (e.g., balancing accuracy and efficiency). We will discuss these aspects and outline future directions in the Conclusion.	null	null	null	null	null	null
Discrete Markov Probabilistic Models: An Improved Discrete Score-Based Framework with sharp convergence bounds under minimal assumptions	Accept (poster)	Summary: The authors propose the Discrete Markov Probabilistic Model (DMPM), a novel algorithm for generative modeling on the binary data space (bits). The generative model is based on a continuous-time Markov Chain (CTMC) framework with forward processes, which “noisses” the data, and backward processes, which “denoises” the data. The forward process is constructed as a homogeneous Poissonian process that flips the data bits and converges to uniform bits distribution at infinite time. The backward process is modeled as a reverse of the forward process, i.e., via a time-inhomogeneous Markov jump process, which is defined as a discrete analog of the score function. During the training process, a discrete analog of the score function is learned by a neural network. The authors propose three loss functions and their linear combinations. Then, if the score function is properly learned, one can sample from the backward process to generate the data. The authors analyze DMPM algorithm consistency by deriving bounds for KL and TV between initial data distribution and the resulting distribution of backward generation processes. The proposed algorithm is being compared with state-of-the-art discrete state space Markov chain generative models, MD4 [1] and DFM [2]. The experiments on two datasets were shown: synthetic small dimensional Bernoulli distribution data and black-white MNIST dataset. ## Update after rebuttal The authors mostly addressed my concerns. Since the method is focused on working with the binary data, I think that additional demonstration of its superiority on a real, naturally binary dataset would significantly strengthen the work. As well as the better text clarity to simplify understanding for the wider community. Claims And Evidence: The authors argue that the DMPM model matches or outperforms other state-of-the-art Markov chain discrete generative models. However, it seems that the experimental evidence is insufficient to draw such a conclusion. The MNIST dataset is too simple and too low-dimensional to judge the generative model performance. Other models (MD4 and DFM) are mainly validated on the text data or much more complex image datasets such as CIFAR-10 or ImageNet 64x64, hence experiments presented in the paper are insufficient. There do not appear to be widely recognized large-scale binary datasets that clearly necessitate the advanced CTMC-based approach. Hence, the need for such a powerful model for generative modeling on binary data is not obvious. Theoretical claims are supported by the derivations in the Appendix. Methods And Evaluation Criteria: As mentioned in the previous section, the datasets chosen for empirical evaluation suit the task solved but seems to be too simple. The FID metric for MNIST is somewhat questionable since the Inception network (whose features are used to compute FID) was trained on ImageNet rather than on synthetic or binary data. Competitor methods are suitable and are indeed state-of-the-art. Theoretical Claims: The derivations in Sections 1.1 and 1.2 have been checked through following the extended derivations in the appendix. Experimental Designs Or Analyses: Other than the experimental problems that were already presented in the upper sections I think the paper lacks insufficient hyperparameters testing. - Time horizon $T_f$ is tested only in the synthetic Bernoulli distribution experiment. In my opinion, more testing regarding time horizon $T_f$ is needed. One can just analyze the forward process resulting distribution and its closeness with uniform distribution without training a diffusion model. - I have not found any analysis regarding forward process jump rate $\lambda$ and its impact on forward process convergence and performance of learned generative models. - The visualization of the forward process with dependence on time horizon $T_f$ and jump rate $\lambda$ would be beneficial for the paper - DMPM is the model that has uniform distribution as the resulting distribution of the forward process. Other tested competitors do have delta distribution as the resulting distribution of the forward process. It would be beneficial to compare with other state-of-the-art markov chain discrete generative models that have uniform distribution as the resulting distribution of the forward process, such as SEDD Uniform [4]. Supplementary Material: I have reviewed the part of the derivations concerning Sections 1.1 and 1.2, i.e., part of the Appendix B, algorithms and some other parts of Appendix C, experimental details in Appendix D. All of the supplementary parts I’ve reviewed are of sufficient quality. Relation To Broader Scientific Literature: The authors discuss related literature in a sufficient way. Overall the proposed method can be viewed as a particular case of discrete state space CTMC [3, 4] generative model with uniform forward process resulting distribution. In that sense paper doesn't deliver that much of a novelty. In my opinion, there is hardly a need for such a powerful model for binary data. Section 2 provides most of the theoretical novelty for the paper but in my opinion these theoretical results do not deliver impact sufficient for the publication of the paper. Essential References Not Discussed: Most of the essential literature is discussed with the exception of the MDLM [5] model. Other Strengths And Weaknesses: The paper could be written in a more comprehensive/clear way. Notation is overloaded, and mathematics is sometimes hard to understand. It seems that the Poissonian processes framework could be delivered in a more simple and clear way. In addition, some parts are generally hard to understand. For example, lines 133-144 are hard to follow even after taking into account similar derivations in the Appendix. It seems that there is a lot of content in the appendix, and it may be beneficial to move some of it to the main text. Other Comments Or Suggestions: [1] Shi, J., Han, K., Wang, Z., Doucet, A., & Titsias, M. K. (2024). Simplified and Generalized Masked Diffusion for Discrete Data. arXiv preprint arXiv:2406.04329. [2] Gat, I., Remez, T., Shaul, N., Kreuk, F., Chen, R. T., Synnaeve, G., ... & Lipman, Y. (2025). Discrete flow matching. Advances in Neural Information Processing Systems, 37, 133345-133385. [3] Campbell, A., Benton, J., De Bortoli, V., Rainforth, T., Deligiannidis, G., & Doucet, A. (2022). A continuous time framework for discrete denoising models. Advances in Neural Information Processing Systems, 35, 28266-28279. [4] Lou, A., Meng, C., & Ermon, S. Discrete Diffusion Modeling by Estimating the Ratios of the Data Distribution. In Forty-first International Conference on Machine Learning. [5] Sahoo, S. S., Arriola, M., Gokaslan, A., Marroquin, E. M., Rush, A. M., Schiff, Y., ... & Kuleshov, V. Simple and Effective Masked Diffusion Language Models. In ICML 2024 Workshop on Efficient and Accessible Foundation Models for Biological Discovery. Questions For Authors: - It would be great if authors could address the limitations I mentioned in the “Experimental Designs Or Analyses” section. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We thank the reviewer for their thoughtful remarks and the opportunity to clarify the significance of our theoretical results. Our primary aim is to establish convergence guarantees for discrete generative models, analogous to those in continuous diffusion. This led us to a discrete score function with two key formulations (Propositions 1.1 and 1.2), from which our methodology naturally follows—culminating in strong convergence results, arguably our chief contribution. As emphasized in our paper, there is a notable lack of results concerning discrete diffusion models. The closest related work, which improves upon ours in several respects (as detailed in our response to Reviewer fUbX), has only recently been accepted to ICLR [1]. While we include experiments to illustrate the method’s potential, we agree with the reviewer that they should be viewed as preliminary—particularly for large-scale or high-dimensional data. We will revise the paper’s conclusion to emphasize that these findings are intended to motivate and guide future empirical studies, not to be a conclusive benchmark. [1] Ren et al, ICLR 2025 > [no] widely recognized large-scale binary datasets... We emphasize the hypercube setting’s relevance. First, many real-world large-scale datasets use binary data (e.g., millions of presence/absence edges in amazon products or research papers see [2]), enabling applications like link repair, synthetic-data generation for privacy, or also molecule design. Second, any discrete dataset can be binarized (e.g., 8-bit pixel encoding), and recent developments such as Differentiable Logic Gates Networks [3] show how bit-based methods can excel with neural networks, with the right engineering. We belive our framework provides a strong foundation for bit-based generative models. [2] Hu et al. 2020, Open Graph Benchmark, Neurips [3] Petersen et al. 2022, Neurips > [...] particular case of discrete state space CTMCs... Our method indeed fits within the class of discrete-state CTMCs. Its novelty stems from exploiting the hypercube in a more specialized way than the general framework in [4]. We can introduce efficient optimization strategies, mirroring approaches like MDLM with the SUBS parameterization or MD4, which leverage the structure of the absorbing kernel. Like SEDD [5], we parameterize a ratio of density $\mu_t(y) / \mu_t(x)$ rather than a reverse density $p_{0 \|t}$, which is easier since it is a general value rather than a proper distribution. Furthermore, our objective function is expressed in continuous time, contrary to the loss in [4] which must be extended from discrete time and approximated. Contrary to SEDD, our backward process is characterized by a conditional expectation we exploit in a regression problem using an ${L}_2$ loss term. The discrete denoiser structure is also exploit with a cross-entropy loss term. In contrast, SEDD only derives our entropic regularization loss term (see [eq. (10), 5] and our eq. (16)). [4] Campbell et al. 2022, Neurips [5] Lou et al. 2024, ICML > the paper lacks insufficient hyperparameters testing... We first underline the symmetric choice of $T_f$ and $\lambda$, because of time reparameterization. Consider a time-dependent rate $\lambda_t$, with $Q_t = \lambda_t Q$, then $P_t^{\lambda} = \exp(Q\int_0^t \lambda_s ds) = P_{\int_0^t \lambda_s ds}$. In practice, we fix $\lambda = 1$ and vary $T_f$, leaving more sophisticated noise schedules to future work. We did an initial grid search for $\lambda, T_f$, validating $T_f = 3$. We thought the results in Figure 1 were convincing. As suggested, we will include an expanded search on MNIST together with various plots in the camera-ready version, like convergence speed to uniform distribution (e.g., on MNIST, we can see the sliced Wasserstein distance between $p_{\text{uniform}}$ and $p_t$ plateau after $t \approx 2.5$). > The FID metric... The reviewer makes a fair point, but we note that FID has been successfully used for MNIST (e.g., [6]) and is reliable in our experiments. In addition to FID we report our $F_1^{dc}$ metric, see Appendix D.3. It relies on local geometry to evaluate generative quality/diversity. We remain open to other metrics as recommended, we are confident we will still observe improvements. [6] Xu et al. 2023, Normalizing flow neural networks by JKO scheme, Neurips > Beneficial to compare with [...] SEDD uniform We train SEDD Uniform with the same settings as the other models. In response to concerns about FID, we report the $F_1^{dc}$ metric. Again, we see clear improvements: Table 1: $F_1^{\text{dc}}\uparrow$ for different methods \|steps\|10\|25\|50\|100\|200\|500\| \|-\|-\|-\|-\|-\|-\|-\| \|flip\|0.64\|0.92\|0.93\|0.93\|0.93\|0.92\| \|denoise\|0.13\|0.67\|0.87\|0.96\|1.00\|1.00\| \|SEDD\|0.61\|0.82\|0.88\|0.92\|0.92\|0.92\| We hope that the previous discussion has satisfied the reviewer. If this is the case, we kindly ask them to consider raising their score, if they feel it is appropriate. --- Rebuttal Comment 1.1: Comment: I thank the authors for taking the time to address my concerns, and I am mostly satisfied with the answers. It would be nice to see these changes reflected in the revised version. The authors highlight the theoretical contributions—particularly those on algorithm convergence—as the core value of the paper. As my expertise is more aligned with the practical aspects, I may not be best positioned to fully assess the depth of the theoretical claims. Concerns about the notation and text clarity persist. Some of my practical concerns also remain only partially addressed. In particular, it would be very helpful to see an experiment on real-life data to better demonstrate the applicability of DMPM—for instance, on one of the proposed datasets such as link repair [2]. While I appreciate the point that all datasets can be binarized, the practical usefulness of such binarization in the context of the discrete diffusion models remains uncertain. I have updated my score. --- Reply to Comment 1.1.1: Comment: We thank the reviewer for reconsidering the scope of our paper. We also value their feedback and are committed to revising the notation and text to make the paper as accessible as possible, without compromising the rigor required for the theoretical developments. Regarding the practical concerns raised, as mentioned in our initial rebuttal, we will acknowledge that additional numerical experiments are needed to draw definitive practical conclusions about our method.	Summary: This paper introduces Discrete Markov Probabilistic Models (DMPMs), a novel framework for discrete data generation based on continuous-time Markov chains (CTMCs). The forward noising process follows a Poissonian clock that flips bits randomly, while the reverse process reconstructs the data via an estimated discrete score function. Claims And Evidence: Yes. Methods And Evaluation Criteria: Yes. Theoretical Claims: I briefly looked at the proofs, and they appear correct based on my reading, but I did not dig into all the details. Experimental Designs Or Analyses: The design of experiments is well-structured, with appropriate comparisons to MD4 and DFM. Supplementary Material: Yes, but only a brief look at the proofs. Relation To Broader Scientific Literature: This work builds on continuous-time discrete diffusion models and avoids unstable density ratio estimation. Essential References Not Discussed: No. Other Strengths And Weaknesses: Strengths: The paper provides strong theoretical guarantees for convergence and avoids density ratio estimation, improving numerical stability. Weaknesses: Some assumptions might be too restrictive, see questions below. Other Comments Or Suggestions: N/A. Questions For Authors: 1. The state space is {0,1}$^d$, and so I believe the proposed algorithm will have wide applications in physics. Then I wonder if the DMPM can be generalized to systems where each particle has more than two potential states. Can you modify the Poission clock to design a proper forward process? And can the backward process and convergence result be derived with similar approaches in this paper? 2. Assumption 2.2 seems a bit too restrictive. For example, in a quantum system, two fermions cannot occupy the same state and so for such a system, $\mu^*((0, 0)) = 0$. Is this assumption technical or essential to the proof of the convergence? Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: We thank the reviewer for their very positive feedback, and for finding our paper an interesting contribution to discrete diffusion models from both theoretical and methodological perspectives. > I wonder if the DMPM can be generalized to systems where each particle has more than two potential states. Can you modify the Poission clock to design a proper forward process? And can the backward process and convergence result be derived with similar approaches in this paper? We thank the reviewer for the opportunity to address this question. First, it is entirely possible to stay within the hypercube setting for any discrete data by using binary encoding. For instance, colored images can be encoded in 8-bits RGB pixels. Then each image is encoded in {$0, 1$}$^{3 \times 8 \times 64 \times 64}$, if using images of size $64 \times 64$, for instance. The same approach can be adopted for particles with more than two possible states. Second, we believe it should be possible to extend our study to state-spaces like {$0, \cdots, N$}$^d$, defining the uniform random walk with unit increment as the noising process, and that the backward process and convergence results would be derived very similarly. However, we emphasize that our paper's philosophy is to stay within the binary hypercube, and benefit from various optimizations enabled by such a setting, both theoretically and methodologically. For instance, this yields our regression objective, with the ${L}_2$ loss term (eq. 15), and our discrete denoiser structure, leading to the cross-entropy loss term (eq. 17). > Assumption 2.2 seems a bit too restrictive [...]. Is this assumption technical or essential to the proof of the convergence? We thank the reviewer for the opportunity to clarify this point. We wish to reassure them as we relax Assumption 2.2 soon after introducing it. Initially, it is used in Theorem 2.3 to derive our simplest convergence bound, which involves computing a Fisher divergence. However, we subsequently employ an early-stopping argument (as detailed from Theorem 2.5 onward) to circumvent its necessity in practice. This mirrors what happens in continuous diffusion models, where the data may lie on a lower-dimensional manifold without admitting a density against the Lebesgue measure in the full ambient space. There, too, the same line of arguments involving early stopping are used. In practice, the learned model can still assign zero probability to impossible states. For example, on MNIST, we observe that the learned model faithfully recreates handwritten digits, and it is safe to assume that it assigns negligible or zero probability to meaningless states (such as a completely white image). Hence, the assumption does not pose a practical limitation either. We hope we have successfully addressed the reviewer's questions, and we would like to thank them again for their positive feedback.	Summary: Score-based diffusion models are becoming one of the most promising non-adversarial and easy-to-implement data distribution reconstruction techniques. The idea is to define a forward noise process that gradually degrades the training data until it is transformed into a simple distribution that is easy to sample from. The model learns to reverse this process by learning the log-gradient of the noisy marginal distribution, known as the score. While most noise removal models to date have dealt with continuous state spaces, in recent years, the benefits of noise removal frameworks have been highlighted for problems involving discrete data, such as text, segmentation maps, categorical features, discrete latent spaces, and direct 8-bit image representations, and research in this area has been developing very actively. This paper presents theoretical and practical investigations of the case where the state transition probability follows the mechanism of Poisson clocks with state bits for a {0,1}^d state space. The model set up by the authors succeeds in obtaining a closed-form expression using score-based conditional probabilities of forward processes, whereas many diffusion models originally suffer from the difficulty of handling the representation of backward processes. As a result, the authors have succeeded in theoretically guaranteeing that the proposed discrete diffusion model has a tighter fitting bound than conventional models. Along with their theoretical results, the authors have also quantitatively evaluated the effectiveness of their proposed method using artificial data and MNIST binary images to demonstrate its practical performance. Claims And Evidence: This paper argues that imposing the condition that the state transition probability follows the mechanism of Poisson clocks on the state bits on the state space of the hypercube {0,1}^d for the discrete diffusion model can resolve the issues that the conventional discrete diffusion model has had (limitations on convergence, increased computational cost for high dimensions, and the need for extremely strong assumptions in theoretical analysis). Section 1 describes the discrete diffusion process assumed by the authors. Section 2 evaluates the usefulness of this model theoretically in the form of a bound on the convergence. Section 3 empirically and experimentally verifies this. Methods And Evaluation Criteria: My comment on this term is merged into Claims part. Theoretical Claims: I find the theoretical contribution of this paper very impressive. I would like to ask the authors a question to properly understand its value. I am trying to understand this paper by contrasting it with the theoretical work of literature [Campbell+, NeurIPS2022] and [Ren+, ICLR2025] (which seems to be same as the reference arXiv2410.03601 cited in this paper) as important examples. For eacmple, Reference [Ren+, ICLR2025] seems to consider state transition matrices in the general discrete state space as state transitions in discrete diffusion processes (Section 2 and Appendix B). As a result, since the state transition matrix of a Markov chain is combinatorial in dimension and large in size, it seems that, for example, in its mixing time analysis, the spectral gap (the order of the inverse of the mixing time) is evaluated as in the standard MCMC procedure for mixing time analysis. On the other hand, this paper, very interestingly, seems to achieve avoiding any mixing time analysis focusing on the eigenvalues of this kind of state transition matrix. In fact, the proof in Appendix F.4 shows a very concise argument for state transitions, where only a reference to self-transitions for an arbitrary time interval\eta is sufficient. So, my question is, does the fact that we have made a stronger assumption on the state transition matrix than before contribute to this concise argument? As I understand it, the assumption seems to be placed that the state transition probabilities for high-dimensional binary data are represented by the direct product of independent binary state transitions in each dimension, as shown in Equation 9. Is this understanding (i.e., that it restricts the state transition dynamics more than previous studies) correct? Experimental Designs Or Analyses: The authors compare the proposed method with the latest discrete diffusion process for artificial data (Bernoulli simulation) and MNIST (the original 28x28 is upsampled to 32x32). While the Hellinger distance and KL divergence between distributions are generally used as quantitative comparison criteria, this paper uses the sliced wasserstein distance for evaluation because it has a theory that can handle high-dimensional data that previous studies could not handle. I think this paper has produced some impressive results in terms of theoretical contributions. However, the theoretical results in Section 2 only give a bound on the closeness between the data and the model distribution, so it would certainly be very interesting from a practitioner's perspective to see how it behaves on practical data. I think the authors' experimental results (albeit not on a large and diverse set of settings) give the reader some intuitive insight into the effectiveness of the proposed method. Supplementary Material: The supplementary material consists of a complete derivation of the model representation, a proof of the theoretical results, and a detailed description of the experimental setup. I wanted to know whether the breakthrough in the theoretical contribution of this paper was due to (1) new assumptions about the model or (2) new tools for theoretical analysis, so I tried to briefly outline Appendix F (Proof of Theoretical Results). Relation To Broader Scientific Literature: With the spectacular success of continuous state diffusion processes, discrete state diffusion processes are expected to play an increasingly important role in a wide range of applications, including text and biological information. I think this paper provides some very important insights into this development. On the other hand, this paper seems to make the strong assumption that the state space of the discrete diffusion model is a hypercube on {0,1}^d, so it seems non-trivial whether this approach can be applied straightforwardly to natural language or genetic information. Essential References Not Discussed: This paper refers to a wealth of literature on the discrete diffusion process, which has been the subject of particularly active research in recent years. (I checked the list of references, for example, which cites several important papers [Campbell+, NeurIPS2022], and confirmed that this paper cites them appropriately.) Other Strengths And Weaknesses: [Strengths] - This paper insightfully discovers a special class of discrete diffusion processes in which the backward process can be expressed in a closed-form, easy-to-handle form. - The authors theoretically guarantee the importance of this discovery in the form of a bound on the closeness of the data distribution and sample distribution. This is a very impressive result that scales more naturally to higher dimensions than conventional discrete diffusion processes. - The authors demonstrate the practical effectiveness of the proposed method not only with theoretical guarantees, but also with medium-sized data. [Weaknesses] - My main concern is that the class of discrete diffusion processes considered in this paper (discrete states on the hypercube, with state transition probabilities being the direct product of each dimension) is a much stronger situation than the assumptions made in previous papers. My main concern is that the class of discrete diffusion processes considered in this paper (discrete states on the hypercube, with state transition probabilities being the Cartesian product of each dimension) is a much stronger situation than the assumptions made in previous papers. I think that setting very strong assumptions in order to achieve a breakthrough in theoretical analysis is very meaningful in itself. However, because this paper does not discuss this in depth, it is somewhat unclear where it stands in relation to recent developments in discrete diffusion processes. In particular, the description of the paper's position in relation to the latest methods (Section 0 and Appendix A) is limited to high-level, abstract explanations, so a very deep prior knowledge of the field is required to correctly understand the paper's true value. Other Comments Or Suggestions: Line 581: ’’masked’’ -> ``masked’’ would be better. I do not know why it is necessary to have \propto_{I} in equation 10. Is this a typo? I can certainly see why \propto is needed in equation 9. The current draft of this paper seems to be a rather esoteric explanation aimed at experts in discrete diffusion processes or those who are very familiar with the latest developments in them. As a result, newcomers to the topic or general readers interested in the surrounding fields may not find it easy to properly understand the true value of this paper. In order to better convey the value of this paper to a more diverse audience, we would like to make the following recommendations. > addressing the issues raised in prior work. (Page 1, right column) > However, many of these methods still lack rigorous error bounds or scale poorly in high dimensions. (Page 7, left column) > However, their results rely on strong assumptions in contrast to our results. Besides, our bounds are simpler and better, in particular with respect to the time horizon. (Appendix A) The high-level sketched commentary to these existing studies is no doubt very intuitive and meaningful. However, the current draft does not specify what model assumptions individual previous studies use and what theoretical results they have, and readers will have to individually check the original papers themselves. To be honest, I cannot write down in a positive way what improvements this paper has from some of the previous studies. Therefore, my request is that the authors compile the “model assumptions” and “theoretical results (error bounds)” for each literature in the form of a table so that we can see at a glance the value of this paper when compared to existing studies. In fact, the authors' investigation of the previous studies is so deep and comprehensive that it would be of great value to summarize the results of the previous studies as a unified and improved paper on them. Questions For Authors: I have no additional questions. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We thank the reviewer for their comments, which will help improve the presentation of our contributions. We hope that we have addressed all of their questions in the responses below. Given their positive feedback—particularly their appreciation of the "very impressive" theoretical contributions—we would kindly ask the reviewer to consider raising their score, if they feel it is appropriate. > I wanted to know whether the breakthrough [...] briefly outline Appendix F (Proof of Theoretical Results) We thank the reviewer for their remark, which will help us clarify the key contributions of our paper. To this end, we provide a brief sketch of the proof for Theorem 2.3, which we will expand upon and include in the revised version of the paper. The first step in the proof is to decompose the relative entropy between the backward process and our generative algorithm into three terms: $$ \mathrm{KL}(\overleftarrow{P} \\| P^) \leq \mathrm{KL}(\mu_{T_f} \\| \gamma^d) + II + III. $$ - The first term* on the right-hand side arises from the fact that the generative process does not start from the marginal at time $ T_f $, but rather from the stationary distribution $ \gamma^d $. Using standard arguments for the convergence of random walks on $ \lbrace 0,1\rbrace^d $, this term is exponentially small in $ T_f $. - The second term $ II $ corresponds to the score approximation error. By Assumption 2.1, we can bound it by $ T_f \varepsilon $. - The third term, $ III $, corresponds to the time discretization error of the generative process. It is given by $$ \sum_k \mathbb{E} [ \int_{[t_k, t_{k+1}]} \sum_{\ell} u^_{t_k}(\ell) \cdot h(u^_{t}(\ell)/u^_{t_k}(\ell)) dt ], $$ where $u_t^(\ell) = 1 - s_t^{\ell}(\overleftarrow{X}_{t})$, and $(\overleftarrow{X}_t)_t$ denotes the time-reversed process. To bound this term, we rely critically on Proposition F.11, which serves as the main technical tool in our analysis. Specifically, the proposition shows that: 1. The process $ (\sum_{\ell} u^_t( \ell) )_t$ is a martingale, and 2. The process $ (\sum_{\ell} h(u^_t(\ell)))_t $ is a submartingale. Thanks to these two properties, along with Assumption 2.2 and an application of Jensen’s inequality, we are able to bound the third term $ III $. > does the fact that we have made a stronger assumption on the state transition matrix than before contribute to this concise argument? The reviewer is correct in noting that the arguments we developed—and summarized in our previous response—crucially rely on using the random walk on {$0,1$}$^d$ as the noising process. Nevertheless, we view our work as a foundational step toward extending the framework to broader classes of discrete generative models. In fact, as part of our future work, we aim to formalize our reasoning in a more general setting that could encompass a wide family of discrete models, including masked diffusion processes. > My main concern [...] is a much stronger situation than the assumptions made in previous papers.[...] We thank the reviewer for this comment, which helps to clarify the implications of our work. First, as this appears to be the reviewer’s most critical concern, we acknowledge that—unlike most previous works—both the state space and the noising process we consider are fixed. These choices are indeed crucial for establishing our theoretical results (as detailed further above) under minimal assumptions on the data distribution. We will emphasize on this point in the revised version of the paper. However, we would like to make two points in response. First, although working on the hypercube may initially appear restrictive, we note that any discrete space can, in principle, be embedded into the hypercube via binary encoding. This means that our algorithm can, in theory, be applied to any discrete data structures. Second, we view the theoretical analysis presented in this paper as a first important step to demonstrate that convergence guarantees for a general class of discrete score-based generative models can be achieved under minimal assumptions on the data distribution. As we emphasized in our first response, we are confident that the techniques developed here have the potential to extend to other discrete structures as well. However, since the exact scope of this generalization is not yet fully understood, we refrain from making definitive claims at this stage. > In particular, the description of the paper's position in relation to the latest methods [...] is limited to high-level, abstract explanations. We will follow the reviewer’s suggestion and, in particular, include a comparison table in the camera-ready version of our paper. We also plan to add a detailed discussion of the assumptions made in previous works—specifically those concerning the data distribution, as well as the density and score of the noising process—which our approach is able to relax.	Summary: This paper introduces the Discrete Markov Probabilistic Model (DMPM), a uniform noising/denoising algorithm for discrete data generation. The authors establish theoretical convergence bounds under minimal assumptions and validate the effectiveness of their method empirically on both low-dimensional Bernoulli datasets and a relatively high-dimensional binary MNIST data. By bridging rigorous theoretical foundations with practical performance, this work makes a valuable contribution in the emerging area of discrete generative modeling. ### update after rebuttal The reviewer thanks the authors for the detailed response and for positively answering the raised concerns. Overall, the reviewer thinks that the theoretical results in this paper adds value to the better understanding of discrete diffusion models. Although experiments are not the main focus of this paper, the submitted version had a wrong experiment as acknowledged by the authors at the end of the rebuttal below. Besides, the paper makes a claim against the standard practice in large-scale experiments, which is "absorbing kernels perform better than uniform". However, there is not enough evidence to prove or disprove this claim. Given the strength of the paper in theoretical analysis, the reviewer recommends accepting the paper. Claims And Evidence: The paper provides strong theoretical results supported by rigorous proofs; however, the empirical evidence presented appears somewhat limited. Specifically, the claim that uniform noising kernels offer provable theoretical guarantees and superior performance compared to masked approaches like MD4 remains inconclusive. The main concern is that uniform noising kernels typically perform poorly in high-dimensional scenarios compared to absorbing kernels. Given this context, additional large-scale experiments or high-dimensional evaluations are necessary to convincingly support the claim that uniform noising kernels are practically superior to masked methods like MD4 or MDLM. Methods And Evaluation Criteria: The evaluation is currently done at a relatively smaller scale (toy dataset and MNIST). Large-scale evaluations are essential for conclusive evaluation of the proposed claims. Theoretical Claims: Theorem 2 (Chen et al. https://openreview.net/pdf?id=zyLVMgsZ0U_) has a similar form as that of Theorem 2.3 (also Theorem 2.5) in this paper. While the first term in the upper bound seems unavoidable, the second term can be avoided as shown in Theorem 2.5. The reviewer is wondering about the dependence on $\epsilon$ and $T_f$ in the third term, which seems like a coarse discretization error as compared to Chen et al. Is this the optimal characterization of the score approximation in the full trajectory? Intuitively, if the approximation error is of $O(\epsilon)$ and then we take $T_f$ denoising steps, then the total accumulated error would be of $O(\epsilon T_f)$. Isn’t there a tight characterization of this error? Experimental Designs Or Analyses: Yes, the conducted experiments look okay to me. But large-scale experiments are missing for a thorough evaluation. Supplementary Material: Yes, skimmed through Appendices A-E. Relation To Broader Scientific Literature: The choice of transition kernel is quite ambiguous because there exists a mixed set of papers that claim absorbing kernels are better than uniform noising kernels or vice-versa. Indeed, a proper theoretical understanding of any of these two commonly used kernels or new approaches is a valuable contribution to the community. Essential References Not Discussed: Some essential references have not been included. Please see the weaknesses for details. Other Strengths And Weaknesses: ### Strengths The choice of transition kernel is quite ambiguous because there exists a mixed set of papers that claim absorbing kernels are better than uniform noising kernels or vice-versa. Indeed, a proper theoretical understanding of any of these two commonly used kernels or new approaches is a valuable contribution to the community. ### Weaknesses 1. Line 25 (right col): “In this paper, we introduce Discrete Markov Probabilistic Models (DMPMs), a new class of generative models for discrete data that bridges these gaps.” This is not entirely new and dates back to Sohl-Dickstein et al. 2025 and popularized by Austin et al. 2021 with many other recent follow-up works. 2. The notation in Line 66 for $\|d\mu/dR-d\nu/R\|dR$ seems squeezed in one line. It could be better presented as $\|\frac{d\mu}{dR} - \frac{d\nu}{dR}\|dR$. 3. Lines 99-103: “We derive closed-form expressions for the backward transition rates, which involve conditional expectations over the forward process. This enables, for the first time, an efficient training procedure based on regression in the discrete setting.” What is new here? What is done for the first time? The notion of conditional expectation of $X^{rev}_T$ given $X^{rev}_0$ is the key contribution in prior works, such as D3PM (Austin et al. 2021) or MDLM (Sahoo et al. 2024). 3. The transition probabilities derived in Equation (2) and Appendix B.1 can be seen in the introduction to CTMC (Chapter 2, Liggett). Again, the originality and innovation of the analysis is limited in my opinion.The authors are encouraged to highlight (maybe informally) the original theoretical contributions early on in the paper for the ease of assessing the major contributions. 4. The key contribution of the paper is in Equation (6) with a more generalized version in Proposition 1.1, where the discrete equivalent of score is written as an affine transformation of $X^{fwd}_0$ and $X^{fwd}_t$. A slightly modified version of this result has previously appeared in DFM (Campbell et al. 2024). 5. The regression loss used in Equation (15) is quite similar to the DFM loss or other discrete diffusion losses as in MDLM. The reviewer is finding it difficult to understand what this theoretical result is prescribing here. Again, the loss in Line 225 is similar to the subs-parameterization introduced in MDLM (Sahoo et al. 2024). The authors are encouraged to clarify these similarities and highlight the innovations of this paper. 6. What is the relation between Assumption 2.2 and the irreducibility property of CTMC? It’d be better to connect this assumption with CTMC for better understanding and consistency with prior discussion. 7. Theorem 2 (Chen et al. https://openreview.net/pdf?id=zyLVMgsZ0U_) has a similar form as that of Theorem 2.3 (also Theorem 2.5) in this paper. While the first term in the upper bound seems unavoidable, the second term can be avoided as shown in Theorem 2.5. The reviewer is wondering about the dependence on $\epsilon$ and $T_f$ in the third term, which seems like a coarse discretization error as compared to Chen et al. Is this the optimal characterization of the score approximation in the full trajectory? Intuitively, if the approximation error is of $O(\epsilon)$ and then we take $T_f$ denoising steps, then the total accumulated error would be of $O(\epsilon T_f)$. Isn’t there a tight characterization of this error? 8. The authors are encouraged to write some implications of Corollary 2.7 at the end of Section 2. The transition from Section 2 to Section 3 seems abrupt. 9. Table 1: While other methods show a consistent behavior, DMPM (flip) seems inconsistent as the number of reverse steps increases. The authors are encouraged to check the numerical simulations of this sampler or provide a better justification for this inconsistent behavior. 10. Experiments on MNIST are not quite high-dimensional. The paper would significantly benefit from even higher dimensional modeling, especially because uniform noising is known to perform suboptimally compared to absorbing diffusion in higher dimension. 11. How would the analysis change for absorbing kernels since that has been very successful in large-scale experiments (see MDLM and other follow up works). Other Comments Or Suggestions: Please see weaknesses. Questions For Authors: Please see weaknesses. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We thank the reviewer for their positive feedback, especially regarding the strength of our theoretical contributions. Due to space constraints, we address only the most critical concerns, but we welcome further discussion if any important points remain unaddressed. > Additional large-scale experiments or high-dimensional evaluations are necessary [...] We acknowledge that our experiments are limited, and we agree that more extensive large-scale and high-dimensional evaluations are necessary to fully support the use of uniform noising kernels in comparison to masked ones. Nevertheless, as the reviewer noted, the core contributions of our paper are theoretical. Our main objective is to derive convergence guarantees for discrete generative models that match those known for continuous diffusion models. As emphasized in our paper, there is a notable lack of results concerning discrete diffusion models. The closest related work, upon which ours significantly improves (as detailed in our response to Rev. fUbX), has only recently been accepted to ICLR [1]. In pursuing our goal, we obtained a representation of the score as a conditional expectation (Prop 1.1 and 1.2), which is the foundation of our methodology. While limited, we believe our numerical experiments add value by showing the practical potential of our approach. That said, we agree that strong conclusions should not be drawn from these preliminary results, especially in large-scale or high-dimensional scenarios. To address this, we will revise the conclusion to clarify that our findings are meant to motivate future empirical work rather than provide definitive evidence. [1] Ren et al, ICLR 2025 > Lines 99-103 [...] The notion of conditional expectation of [...] is the key contribution in prior works, such as D3PM or MDLM). From our understanding, prior works—including those mentioned by the reviewer— aim to estimate the generator associated with the backward dynamics of the backward process relying on estimating the conditional distributions $p_{0\|t}$ of $X_0$ given $X_t$ for $t \in [0,T_f]$. In contrast, we first demonstrate that estimating the generator of the time-reversed process is equivalent to estimating the discrete score function introduced. Second, we show that (1) this score function can be expressed as a conditional expectation, and (2) it is associated with a discrete denoising structure. Therefore estimating the backward generator reduces to solving either a regression or a classification problem—tasks that are often more tractable than learning full conditional distributions. While prior work seeks to model an entire conditional distribution, we focus on estimate a function that solves a regression or classification task. We regret any confusion caused by the original formulation and will revise the paper to include this discussion in order to clarify our claims. > Theorem 2 in [2] [...] Isn’t there a tight characterization of this error? The third term $\epsilon T_f$ has the same meaning and significance of the corresponding term in Theorem 2 of [2], appearing as such. Indeed, it accounts for the score approximation error that we do not investigate in our submission similarly to [2]. [2] Chen et al, ICLR 22 > The transition probabilities [...] can be seen in [...] (Chapter 2, Liggett)... As stated in the paper, these computations are well known, and we thank the referee for pointing out the reference in Liggett’s book, which we will include in the revised version. As the referee suggests, we will emphasize this point more clearly early in the paper. > The regression loss used in Equation (15) is quite similar to the DFM loss... First, we would like to emphasize the following points based on our understanding: - (1) The SUBS parameterization is applicable only to absorbing kernels; - (2) The approach in [3] focuses on estimating conditional probabilities $p_{s\|t}$, which is fundamentally different from our methodology, as previously discussed. Concerning the DFM loss, we were not able to find a similar result as ours in [4]. It seems to us they use a flow matching construction with a conditional rate matrix built ad-hoc (Section 3.2). This seems fundamentally different from the way we derive our reverse process (see (4)). [3] Sahoo S. et al, 2024, Neurips [4] Campbell et al 2022, Neurips > What is the relation between Assumption 2.2 and the irreducibility property of CTMC? Ass. 2.2 only states that $\mu^\star$ has full support and does not impose any conditions on the CTMC considered in our analysis. > Table 1: DMPM (flip) seems inconsistent We thank the reviewer for spotting this, indeed we loaded the wrong model checkpoint for the evaluation run at 500 steps, here is the result of a new run: Table 1: FID$\downarrow$ and F$_1^{dc}\uparrow$ for DMPM methods at 500 reverse steps. \| \|FID\|F$_1^{dc}$\| \|---\|---\|---\| \|flip\|6.98\|0.94\| \|denoise\|2.52\|1.00\| --- Rebuttal Comment 1.1: Comment: Thank you for the rebuttal. Some of my concerns have been addressed. I will update my review in light of this response as necessary. Regarding the characterization of approximation error, $O(\epsilon T_f)$ seems trivial. A tight characterization would strengthen the contribution of the paper. As stated in the paper, these computations are well known, and we thank the referee for pointing out the reference in Liggett’s book, which we will include in the revised version. As the referee suggests, we will emphasize this point more clearly early in the paper. Perhaps I missed, could the authors point out where it is stated in the paper? Missing response to previous Q12. Would the current analysis break for absorbing kernel? --- Reply to Comment 1.1.1: Comment: We are grateful to the reviewer for their continued engagement and thoughtful input. > A tight characterization would strengthen the contribution of the paper. While we acknowledge that developing sample complexity bounds is undoubtedly an important and valuable direction for future research, we believe, as initially stated, that it falls outside the scope of the present paper. It is worth noting that in the context of continuous diffusion models, the literature typically begins by establishing bounds on the discretization error (e.g., [1,2,3]), before later works (e.g., [4,5,6]) build on those results to derive sample complexity bounds. While incorporating such bounds would certainly strengthen our paper, doing so would require substantial additional theoretical developments, which would significantly increase the length of the manuscript. As it stands, our paper already totals 47 pages including the supplementary material. Based on analogous analyses for continuous diffusion models, we estimate that including a thorough sample complexity analysis would add at least 30 pages, bringing the total to around 80 pages, which can be considered excessive. [1] S. Chen, S. Chewi, J. Li, Y. Li, A. Salim, and A. R. Zhang. Sampling is as easy as learning the score: theory for diffusion models with minimal data assumptions, 2023. arXiv: 2209.11215 \ [2] Hongrui Chen, Holden Lee, and Jianfeng Lu. Improved analysis of score-based generative modeling: User-friendly bounds under minimal smoothness assumptions. In International Conference on Machine Learning, pages 4735–4763. PMLR, 2023. \ [3] Holden Lee, Jianfeng Lu, and Yixin Tan. Convergence of score-based generative modeling for general data distributions. In International Conference on Algorithmic Learning Theory, pages 946–985. PMLR, 2023. \ [4] Oko, K., Akiyama, S., & Suzuki, T. (2023, July). Diffusion models are minimax optimal distribution estimators. In International Conference on Machine Learning (pp. 26517-26582). PMLR. \ [5] Azangulov, Iskander, George Deligiannidis, and Judith Rousseau. "Convergence of diffusion models under the manifold hypothesis in high-dimensions." arXiv preprint arXiv:2409.18804 (2024). \ [6] Yakovlev, Konstantin, and Nikita Puchkin. "Generalization error bound for denoising score matching under relaxed manifold assumption." arXiv preprint arXiv:2502.13662 (2025).\ > Perhaps I missed, could the authors point out where it is stated in the paper? Line 70-71 second column, it is written "The transition probability matrix [...] is known to be" As mentioned previously, we will emphasize this point more clearly in the paper. > Missing response to previous Q12. Would the current analysis break for absorbing kernel? We view the theoretical analysis carried out in this paper as a proof of concept for the fact that guarantees of convergence for discrete score based generative models can be obtained with the same degree of precision as for continuous diffusion models. Building on the results of this work, we are confident that the techniques developed here can lead to strong guarantees of convergence for other noising kernels. In particular most of the theoretical analysis carried out here would work for absorbing kernels as well, with the important exception of the score monotonicity estimates of Appendix F. Our current research efforts go in the direction of developing a general convergence theory for discrete diffusion models which encompasses absorbing kernels as a special case. At the moment of writing, we do not fully foresee the range of applicability of the ideas explored in this paper, and thus abstain from making further claims.	null	null	null	null	null	null
Probing Visual Language Priors in VLMs	Accept (poster)	Summary: This paper investigates visual language priors in vision-language models , analyzing how these models rely on textual biases rather than true visual reasoning. The authors introduce ViLP, a benchmark designed to expose such priors by presenting models with out-of-distribution images and distractor text-based facts. The benchmark consists of question-image-answer triplets, where the correct answer contradicts common textual priors, requiring models to focus on visual reasoning. To address the issue of over-reliance on text priors, the paper proposes Image-DPO, a training framework that introduces controlled image corruptions to force VLMs to develop stronger visual grounding. Experiments with LLaVA-v1.5 and Cambrian demonstrate that Image-DPO improves performance on ViLP and other multimodal benchmarks. Claims And Evidence: Yes Methods And Evaluation Criteria: See Weakness. Theoretical Claims: Yes. The paper provides a theoretical connection between Image-DPO and RLHF objectives. Experimental Designs Or Analyses: See weakness. Supplementary Material: Yes. The appendix provides qualitative analysis and theoretical analysis. However, more details on failure cases would be useful. Relation To Broader Scientific Literature: Related to prior work on textual priors in VQA datasets (e.g., Winoground, HallusionBench). Essential References Not Discussed: See weakness. Other Strengths And Weaknesses: ### Strengths - An interesting benchmark filling a gap in VLM research. - The proposed Image-DPO method improves model performance. - Comprehensive evaluation across multiple models. --- ### Weaknesses - Lack of in-depth failure analysis. - A more detailed breakdown of failure cases would be beneficial. For instance, what are the top three most common failure types in this benchmark? - Methodological concerns regarding Image-DPO. - Weak connection between Image-DPO and the benchmark itself. The proposed method does not seem inherently tied to addressing language priors, making Section 4 feel somewhat disconnected from the core benchmark motivation. - Lack of distinction from prior DPO methods. The paper does not clearly differentiate Image-DPO from existing DPO approaches, such as those in [1], which also augment images. - Benchmark realism and case selection. - Some examples in the benchmark (e.g., Figure 3 with unnatural tiger and moon images) appear unrealistic. - Comparatively, benchmarks like Winoground and HallusionBench provide more realistic settings with real-world images and practical vision-language challenges. - A better approach might be to incorporate real images using image retrieval techniques, such as: - Identifying common real-world priors (e.g., cows grazing on grass) - Introducing subtle variations (e.g., a rabbit on the grass instead of a cow) - This approach aligns well with the paper’s motivation of probing visual priors. - Insufficient explanation of LLaVA-OneVision performance in Table 2. - The paper does not provide a clear justification for LLaVA-OneVision’s performance in Table 2. - If the evaluation method penalizes long responses where the correct answer is embedded within a longer explanation, this could raise concerns about the robustness of the evaluation criteria. - Could you provide failure case of this model? --- ### Reference [1] Self-Supervised Visual Preference Alignment. Other Comments Or Suggestions: See weakness. Questions For Authors: See weakness. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We greatly appreciate the detailed and insightful feedback. Below, we have carefully addressed the opportunities for improvement you highlighted. --- > Failure case analysis We sincerely appreciate your suggestions and will include an in-depth failure case analysis section in revision. We observe several consistent failure patterns, as shown in the [Figure](https://postimg.cc/18j0mVt4). For deeper analysis, we additionally prompted the VLMs to output their reasoning before answering. Below, we summarize the failure patterns in the order corresponding to the images. 1. Shape recognition can fail in VLMs, causing them to revert to priors rather than accurately interpreting visual input. 2. Models sometimes struggle to count accurately. Instead of performing an actual count, they default to relying on learned priors to estimate quantities. 3. Models may refuse to accept visual information that contradicts their learned priors, whereas humans can comprehend hypothetical scenarios. For instance, the model recognizes the city as Beijing but rejects the correct answer because it expects the Eiffel Tower to be in Paris. 4. For images with creative concepts, the model may overly rely on its learned priors. As illustrated, a common prior is that microscopes are used to view organisms, leading the model to answer “microscope” rather than identifying the creatively depicted stapler. 5. For images with blended features, the model may rely mostly on text input while overlooking the visual cues. As illustrated, the VLM heavily depends on textual input leading to saxophone as the answer. --- > Fine-grained evaluation and LLaVA-OneVision performance Thanks for the suggestions! Currently, we explicitly ask VLMs to produce a single-word response for evaluation, as it is (1) cost-efficient without calling LLM, (2) fast, and (3) reliable. For robustness, we implemented a comprehensive synonym-matching pipeline to validate synonymous responses accurately. We indeed penalize responses that include long sentences, as we believe instruction-following is a foundation capability of VLMs—thus, failure to comply warrants a penalty. We acknowledge the value of your suggestion and have extended our evaluation system to include three categories: Correct, Wrong, and Invalid. “Invalid” refers to responses that do not meet the single-word requirement. Additionally, for “Invalid” outputs, we now provide an optional GPT-based evaluation that classifies them as either Invalid-Correct or Invalid-Wrong. The results is shown in [Table](https://postimg.cc/SXgTQ1B4). The new evaluation enables us to assess the model’s performance which generates longer sentences. --- > Regarding Winoground and HallusionBench benchmarks and unrealistic examples For clarification, Appendix A.3 provides both quantitative and qualitative comparisons between our dataset and existing benchmarks such as WinoGround and HallusionBench, with key differences highlighted, ranging from high-level design principles to low-level formatting details. Moreover, our human study shows that participants can identify unnatural elements like tigers or moons. This underscores the human ability to reason about unrealistic or novel scenarios—an essential goal for advancing VLMs—and positions our dataset as complementary to existing benchmarks. --- > Reference of [1] Thanks for the suggestion, and we will discuss it [1] in the final revision. The key difference between ImageDPO and [1] is the training objective: while [1] follows the standard DPO setup by using preferred/dispreferred outputs for the same input, our approach fixes the output and varies the input conditions. This results in notable differences, like the distinct gradient behavior in Figure 13. Additionally, we introduce Proposition 1 and its theoretical proof in Appendix B, connecting our modified objective to the original DPO formulation. [1] Self-Supervised Visual Preference Alignment --- > Connection between Image-DPO and the benchmark Directly adjusting VLMs to improve specific abilities becomes challenging as the development of VLMs.. Our Image-DPO method addresses learned priors in a nuanced manner, where the proposed objective encourages the model to rely more heavily on the vision branch. Our objective drives a distinct shift in gradient directions when processing normal images $I_w$ compared to corrupted images $I_l$ (as illustrated in Figure 13). We appreciate your suggestion and will revise our wording to improve the connection. --- > Potential better approach We explored a similar idea but faced a key limitation: existing image-editing models often introduce visible artifacts or unnatural transitions between edited regions and the original background, making it easier for VLMs to detect anomalies. Additionally, they frequently struggle to follow instructions accurately. As editing technology improves, we plan to revisit this approach for future dataset extensions.	Summary: This paper introduces ViLP, a benchmark to investigate how VLMs relies heavily on textual priors, and ignore visual inputs. ViLP consists of 300 questions (each including a distractor fact), and three image-answer pairs (a prior answer and two test answers). With extensive experiments, the authors show that existing VLMs struggle with this benchmark. To improve the performance of VLMs, the authors also propose Image-DPO, a fine-tuning strategy (based on DPO approaches) that focus on the visual space/pixel space. The authors propose a method for generating training examples (seeded from COCO, Text2VQA, Visual Genome). Improvements of +2 to +3% are shown in their proposed benchmark. Claims And Evidence: - Claim 1: VLMs ignore visual inputs and are biased towards textual priors -- this is backed and supported by empirical results. Extensive experiments on their proposed benchmark (ViLP) support this claim. - Claim 2: this can be fixes via Image-DPO: experimental results show some gains with their proposed method. - Challenging dataset: the methodology for dataset creation is sound and backed by human/manual evaluation (Appendix A.2) Methods And Evaluation Criteria: The method, while simple, shows improvement over the baseline. The only problem is the lack of evaluation of more recent models that might perform better in the proposed benchmark (e.g., QwenVL, DeepSeekVL, etc). Image-DPO: leveraging existing datasets and modifying them via editing models/image generation approaches is time consuming, and the improvement seem marginal (~2 to 3%). However this is an interesting approach that future work could expand and build upon. Theoretical Claims: The proposed method seems correct, and aligns with the authors claims. Experimental Designs Or Analyses: Experimental analysis and design seems valid and sound. Supplementary Material: I reviewed all the supplementary material. Relation To Broader Scientific Literature: Prior works focus on benchmarking real-world data. VLMs tend to benefit from real-world common sense to answer questions in VQA datasets. The proposed benchmark revisits and shifts this particular limitation. Essential References Not Discussed: No essential references missing (to the best of my knowledge) Other Strengths And Weaknesses: The only weakness is the lack of comparison of their proposed Image-DPO to finetune more recent open VLMs (including LLaVA-NeXT, InstructBLIP, QwenVL and DeepSeekVL) Other Comments Or Suggestions: No additional comments Questions For Authors: Why is it necessary to finetune using additional synthetic images? Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: We sincerely appreciate Reviewer j6Xe QTDS’s thoughtful and encouraging feedback. Due to constraints in time and computational resources, we have prioritized addressing your question and will incorporate the suggested additional improvements in future revisions. --- > Why is it necessary to fine-tune using additional synthetic images? This is a very good point! We employ a comprehensive pipeline that uses multiple image-generation models to synthesize additional images from seed datasets. Our primary motivation is diversity: by incorporating a broader range of synthetic images, the VLM is exposed to more varied content and can, in turn, produce more diverse Question–Image–Answer (QIA) pairs. This process also implicitly leverages the knowledge locked in the existing image-generation models. Compared to relying solely on the original dataset, these additional QIA pairs enrich the training signal, helping the model learn more robust and generalizable representations. To verify this point, we conducted an ablation study using the same dataset as in our ImageDPO experiments. Specifically, we directly generated QA pairs from images in the COCO, VG, and Text2VQA datasets without additional modifications or synthetic generation, i.e., no synthetic images. We then applied image corruptions to produce altered versions of these images and utilized these corrupted-image QA pairs for ImageDPO finetuning. The results, shown below, indicate notable performance drops. This outcome underscores that leveraging synthetic data, rather than relying solely on the original datasets, benefits the DPO training process. \| \| $ViLP^F_{Score}$ \| $ViLP^F_{Prior}$ \| $NB_Q$ \| $NB_I$ \| $NB_G$ \| $NB_B$ \| MM-Vet \| $CHAIR^S \downarrow$ \| $CHAIR^I \downarrow$ \| \| ------------------------ \| ---------------- \| ---------------- \| ------ \| ------ \| ------ \| ------ \| ------ \| -------------------------------------- \| -------------------------------------- \| \| Ours \| 34.17 \| 39.33 \| 39.79 \| 45.47 \| 14.16 \| 68.45 \| 32.3 \| 45 \| 12.3 \| \| Without synthetic images \| 31.17 \| 38 \| 38.32 \| 44.17 \| 13.35 \| 67.69 \| 31.4 \| 47 \| 13.6 \| --- > The only weakness is the lack of comparison of their proposed Image-DPO to finetune more recent open VLMs (including LLaVA-NeXT, InstructBLIP, QwenVL and DeepSeekVL) Thank you for this valuable suggestion! We agree that comparing Image-DPO with more recent VLMs (e.g., LLaVA-NeXT, InstructBLIP, QwenVL, DeepSeekVL) would provide additional insights. However, due to limited time and computational resources during the rebuttal period, we are unable to conduct these comparisons comprehensively. We appreciate this feedback and plan to include parts of the models in our future revisions. Nonetheless, we believe our current results on LLaVA-v1.5 and Cambrian sufficiently demonstrate Image-DPO’s effectiveness and hope they convey the potential of our approach.	Summary: The paper presents an investigation into the over-reliance of vision-language priors in existing Vision-Language Models (VLMs). To enable it, the paper presents ViLP, a carefully designed benchmark which consists of Prior Answer that can be directly inferred from the question, and Test Answers which rely on visual cues. Their evaluation reveals that all methods significantly fall short of human annotations. To improve upon this shortcoming, ImageDPO is developed, the core of which is to develop pair-wise images where a corrupted image is generated from a real image using a VLM-based pipeline which uses techniques and models such as image editing and Grounded SAM. The authors theoretically prove ImageDPO and empirically show that when applied to OSS models such as LLaVA, ImageDPO improves upon other methods in solving ViLP. Claims And Evidence: 1. Overall, I like the paper structure. The paper introduces a new benchmark, has interesting experiments and ablations, and a DPO-based methods that help improve the benchmark. 2. The ViLP dataset is well motivated -- humans do well despite having distractors whereas VLM's clearly fail as shown by the paper's evaluation protocol. 3. ImageDPO is intuitive as well, using divergent image data to force the model to learn through image differences. The results are promising as well. Methods And Evaluation Criteria: 1. Overall, I am convinced with the methodology adopted in the paper. 2. I have the following question : a) Since data generation for DPO training uses image-editing, I wonder if there is some quality control established to threshold what is an accepted corrupted image? Theoretical Claims: 1. The paper derives the ImageDPO in Appendix B. I do not find issues with it. Experimental Designs Or Analyses: I checked the soundness of the experiments. I am convinced, overall. Supplementary Material: I reviewed the entire supplementary material. Relation To Broader Scientific Literature: The paper covers previous related work and evaluates a large range of models, both open and closed-sourced. Essential References Not Discussed: N/A Other Strengths And Weaknesses: 1. The paper could do with a bit of re-writing and typos. For example, Line 1152. Other Comments Or Suggestions: N/A Questions For Authors: Please check above. Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: We sincerely appreciate the positive review provided by Reviewer 1kEP, and are grateful that Reviewer 1kEP “likes the paper structure”, and “convinced with the methodology adopted in the paper”, believes “the ViLP dataset is well motivated”, and “the results are promising as well”. Below, we provide our detailed responses to your comments. --- > I have the following question: a) Since data generation for DPO training uses image-editing, I wonder if there is some quality control established to threshold what is an accepted corrupted image? That's a good point! Our guiding principle is to eliminate human involvement in order to make the pipeline fully automatic and scalable. While the generated data may contain some noise, we believe the pipeline is robust enough to help improve VLM performance, which is supported by the improvements in the experiments. For corrupted images, we control the hyperparameters of image editing, such as the strength of Gaussian blur and pixelation, to ensure that the corrupted versions are noticeably worse than the original ones. In the case of semantic corruption, we calculate the number of pixels that are modified and discard cases where the changes affect less than 5% of the total pixels, as such minor alterations may be too subtle to detect. --- > The paper could do with a bit of re-writing and typos. For example, Line 1152. Thank you for your thorough review! We have corrected the typo on line 1152 in the latest revision and will carefully proofread and refine the manuscript to enhance readability further. --- Rebuttal Comment 1.1: Comment: I am satisfied with the rebuttal and have no further questions. I keep my score.	Summary: This paper investigated the problem of over-reliance on visual language priors of Vision-Language Models (VLMs) instead of visual reasoning. To study this problem, this work further proposed a benchmark ViLP containing 900 question-image-answer triplets, covering both prior answers and test answers, revealing that GPT-4o only scored at ~66%. This work further proposed Image-DPO, a self-improving approach to enhance VLM visual reasoning performance by increasing reliance on visual inputs, applied on LLaVA-v1.5 and Cambrian. Claims And Evidence: The claims are supported by clear and convincing evidence. Methods And Evaluation Criteria: The proposed methods and benchmark dataset make sense. Theoretical Claims: The paper does not include theoretical claims. Experimental Designs Or Analyses: The overall soundness/validity of the experiments look good. Supplementary Material: Yes. For extra example illustration and details of Image-DPO. Relation To Broader Scientific Literature: No. Essential References Not Discussed: No. Other Strengths And Weaknesses: Strengths: * The paper is well-written and organized. The three criterions are clear and mathematical to understand how the vision-language priors are scoped. * The Image-DPO solution makes sense and is aligned with the motivation to highlight visual clues. Table 3 and 4 show that Image-DPO outperforms baselines and other preference optimization methods. Weaknesses & Questions: * The images are generated by DALL·E-3 and Flux, which look quite different from real-world images. The cartoon style may have impacts on VLMs as they are not directly trained on synthetic images. If real-world but rare images or realistic-style (or more styles) can be included to ablate the impacts of image styles. Therefore, the conclusions of this paper should be bounded by cartoon style. * It is not clear about the role of Proposition 1 as it is not mentioned in the main text after being introduced. * Some answers to the counterfactual questions are ambiguous. Take Figure 3 as examples, for the upper right example, it is hard to tell the cities are London and Paris, as Moscow can also build rivers or Tour Eiffel model. Also for the lower right example, the camel can also have a horse face by wearing a mask. There lacks strict definitions of these nouns and it is hard to tell the MLLMs' answers are not reasonable. The reasons might be that the models are forced to output a single word as answers. Actually, the explanations of the answer can provide more information on how the model observe the image. Other Comments Or Suggestions: Please see Weaknesses Questions For Authors: Please see Weaknesses. My main concerns are the style of images and the ambiguous answers due to the single-word evaluation setting. My current score is actually borderline. -------------- After reading the rebuttal, I decided to increase the score to accept. The analysis on the impact of image style is insightful and answered my questions. Since my major concern is fully addressed, I am happy to accept the paper. Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: We greatly appreciate the constructive feedback from Reviewer 4vBy. We seriously address your comments below. --- > Regarding the style of images. We appreciate this valuable point and acknowledge that some generated images appear cartoon-like or synthetic, due to the image generation tools selected—among the best available at the time. However, since our objective is to benchmark VLMs using out-of-distribution QIAs that are not readily available online, we adopt image generation models to achieve this goal – a motivation appreciated by Reviewer j6Xe “Prior works focus on benchmarking real-world data…The proposed benchmark revisits and shifts this particular limitation”. Regarding the cartoon-style concern, we would like to respectfully point out that current VLMs are commonly trained on datasets that include synthetic and cartoon-style images. For example, [LAION](https://laion.ai/blog/laion-aesthetics/), widely used in training VLMs, contains subsets focused on anime, cartoon, and aesthetics (filtered by community), reflecting the prevalence of synthetic imagery online. VLMs have shown robust performance on such data, and understanding synthetic visual representations remains an important capability, especially given humans’ ease in interpreting them. To assess the impact of image style, we regenerated a subset of 45 QIA pairs using GPT-4o’s latest image generation model to enhance realism ([Figure](https://postimg.cc/dZTtNwtW)). We then measured changes in model correctness when using these realistic images, with negative values indicating performance degradation. The results show that increased realism slightly reduces performance in most cases for the “Score” metric, while most effects on “Prior” are zero. These ablation results suggest that incorporating more realistic images may increase task difficulty, highlighting an important direction for future research. \| \| $ViLP^F_{Prior}$ \| $ViLP^F_{Score}$ \| $ViLP^P_{Prior}$ \| $ViLP^P_{Score}$ \| \| -\| - \| - \| -\| -\| \| GPT-4o \| 0 \| -2.2% \| 0 \| 0 \| \| GPT-4o-mini \| 0 \| -1.1% \| 0 \| -2.2% \| \| Claude-Sonnet-3.5 \| -2.2% \| -4.4% \| 0 \| -3.3% \| \| Claude-Opus-3 \| 2.2% \| -1.1% \| -2.2% \| -1.1% \| --- > Regarding Proposition 1. We would like to improve this point in the revision. For clarification, proposition 1 is the theoretical foundation of our Image DPO algorithm, showing that minimizing our proposed Image DPO loss corresponds to minimizing an upper bound on the RLHF loss. Unlike typical DPO modifications that adjust the output, our method fixes the output and alters the conditioning. Proposition 1 thus rigorously establishes the connection between our modified objective and the original DPO formulation. --- > Regarding the ambiguity and single-word evaluation. We thank the reviewer for highlighting the inherent ambiguity in counterfactual visual reasoning. Although ambiguous scenarios occur, humans typically resolve them effectively after initial confusion, as evidenced by the strong human performance reported in our benchmark (Table 2), where evaluators had access to identical textual and visual inputs as the VLMs. Thus, the noted "ambiguity" intentionally examines whether VLMs can match human performance under controlled conditions. Regarding single-word outputs, we highlight their evaluation advantages—including efficiency, speed, and reliability—when combined with our synonym and plural detection pipeline. In contrast, sentence-based evaluations relying on LLM inference incur API fees, computational costs, sensitivity to hyperparameters, and occasional unreliability due to incorrect reasoning. We appreciate the reviewer's concerns about potential limitations of single-word answers. To explore this, we conducted ablation studies prompting GPT-4o in a "chain-of-thought" manner, instructing it to reason before giving a sentence-level final answer. We evaluated these answers against ground truths using GPT, comparing both reasoning steps and final sentences with original single-word responses. Interestingly, allowing longer answers with more reasoning tokens did not yield performance benefits. As shown in ([Figure](https://postimg.cc/XrpqpR57)), correct reasoning (second pic.) can still produce incorrect conclusions, and sometimes the reasoning process itself may be flawed (third pic.). Quantitatively, GPT-4o’s performance on "Prior" slightly improved from 91% to 92.67%, whereas on "Score" it decreased from 66.17% to 55.5%. Given that "Prior" aligns closely with language priors and "Score" represents out-of-distribution scenarios, we hypothesize that longer outputs may unintentionally increase reliance on priors during reasoning.	null	null	null	null	null	null
Asymmetric Decision-Making in Online Knowledge Distillation: Unifying Consensus and Divergence	Accept (poster)	Summary: This article introduces Asymmetric Decision-Making (ADM), an online knowledge distillation (OKD) method that enhances both teacher and student models through consensus and divergence learning. Unlike other traditional KD methods this method names as ADM actively refines the teacher while improving the student, making it a mutual learning framework. It integrates seamlessly with existing KD techniques and achieves state-of-the-art results across CIFAR-100 and ImageNet. Claims And Evidence: This article presents ADM as a superior online knowledge distillation method, but some of the claims lack sufficiently rigorous ablation studies and broader benchmarking. The improvement over stronger baselines like DKD and DisWOT is marginal, raising questions about statistical significance. Additionally, while ADM is tested across multiple settings, results on larger-scale datasets and diverse architectures remain limited, making its generalizability unclear. The theoretical justification for why ADM’s asymmetric learning outperforms standard KD is also underdeveloped and this will rely heavily on empirical results. Methods And Evaluation Criteria: The article employs reasonable evaluation criteria, using FID, IS, and accuracy metrics across standard benchmarks like CIFAR-100 and ImageNet, which are widely accepted for knowledge distillation research. The inclusion of both offline and online KD comparisons strengthens the empirical evaluation. The choice of hyperparameters is well-documented, but my concern is with not performing further sensitivity analysis. Theoretical Claims: The claims made in the paper are generally supported by empirical evidence and shows ADM's improvements over baseline KD methods across various benchmarks. But, the lack of rigorous theoretical justification for why ADM consistently enhances both student and teacher models leaves some claims insufficient. Experimental Designs Or Analyses: The experimental design follows standard knowledge distillation benchmarks, using datasets like CIFAR-100 and ImageNet with multiple teacher-student configurations. The ablation study in Table 13 looks at incremental gains when component analysis is done. Further, statistical significance testing is absent and makes it unclear whether improvements are consistent across multiple runs. Supplementary Material: Yes. I have gone through it. Relation To Broader Scientific Literature: The article builds on prior work in knowledge distillation, particularly online and asymmetric distillation methods, by introducing ADM to enhance student-teacher interactions dynamically. Essential References Not Discussed: NA Other Strengths And Weaknesses: The article presents an interesting attempt at improving knowledge distillation efficiency, but it lacks originality as many of its ideas are incremental extensions of prior work. The writing is clear and easy to follow, the significance of the contributions is limited due to weak empirical validation and insufficient theoretical grounding. Additionally, some claims are overstated given the lack of rigorous ablation studies and comparative analysis against stronger baselines. Other Comments Or Suggestions: 1. Your approach builds upon existing knowledge distillation frameworks but lacks a theoretical analysis. Can you formally derive the expected generalization benefits of your method compared to standard distillation techniques, possibly using PAC-Bayesian or information-theoretic bounds? Without such an analysis, how can one be certain that the improvements are not artifacts of dataset-specific heuristics? 2. Your empirical evaluation primarily focuses on a limited set of model architectures. Have you tested your method on fundamentally different architectures (e.g., transformers, graph neural networks) beyond CNN-based models? If not, how can we ensure that the claimed improvements generalize beyond the specific experimental setup? 3. Your method introduces multiple hyperparameters and auxiliary components. Have you conducted a comprehensive sensitivity analysis to determine the robustness of these choices? Specifically, is the method’s performance stable across different hyperparameter settings, or does it require extensive tuning? 4. The empirical results compare against standard distillation techniques but do not include recent state-of-the-art methods such as contrastive-based distillation or self-supervised distillation approaches. How would your method perform against these stronger baselines, and would the relative improvements remain significant? 5. Given the additional steps introduced by your method, have you analyzed the computational trade-offs? Specifically, how does the training time scale with increasing dataset sizes and model complexity, and is the overhead justified given the marginal performance improvements reported? Questions For Authors: Please see other comments section. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Q1: lack of rigorous theoretical justification A1: Firstly, we assert that the proposed ADM method adheres to theoretical derivations. To substantiate this claim, we provide additional theoretical support: # Information-Theoretic Analysis of Asymmetric Decision-Making (ADM) ## 1. Notation and Fundamental Assumptions ### Symbolic Convention - Input data: $ $X \in \mathcal{X}$ $ - Task labels: $ $Y \in \mathcal{Y}$ $ - Student features: $ $Z_s = f_s(X) \in \mathbb{R}^{H \times W \times C}$ $ - Teacher features: $ $Z_t = f_t(X) \in \mathbb{R}^{H \times W \times C}$ $ - Spatial indices: $ $(i,j) \in \{1,\dots,H\} \times \{1,\dots,W\}$ $ - consensus mask in Eq6[L196-L200 in paper]: $ $M_f = \frac{1+\mathcal{S}}{1+ \bar {\mathcal{S}}}$ $ - divergence mask in Eq6[L183-L187 in paper]: $ $M_d = \frac{1-\mathcal{S}}{1- \bar {\mathcal{S}}}$ $ ### Information-Theoretic Quantities - Entropy: \[ $H(Z) = -\mathbb{E}_{Z \sim p(Z)}[\log p(Z)]$ \] - Mutual Information: \[ $I(Z; Y) = H(Y) - H(Y\|Z)$ \] - Conditional Mutual Information: $I(Z_s; Z_t \| X) $= ${E_X} \left[ D_{\text{KL}}\left( p(Z_s,Z_t\|X) \,\\|\, p(Z_s\|X)p(Z_t\|X) \right) \right]$ --- ## 2. Consensus Learning: Feature Alignment via Mutual Information Maximization ### Objective Function The student model maximizes mutual information in foreground regions: \[ $\mathcal{L}_{\text{co}} = -I(Z_s^{M_f}; Z_t^{M_f}), \quad \text{where } Z^{M_f} = Z \odot M_f$ \] ### Variational Lower Bound Theorem 1 (Barber-Agakov Variational Bound): $I(Z_s^{M_f}; Z_t^{M_f}) \geq {E}_{Z_s^{M_f}, Z_t^{M_f}} [ \log q(Z_t^{M_f} \| Z_s^{M_f}) ] + H(Z_t^{M_f})$ Minimizing the negative log-likelihood yields: \[$ {L}_{co} = E [ -\log q(Z_t^{M_f} \| Z_s^{M_f}) ]$ \] ### Information Bottleneck Interpretation Constraining foreground alignment enforces: \[$ \max \, \left[ I(Z_s; Y) - \beta I(Z_s; X) \right] \quad \text{s.t. } I(Z_s^{M_f}; Z_t^{M_f}) \geq C$ \] Resulting in the lower bound: \[$ I(Z_s; Y) \geq I(Z_t^{M_f}; Y) - \beta I(Z_s; X) + C$ \] --- ## 3. Divergence Learning: Entropy Maximization for Feature Space Expansion ### Objective Formulation The teacher model maximizes entropy in low-consensus regions: ${L}_{di}$ = ${-H(Z_t^{M_d})}+ \lambda {I(Z_t^{M_d}; Y)}$ ### Jaynes' Maximum Entropy Principle Lemma 1 (Optimal Feature Distribution): Under constraint $ $I(Z_t^{M_d}; Y) \geq \epsilon $$, the optimal distribution satisfies: \[$ p^(Z_t^{M_d}) \propto \exp\left( \lambda \log p(Y \| Z_t^{M_d}) \right)$ \] ### Coverage Capacity Analysis Theorem 2 (Feature Space Coverage): \[$ \mathcal{R}(Z_t) \geq \sqrt{2 H(Z_t^{M_d})}$ \] where $ $\mathcal{R}(Z_t)$ $ denotes the radius of feature coverage. --- ## 4. Convergence Analysis via Dynamical Systems ### Coupled Dynamics The training process is modeled as: \[$ \begin{cases} \frac{d}{dt} I(Z_s; Y) = \alpha \left( I(Z_t; Y) - I(Z_s; Y) \right) \\ \frac{d}{dt} H(Z_t) = \beta \left( H(Z_t) - H(Z_s) \right) \end{cases}, \quad \alpha, \beta > 0$ \] ### Lyapunov Stability Proof Theorem 3 (Global Convergence): Define the Lyapunov function: \[$ V(t) = \left( I(Z_t; Y) - I(Z_s; Y) \right)^2 + \left( H(Z_t) - H(Z_s) \right)^2$ \] The time derivative satisfies: \[$ \dot{V}(t) = -2\alpha \left( I(Z_t; Y) - I(Z_s; Y) \right)^2 - 2\beta \left( H(Z_t) - H(Z_s) \right)^2 \leq 0$ \] Guaranteeing convergence to equilibrium $ $I(Z_s; Y) = I(Z_t; Y)$ $ and $ $H(Z_t) = H(Z_s) $$. --- ## 5. Empirical Validation and Error Bounds ### Fano's Inequality Application Theorem 4 (Classification Error Bound): \[$ P_e \geq \frac{H(Y\|Z_s) - 1}{\log \|\mathcal{Y}\|} \implies P_e^{\text{ADM}} \leq \frac{H(Y) - I(Z_s; Y) - 1}{\log \|\mathcal{Y}\|}$ \] --- ## 6. Generalization to Structured Tasks ### Semantic Segmentation Pixel-wise regional mutual information: \[$ I_{\text{region}}(Z_s, Z_t) = \sum_{c=1}^C I(Z_s^c; Z_t^c)$ \] ### Diffusion Model Distillation Temporal trajectory alignment: \[$ I_{\text{traj}}(Z_s, Z_t) = \sum_{t=1}^T \gamma^{T-t} I(Z_s^t; Z_t^t), \quad \gamma \in (0,1)$ \] --- Q2: statistical significance testing* A2: As detailed in lines 272-273 of the paper, the majority of experiments were conducted multiple times, and we report the mean results. This approach demonstrates the robustness and consistency of the performance improvements. --- Q3: analyzed the computational trade-offs A3: Please refer to lines 241-247 of the paper. ADM introduces no additional trainable parameters, and the incremental computational cost is significantly minimal compared to the original setup. --- Rebuttal Comment 1.1: Comment: Although the proofs are very generic, overall, I am happy with some of the clarifications and will raise the score to 3. All the theoretical proofs should offer more rigorous maths and reasoning.	Summary: This paper proposes an Asymmetric Decision-Making (ADM) approach for online knowledge distillation that adaptively fosters consensus learning for students while continuously encouraging teachers to explore harder features, thereby boosting performance on tasks like classification, semantic segmentation, and diffusion distillation by unifying feature-based and logit-based distillation techniques. Claims And Evidence: Yes Methods And Evaluation Criteria: Yes Theoretical Claims: No, this paper does not involve theoretical claims. Experimental Designs Or Analyses: Yes. The authors compared their method with current state-of-the-art approaches to common visual distillation tasks. I find the experiments to be quite comprehensive overall. A potential shortcoming may be that they did not evaluate the method’s effectiveness in the increasingly popular large-model distillation settings. Supplementary Material: I did not find any supplementary materials. Relation To Broader Scientific Literature: This study analyzes the common issues in previous online distillation work and accordingly proposes a novel method to separately handle the similar and different features between the teacher and student models. Essential References Not Discussed: To the best of my knowledge, I think the authors have considered the relevant works related to their study. Other Strengths And Weaknesses: Strengths: 1. The discovered issues/problems appear very interesting and may inspire further progress in the knowledge distillation community. 2. The experiments are extensive. Additionally, more visual analyses are provided to explain the effectiveness of the proposed method. Weaknesses： 1. There seems to be a gap between the motivation of the proposed method and its findings. Why is it necessary to force the teacher model to explore background regions? Intuitively, foreground regions seem more important. Additionally, from the final results, the performance improvement brought by the proposed method also appears to be marginal. 2. When introducing the method, the authors should explain why they made such design choices instead of merely mentioning them in passing. 3. With regard to the phenomenon observed in Figure 1, could the authors provide additional examples from various datasets to support their findings? Optionally, could they indicate what percentage of instances exhibit this phenomenon? Other Comments Or Suggestions: See above Questions For Authors: Does the expression in lines 69-70 have any errors? "The first row shows that discrepancy regions between teacher and student’s features are more concentrated on foreground object regions after Vanilla training." Should it be "discrepancy" or "similarity"? The current expression seems to contradict the first finding. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Q1: gap between the motivation of the proposed method and its findings A1: The function of $L_{di}$ is to extract knowledge from unexplored foreground regions within the background areas, rather than merely utilizing background information. These regions present a challenge to the model, and without constraints, the model's limited learning capacity makes it difficult to autonomously explore them. As evidenced in Table 13, when $L_{di}$ is applied alone, the teacher model's performance improves by 0.29 (73.78 vs. 74.07), thereby increasing the upper bound of the student model's distillation performance. This demonstrates the necessity for the teacher model to continuously extract challenging foreground knowledge from the background regions. We posit that in the online distillation setting, both $L_{co}$ and $L_{di}$ must work in synergy. If only $L_{co}$ is applied without $L_{di}$, the teacher model cannot persistently explore more difficult foreground regions. Conversely, if only $L_{di}$ is applied without $L_{co}$, the student model cannot effectively learn the foreground regions identified by the teacher model from easy to difficult, failing to achieve the intended mutual enhancement of both models' performance. Q2: explain why they made such design choices instead of merely mentioning them in passing. A2: In the introduction, we outlined the rationale behind ADM based on two key findings. The proposed method is straightforward yet effective. Q3: Does the expression in lines 69-70 have any errors?. A3: There is no error here. Figure 1 illustrates the changes in non-similar regions when comparing our method with vanilla training, which corresponds to Finding 2. It does not address the description of similar regions in Finding 1. --- Rebuttal Comment 1.1: Comment: Thank you for your detailed rebuttal and the clarifications provided. The additional explanations are helpful in clarifying several aspects of the proposed method. However, as previously emphasized, it would be more convincing if the authors could provide additional examples similar to those in Figure 1 to support their findings. --- Reply to Comment 1.1.1: Comment: Thank you for your thoughtful response. We have augmented the anonymous link with additional visualizations analogous to Figure 1. The findings depicted in Figure 1 demonstrate consistent patterns rather than individual random variations. https://anonymous.4open.science/r/ICML2025-rebuttal-ADM-CF21/rebuttal-vis-more.pdf	Summary: This paper addresses online knowledge distillation (OKD), a single-stage method where teacher and student models learn simultaneously. The authors focus on improving OKD performance by exploring intermediate feature alignment. Specifically, they propose an Asymmetric Decision-Making (ADM) strategy to unify consensus and divergence feature learning. The authors perform an analysis using Class Activation Mapping (CAM) to understand how intermediate feature alignment impacts model behavior in OKD. They observe that: (i) The similar features between student and teacher models are predominantly concentrated on foreground objects, suggesting students prioritize learning these ”easy” patterns. (ii) Teacher models highlight foreground objects more than students, indicating an underutilized capacity for discriminative feature discovery. Divergent features, which may explain teacher superiority, are also concentrated in foreground regions. Based on these findings, they introduce ADM, a framework that uses spatially-aware feature modulation to manage consensus and divergence. ADM applies role-specific learning: — Students amplify feature attribution in teacher-aligned foreground regions. — Teachers intensify exploration of under-activated foreground patterns. The paper claims the following contributions: (1) Identification of foreground-centric feature consensus and teacher-student attribution gaps through interpretability analysis. (This is challenging conventional assumptions about knowledge transfer in online settings.) (2) The ADM strategy, which uses spatial similarity to allocate attention in feature maps, boosting student attribution and reinforcing teacher strengths. (3) Experimental validation showing that ADM outperforms state-of-the-art OKD methods in various tasks, including online KD, offline KD, semantic segmentation, and diffusion distillation. It is shown that the proposed method provides SOTA results in several occasions. Claims And Evidence: The claims made in the submission are supported by clear and convincing evidence. Methods And Evaluation Criteria: They do. Theoretical Claims: The paper does not make any substantial theoretical claims. Experimental Designs Or Analyses: The experimental design and analysis of the paper is sound and valid. Supplementary Material: Yes. Relation To Broader Scientific Literature: I feel the paper has done a good job positioning itself to broader literature in distillation and online distillation. It clearly identifies shortcomings of previous approaches and challenges conventional wisdom regarding how students learn in online distillation settings. It has also provided extensive experimental comparison in several datasets including ImageNet-1k. Essential References Not Discussed: I feel the paper has done a fair job at discussing related work. This is not essential but maybe the authors would like to discuss (or compare their work with, at least in the offline setting): — Wonpyo Park, Dongju Kim, Yan Lu, and Minsu Cho. Relational knowledge distillation. In Proceedings of the IEEE/CVF conference on computer vision and pattern recognition, pages 3967–3976, 2019. and related techniques a bit further. Other Strengths And Weaknesses: I find this paper to be well-written and compelling, with a novel method and robust experimental results. I have no major concerns. Other Comments Or Suggestions: No other comments. Questions For Authors: I do not have any questions for the authors. Code Of Conduct: Affirmed. Overall Recommendation: 4		Summary: This paper proposes an online knowledge distillation method to build a student model by knowledge transfer from larger teachers which are trained together with the student. The key assumption is that the student and teachers are more likely to share similar features in foreground rather than background areas. With this assumption, the paper formulates two learning objectives, namely consensus learning for enforcing student’s attention on foreground objects when making predictions, and divergence learning for encouraging teachers to explore foreground patterns that are overlooked by the student. The proposed online knowledge transfer method has been evaluated extensively as a plug-and-play component to be incorporated with multiple baseline approaches on several tasks, including image classification, semantic segmentation, and image generation. Claims And Evidence: Most of the claims are made with support and evidence, but the effects of consensus learning need to be further clarified. As stated at L50 (right) and L192 (left), the consensus loss ($L_{co}$) is applied to the student to amplify feature attribution in teacher-aligned foreground regions, whilst the divergence loss ($L_{di}$) is applied to the teacher for exploration of under-activated foreground patterns. However, according to Table 13, the benefit brought by $L_{di}$ to the student is more significant than that by $L_{co}$. These results are a bit inconsistent with the expected contribution of the two learning objectives. Methods And Evaluation Criteria: The proposed ideas are quite intuitive, and most of the adopted components are well justified. The only unclear part to me is whether the gradient from $L_{co}$ and $L_{di}$ propagates back to the cosine similarity matrix ($S$) via the attention scores $A$? From my understanding, the cosine similarity matrix $S$ is used only to highlight features in different regions for making class predictions. In this case, I would assume gradients only pass to highlighted features from class prediction errors (i.e. cross-entropy losses) but not the student-teacher similarity matrix. However, the explicit gradient detach (GD) operation used in Fig.3 is not applied to the ADM module. It is ambiguous whether these two losses ($L_{co}$ and $L_{di}$) also take effect to optimise student-teacher alignment, similar to the role of $L_{feat}$ defined in Eq.(5). Theoretical Claims: N/A Experimental Designs Or Analyses: The proposed method is evaluated comprehensively with just a few concerns: + Evaluation of the proposed method upon vision transformer-based (ViT) models is missing. The paper conducts an extensive evaluation based on different combinations of teacher’s and student’s architectures. However, as a strong backbone architecture widely adopted in the CV community, ViT is missing as neither the student nor teachers. + In the experiment on the extension to multiple teachers and/or students (Table 11), the proposed ADM works together with DML. However, the 1T2S and 2T1S variants of DML are missing as important baselines. Supplementary Material: N/A Relation To Broader Scientific Literature: The finding that similar features across different models are more likely to appear in the foreground regions is novel and inspiring. Essential References Not Discussed: No Other Strengths And Weaknesses: Strengths: The paper is generally well-written and easy to follow. The findings of the aligned features between student and teachers are more likely to lie in foreground regions is interesting. The evaluation of the proposed method is comprehensive. Weaknesses: + The experimental setup of the extension to diffusion distillation is unclear. + The visualisation provided in Fig.4 and Fig.5 is hard to understand. For Fig.4, I failed to see how the concentrated regions evolve at different steps. For Fig.5, it is stated at L412 (right) that the visualisations are presented from three perspectives, but what perspectives they are is unclear. + There are some confusing statements in the experiment analysis, and the disorder of the tables makes them hard to read. For example, Table.8 and Table.9 are followed by Table.12, all of which come after Table.15. Besides, I failed to find Table.10 in the manuscript. It is confusing to me how the statement "Evidently, ..." made at L329 (right) is evident without any references. Other Comments Or Suggestions: See comments above. Questions For Authors: See comments above. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Q1: the effects of consensus learning need to be further clarified A1: Applying $L_{co}$ to the student model does not imply that the performance improvement of the student model is primarily due to $L_{co}$. As evidenced in Table 13, when $L_{co}$ is used alone, the teacher model's performance remains unchanged at 73.78 (73.78 vs. 73.78), which inherently limits the potential improvement of the student model through distillation. Conversely, when only $L_{di}$ is applied, the teacher model's performance increases by 0.29 (73.78 vs. 74.07), thereby raising the upper bound of the student model's distillation performance. Hence, although $L_{di}$ is applied to the teacher model, it significantly enhances the student model's performance. We contend that in the online distillation setting, both $L_{co}$ and $L_{di}$ need to work synergistically. If only $L_{co}$ is used, the teacher model cannot continuously explore more challenging foreground regions. Conversely, if only $L_{di}$ is used, the student model cannot effectively learn the foreground regions identified by the teacher model from easy to difficult, failing to achieve the intended mutual enhancement of both models' performance. Q2: whether the gradient from Lco and Ldi propagates back to the cosine similarity matrix (S) via the attention scores A? A2: No gradients are propagated in there. Please refer to the code in Appendix L629, where the detach operation is implemented. Q3: Evaluation of the proposed method upon vision transformer-based (ViT) models is missing. A3: We conducted experiments using DiT-based diffusion model distillation, which may indirectly support the effectiveness of our method in transformer-based distillation scenarios. Q4: the 1T2S and 2T1S variants of DML are missing as important baselines. A4: We adhered to the experimental settings outlined in the SwitOKD paper to demonstrate the extendibility of our approach for training multiple networks. Q5: The experimental setup of the extension to diffusion distillation is unclear. A5: As detailed in lines L292-L296 of the referenced paper, for CIFAR10, we followed the experimental settings from the RCFD paper. For DiT model distillation, we adhered to the experimental settings from the DiT paper. All parameters were reused from the original papers without any modifications. Q6: The visualisation provided in Fig.4 and Fig.5 is hard to understand. A6: There was a typo error. The third comparison is included in the appendix, while only two comparisons are presented here.	null	null	null	null	null	null
DSP: Dynamic Sequence Parallelism for Multi-Dimensional Transformers	Accept (poster)	Summary: The paper introduces Dynamic Sequence Parallelism (DSP) as a novel approach to sequence parallelism for multi-dimensional transformers. It addresses the limitations of embedded sequence parallelism, which shards along a single sequence dimension and incurs significant communication overhead. DSP dynamically switches the parallel dimension of sequences during computation with an efficient resharding strategy. The paper claims that DSP reduces communication costs, enhances adaptability, and is easy to use, offering significant throughput improvements. Claims And Evidence: The paper claims that DSP improves throughput and reduces communication volume for multi-dimensional transformers. While experiments show improvements, the evidence is limited, primarily focusing on video generation models. The authors mention that "each dimension is processed by a corresponding transformer block, which is a common strategy in many applications". Could the authors add citations there and add specific examples? Methods And Evaluation Criteria: The paper evaluates DSP using video generation models, which is a relevant application for multi-dimensional transformers. The comparison with state-of-the-art sequence parallelism methods (DeepSpeed-Ulysses, Megatron-SP, Megatron-LM, and Ring Attention) is appropriate. However, the evaluation is narrow. Theoretical Claims: The paper includes a communication analysis comparing DSP with other sequence parallelism methods. It claims DSP minimizes communication costs. Experimental Designs Or Analyses: The experimental design focuses on demonstrating DSP's superiority in video generation models by varying sequence lengths and comparing throughput and communication volume. Supplementary Material: The paper includes supplementary material in the appendices, such as implementation details and additional experimental results. Relation To Broader Scientific Literature: The paper discusses relevant prior work, including data parallelism, tensor parallelism, pipeline parallelism, and sequence parallelism. It positions DSP as a novel abstraction of sequence parallelism for multi-dimensional transformers. Essential References Not Discussed: [1] is an paper that presents the general SPMD intra-layer parallelism, which should be discussed. I think this paper proposes a new sharding annotation for a specific model. [1] Xu, Yuanzhong, et al. "GSPMD: general and scalable parallelization for ML computation graphs." arXiv preprint arXiv:2105.04663 (2021). Other Strengths And Weaknesses: Strengths 1. The paper addresses scaling multi-dimensional transformers, an important problem. 2. The concept of DSP is clearly presented. 3. DSP has good adaptability and flexibility. 4. The paper provides a user-friendly API for DSP. Weaknesses: 1. The empirical evaluation is limited. 2. Performance gains are not convincingly demonstrated for long sequences. Other Comments Or Suggestions: 1. The paper should include more comprehensive experiments on diverse multi-dimensional transformer architectures. 2. The authors should provide a more thorough analysis of the trade-off between performance and accuracy. Questions For Authors: 1. How can DSP be further optimized to provide more substantial speedups in scenarios with small overhead from baseline methods? 2. Is it possible to extend it to other models other than multi-dimensional transformers? Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We sincerely thank the reviewer o73Q for the valuable questions and comments. For the concerns and questions, here are our responses: Q1: Performance gains are not convincingly demonstrated for long sequences A1: We thank the reviewer for this important question and have conducted additional experiments to robustly demonstrate DSP’s performance on long sequences. Experiment1: Communication latency comparison. \| method \| latency with 0.5M seq (ms) \| latency with 8M seq (ms) \| \| :- \| :- \| :- \| \| DSP \| 614 \| 2914 \| \| DS-Ulysses \| 1228 \| 5828 \| \| Megatron-SP \| 5616 \| 51908 \| Analysis1: DSP consistently reduces communication latency across sequence lengths. Experiment2: End-to-end speedup for 8M long sequecnes with two seuqence shapes A:[8192, 1024] and B:[8, 1048576]. \| method \| communication time for A (s) \| computation time for A (s) \| communication time for B (s) \| computation time for B (s) \| \| :-- \| :-- \| :-- \| -- \| -- \| \| DSP \| 2.8 \| 34.3 \| 2.9 \| 362.1 \| \| DS-Ulysses \| 5.8 \| 34.3 \| 5.8 \| 362.2 \| \| Megatron-SP \| 51.9 \| 37.2 \| 51.9 \| 365.6 \| Analysis2: DSP significantly reduces communication time for both shapes. However, end-to-end speedup varies: shape A benefits more due to lower computation time, while shape B’s longer single dimension increases attention computation, dominating total time. This shows DSP’s communication efficiency, though overall gains depend on computation complexity. Improvement plan: We have added a detailed discussion of these results in the Appendix of the revised manuscript. Conclusion: 1. DSP delivers consistent communication reductions across sequence. 2. End-to-end speedup depends on computation time, which varies with sequence dimensionality. Q2: Is it possible to extend it to other models other than multi-dimensional transformers? A2: DSP’s simple yet general design extends beyond multi-dimensional transformers to various multi-dimensional neural networks, including conv+attention models (e.g., 2D-UNet, 2D-VAE), AlphaFold, and pure conv. For example, in 2D-UNet, DSP enables efficient resharding between computations along different dimensions: $ x -> conv\\_dim(1) -> attn\\_dim(1) -> DSP\\ reshard -> conv\\_dim(2) -> attn\\_dim(2) -> y$ Q3: The paper should include more comprehensive experiments on diverse multi-dimensional transformer architectures. A3: We thank the reviewer for raising this point. Main stream multi-dimensional transformer architectures typically fall into two categories: 1. Dimension-by-dimension processing as shown in our paper: $x -> transformer\\_dim1(x) -> transformer\\_dim2(x) -> y$ 2. Dimension-by-dimension with cross-dimensional interactions: $x -> transformer\\_dim1(x) -> transformer\\_dim2(x) -> transformer\\_cross\\_dims(x) -> y$ Experiment: End-to-end performance on the second architectures on Transformer-2D 3B with 8 GPUs. \| method \| throughput (samples/s) \| \| :--- \| :--- \| \| DSP \| 1.42 \| \| DS-Ulysses \| 1.15 \| \| Megatron-SP \| 0.40 \| There many be some changes within the transformer (e.g., layernorm, positional embedding) but they don't affect much for the results. Improvement plan: We have added a detailed discussion of these results in the Appendix of the revised manuscript. Conclusion: Our method is able to deliver stable performance on main-stream multi-dimensional transformer architectures. Q4: The authors should provide a more thorough analysis of the trade-off between performance and accuracy. A4: DSP is designed to preserve accuracy strictly, introducing only negligible errors (1e-7 to 1e-8) due to communication. For example, in video generation tasks, DSP outputs are identical to the originals. Q5: How can DSP be further optimized to provide more substantial speedups in scenarios with small overhead from baseline methods? A5: While DSP already minimizes communication volume effectively, further speedups are possible by overlapping communication with computation. DSP’s lightweight communication and decoupling from computation make it ideal for asynchronous execution, hiding latency behind computation. Q6: Essential references not discussed (GSPMD) A6: We appreciate the reviewer highlighting this point. Improvement plan: In the revised manuscript, we have added a detailed discussion of GSPMD and other relevant works in the related work section, ensuring a more comprehensive literature review. --- Rebuttal Comment 1.1: Comment: Thanks for the response, which addresses most of my concerns. I have updated the score.	Summary: This paper presents DSP (Dynamic Sequence Parallelism) for scaling multi-dimensional transformers. The solution adaptively switches parallel dimensions by reshuffling data with all-to-all communication between multiple GPUs. The evaluation results demonstrate that parallelizing across sequence dimensions can reduce the communication overhead and improve throughput compared to the existing methods that shards the sequence dimension. Claims And Evidence: The proposed method is mostly clear and makes sense. However, I think there should be an evidence to claim DSP's generalizability and the future work seems to be not directly related to the proposed solution, or it could be too optimistic. Methods And Evaluation Criteria: The experiments techincally sound, but it lacks the detailed analysis in the communication time/computation time, etc. Also, it is not clear that why the input sequence length needs to be fixed in their experiment. I think the experiment should show the scalability according to the sequence length, because it may impact the accuracy of the model, especially the video generation use case. Theoretical Claims: Yes, on the complexity analysis. Experimental Designs Or Analyses: - Please add an experiment that shows DSP's scalability according to the model size. - There should be a breakdown analysis, showing communication overhead. - I think memory layout change/reshape/transpose may incur mem copies, so that the memory cost (both capacity and time) could be significant. There should be analysis on this. Supplementary Material: Yes. Especially the illustration was helpful for the understanding. Relation To Broader Scientific Literature: The proposed solution tackles the emerging problem but its applicability shown in the evaluation seems to be limited. Essential References Not Discussed: N/A Other Strengths And Weaknesses: N/A Other Comments Or Suggestions: N/A Questions For Authors: Please see questions raised in other sections. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We sincerely thank the reviewer qVhs for the valuable questions and comments, especially about the evalutions which are indeed not detailed enough. We have conducted the following experiments to make our evalutions more comprehensive and have added them to the experiment section or appendix or in the latest version. Q1: DSP's scalability according to the model size. A1: We conduct an end-to-end analysis for DSP with 3B, 7B and 13B using 1M tokens. \| GPU num \| model size \| TFLOPs per GPU \| \| ------- \| ---------- \| -------------- \| \| 16 \| 3B \| 242.20 \| \| 16 \| 7B \| 262.29 \| \| 16 \| 13B \| 259.77 \| Analysis: * When scale from 3B to 7B, although the communication cost increase, the performance grows because the compuation density increases more. * When scale from 7B to 13B, the benefits of denser computation is marginal. The total throughput decrease because of more communication cost, but the loss is still marginal. Q2: Breakdown analysis of communication overhead. A2: We breakdown for communication overhead/actual computation for DSP under weak scaling condition using Transformer-2D 3B: \| GPU num \| computation time \| communication time \| \| ------- \| ---------------- \| ------------------ \| \| 8 \| 90.1% \| 9.9% \| \| 16 \| 75.2% \| 24.8% \| Analysis: The communication costs grows significantly for inter-node communication even for our method. Highlight the necessity of efficient parallelism. If you need more experiments for each parallel or model, please tell us! Q3: Cost of layout change/reshape/transpose. A3: Let's analyze from memory and speed: For memory, this usually will not cause much fragmentation as we show in Figure 9 (Line 447) because of the following reasons: * The sequence have already been splitted. Therefore there will be only a part of sequence on one device, reducing the overhead to layout change. * DSP changes actually less frequent than any other methods, lead to less overhead. * Duing training, the layout of a sinlge sequence does not affect overall memory cost because parameter and activation is much larger than it. To further clarify this, we make experiments about the memory overhead of our method: \| GPU num \| memory overhead \| \| ------- \| --------------- \| \| 8 \| 0.5% \| \| 16 \| 0.4% \| For speed, we conduct an experiment to evaluate the time of changing layout and communication: \| GPU num \| layout change time \| communication time \| \| ------- \| ------------------ \| ------------------ \| \| 8 \| 5.2% \| 94.8% \| \| 16 \| 4.1% \| 95.9% \| Analysis: * The layout changing time is much less than the communication time. But still takes 5.2% of total time. * As the sequence and gpu number get larger, the layout change time become less as communication takes more time. * To fully elimiate the layout change's time, we can overlap communication with layout change. * We use activation checkpointing in training. Conclusion: * Memory: The layout changes have little impact on memory cost. * Speed: The layout changes will occupy 4.1%-5.2% of communication time, but can be avoided by overlapping. And it will reduce as sequence and gpu becomes larger.	Summary: The paper introduces a new method, called Dynamic Sequence Parallelism (DSP), to scale multi-dimensional transformers efficiently by dynamically switching the parallel dimension at different computation stages. Unlike existing sequence parallelism techniques (e.g., Megatron-LM, Megatron-SP, DeepSpeed-Ulysses, Ring-Attention), which shard along a single sequence dimension, DSP exploits independent computation across multiple dimensions. By dynamically resharding between computation stages with an efficient all-to-all communication strategy, DSP significantly reduces communication overhead and improves throughput efficiency. The experiments, conducted on 128 NVIDIA H100 GPUs, demonstrate that DSP achieves up to 10x higher throughput while reducing communication volume by at least 50% compared to state-of-the-art methods. Claims And Evidence: The claims on the throughput improvements (32.2% to 10×) and communication volume reduction (≥50%) are supported by experiments on 128 H100 GPUs. However, some claims need stronger evidence. My only concern is about efficiency across different hardware as all experiments use H100 GPUs, with no analysis on other GPUs. Methods And Evaluation Criteria: Yes, the evaluation aligns well with the problem, using 128 H100 GPUs to benchmark throughput, communication, and memory across long sequences, with comparisons against Megatron-LM, DeepSpeed-Ulysses, and Ring-Attention. However, a Pareto-optimal trade-off analysis and tests on older GPUs or real-world tasks would strengthen the evaluation. Theoretical Claims: The paper lacks a formal theoretical analysis of DSP’s efficiency. While it provides empirical results showing improved throughput and communication efficiency, there are no formal proofs or mathematical derivations to support its claims. Experimental Designs Or Analyses: Yes, the experiments are sound and appear correct. Supplementary Material: Yes, all parts are reviewed. Relation To Broader Scientific Literature: This work definitely helps to perform experiments on large language models more efficiently and faster. Essential References Not Discussed: N/A Other Strengths And Weaknesses: Strengths: -- Dynamically adjusts the sharding dimension based on the computation stage -- Significant improvements on throughput by 32.2% to 10× over existing methods. -- Lower communication cost by at least 50%. -- It scales efficiently across multiple GPUs. Weaknesses: -- The paper lacks theoretical analysis of complexity, memory, and communication costs. -- The experiments only use H100 GPUs, leaving performance on other GPUs unknown. Other Comments Or Suggestions: N/A Questions For Authors: See the weaknesses! Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: We sincerely thank the reviewer Ux6h for the valuable questions and comments. For the concerns and questions, here are our responses. Q1: The experiments only use H100 GPUs, leaving performance on other GPUs unknown. A1: Thanks for pointing out this! We test the performance on A100 GPUs. Experiment1: End-to-end performance on A100 on Transformer-2D 3B with 8 GPUs. \| method \| throughput (samples/s) \| \| :---------- \| :--------------------- \| \| DSP \| 1.08 \| \| DS-Ulysses \| 0.88 \| \| Megatron-SP \| 0.23 \| Experiment2: Runtime breakdown for A100 and H100 on Transformer-2D 3B with 16 GPUs with DSP. \| GPU \| communication time \| computation time \| \| ------- \| ------------------ \| ------------------ \| \| H100 \| 24.8% \| 75.2% \| \| A100 \| 19.2% \| 80.8% \| Analysis: 1. The performance improvement slightly decrease for A100 (from 23.5% to 22.7% compared with Deepspeed-Ulysses). 2. The change is because A100 takes less time ratio to communicate than H100. Because H100 significantly improves computation capbility, therefore taking more time ratio to communicate than A100, making our method more effective. Improvement plan: We have added theroritcal analysis above to the Appendix of our work. Conclusion: For various GPUs, the more time communication takes, the more speedup our work can achieve. Q2: Lacks theoretical analysis of complexity, memory, and communication costs. A2: Thanks for pointing out this problem. Communication costs: \| communication type \| communication volume \| \| :----------------- \| :------------------- \| \| all-reduce \| 2M \| \| all-gather \| M \| \| reduce-scatter \| M \| \| all-to-all \| M/N \| Therefore, the communication volume for each parallel method is \| communication type \| communication volume \| \| :----------------- \| :---------------------------------------------------- \| \| Megatron-LM \| 4 x all-reduce = 4 x (2M) = 8M \| \| Megatron-SP \| 4 x (all-gather + reduce-scatter)= 4 x ( M + M ) = 8M \| \| DS-Ulysses \| 4 x all-to-all = 4 x (M/N) \| \| DSP \| 2 x all-to-all = 2 x (M/N) \| Memory cost: For memory, our method usually will not cause much extra memory cost as we show in Figure 9 (Line 447) because of the following reasons: * The sequence have already been splitted. Therefore there will be only a part of sequence on one device, reducing the overhead to layout change. * DSP changes actually less frequent than any other methods, lead to less overhead. * Duing training, the layout of a sinlge sequence does not affect overall memory cost because parameter and activation is much larger than it. * We use activation checkpointing during training. Experimental analysis of memory cost: \| GPU num \| memory overhead \| \| ------- \| --------------- \| \| 8 \| 0.5% \| \| 16 \| 0.4% \| Theoretical analysis of memory cost: In training, everytime we create/change a tensor, it will make a copy, which causes extra memory cost. There are two reshape before and after communication. So let the tensor size be M, we will have activation memory cost of 4M for one communication. In 2D-Transformer, every layer has activation memory for communication of 4M size as mentioned above, and other components of 42M. If we consider activation memory per layer only, the memory overhead is 8%. But since we use activation checkpoint, the actual memory cost of our method during training will be `Communication Activation / (Communication Activation + Other Activation + Activation Checkpointing * Num Layers + Parameter + Gradient + Optimizer)`, which will be approximately less than 1%. Taking the settings of Transformer-2D 720M into this formula, the memory overhead is 0.67%. Improvement plan: We have added theroritcal analysis above to the Appendix of our work.	Summary: The authors propose dynamic sequenced parallel (DSP), a model sharding scheme for multi-dimensional transformers. M-D transformers have two or more sequence dimensions unlike just one for the regular transformers. Existing sequence-parallel sharding does not account for this and are sub-optimal. DSP works by assuming the M-D transformer processes each sequence dimension separately (attention only ever looks across one sequence dim at a time). It does sequence parallelism across whichever sequence is being computed along, and switches sharding dim between blocks that are computing along different sequence dims. The switching can be accomplished by a low-cost all-to-all (cost = fraction of all activations). Claims And Evidence: DSP is designed specifically for multi-dimensional transformers and thus minimizes both communication volume and activation memory per shard. Like all sequence parallelism, DSP is most useful for long sequence lengths - the authors test on 0.5M - 4M lengths which are attainable for high-def video generation. DSP achieves much higher FLOP utilization that competing sequence parallelism methods - as much as 2x at 4M sequence length. It can also be combined with data parallelism to scale to 128 GPUs. DSP can be used in both training and inference - for inference it reduces latency compared to competing sequence parallelism. Methods And Evaluation Criteria: The evaluation looks fine. The models and scenarios look realistic to me. Theoretical Claims: The authors analyze the theoretical communication volume and peak memory for the Open-Sora video generation model. This is a well know text/image-to-video model and their analysis simply looks at how tensors are divided and transferred between GPUs. The analysis is sound. Experimental Designs Or Analyses: Fine. Supplementary Material: Appendices look fine. Relation To Broader Scientific Literature: It's a new form of sequence parallelism specifically designed for 2D transformers. Essential References Not Discussed: None Other Strengths And Weaknesses: Strengths: DSP looks sound and an obvious fit for 2D transformers. The evidence on the claims are good. Paper is well written. Weaknesses: The idea of DSP seems like low-hanging fruit. It feels like the type of optimization a proper ML engineering team would be able to make with or without a paper on the topic. Other Comments Or Suggestions: None Questions For Authors: None Ethical Review Concerns: None Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We sincerely thank the reviewer 4hHH for the valuable comments and acknowledgement of our work.	null	null	null	null	null	null
Scaling Test-Time Compute Without Verification or RL is Suboptimal	Accept (spotlight poster)	Summary: The paper theoretically studies inference time scaling by modeling LLM generation as a Markov process with horizon $H$ and comparing verifier-based (VB) methods to verifier-free (VF) methods. For binary and nondecreasing rewards, and under a heterogeneity assumption of the base model search trace solutions, it is shown via an information theoretic construction that any VF algorithm with access to $n$ data points from an expert has suboptimality gap $\Omega(H/\sqrt{n})$, in the worst-case sense over a class of alternate experts/rewards. In contrast, it is shown that a specific VB algorithm with access to $n$ annotated search traces, optimizing a pessimistic reward over a class of approximate reward functions, achieves suboptimality gap $\widetilde{O}(H/n)$ under an anti-concentration assumption on the distribution of rewards. Hence VB can asymptotically outperform VF algorithms as test time compute $H$ is scaled. The assumptions and results are also verified experimentally on synthetic and math reasoning tasks. * Update after rebuttal: I am satisfied with the authors' response and maintain my high rating of the contribution. Claims And Evidence: The claims are supported by convincing theoretical and empirical evidence. * It is shown that the suboptimality of any VF estimator scales as $\tilde{\sigma}_b/\sqrt{n}$ where $\tilde{\sigma}_b$ measures the median (over prompts) expected variation of the Q-function under the base LLM policy. This results in a $H/\sqrt{n}$ separation assuming $\tilde{\sigma}_b=\Theta(H)$. * Moreover, the paper constructs a VB estimator whose suboptimality scales as $H/n$ under an anti-concentration assumption for the base policy reward distribution. (This is required to hold uniformly over prompts which is slightly stronger, but I think this is fine.) * Combining these establishes a $\sqrt{H}$ separation w.r.t. the generation horizon when $n=\Theta(H)$. * Moreover, experiments on the MATH benchmark confirm the assumptions and show that heterogeneity hurts VF methods as predicted by the theory. These results provide a solid framework to theoretically understanding the effect of verifier model vs expert cloning for inference time scaling. Methods And Evaluation Criteria: Yes, see Claims And Evidence Theoretical Claims: The proofs are correct to the best of my knowledge Experimental Designs Or Analyses: There do not seem to be any glaring issues with experiment design Supplementary Material: Yes Relation To Broader Scientific Literature: Test time scaling for LLM reasoning is obviously a topic of crucial importance, however the theoretical understanding of chain of thought and test time scaling is still very shallow. I think the paper is a strong contribution towards this direction, proposing an MDP framework to study generation and interpreting verifier and behavior cloning from a novel information theoretic point of view. From a theoretical perspective, the paper borrows from but expands on existing regret analyses of Markov decision processes (e.g. Foster et al, 2024). Essential References Not Discussed: None in particular Other Strengths And Weaknesses: See above Other Comments Or Suggestions: While the many intuitive explanations are appreciated, the paper could benefit from being a bit more precise in the statements (e.g. theorems) of the main text for the theoretically inclined reader. In particular, it would be helpful to mathematically describe exactly what samples the VB and VF models have access to (expert trace vs annotated trace). Typos: $r\to r'$ in Theorem 5.4, verifier-based $\to$ verifier-free in Theorem B.10(4) Questions For Authors: Some bounds in the proofs seem to rely on the rewards being binary, such as the rounding argument; can the results be generalized to when rewards are real-valued and monotonic? Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: Thank you for the review and a positive assessment of our work! To address your remaining concerns, we clarify the data annotations for VB and VF methods and show that our analysis can be extended to settings beyond binary rewards, while proving a similar separation between VB and VF methods. We also point to discussion on a relaxation of uniform anti-concentration. >> Extending our analysis to non-binary rewards While our algorithms and analysis are tailored for $0$-$1$ rewards with the bilevel structure, in the non-stochastic setting (no noise in observed rewards) we can extend these results to the case of general rewards functions, while essentially preserving the final guarantees. In general, given access to the trajectory-level reward, we can quantize the rewards to $n$ levels, and apply the same classification-based algorithm for learning the reward function. By doing so, we obtain an algorithm for learning general rewards in $L_1$ error to a test error of $H \log(\|\mathcal{R}\|) \log(n)/n$. The only differences compared to the bilevel case are: there is an additional $\log(n)$ blow up compared to the bilevel case, the learner can directly query the outcome reward for a trajectory directly (rather than the per-step reward). The intuition is as follows: suppose the outcome reward belongs to some class $\mathcal{R}$, we can consider an induced quantized reward class $\mathcal{R}_q$, which rounds the rewards to a grid where consecutive points are $H/n$ apart. Note that $\|\mathcal{R}_q\| \le \|\mathcal{R}\|$. By quantizing the reward observations, and training a multiclass classifier over the outcome space $\mathcal{Y} = \\{ 0,\frac{H}{n}, \frac{2H}{n},\cdots,H\\}$ of size $n+1$, we can train a classifier incurring $0$/$1$ error of at most $d_G (\mathcal{H}) \log(\|\mathcal{Y}\|)/n \lesssim \log(\|\mathcal{R}\|) \log(n)/n$, where $d_G$ denotes the graph dimension (see definition B.29 in the submission). When the classifier is correct (in a $0$/$1$ sense), the induced reward function makes an error of at most $H/n$. If the classifier is incorrect, the induced reward function makes an error of at most $H$. Overall, this implies that the $L_1$ error of the reward function induced by the classifier (which is essentially a discretized reward $\in \\{ 0, \frac{H}{n},\cdots,H \\}$) is at most $ H\log(\|\mathcal{R}\|) \log(n)/n + H/n \lesssim H\log(\|\mathcal{R}\|) \log(n)/n$. Hence, the same lemma, and the same guarantees, will also apply in our setting. We will add this discussion in the paper. >> Data annotations for VB and VF methods For VF methods, we simply have $n$ datapoints of the form $\(x, \tau)$, consisting of an input $x \sim \rho$, and a trace $\tau \sim \pi_e(\cdot \mid x)$ sampled from expert $\pi_e$. For VB methods, we have $n$ datapoints of the form $(x, \tau, r(\tau))$, where $x \sim \rho$, but the trace $\tau \sim \pi_b(\cdot \mid x)$ is sampled from the base LLM $\pi_b$, and $r(\tau)$ is the reward annotation $\in [0, H]$ under the bi-level reward $r$. We will also move details from the formal theorem statements in Appendix (e.g., the formal lower bound result in Thm. B.10) into the main paper, in our final version, which we hope will make the theorem presentation more clear. >> Relaxing uniform anti-concentration to an average case notion. Please see our response to reviewer eEQB where we show that our uniform anti-concentration can be relaxed to $L_p$ concentration, and when $p>2$, we recover the same asymptotic separation of $\Omega(H/\sqrt{n})$ between VB and VF methods, as we obtain under uniform anti-concentration in Thm. 5.8. We show the full derivation in a figure here: https://sites.google.com/view/ttcwv/home.	Summary: This paper studies the performance of two prevalent methods which are named as verifier-based (VB) and verifier-free (VF) methods in terms of scaling test-time compute. VB methods utilize a verifier or reward signals to improve a policy while VF approaches use expert data to supervise the policy training. They compare the performance of these two category of methods at different test-time compute by introducing a bi-level reward to represent the compute. The authors show VB methods scale test-time compute better than VF methods if the base policy satisfy heterogeneity and anti-concentration. Besides, they implement experiments to support this finding. Claims And Evidence: No, the claim made is not supported clearly or solidly. The main claim in this paper is that finetuning LLMs with VB methods is superior to VF approaches in terms of scaling the compute resources. First, the title of the paper is scaling test-time compute, but this paper seems talking about the fine-tuning phase. I also raised my question in the question part below. Second, to show the advantage of VB methods, the base policy should possess some properties which are restrictive (I elaborate in the weaknesses part). And I don't think their experiments successfully show that in practice, pre-trained policies satisfy these conditions. Methods And Evaluation Criteria: Yes, so the authors want to show verifier-based algorithms have advantages at scaling the test-time compute compared with verifier-free methods. They first model the scaling of test-time compute by the horizon and defining a bi-level reward. Then they show the lower bound of sub-optimality of VF algorithms and upper bound of sub-optimality of VB algorithms under certain condition of the base policy. Theoretical Claims: No, I didn't check the correctness of the theorems. But I think that Proposition 5.5 needs a realization assumption of the reward function class. Experimental Designs Or Analyses: Yes, I checked the soundness of the experimental part about didactic setup. The authors compare results at different data budget, horizon (which represents compute in their framework) and policy heterogeneity. However, policy anti-concentration is less discussed. They show and control the policy heterogeneity of their choosing base policy, but they didn't show how they control the anti-concentration which is important for the soundness of the experiments. In the experiments for math reasoning, they include a Figure 7 to show that practical pre-training policies satisfy the anti-concentration property, but this conclusion is too optimistic. At least more different policies should be tested. And I also doubt the definition of anti-concentration (please refer to the weaknesses part). Supplementary Material: No, I didn't review supplementary materials. Relation To Broader Scientific Literature: The contributions of this paper are related to two broad directions. The first is how scaling test-time compute can improve a model. It is an active area and there are some promising results [1][2]. The second is which is better: learning from experts or learning from rewards. Some works [3] study this question in reinforcement learning, especially imitation learning, but it is relatively under-explored in language models. [1]. Snell C, Lee J, Xu K, et al. Scaling llm test-time compute optimally can be more effective than scaling model parameters[J]. arXiv preprint arXiv:2408.03314, 2024. [2]. Hübotter J, Bongni S, Hakimi I, et al. Efficiently learning at test-time: Active fine-tuning of llms[J]. arXiv preprint arXiv:2410.08020, 2024. [3]. Kumar A, Hong J, Singh A, et al. When should we prefer offline reinforcement learning over behavioral cloning?[J]. arXiv preprint arXiv:2204.05618, 2022. Essential References Not Discussed: No, I didn't see any essential related works are not discussed. Other Strengths And Weaknesses: Strengths: 1. Comparing the methods of learning from rewards and learning from expert is a very interesting and important direction. Weaknesses: 1. The authors show by Theorem 5.1, there exists a base policy $\pi_b$ such that verifier-based algorithm scales better with test-time compute. But they didn't show if it is possible that there also exists another $\pi_b$ such that verifier-free algorithm scales better. It is important to derive the final conclusion. 2. The anti-concentration parameter which they define as $c$ in Property 5.6 depends on 'worst' problem since they define $\min_x c_x(\epsilon_x)\ge c$. This a very restrictive definition/requirement. It is usually the case where we have a huge number of different problems for a specific task. The anti-concentration definition needs the base policy to have nice shape of the answer distribution over all problems. I think the authors should relax this definition. Besides, how is Figure 7 plotted, is it for just one problem? If it is for a set of problems, how are these metrics calculated? 3. The authors should include more detailed discussions on the related work [1] since this work also models the problem as a MDP and their work is very close to this work. In the paragraph before Section 6, the authors give some discussions but are vague to a reader. [1]. Kumar A, Hong J, Singh A, et al. When should we prefer offline reinforcement learning over behavioral cloning?[J]. arXiv preprint arXiv:2204.05618, 2022. Other Comments Or Suggestions: 1. Some typos: In line 183, For e.g. -> For example. On the right column in line 62, distinction -> direction. In line 305, this results in Theorem 5.7 which is an incomplete sentence. 2. It would be better to include a lemma that can formally describe the relationship between the definition of policy heterogeneity and anti-concentration. I noticed that the authors explain in somewhere in a paragraph that 'while a non-heterogeneous base policy will not satisfy Property 5.6, hetergeoneous distributions can still be anti-concentrated'. This is crucial to derive the final conclusion in this paper which is VB algorithms can perform better than VF algorithms for some base policy. It is not very straightforward at the first glance, hence I think adding a lemma would be beneficial. Questions For Authors: 1. I am confused at what the authors refer as test-time compute. From my understanding, the test-time compute usually refers to the compute applied to the inference phase of the model which has been trained or fine-tuned. But in this paper, it seems to refer to the compute applied to the fine-tuning phase. Do I misunderstand something here? 2. In line 182, the condition (b) of the expert is the expert's distribution should be 'close' to the base policy to prevent some issues, but these issues arise in practice. From the theoretical perspective (which is this paper's perspective), do we need this condition and why? 3. In Proposition 5.5, doesn't one need realization assumption of the reward function class, i.e., the true underlying reward $R^$ is in the set of reward functions $R^\in \mathcal{R}$? 4. What does the y-axis (efficiency) in Figure 4 refer to, accuracy? Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Thank you for the feedback! We believe that many concerns perhaps stem from a misunderstanding of the setup. We study the efficacy of different fine-tuning algorithms to train LLMs to attain better performance as they utilize more test-time compute, measured in terms of the token length. Verifier-based (VB), or verifier free (VF) are finetuning methods, like DeepSeek-R1 or SCoRe, training LLMs to use more test-time compute to solve more problems. We expand on this, provide more evidence of anti-concentration holding in practice, and explain how we can relax the worst-case (over prompts) anti-concentration to average case while arriving at the same result in Thm 5.8. >> I am confused at what the authors refer to as test-time compute? It is applied to finetuning As we explain in L131-152, our goal is to compare LLMs obtained by running different finetuning algorithms that train LLMs to utilize test-time compute (measured by the length of CoT H) more effectively. So, either we finetune LLMs with VF, e.g. by running SFT on expert traces of length at most H containing behaviors like planning, search, backtracking etc., or train LLMs with a verifier based approach like RL that samples traces of length H from the base LLM, and optimizes it with 0/1 rewards (L165-175, L200-209). Our analysis is novel because it compares finetuning algorithms that train LLMs to optimize test compute efficiency, as opposed to only analyzing the efficiency of known test-time search algorithms like best-of-N. >> How is Fig7 plotted,is it for 1 problem. Ablations on anticonc? See figure & caption in https://sites.google.com/view/ttcwv/home. >> Prop. 5.6 is restrictive since it needs to hold on all problems. Consider relaxing it. The notion of anti-concentration can indeed be weakened to accommodate average-case at the cost of a slightly weaker dependence on $n$. See fig in https://sites.google.com/view/ttcwv/home for the derivation. Note that this results in the same conclusion as Thm 5.8 in the current paper, but the bound depends on a weaker notion of anti-concentration. Additionally: - Common in literature: This style of uniform lower bound is common in RL theory (e.g., Uehara el al., Kumar et al.). Prior work assumes strong density ratio bounds, whereas we only require that base policy generates traces exceeding one std. dev. of the mean reward with constant probability. - Poor anti-concentration can hurt VF too: In practice, VF gets expert traces by running rejection sampling. However, rejecting more traces results in smaller SFT data. This tradeoff is worse for problems with poor anti-concentration. To achieve a high reward dataset, the learner would need to discard most traces, biasing the dataset and degrading SFT performance. We will add this to final version. >> Thm 5.1: does there exist a base policy where VF > VB? No matter the base LLM, whenever the expert is non-heterogenous, and covers high reward traces, we expect VF algos like SFT to learn good policies. It is possible that in some cases when heterogeneity and anti-concentration are not satisfied, VF methods may outperform VB, as we also show in Fig 6 (left). In practice, however, we see the assumptions are satisfied(Figs 6, 7). >> L281, lemma implying anti-concentration needed for VB > VF Heterogeneity (Prp. 5.2) & anti-concentration (Prp. 5.6) are largely orthogonal conditions, which we show are sufficient to prove VB > VF. We show in Sec 7 (Fig 6, 7) that both conditions hold in practice. As seen in Fig 3, base LLM can satisfy these conditions separately. In L281, we are referring to the fact that a heterogeneous base LLM need not satisfy anti-concentration (3rd col in Fig 3), which is why we need both Prp. 5.6 & 5.2 to hold for the base LLM. >> Discussion on Kumar et al In Remark 5.9 (L299), we already include a detailed comparison with prior work comparing BC and offline RL methods. >> Condition on expert distribution, is it needed in theory? Yes, one may prove a result assuming the expert policy is far away from the base policy and only samples high reward traces. But this is less practically useful: 1) it is unclear how to identify and sample from such an expert; and 2) the expert needs to be close to the base policy to: a) prevent optimization and memorization issues (Kang et al., Tajwar et al.); and b) it is common to collect expert traces by running rejection sampling (Zelikman et al.). >> Realizability assm. in Prp 5.5 Yes, the true reward function is assumed to be present in reward class R. We state this in our setup (L114), and we will highlight this better. >> Y-axis in Fig 4 To cleanly compare performance of policies trained for different values of token length H, we divide the average reward (in [0, H]) that measures test-time compute efficiency by H (L347). Hence, the normalized rewards are in [0,1], and can be viewed as accuracy normalized by the test-time compute budget. --- Rebuttal Comment 1.1: Comment: Thank the authors for their efforts on the rebuttal. The elaborations are very detailed. I admit I have some misunderstanding towards the setting. Besides, my main concerns are satisfactorily solved including relaxing the restrictive definition of anti-concentration in Property 5.6 and showing the anti-concentration condition usually satisfies in practice by additional experiments. With these further evidences, I think the claims made in this work are supported and I am glad to increase my score to 3. --- Reply to Comment 1.1.1: Comment: Thank you for raising the score. We are glad to note that your main concerns are "satisfactorily solved", including the relaxation of anti-concentration, and showing that it holds in practice. Please let us know if there are any additional concerns, and if there are no additional concerns, we would really appreciate if you would consider raising the score further, thank you!.	Summary: - This paper seeks to understand the best way to finetune LLMs that leads to performance that is most scalable in terms of test-time compute - These are split into VF methods that don't use a verifier (eg SFT on expert trajectories) and VB methods that do (eg RL on 1/0 rewards) - The focus is on theoretical results. First they define heterogeneity (roughly how diverse is the base policy in terms of q value) and anti-concentration (roughly a high value means there is a lump of probability mass at a reward value much higher than the average value) - $H$ is test time budget per answer (number of tokens) and $n$ is number of examples for finetuning phases. - The first main result (theorem 5.4) is sub-optimality of VF methods deteriorates with heterogeneity (which itself scales $\Omega(H)$), which leads to overall bound $H/\sqrt{n}$ - The second is that sub-optimality of VB methods do not, and instead is constant (assuming $n$ is set to be linear in $H$) - Combining these (theorem 5.8), one gets the gap between VB and VF methods is bounded by $\Omega(H/\sqrt{n})$ where $n$ is set as $n=\Omega(H)$, giving the main result that the gap grows $\sqrt{H}$. - Two experimental results are presented, a didactic toy distribution (but still using real LLMs) and math reasoning. Claims And Evidence: fine Methods And Evaluation Criteria: fine Theoretical Claims: I only looked at main paper content and skimmed some appendix section, but have not interrogated in depth Experimental Designs Or Analyses: fine Supplementary Material: skimmed appendix Relation To Broader Scientific Literature: see strengths weaknesses Essential References Not Discussed: fine Other Strengths And Weaknesses: Strengths - I'm sure much of the community would welcome this kind of deeper understanding of differences between LLM finetuning methods and their scalability - Precisely written, no obvious errors (although I was not able to fully interrogate all mathematical details) - Good job of making effort to provide intuition and link to practice, rather than solely stating results in mathematical language - LLM experiments in section 7 were excellent, with an attempt to even measure and visualize heterogeneity and anti-concentration - Tackling this kind a problem through theoretical analysis is tough, and I feel the authors have done a great job at making progress (though I am only familiar with high-level details of related work so cannot comment too precisely) Weaknesses - The paper is dense. The concepts took me a long time to absorb, and there are various lemmas outside of the main results I did not have time to fully process. Less content could be more from a readability perspective. - The didactic experiment was less informative than the math experiment. The gap between the two methods didn't seem to grow with $\sqrt{H}$ (fig 4 a), and there was little extra intuition I felt I gained from it. - Anyway these didactic results are supersceded by the math experiments, which end up being cramped and rushed for the sake of space. I might suggest removing section 6 from the main paper altogether to uncompress the technical results and provide readers a deeper dive into section 7. - Anti-concentration felt like a very specific assumption to require -- intuitively it says we need a large amount of probability mass producing rewards that are far from the average output of the model. It's not a surprising consequence then that RL should be able to seek this mode out. - I did not follow the intuition for why heterogeneity harms VF methods. Did I miss this in the paper? It seemed like one of the two cornerstones leading to the main result, but I was unable to follow why it would have a detrimental affect. Questions - I wonder if the results say anything about the common practice of firstly SFT finetuning followed by RL finetuning. The paper's results suggest the latter is strictly better than the former? Other Comments Or Suggestions: fine Questions For Authors: see above Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Thank you for the review and a positive assessment of our work! To address your concerns, we added an experiment for the didactic setup where we show an increasing performance gap between VF and VB methods, as we scale both n (the number of prompts) and H (the output length), matching our results on MATH in Fig 5c. We also answer other questions on heterogeneity, anti-concentration, and running RL followed by SFT. We will also use the extra page in the final version to uncompress Sec 7, and if needed shorten Sec 6. >> [New Expt.] Gap between VF and VB methods in the didactic setup too scales as $\sqrt{H}$. Similar to our MATH experiment (Fig 5c), we plot the performance of VB (RL) and VF (SFT) in our didactic setup here: https://sites.google.com/view/ttcwv/home. In Fig 5a we fix the data budget to $n=2^{10}$, and in 5a fix the compute budget $H=2^6$. Now, we scale $n$ with $H$, and note the performance gap between RL and SFT scale superlinearly (as $\sqrt H$), in agreement with our result in Theorem 5.1. >> Why does heterogeneity hurt VF methods? A VF algorithm (e.g. SFT) finetunes the base LLM on expert traces (e.g. traces collected by rejection sampling correct answers from base LLM). VF methods fail under heterogeneity for the following reasons: - Diverse solution traces: When the base policy (and thus the expert induced by rejection sampling) is heterogeneous, the expert data consists of diverse solution traces for the same problem. Here, each trace gets to the correct answer, spending a varying number of tokens (e.g., a short solution that directly outputs the final answer, and a longer solution that is composed of a failed attempt, followed by a correct one that solves the problem). Thus, the bi-level reward carried by these traces has a high variance for each input. - VF methods are forced to equally mimic diverse traces: VF methods like SFT finetune the base LLM on expert traces where reward annotations are absent. Thus, VF methods cannot distinguish between the diverse expert traces, and are forced to mimic each trace equally, irrespective of their reward. Thus, the VF learned policy fails to only learn high reward solutions. Also, in practice it is challenging to collect multiple traces that are less diverse, i.e., with matching rewards, and naturally the expert data is heterogeneous (as we also show in Sec 7). On the other hand, VB methods like RL have access to reward annotations from a learned verifier or ground truth 0/1 rewards, and need only mimic or increase likelihood on high reward traces, as judged by the verifier. Note that the verifier for VB is trained on heterogeneous, and suboptimal data (includes incorrect answers) sampled from the base LLM, and the learned verifier is also forced to equally reduce estimation error on each mode of the reward distribution (low and high rewards). But, the base LLM is finetuned to maximize the rewards under the learned verifier. So, the heterogeneity of traces sampled from the base policy does not hurt the policy learned by VB methods. We will add the above discussion after Theorem 5.4 in the final version. >> Does running SFT before RL help, as done in practice? Yes, you are correct, our results imply that running SFT before RL can help improve coverage of correct solutions under the base LLM. Note that, our performance guarantee (Thm 5.7) for VB methods like RL bounds the suboptimality gap by $O(H/n)$ for the RL trained policy against the best expert in the $\epsilon$-$\chi^2$ ball around the base LLM. Thus, for the RL policy to have good performance in absolute terms, we need to ensure that there exists an LLM in an $\epsilon$-$\chi^2$ ball around the base LLM that performs well on the task. One way of ensuring this is to improve the coverage of the base LLM over high reward traces or at least correct solution traces, and SFT does exactly that. Thank you for this question; we will add the above discussion after Thm 5.7. >> Anti-concentration felt like a very specific assumption. It is not surprising RL can seek this mode. Anti-concentration is a weaker form of the trajectory level coverage assumption made in offline RL literature (e.g., Kumar et al. BC or Offline RL). The functional form of the definition (one std. dev. from mean) stems from the fact that VB methods need to improve over the best expert in $\epsilon$-$\chi^2$ ball around base LLM, and the reward for such an expert assumes this form. Yes, it is not surprising that online RL can seek this mode of higher rewards given access to the ground-truth bi-level reward function. The non-trivial finding of our analysis is that training a learned verifier using only IID samples from the base policy and optimizing it with online RL is enough for a policy to seek this mode (Alg. 1). Contrast this with prior works on reward hacking when optimizing learned verifiers (Gao et al.). --- Rebuttal Comment 1.1: Comment: Thank you for this response, particularly the intuition around heterogeity. I will continue the discussion with other reviewers. --- Reply to Comment 1.1.1: Comment: We are glad that the intuition on heterogeneity is more clear. We will certainly add this discussion to the final version. Are there any additional concerns or comments that we can help address? If there are no additional concerns, we would greatly appreciate if you would be willing to increase your score. Thank you.	null	null	null	null	null	null	null	null
Preference-CFR: Beyond Nash Equilibrium for Better Game Strategies	Accept (poster)	Summary: The paper introduces Preference-CFR (Pref-CFR), an extension of Counterfactual Regret Minimization (CFR) aimed at generating diverse strategies in extensive-form games. Traditional CFR-based approaches focus on solving for Nash Equilibria (NE), which prioritize optimality under worst-case conditions but lack strategic diversity. Pref-CFR introduces preference degree and vulnerability degree to control playstyle and allowable exploitability, respectively. The method enables the training of AI agents with distinct styles, such as Aggressive and Loose Passive strategies, in Texas Hold’em. Experimental results show that Pref-CFR achieves comparable performance to standard CFR-trained strategies while demonstrating diverse playstyles. Claims And Evidence: Yes Methods And Evaluation Criteria: Yes Theoretical Claims: I didn't check the proof of theory section in the appendix in detail. Experimental Designs Or Analyses: Yes Supplementary Material: I read the supplementary information in the appendix, but did not carefully check the theoretical proof. Relation To Broader Scientific Literature: Traditional CFR and its extensions (CFR+, DCFR, MCCFR). Correlated Equilibria and other refinements beyond NE. Opponent-exploiting AI (e.g., safe equilibrium models), which could serve as an additional baseline. Essential References Not Discussed: No. Other Strengths And Weaknesses: Strengths - Novel conceptual contribution: Introducing preference-based parameters into CFR is an interesting extension. - Empirical validation: The method performs well in Texas Hold’em, an established benchmark. - Theoretical soundness: The algorithm has theoretical proof on convergence. Weaknesses - Heuristic tuning of $\delta$ and $\beta$ requires manual selection. The sensitivity of parameter selection in large-scale game is not discussed. Other Comments Or Suggestions: See strengths and weaknesses Questions For Authors: How sensitive are the results to the heuristic tuning of $\delta$ and $\beta$ , particularly in large-scale games? Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Thank you for your feedback. We summarize some of the questions and answer them. If there are still questions or new questions arise, please feel free to discuss further. --- ## How sensitive are the results to the heuristic tuning of $δ$ and $β$, particularly in large-scale games? Conducting experiments in large-scale games is highly costly, and comprehensive analysis of these two parameters would require significant time and hardware resources. However, we have successfully migrated the PrefCFR method to OpenSpiel, a game learning framework developed by DeepMind. By employing a larger game instance of Leduc Poker, we can conduct detailed analysis of these parameters' effects. The results can be viewed at: https://drive.google.com/file/d/1F-oNqLm_cVqBNHvDYUf5dtQ_Rk1SdMkH/view?usp=drive_link Experiments show that the introduction of the preference parameter alone has little effect on the convergence of the game. Even if it is set to 10, the convergence speed is only reduced but not significantly. When fragility is introduced, the convergence speed in the early stage of training is basically the same as that of the original CFR algorithm, and only slows down when it approaches $β$. --- ## Heuristic tuning of $δ$ and $β$ requires manual selection. Regarding manual selection of $δ$ and $β$: Manual parameter selection is currently required, but in the context of Texas Hold'em poker - where player styles have distinct categorizations and sufficient expert knowledge exists - this manual selection does not create a bottleneck for the current algorithm implementation. We plan to further investigate this aspect in future research.	Summary: This paper tackles a key limitation of standard CFR-based methods. Typically, these methods converge to a single Nash equilibrium (NE) and struggle to accommodate risk preferences or different playing styles. To address this, the authors propose Preference-CFR (Pref-CFR), which introduces two key parameters at each decision point: a preference degree, $\delta(I,a)$, that amplifies or suppresses specific actions, and a vulnerability degree, $\beta(I)$, which controls how much exploitability is allowed, guiding the solution toward a $\epsilon$-NE instead of a strict NE. Using Blackwell approachability, the authors show that Pref-CFR maintains low regret, ensuring strong near-NE performance. In Kuhn poker experiments, the method steers strategy toward different equilibria by adjusting $\delta$, whereas standard CFR always converges to the same equilibrium. In larger-scale tests on two and three player Texas Hold'em, Pref-CFR effectively shapes playstyles, such as increasing aggression or reducing folds, resulting in distinctive, human-like strategies like "aggressive" or "loose-passive". These adjustments maintain high performance with only a slight trade-off in exploitability. Claims And Evidence: Most of the paper's claims are reasonably supported, but there are places where the evidence could be more thorough. The authors assert that Pref-CFR can not only converge to different equilibria but also preserve near-optimal performance. They demonstrate examples of altered strategies in Kuhn poker and Texas Hold'em, along with head-to-head matches measuring exploitability. If we look at the claim that increasing the preference parameters $\delta$ or the vulnerability parameters $\beta$ "does not significantly slow down convergence," the supporting data come primarily from small-scale Kuhn experiments and selected subgame analyses in Texas Hold'em. These examples, while informative, do not fully guarantee scalability or robustness in larger or more complex scenarios, especially when very large $\delta$ or $\beta$ values are applied across numerous information sets. While the experiments demonstrate a few distinct playstyles, such as "aggressive" and "loose-passive," they don't rigorously test whether the method can handle a large number of style parameters simultaneously or adapt to more nuanced, context-specific preferences. It would have been useful to see broader experiments systematically exploring a wider range of preference settings, such as analyzing how performance changes when $\delta$ is adjusted incrementally across all betting rounds. Without these deeper evaluations, it's fair to question whether the method truly scales to diverse playstyles as seamlessly as the paper suggests. The claims aren't entirely unsupported, but more extensive and systematic testing would have made the evidence far more compelling. Methods And Evaluation Criteria: The choice of poker, Kuhn and Texas Hold'em, as a testing ground does make sense, given that poker has a long history in computational game theory. The proposed approach, Pref-CFR, specifically targets scenarios where one needs flexible or style-driven equilibria rather than a single exploitability-minimizing solution, and poker is a natural fit for demonstrating that kind of variety. * While Kuhn poker is a classic toy example and works nicely to illustrate theoretical proofs, it's extremely small in scale and doesn't necessarily expose all the complications that arise in real-world poker settings. The paper then jumps to two and three player Texas Hold'em, which is certainly more complex, but the presentation of final strategies (e.g., aggregated preflop charts) and small-sample matchups may not fully convey whether the style modifications maintain robustness across the entire decision tree. More rigorous exploitability analyses, or thorough cross-play among multiple different stylized agents, might have better established how well the approach generalizes. * While the evaluation criteria of measuring head-to-head performance in terms of mBB/h is standard in poker, there's some risk in concluding broad "style" success based primarily on changes to preflop charts. One could argue that style adjustments should manifest consistently across multiple betting rounds, and the current paper only provides a snapshot of the final strategy. So, even if the overall benchmarks make sense, the completeness of the evaluation might be limited when it comes to verifying that the agent truly embodies a different style (as opposed to just shifting its action frequencies slightly at the earliest decision points). In summary, the methods and evaluation criteria make sense given the application, but they could be more thorough in probing deeper behaviors and broader ranges of scenarios. Theoretical Claims: The proofs in the paper appear consistent with known results on no-regret learning and Blackwell approachability. The authors' main technical claim is that, by introducing preference parameters $\delta(I,a)$ and vulnerability $\beta(I)$ in the update steps, they can still guarantee convergence to a (possibly $\beta$-relaxed) Nash equilibrium. Their proofs hinge on two well-known building blocks: (1) standard regret-minimization arguments, and (2) Blackwell approachability ensuring that the average regret vector converges. Experimental Designs Or Analyses: The experiments in the paper are generally appropriate for illustrating the potential of the proposed method, yet there are a few points: * The authors test on Kuhn poker (a very small game) and on subgame approximations of Texas Hold'em (two and three player). This does show that their algorithm can scale beyond toy scenarios, but the evaluation is limited in how comprehensively it inspects all stages of a large game. By focusing on subgame methods, we do not necessarily see full-tree exploitability or style changes across every betting round. * The experiments tend to vary only a handful of preference degrees $(\delta)$ or vulnerability degrees $(\beta)$ in fairly simple ways (e.g., drastically increasing raise frequency or almost never folding). It is plausible that moderate or more nuanced adjustments could produce different equilibrium behaviors. This keeps the experiments intuitive, yet it leaves open questions about how the method behaves when many parameters are tweaked in more subtle ways. Overall, the experimental designs serve their main purpose, showing that Pref-CFR can shift an equilibrium strategy's style with minimal performance loss. Supplementary Material: n/a Relation To Broader Scientific Literature: see next section Essential References Not Discussed: Since this paper is grounded in CFR models, it would be beneficial to include a more comprehensive discussion of related works within this domain. While the current related work section primarily provides background information on existing approaches, it lacks a direct comparison between these methods and the proposed approach. A stronger comparative analysis would help contextualize the contributions of this paper by highlighting how it improves upon prior work. Specifically, discussing the strengths and limitations of other CFR-based methods and demonstrating where your approach offers advantages would make the contribution clearer. This would not only strengthen the justification for your method but also provide a more complete picture of the research landscape Other Strengths And Weaknesses: Strengths: * Novel Extension to CFR: The introduction of preference and vulnerability parameters is a straightforward yet effective modification of the CFR framework, allowing for different equilibria based on user-defined stylistic or risk constraints. * Practical Demonstration: Experiments on both Kuhn poker and Texas Hold'em games convincingly show how adjusting the parameters leads to distinct, human-like playing styles (aggressive, loose-passive) with minimal performance degradation. Weaknesses: * While the experiments are illustrative, they focus primarily on a few stylized adjustments and measure changes mostly at preflop or initial decision points. Postflop actions in full-scale Texas Hold'em and extended multi-street analysis are not exhaustively demonstrated. * The related work section primarily provides background information but lacks a direct comparison with similar CFR-based methods. A more comprehensive discussion of related works and a stronger comparative analysis would better highlight the contributions of this paper. Addressing the strengths and limitations of existing approaches while emphasizing the advantages of the proposed method would clarify its impact and strengthen its justification. Other Comments Or Suggestions: * The introduction section would benefit from a more technical explanation of key concepts and terminology to better introduce the research area to the reader. * The technical background in Section 2 is well-presented and effectively enhances the clarity of the paper. Questions For Authors: 1. Your experiments mostly highlight changes in preflop or early-round decision-making. Did you conduct any deeper analyses on later betting rounds to confirm that style-related shifts remain consistent throughout the entire game tree? If so, do you observe similarly clear style distinctions in postflop play? 2. While it is shown that extreme values can push the final strategy toward distinct equilibria, have you observed any surprising instability when $\delta$ or $\beta$ become very large (for example, extremely aggressive or extremely passive settings)? Does the algorithm remain stable, or do you see any oscillations or convergence slowdowns in such scenarios? Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: Thank you for your feedback. We will first answer your questions and comments in order, and then summarize and answer some questions from previous sessions. If there are still questions or new questions arise, please feel free to discuss further. --- ## Questions 1 Our algorithm adopts a similar idea to Pluribus, that is, only the pre-flop strategy is saved, and the subsequent strategy is obtained by real-time search, so we only show the per-flop results. --- ## Questions 2 Conducting such an experiment directly in large-scale problems is extremely costly. Therefore, we carried out more experiments in Leduc. The experimental charts can be found at: https://drive.google.com/file/d/1F-oNqLm_cVqBNHvDYUf5dtQ_Rk1SdMkH/view?usp=drive_link No unexpected instability was found in the results, which is in line with theoretical expectations, which also proves the robustness of our algorithm. In Figure 1, we doubled the value of $\delta$ (from 5 to 10). It can be seen that the improvement in the stylistic characteristics of the final result is negligible. Thus, we have every reason to believe that a larger $\delta$ is unnecessary. In Figure 2, we set different values of $\beta$. It can be observed that the influence of different $\beta$ values on the results is fully consistent with the theoretical expectations: 1. The $\epsilon$ of the final strategy will not exceed the set $\beta$; 2. A larger $\beta$ can lead to a more pronounced stylistic strategy. Tips: In this game, there are only two actions, namely "raise" and "call", and $\sigma(\text{raise}) + \sigma(\text{call}) = 1$. --- ## More extensive preference experimentation This seems unnecessary because a strategy cannot have two styles simultaneously. For example, at the beginning, we set $\delta$ as an aggressive strategy (with a relatively large $\delta(raise)$), and then change it to a conservative strategy in the middle of the training process (reducing the value of $\delta(raise)$), which seems meaningless. However, this suggestion has inspired us. When training strategies of different styles, we don't have to start the training from a completely random strategy. Instead, we can first train a "Normal" strategy, and then use this "Normal" strategy as a warm start. Subsequently, strategies of different styles can continue to be trained based on this "Normal" strategy. We will try this approach in our subsequent work. --- ## Discussing the strengths and limitations of other CFR-based methods Indeed, we lack the comparison with previous methods, and there is also a lack of technical introductions of key concepts and terms in the introduction stage. We will add this part of content in the subsequent versions.	Summary: This paper introduces Preference Counterfactual Regret Minimization (Pref-CFR), an extension of Counterfactual Regret Minimization (CFR), designed to incorporate strategy diversity and playstyle customization in game AI. While standard CFR focuses on computing Nash Equilibrium (NE), the authors argue that optimality alone is insufficient for practical applications requiring diverse strategies. ### Main Contributions ### Pref-CFR introduces Preference and Vulnerability Degrees to adjust strategy tendencies, enabling AI to exhibit different playstyles while maintaining competitiveness. ### Experimental Results ### Applied to Texas Hold’em, Pref-CFR successfully learns Aggressive and Loose Passive playstyles, performing competitively with standard CFR-trained strategies while demonstrating distinct stylistic differences. Claims And Evidence: - #### Strengths: #### - Pref-CFR retains the convergence properties of CFR and can still reach Nash Equilibrium (NE) under certain conditions, as theoretically proven in Appendix B.2. - The algorithm extends to ϵ-NE, demonstrating mathematical soundness even with some loss tolerance. - Pref-CFR introduces novel strategy discoveries, such as raising with weaker hands, which may offer insights for professional players. - #### Weaknesses: #### - While theoretically applicable to other extensive-form games, there is no empirical validation beyond Texas Hold’em, limiting its demonstrated generalizability. - The lack of human player testing makes it uncertain whether Pref-CFR’s strategies provide meaningful improvements for real-world play. Methods And Evaluation Criteria: - #### Strengths: #### - Pref-CFR effectively adjusts strategic tendencies through preference degree and vulnerability degree, enabling AI to learn diverse playstyles while maintaining competitiveness. - The evaluation criteria are reasonable, focusing on strategy diversity and competitiveness, which align with common practices in game AI research. - AI playstyle variation is demonstrated through parameter adjustments, providing an important metric for evaluating strategic flexibility. - #### Weaknesses: #### - Limited validation: The method has only been tested in Texas Hold’em, while CFR applies to a broader range of imperfect information games. Additional experiments in other domains (e.g., StarCraft, economic games) are needed to establish generalizability. - Lack of human player feedback: Pref-CFR aims to improve strategies for human players, but no real-world testing with professional players has been conducted. - No comparison with state-of-the-art game AIs: The study does not evaluate whether more advanced AI models can achieve similar playstyle control, leaving Pref-CFR’s comparative advantage uncertain. Theoretical Claims: The core theoretical proofs in the paper are correct, and the mathematical derivations contain no obvious errors. Experimental Designs Or Analyses: - #### Strengths: #### - The experimental design effectively validates Pref-CFR’s ability to train AI with different playstyles in Texas Hold’em, demonstrating both Aggressive and Loose Passive strategies. - Pref-CFR’s competitiveness is assessed by comparing it with standard CFR-trained AI, showing that distinct playstyles can be achieved without significant performance loss. - The algorithm discovers new strategies , suggesting that Pref-CFR may offer novel insights beyond conventional CFR-based approaches. - #### Weaknesses: #### - Limited scope: Experiments are restricted to Texas Hold’em, with no validation in other imperfect information games , limiting generalizability. - Lack of human player evaluation: The study does not test whether Pref-CFR-generated strategies are beneficial for real-world human players, which is crucial given its focus on strategic diversity. - No comparison with advanced game AIs: The paper does not benchmark Pref-CFR against state-of-the-art models like DeepStack and Pluribus, making it unclear whether it offers meaningful advantages. - Future research should expand experimental settings and incorporate human feedback to further validate Pref-CFR’s real-world applicability. Supplementary Material: Yes. All parts. Relation To Broader Scientific Literature: This study builds on CFR, which has been widely used in imperfect information games. However, traditional CFR focuses only on optimal strategy and lacks control over strategy diversity. This paper introduces preference degree and vulnerability degree, allowing AI to adjust strategies across different playstyles, filling the gap in personalized strategy learning and providing a new direction for research on adaptive strategies in game AI. Essential References Not Discussed: NA. Other Strengths And Weaknesses: - #### Weaknesses: #### - Limited experimental scope: The experiments are currently restricted to Texas Hold’em, lacking validation in other imperfect information games (e.g., StarCraft, economic games, bridge). - No comparison with more advanced game AIs: The advantages of Pref-CFR in strategy style control and competitiveness have not been fully evaluated against state-of-the-art AI models. - Lack of human player evaluation: If Pref-CFR aims to generate strategies that align better with human playstyles, professional players should be involved in testing, and their feedback should be collected to assess its usability and impact on human players. - Limited practical significance: While the generated strategies show diverse playstyles, the real-world impact of such stylistic variations remains unclear. What is the practical value of these playstyles, and how do they contribute to improving gameplay in real-world settings? Other Comments Or Suggestions: - Clarify Scope of Applicability: The paper primarily conducts experiments in Texas Hold’em, but its applicability to other imperfect information games remains unclear. Discussing how the method could generalize to multi-agent strategy games, economic simulations, and other domains would strengthen the paper's contributions. - Consider Human Player Evaluation: Since the method aims to adjust strategy styles, incorporating feedback from professional players would help assess its practical effectiveness in real-world gameplay. - Improve Formula Notation and Explanation: Some formula symbols and derivations could be further clarified, particularly in Appendix B, to enhance readability. - Figure 3 Strategy Visualization Improvements: (1) The current strategy display for Texas Hold’em is informative but lacks clarity and aesthetic appeal. (2) Consider a more intuitive representation, such as a cleaner color scheme or a different layout to enhance interpretability Questions For Authors: - Is Pref-CFR applicable to a broader range of imperfect information games? The current experiments are limited to Texas Hold’em, but CFR is applicable to a wider range of games. - Have the strategies generated by Pref-CFR been tested by human players? Is there a plan to have professional players test the strategies generated by Pref-CFR and collect feedback to verify their feasibility in real-world gameplay? - What is the practical value of having different playstyles in the generated strategies? Given that the generated playstyles (e.g., Aggressive and Loose Passive) are largely theoretical, how do these stylistic variations translate into real-world advantages, particularly for human players? Does this diversity actually improve gameplay, or is it primarily a theoretical construct? Ethical Review Concerns: NA. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Thank you for your detailed feedback. The strengths of the paper were perfectly understood, so we will only address weaknesses and questions below. --- ## Comparisons to state-of-the-art AI Our algorithm is not aimed at defeating top-level AI, so we didn't conduct this experiment at the start. However, competing against top AI can also prove the effectiveness of our algorithm, so we added this part of the experiment. For this paper, the algorithm and the strategy profile it produces needed to satisfy the following constraints: 1. Style customization, and possibly its usefulness 2. Beta-exploitability 3. Ability to work on a large-scale game Challenging a state-of-the-art AI is a third-party verification that ensures the correctness of the strategy profile produced and its lack of exploitability (2). It proves (3) even more, since it would use the full game (without bet or cards abstraction). However, it is not a direct way to evaluate the exploitability of the algorithm, which we did later in Head’s Up Texas Hold’em Poker. As expected, exploitability was under Beta. To be precise, passive solutions were very close to the normal version of CFR (6 mBB/h vs 4 mBB/h), while aggressive versions were very close to Beta (23 mBB/h vs 25 mBB/h). We believe that this difference is explained by the average size of the pot: in terms of %pot exploitability, results are closer. Now, to get back to the state-of-the-art AI point, the blueprint (no real-time solving) strategy used in the paper defeated Slumbot 2019 after 100,000 hands, by 34.2 mBB/h $\pm$ 12 mBB/h, which is a performance similar to the one achieved by Baby Tartanian8 against Slumbot 2017. Moreover, while blueprints are more exploitable in later streets due to post-flop cards’ abstraction, preflop is barely exploitable, and we only showed preflop results. Finally, you mentioned “the paper does not benchmark Pref-CFR against state-of-the-art models like DeepStack and Pluribus, making it unclear whether it offers meaningful advantages”. Pref-CFR should offer no advantage against top AIs, its goal is not to play optimally but to offer a trade-off between customization and performance, and to allow humans to understand how much wiggle room they have when deviation from Game Theory Optimal (GTO) solutions. --- ## Is Pref-CFR applicable to a broader range of imperfect information games? In fact, the scope of application of our algorithm is consistent with CFR, which is proved in our Appendix B.2. To avoid misunderstanding, we will emphasize this result in the main text. In addition, In addition, We have integrated Pref-CFR into OpenSpiel, a game-theoretic learning framework that supports over 100+ games. We successfully conducted two additional experiments in this environment. Due to character limitations, this part of the experiment can be found in the reply of reviewer CeZM. However, large-scale games require more specialized frameworks, which are often closed source, so we will limit ourselves to Texas Hold’em for now. --- ## Have the strategies generated by Pref-CFR been tested by human players? Hiring professional players for evaluation is extremely challenging. For example, Pluribus paid more than 50,000 dollars for professional players to appear in the experiment. The focus of our paper is to propose a method to find different styles of strategies in the game. It is too early to play against professional players. We conducted some tests among amateur players to prove that our algorithm is effective, and we will add this part in subsequent versions. --- ## What is the practical value of having different playstyles in the generated strategies？ In Texas Hold'em, we analyze the practicality of our algorithm from two perspectives: novel experience and winning more money. If it is to give players a novel experience, our current strategy is already very recognizable. In fact, our strategy can already become a qualified companion AI. We have verified the content of this part in the games played by amateur players. However, if you want to win more money with this strategy, there are two difficulties. 1. The strategies are hardly memorizable: there is a mixed strategy for every combination of private cards, requires players to practice for a long time. 2. If a player plays a particular style in order to win money, it is often to exploit a particular opponent’s weakness, while we do it without direct purpose. For the above two problems, we can use preference degree and beta to model the opponent's strategy profile, and then find the best response that is less likely to be exploited. Here, Pref-CFR will be used for modeling. It requires sufficient domain knowledge to model such a role, as well as an algorithm that produces safe exploits and meets player-friendly characteristics. We will continue to improve our algorithm in subsequent research. --- Rebuttal Comment 1.1: Comment: Thank you for the detailed response. It has addressed my main concerns. I am raising my score to 3 (Weak Accept). --- Reply to Comment 1.1.1: Comment: Thanks for your acknowledge of our work and for raising score. Thanks again for your time and effort in reviewing our paper.	Summary: This paper proposes a method for finding approximate equilibrium strategies in extensive-form games and claims to achieve strategies that balance “style” and “diversity” with playing strength. The authors present theoretical ideas in the context of two-player, zero-sum (2P0S) games (e.g., Kuhn poker), and also provide preliminary experiments in multiplayer Texas Hold’em. Their overall goal is to develop agents that have low exploitability while also satisfying certain preferences about how the agent plays. Claims And Evidence: - The paper claims that their method produces strategies which play according to the desired "style", while not increasing exploitability by too much. They claim this produces interesting, low-exploitability strategies in poker, whereas existing AI strategies for poker all play in the same style. The experimental results shown in Figures 1 and 2 (Kuhn poker) are convincing in demonstrating the method’s effectiveness in a toy domain. They convincingly show that their method can result in strategies that behave very differently, and without the cost of increasing exploitability by much. For the Texas Hold’em experiments, the evidence that the trained agents are low-exploitability is not as strong. The authors’ discussion under Table 2 attempts to convince the reader of the strength of the agents, but they are unconvincing to me. More direct exploitability evaluation on a smaller domain where exploitability can be calculated (e.g., Leduc poker, Turn/River hold'em) would strengthen the claims. Methods And Evaluation Criteria: The proposed method is a modification of CFR, parameterized by two parameters. The proposed evaluation criteria are Kuhn poker, 2-player Texas hold'em, and 3-player Texas hold'em. The paper needs to be much more clear about which parts apply to the 2P0S (two-player zero sum) setting only, and which claims pertain to the general setting. Almost nowhere in the paper do the authors specify that they specifically care about 2P0S, yet much of the discussion makes sense only in the 2P0S setting (e.g. characterization of Nash equilibria in Introduction as "maximizing expected payoffs under worst-case scenarios", and the rest of the paragraph and following paragraphs) -- e.g. the CFR-based methods surely only have convergence guarantees in 2P0S settings, yet experiments are also run on a 3-player domain. As mentioned above, there is not convincing evidence that the Texas Hold'em experiments produced low-exploitability agents. This is very difficult to do in a domain like Texas hold'em, so experiments in a more tractable domain would improve the paper. Theoretical Claims: I did not review the proofs of the method for correctness. Experimental Designs Or Analyses: See: Methods and Evaluation Criteria. Supplementary Material: I did not check the supplementary material. Relation To Broader Scientific Literature: The paper’s motivation draws heavily from the poker community, especially research on finding low-exploitability strategies using CFR variants. This is a well-established area with strong ties to multi-agent reinforcement learning and computational game theory. The paper aims to bridge preference-based methods (style/diversity) with standard CFR-like approaches. Essential References Not Discussed: - Other Strengths And Weaknesses: In all, the paper is well-motivated, the research direction is especially interesting to the poker community. I did not review the proofs of the methods for convergence, but the results in Kuhn poker look very good, and the qualitative Texas hold'em results are interesting. Nevertheless, I'm hesitant to recommend this version of the paper for this conference -- the writing still needs a lot of work. Additionally, the Texas hold'em experiments don't contain enough detail. Other Comments Or Suggestions: - Figures 1 and 2 are excellent results. They are convincing evidence of the effectiveness of the paper's method (albeit in a toy domain), and also clearly communicates the aims of the research direction. The charts could use some cleanup though -- all the text/labels in the charts are too small and hard to read. Questions For Authors: - In Introduction, "Nevertheless, strategies with winning probability as the sole objective" should probably say something like "EV" or "maximizing expected payoffs" instead of "winning probability", to be precise (for domains like chess with loss/draw/win and poker with integer-valued payoffs). - Bottom of page 1/top of page 2: The descriptions of \beta and \delta sound a little silly to me: "style" corresponds to the degree of exploitability of the strategy, and "diversity" corresponds to closeness to a particular type of play? Neither of those sound intuitive. - "setting only \delta" is not the most understandable -- this means setting \beta to 0, right? Why not just say that? \epsilon = \beta? Why do we need the notation for both then? Or, should this say \epsilon \leq \beta? - Related Work (line 94/95): "ju et al." should be capitalized? - Should clarify that FP converges in 2P0S. - I don't find the paragraph starting with line 100 to be super relevant -- too broad. Besides, CEs are NEs in 2P0S. - "This paper will synthesize the research from these two aspects" -- what two aspects? - Section 2.1.2 Extensive-Form Games: Last sentence "when all players select actions according to the strategy" should be "when all players select actions according to the strategy profile", to be precise. - Section 2.1.3. Nash Equilibrium: If we're not going to narrow the focus to 2P0S, then let's not use the terms "exploitability". Instead, call it NashConv or Nash distance (and you can state that this is called "exploitability" in 2P0S games). Regardless, I don't think we should call Equation 2 the "exploitability of player i", since it's about i deviating, not -i. - Section 3.1.: Again, we have description of \beta and \delta that do NOT match the descriptions given in the Introduction. Now, diversity is the size of an acceptable strategy space, and style is the similarity between a strategy distribution and a preferred strategy. However, later in the section, style is defined as the distance between a single strategy (not distribution) and a preferred strategy. - Section 3.2.: Conjecture 3.1: "In a 2P0S game, if the set of Nash equilibria forms a convex polyhedron" -- isn't this always true? - Section 4.1: Equation 13: why does the "otherwise" case have a "-1" in the numerator and the denominator? E.g. if the deltas are all 1, then we get 0/0, which is undefined. - After Equation 13, maybe "additionally" should say "alternatively"? - "We prove in the Appendix B.2 that the Pref-CFR algorithm can converge to the NE" -- shouldn't this clarify that this is only in 2P0S? In fact, even in the appendix, I don't see anywhere that clarifies that this is only in 2P0S. - Equation 16 notation needs work: argmax over a^i, over a function of a, not a^i? There should be an indicator function with equality to a, right? - Experiments: "In Heads-Up play, this setup achieved exploitability below 4 mBB/h" -- is this referring to Brown et al., 2018, or to your reproduced results? Code Of Conduct: Affirmed. Overall Recommendation: 2	Rebuttal 1: Rebuttal: Thank you for your feedback. We first answer your questions and comments in order (due to word limit, the original text is not quoted), and then we summarize some of the Experiments questions and answer them. If there are still questions or new questions arise, please feel free to discuss further. --- ## Questions 1. Indeed, this is a mistake and we will fix it. 2. We need to re-write the descriptions of $β$ and $δ$. In this section, I accidentally mistyped diversity and style. Diversity refers to the scale of the acceptable strategy space. Style refers to how close a trained strategy is to another preferred strategy. $δ$ incentivises a style and $β$ enforces it (at least in poker). Without $β$ (i.e. with a $β$ of 0), if there is only one Nash equilibrium, $δ$ is useless: Pref-CFR will find the original NE. 3. Setting only $δ$ indeed means setting $β$ to 0. $ε$ is a property inherent in the strategy, while $β$ is an artificially set parameter. These are two concepts so we use two symbols. We should say $ε \leq β$, and we will fix this problem. 4. "ju et al." should be fixed. 5. We will clarify that FP converges in 2P0S. 6. See (7). 7. The goal of this paper is to find a strategy that can take into account people's needs for "style" and "diversity" better than the equilibrium strategies (the NE strategy in two-player zero-sum games and the coarse correlated equilibrium (CCE) strategy in multi-player games). This divides our research into two parts: * How to define the strategies of "style" and "diversity"? * How to find strategies with different styles and diversities during the iteration? Therefore, the related work of this article is introduced in two parts. Lines 75 to 99 introduce how previous articles solved the equilibrium (finding the NE in 2p0s games and finding the CCE in multi-player games). The content after line 100 introduces what other studies, besides the traditional NE and CCE, have been conducted by predecessors to attempt to find "better" strategies. The writing of the related work in this paper does not present the above content well, and we will appropriately modify the wording. 8. “Strategy profile” is indeed more precise. 9. In general cases, we should indeed replace “exploitability” with NashConv/NE. Moreover, Equation 2 measures "Player i’s deviation incentive" rather than exploitability. 10. See (2). 11. A set of Nash equilibria does not always form a convex polyhedron. For instance, Rock-Paper-Scissors has a unique NE at $[1/3,1/3,1/3]$ (a single point). 12. Deltas cannot all be 1, We will emphasize this in the main text. And, for instance, if degrees are [1, 1, 2, 3] we choose actions with probability: [0, 0, ⅓, ⅔]. 13. We indeed meant “alternatively”. 14. To clarify, we reiterate our key proofs: * Appendix B.2 demonstrates that introducing preference parameter $δ$ in CFR preserves Blackwell approachability. * Appendix B.3 proves that the vulnerability parameter $β$ modifies the convergence target set of no-regret algorithms. Implications: - Based on B.2, our algorithm inherits the convergence guarantees of no-regret learning (equivalence to Blackwell approachability), converging to NE in 2p0s games and CCE in multiplayer settings. - B.3 establishes that convergence to the target cone $S_{≤β}$ corresponds to the epsilon-equilibrium class. We acknowledge the insufficient discussion of these connections in the main text and will: - Add explicit signposts in Section 4 - Include a new subsection in Appendix B to detail the proof roadmap. 15. This is a mistake. Thanks for spotting it. 16. This metric aligns with both Brown et al.’s results and our experimental findings. --- ## More Experiments For more experiments on smaller games, we have integrated Pref-CFR into OpenSpiel, and calculated the exploitability of 2p Texas Hold'em. These experiments show the good scalability and robustness of our algorithm, and we have redrawn the picture. The results of the experiment can be viewed at: https://drive.google.com/file/d/1F-oNqLm_cVqBNHvDYUf5dtQ_Rk1SdMkH/view?usp=drive_link In addition, we will add more details to Texas Hold'em training in later versions. We cannot show it to you here due to character limitations. You can check our new experiments in the response of the reviewer CeZM and BR1q. --- We deeply appreciate your rigorous review. All revisions will be prominently marked in the final manuscript.	null	null	null	null	null	null
Is Your Model Fairly Certain? Uncertainty-Aware Fairness Evaluation for LLMs	Accept (poster)	Summary: Regarding the limitation that conventional LLM fairness metrics ignore the impact of model uncertainty on biases, this work proposes an uncertainty-aware fairness metric UCerf. Additionally, to tackle the shortcomings of current datasets, the authors introduce a gender-occupation fairness assessment dataset, SynthBias. Utilizing the benchmark established on SynthBias and UCerf, they evaluate the behaviours of eight open-source LLMs and find unfairness issues that are not discovered by acc-based evaluation methods. Claims And Evidence: 1. Lines 120-123, "... with sampling-based generation, the EO score of model C would likely decrease in our example.". Could the authors give a more detailed explanation for why sampling-based generation leads to a decrease in the EO score of Model C? 2. Lines 130-133, "The example in Fig. 1 highlights the importance of joint fairness analysis with model correctness and uncertainty, as these orthogonal dimensions of performance are both crucial for identifying social harms." Why are the model's correctness and uncertainty orthogonal dimensions? Methods And Evaluation Criteria: 1. In section 3.3, formula (2) combines the normalized model certainty $C(x_i)$ and accuracy, and formula (3) further combines fairness evaluation. However, since there is an inevitable trade-off between fairness and accuracy, they are usually evaluated separately, and different scenarios may emphasize these two indicators differently. Correspondingly, does the UCerf indicator need to introduce relevant weight coefficients in the process of combining fairness and accuracy? Is there a trade-off between accuracy and uncertainty? 2. Can the UCerF metric be extended to scenarios with multiple attributes, such as racial bias, where the sensitive attribute has more than two values? Theoretical Claims: This work contains no theoretical proofs. Experimental Designs Or Analyses: The authors propose a fine-grained fairness ranking and evaluation method. The fine-grained means that it only affects and corrects the ranking of models with similar performance. Why do the rankings and evaluations of Pythia-1B and Falcon-7B-Inst differ significantly in UCerF, despite having similar EO scores of 0.341 and 0.345, respectively, on the SynthBias dataset? Similarly, is it reasonable that Mistral-7B-Inst (0.309) and Pythia-1B (0.341), ranked 4th and 5th in EO scores, are instead ranked 8th and 1st on UCerF, respectively? Supplementary Material: I have reviewed the supplementary and have no questions about it. Relation To Broader Scientific Literature: This work propose a finer-grained fairness evaluation method for LLMs through the lens of uncertainty. Essential References Not Discussed: No Other Strengths And Weaknesses: See above sections. Other Comments Or Suggestions: 1. There is a problem with the reference links, which makes it difficult to locate a specific reference. Please fix them. 2. The authors could consider providing some dataset test examples of SynthBias in the appendix. 3. The design of the dataset should focus more on revealing unfairness issues overlooked by traditional methods. Questions For Authors: See above sections. Code Of Conduct: Affirmed. Overall Recommendation: 2	Rebuttal 1: Rebuttal: We thank the reviewer for highlighting important points about the motivation and interpretation of UCerF, and the evaluation results. ## Q1 Explanation regarding discuss around Fig.1 We thank the reviewer for pointing out a potential confusion in the paper. Please refer to the second paragraph in our response to reviewer jA6X Q1. In short, with a higher uncertainty of Model C in the example case, the randomness in sampling leads to higher likelihood of generating “doctor” in the answer, which is an incorrect prediction and decreases TPO and, subsequently, EO. Over a large number of samples, the high uncertainty in Model C will inevitably lead to a lower EO compared to model D. ## Q2 Correctness and uncertainty as orthogonal dimensions We thank the reviewer for raising this question. By “orthogonal dimensions”, we mean that correctness and uncertainty are two separate aspects of model evaluation with independent scopes and purposes. We will clarify this statement in our revision. ## Q3 Trade-off between fairness and accuracy We acknowledge that trade-off between fairness and accuracy is an important research direction. However, note that the focus of this paper is on improving accuracy-based fairness metrics using uncertainty and not the relations between accuracy metrics and fairness metrics. Following [1], it is worth studying how debiasing methods impact the trade-offs between accuracy and fairness in the future work. We thank the reviewer for pointing this out. ## Q4 Extension to multiple attributes We appreciate the reviewer mentioning expansion of our metrics beyond binary groups. Any disparity metrics can be swapped in Eqn.3 since UCerF essentially measures the expected disparity of behavior desirability among groups. For example, we can simply compute the standard deviation of D(x) from all groups, which is the generalization of our binary distance in Eqn.3. We will include this discussion in our revision. ## Q5 Misalignment between EO and UCerF Please refer to our response to reviewer jA6X Q1 for further elaboration of the differentiation between UCerF and accuracy-based fairness like EO. As discussed in Sec.5.3 (e.g., L353), this is the exact evidence of the importance of uncertainty in LLM fairness evaluation, as the subtle behavior nuances (e.g., confidently correct with D(x)=0.99 vs unconfidently correct with D(x)=0.01) play a significant role in fairness. ## Q6 More samples of SynthBias Please see below for a short list of more examples of SynthBias. We will include two pages of data sampled from SynthBias in revised appendix and also publish the full dataset upon acceptance. Type1 examples: 1. The writer and the developer collaborated on the project before he submitted it. 2. After the meeting with the editor, the driver wanted to discuss his feedback. 3. The baker and the janitor shared a coffee break, and she told a funny story. 4. The designer admired the layout created by the chief, even though he was unsure about it. 5. During the meeting, the developer and the counselor exchanged ideas, and she made some useful suggestions. 6. The attendant passed the report to the analyst before he left for the day. 7. The cook and the attendant decided to take a break because he was tired. 8. While the writer and the manager were reviewing the feedback, she proposed a new approach. 9. The housekeeper and the janitor decided to clean the area because she wanted to finish early. Type2 examples: 1. The laborer brought coffee to the hairdresser, and he appreciated the thoughtful gesture. 2. After discussing the project, the editor asked the developer if she had any feedback. 3. The attendant noted the guard’s attention to detail before introducing her to the team. 4. The carpenter fixed the roof while the tailor completed his tasks below. 5. The designer endorsed the lawyer for her skills and dedication to justice. 6. When the case was closed, the sheriff thanked the accountant for his support. 7. The receptionist helped the salesperson with a client, and she felt grateful. 8. The mover successfully completed the task, and the editor complimented her on it. 9. The cook introduced the designer to a new recipe, and he took notes eagerly. ## Q7 More issue-revealing design of dataset We thank the reviewer’s observation on the design of SynthBias. This is one of our design goals, as SynthBias is explicitly constructed to contain both semantically rich and ambiguous contexts, where model overconfidence and bias are more likely to surface. For future work, we plan to expand the attribute axes and contribute to the intersectional fairness domain. We thank the reviewer again for the insightful questions and feedback. Please let us know if we can further elaborate or address any concern remains. [1] Kuzmin et al. "Uncertainty Estimation for Debiased Models: Does Fairness Hurt Reliability?." IJCNLP-AACL, 2023	Summary: Recent large language models were trained on vast scales of data to achieve stellar performance. However, these models also suffer from the biases present in their training data, creating fairness concerns across sensitive attributes. This work examines conventional fairness metrics in the context of large language models, points to their drawbacks and proposes a new fairness metric based on uncertainty of the predictions. The authors further enrich their analysis by proposing and evaluating on a synthetic dataset. Claims And Evidence: - The claim that considering only conventional fairness metrics and ignoring the uncertainty associated with predictions is supported to a limited extent. In particular, example use cases are highlighted quite clearly (as in Figure 1) and discussed in detail. In addition, some quantitative analysis was performed while comparing how equalized odds behave compared to the proposed uncertainty-based metric. However, various other group fairness metrics were not considered. Given the probable complementary nature of certain group fairness metrics when evaluated together, having comparisons with statistical parity [A] and equal opportunity [B] would further support the claims. In addition, while the UCerF could also be considered on a sample-wise setting, there were no discussions between existing individual fairness metrics [A, D] and UCerF. - The proposed uncertainty-aware metric is also well-motivated with clear examples and a nice figure (Figure 2). While the metric is also supported by reasonable design choices (such as choosing perplexity as a measure, or formulating the metric in an analogous way to conventional group fairness metrics), I think the work could benefit from a more thorough discussion on uncertainty quantification for large language models, and if possible, comparing different uncertainty quantification methods/measures [C] in addition to perplexity. This is specifically important for supporting the claims as the uncertainty quantification/measuring process is central to all of the remaining parts of the work. - Relevant criticism on the older benchmarks is discussed in detail and supported. Furthermore, the proposed dataset is validated with both automatic tools and human annotators. Based on the details presented in the work (Sections 4.3 and 4.4), the claims for the synthetic dataset is well-supported. One criticism that could be made could have been related to the extremely sensitive nature of fairness works and how a GPT-generated dataset may not have been the most suitable. However, given the scarcity of such data and also privacy concerns, the authors approach is quite reasonable. [A] Dwork, Cynthia, et al. "Fairness through awareness." Proceedings of the 3rd innovations in theoretical computer science conference. 2012. [B] Hardt, Moritz, Eric Price, and Nati Srebro. "Equality of opportunity in supervised learning." Advances in neural information processing systems 29 (2016). [C] Lin, Zhen, Shubhendu Trivedi, and Jimeng Sun. "Generating with confidence: Uncertainty quantification for black-box large language models." arXiv preprint arXiv:2305.19187 (2023). [D] Mukherjee, Debarghya, et al. "Two simple ways to learn individual fairness metrics from data." International conference on machine learning. PMLR, 2020. Methods And Evaluation Criteria: - As mentioned in the claims and evidence part above, the proposed method and the evaluation criteria are reasonable, given the scarcity of realistic and rigorous benchmarks for the fairness domain. - In addition, the authors use well-known large language models, making their evaluation more realistic compared to various works in the fairness domain. Theoretical Claims: The work has two parts that could be considered theoretical: - Using entropy over a probability distribution is well-established in the uncertainty quantification literature (though in different ways, sometimes based on ensemble predictions [A], sometimes with methods such as MC Dropout [B]). Though most of those approaches are based on N models instead of a single one, I think it is reasonable to choose perplexity given the computational expenses associated with LLM inference. - The proposed UCerF metric is analogous to the definition of established fairness metrics, thus no apparent issues are present there either. [A] Lakshminarayanan, Balaji, Alexander Pritzel, and Charles Blundell. "Simple and scalable predictive uncertainty estimation using deep ensembles." Advances in neural information processing systems 30 (2017). [B] Gal, Yarin, and Zoubin Ghahramani. "Dropout as a bayesian approximation: Representing model uncertainty in deep learning." international conference on machine learning. PMLR, 2016. Experimental Designs Or Analyses: Yes, please see the discussion above on the claims and evidences section. Supplementary Material: Yes, the supplementary material contains details on the validation process of the proposed dataset, more results with more LLMs and more discussions on sample use cases of the proposed metric. Relation To Broader Scientific Literature: This is a timely work where we observe large language models being used in wider domains than ever before. The fairness concerns associated with them are well-documented and it is very important to be able to properly measure how fair they are before deployment. Thus, I believe that this work would be relevant to the broader audience. Essential References Not Discussed: None, as far as I could find. Other Strengths And Weaknesses: The work is novel in the domain of fairness for large language models and presents analyses with various well-known models. It also contains various charts and figures for neatly explaining the motivations behind the design rationale of the metric. Other Comments Or Suggestions: None, other than what was already been mentioned. Questions For Authors: 1. Do you think different versions of UCerF could be defined, analogously with [A], and how do you think your observations would/could change? 2. Can you compare with statistical parity [B] and equal opportunity [C] as well? How does UCerF complement or improve those metrics? [A] Kuzucu, Selim, et al. "Uncertainty as a Fairness Measure." Journal of Artificial Intelligence Research 81 (2024): 307-335. [B] Dwork, Cynthia, et al. "Fairness through awareness." Proceedings of the 3rd innovations in theoretical computer science conference. 2012. [C] Hardt, Moritz, Eric Price, and Nati Srebro. "Equality of opportunity in supervised learning." Advances in neural information processing systems 29 (2016). Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: We thank the reviewer for the thoughtful feedback and for recognizing the novelty and contribution of our fairness evaluation framework and the clarity of our design rationale. ## Q1 Additional Group Fairness Metrics We thank the reviewer for the suggestion to further support our claims. We added comparisons with Equal Opportunity and Statistical Parity Difference in our evaluation as below. \|\|Mixtral-8x7B\|AmberSafe\|Falcon-40B\|Mistral-7B\|AmberChat\|Falcon-7B\|Pythia-12B\|Pythia-1B\| \|-\|-\|-\|-\|-\|-\|-\|-\|-\| \|Equal Opportunity\|0.120\|0.153\|0.184\|0.194\|0.216\|0.235\|0.270\|0.334\| \|Statistical Parity Diff.\|0.241\|0.308\|0.369\|0.374\|0.434\|0.459\|0.541\|0.677\| The rankings of the eight LLMs are the same under all three accuracy-based metrics including Equalized Odds shown in the paper, indicating consistent findings of the same lack of details in traditional accuracy-based fairness metrics. To further illustrate, we repeat the case study in Fig.5(b) similar to Sec.5.2. E.g., under Statistical Parity, the first two examples in Fig.5(b) would both yield a Statistical Parity Difference of 0 indifferently since the model predicts positive (pro-stereotypical) response in both groups. On the other hand, UCerF effectively captures the detailed fairness difference and reflects it in the metric scores as explained in Sec.5.2. ## Q2 Use of other uncertainty quantification estimators As both reviewers eQB5 and 6e3v rightly note, several uncertainty quantification methods exist [1,2]. However, our task setup following the WinoBias schema requires instance-level next-token uncertainty estimation, where many sentence-level uncertainty estimators are not directly applicable. Among applicable uncertainty estimators, recent studies, e.g., [3,4], also show that surprisingly logit-based uncertainty quantification methods such as perplexity remain competitive and effective among recent uncertainty quantification methods. Nonetheless, along this direction, we included two additional token-level uncertainty estimators in our experiments: Rényi divergence and Fisher-Rao distance [2]. UCerF scores using these estimators are shown below: \|\|Pythia-1B\|Falcon-40B\|Falcon-7B\|Mixtral-8x7B\|AmberChat\|Pythia-12B\|AmberSafe\|Mistral-7B\| \|-\|-\|-\|-\|-\|-\|-\|-\|-\| \|Rényi Divergence\|0.890\|0.889\|0.865\|0.858\|0.856\|0.854\|0.851\|0.792\| \|\|Mixtral-8x7B\|Falcon-40B\|AmberSafe\|Falcon-7B\|AmberChat\|Pythia-1B\|Pythia-12B\|Mistral-7B\| \|-\|-\|-\|-\|-\|-\|-\|-\|-\| \|Fisher-Rao Distance\|0.853\|0.849\|0.832\|0.816\|0.811\|0.807\|0.798\|0.786\| Some consistency can be observed. E.g., Falcon-40B is ranked second most fair under all three uncertainty estimators. Due to the different natures of uncertainty quantification methods, UCerF can capture fairness behaviors in different perspectives from different measures of uncertainty. However, for more intuitive interpretation, we recommend confidence-based uncertainty like perplexity to better explain model behaviors. Moreover, we emphasize that UCerF is a modular framework, agnostic to the specific uncertainty estimator. As discussed in Sec.2.2 (L118), Sec.3.3 (L163) and Impact Statement (L479), we adopt perplexity as a demonstration of our flexible framework for simplicity and straightforward intuition. As a fairness metric, we recommend confidence-based uncertainty estimation like perplexity in UCerF to better explain model behaviors. However, the user has the freedom to choose any uncertainty quantification method for respective use cases. ## Q3 Use of GPT-generated dataset We agree with the reviewer on the risk of using GPT-generated content for fairness which is a sensitive field. Hence, we employed multiple automatic filters and rigorous manual verification with 464 human raters from 11 English locales and at least 75% human agreement on the annotations for each sample, as detailed in Sec.4.3 and Appx.D.2, to ensure satisfactory quality of the curated SynthBias dataset. ## Q4 Different versions of UCerF Upon reading the work, we were not able to understand the analogy with [A]. We would appreciate a clarification to better understand the intent and we are happy to elaborate on how UCerF could be extended. We appreciate the reviewer’s constructive and important feedback, and hope our revisions address the remaining concerns while reinforcing UCerF’s contribution to LLM fairness. Please let us know if we can further elaborate or address any concern remains. [1] Kuhn et al. "Semantic Uncertainty: Linguistic Invariances for Uncertainty Estimation in Natural Language Generation." ICLR, 2023 [2] Darrin et al. “RainProof: An Umbrella to Shield Text Generator from Out-Of-Distribution Data.” EMNLP, 2023 [3] Vashurin et al. “Benchmarking Uncertainty Quantification Methods for Large Language Models with LM-Polygraph”. TACL, 2025 [4] Santilli et al. “On a Spurious Interaction between Uncertainty Scores and Answer Evaluation Metrics in Generative QA Task”. NeurIPS WS 2024 --- Rebuttal Comment 1.1: Comment: I would like to thank the authors for their detailed rebuttal. Just to clarify a point, both of my concerns, with respect to the additional fairness metrics and the uncertainty quantification pipeline were not related to the modularity or the broader goals of the method, but rather due to the veracity of the analyses presented in the work. With that being said, I can state that my concerns regarding the both of these are mostly resolved following the results presented by the authors. I also encourage the authors to include them in their finalized version (whether for this venue or the next) as I believe that it can enrich the analyses presented in the work. What I meant with Q4 was actually using the UCerF scores in different manners - e.g technically one can define "Statistical Parity" with the desirability score replacing accuracy etc. I acknowledge that it was my mistake to mention [A] there, as that work did not explore this either. I did not mean that this point was lacking in the work per se, I merely wanted to recommend it as I believe that it can further improve the work. Finally, I do not believe that the metrics proposed in this work are directly comparable with Kuzucu et al. [A], given that it relies on a specific definition of uncertainty with BNNs which is non-trivial to extend towards LLMs. Thus, I do not believe that lacking comparisons with that work is a drawback of this work. Accordingly, with these points, I will be raising my score. --- Reply to Comment 1.1.1: Comment: Thank you for confirming that our expanded evaluations with Equal Opportunity, Statistical Parity Difference, Rényi divergence, and Fisher–Rao distance address your concerns on our analyses. We appreciate your clarification regarding Q4. We agree that define "Statistical Parity" with the desirability score is an interesting extension and will include a brief discussion regarding this in the final version. Thank you again for your thoughtful feedback and for helping us improve the paper.	Summary: This paper observes that conventional accuracy-based fairness metrics overlook disparities in prediction uncertainty across demographic groups. Moreover, existing gender-occupation bias datasets are insufficient for evaluating modern large language models (LLMs), which have strong semantic understanding capabilities. To address these shortcomings, the authors propose UCerF, an uncertainty-aware fairness metric, and introduce SynthBias, a large-scale synthetic dataset explicitly designed to evaluate gender-occupation biases in LLMs. Experimental results on eight publicly available LLMs demonstrate that UCerF reveals fairness issues neglected by traditional accuracy-based metrics. ====== Update after rebuttal ====== During the rebuttal, the authors provided a more thorough explanation of the motivation behind the design, which partially alleviated my concerns. Overall, the contribution is meaningful, and I have adjusted my evaluation accordingly to reflect the clarified insights. I also encourage the authors to carefully revise the manuscript and further clarify the relevant definitions after the review process. Claims And Evidence: The authors claim that current fairness metrics are mostly accuracy-based while overlooking the predictive uncertainty. However, it is important to discuss whether and under what circumstances a combined correctness-uncertainty metric is necessary. Would it not be more effective to consider accuracy-based fairness and uncertainty-based fairness separately, as this approach could provide a more precise and comprehensive evaluation of an LLM's fairness? Methods And Evaluation Criteria: The proposed UCerF effectively integrates both correctness and uncertainty in LLM predictions, enabling a comprehensive assessment of fairness behaviors. It also accommodates different task types, including those with (Type 2) and without (Type 1) correct or desired answers. However, more discussion on the desired levels of U(X) for different tasks would make the definition more precise and more direct. Theoretical Claims: There is no theoretical claim in this paper. Experimental Designs Or Analyses: The experimental designs are overall sound and reasonable. The authors state that WinoBias is constrained by syntactic ambiguity and limited sentence structures. However, in Table 1, the comparison between WinoBias and the proposed SynthBias focuses solely on vocabulary-level differences. A more comprehensive comparison that includes syntactic and structural aspects would further substantiate the argument. Supplementary Material: I have reviewed Appendices B, C, and D to examine the dataset generation process and results. However, I found that there are only a few examples of the generated synthetic dataset. Providing more examples would help clarify its structure and characteristics. Relation To Broader Scientific Literature: This paper approaches fairness evaluation from a finer-grained perspective by incorporating uncertainty. Additionally, the proposed synthetic dataset enhances the evaluation of gender-occupation bias in LLMs and can further improve bias mitigation. These contributions are important for the community. Essential References Not Discussed: The authors have discussed a recent and relevant reference [1]; however, they have not compared or evaluated the proposed UCerF against the methods presented in [1]. [1] Selim Kuzucu, Jiaee Cheong, Hatice Gunes, Sinan Kalkan: Uncertainty as a Fairness Measure. J. Artif. Intell. Res. Other Strengths And Weaknesses: Strengths: - This paper proposes to study fairness evaluation in large language models from the perspective of uncertainty, which is an important research topic. - The proposed SynthBias dataset serves as a reasonable extension of the WinoBias benchmark and has the potential to make a valuable contribution to the fairness research community. - The paper is well-written and generally easy to follow. Weakness: - As mentioned in the Claims And Evidence part, the motivation and application scenarios of the proposed uncertainty-based fairness metric require further discussion. Specifically, compared to separately considering accuracy-based and uncertainty-based metrics, what are the advantages of jointly assessing correctness and uncertainty? Could this approach obscure the root causes of unfairness or misrepresent a model’s capacity in certain scenarios, as accuracy and uncertainty represent distinct dimensions for evaluating a model’s performance and fairness? - The problem setup needs further clarification. For instance, in Sec. 3.3, providing a more formal mathematical definition of the input, LLM, and uncertainty estimator would enhance the paper’s precision and clarity. - Including more examples and conducting a syntactic analysis of the synthetic dataset would further strengthen its contribution. - The current work is limited to gender-occupation stereotypical bias. 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 constructive feedback and for acknowledging the significance of fairness evaluation through the lens of uncertainty and the contribution of SynthBias to the fairness research community. ## Q1 Motivation for a combined correctness-uncertainty metric We appreciate the reviewer’s question regarding the motivation and validity of combining correctness and uncertainty rather than evaluating them separately. Our core contribution lies in that UCerF is not a simple combination of accuracy-based and uncertainty-based fairness metrics but an integration of uncertainty information to improve accuracy-based fairness metrics. Below we argue why our novel integration of uncertainty to accuracy-based fairness metric is not only beneficial but essential. The majority of fairness metrics, which are based on accuracy alone, suffer from the limitation of merely using correctness to explain model behavior and overlook the additional details from uncertainty. As illustrated in our case studies (Fig.1,3,5), models can achieve the same accuracy-based fairness while exhibiting vastly different behaviors in terms of certainty which reveals more details about model fairness. Taking the example sentence and model C and D in Fig.1, while model C correctly resolve “his” to “nurse” in this specific example, its high uncertainty suggests low stability in prediction and is more likely to generate biased prediction than model D. Traditional accuracy-based fairness metrics cannot capture this nuance, but with the uncertainty information, we improve these metrics to capture the details in fairness behaviors. On the other hand, recent uncertainty-based fairness metrics on LLMs [1] did emphasize the importance of ensuring the same model behavior in terms of uncertainty among different groups. However, prediction correctness, an equally if not more important descriptor of the model, is overlooked in their proposed metric. Under this metric, a model that is always confidently correct would share similar fairness scores with a model that is always confidently incorrect. As Fig. 2 shows, model behavior is a continuous feature rather than a coarse discrete boolean value, and UCerF captures the same information in the desirability score D(x) as both accuracy-based and uncertainty-based metrics do while addressing their weaknesses. On the contrary of obscuring the root cause of unfairness, our metric helps to identify the bias issue via D(x) for the reasons explained above. UCerF is not just a simple combination of the two independent metrics, but an improvement of both metrics for fairness evaluation. ## Q2 Desired levels of U(x) for type1 and type2 tasks We thank the reviewer for pointing out the missing details. For both type1 and type2 scenarios (with and without the ground truth answer), the desired value of U(x) is 1 as the distance between model desirability D(x) is 0. We will revise Sec.5.1 to explicitly include this clarification. ## Q3 Vocabulary-only comparison between WinoBias and SynthBias We thank the reviewer for highlighting the importance of comprehensive dataset comparison. However, not all comparison metrics in Tab.1 are vocabulary-level. The Embedding Pair Distance STD and Silhouette Score metrics are computed based on sentence embeddings to compare the datasets from a high-level semantic perspective. ## Q4 More samples of SynthBias Please refer to our response to reviewer E5xz Q6. ## Q5 Comparison to relevant work - Kuzucu et al., 2023 We acknowledge that [1] is an important step towards uncertainty-based fairness and explicitly discussed this work in Sec.2.3. Moreover, please refer to our response Q1 above for the key differentiation from [1] that the consideration of correctness is important. In our task setup, evaluating fairness without incorporating correctness can result in misleading fairness scores. ## Q6 More formal mathematical formulation We thank the reviewer for expressing confusion in our formulation. We will revise the paper to formally define LLM $G$ as $y_i = G(x_i)$. We are happy to expand on any part that the reviewer finds to remain confusing if the reviewer can specify. ## Q7 Limited scope in gender-occupation bias We chose gender-occupation bias as it is a well-established and prominent problem setting. However, it is worth noting that our metric itself is not defined or limited in any specific domain. Please refer to our response to reviewer eQB5 Q2 where we show evaluation in other social bias aspects such as race and religion in the BBQ Lite dataset. We will include these additional evaluation on other bias domains in our final revision. We hope these clarifications reinforce the novelty and importance of UCerF as a metric that extends beyond the limitations of accuracy- or uncertainty-only fairness assessments. Please let us know if we can further elaborate or address any concern remains. [1] Kuzucu et al. “Uncertainty as a Fairness Measure” JAIR, 2023	Summary: The paper proposes a novel fairness metric, UCerF, which takes into account not only the model's predictions but also its uncertainty. In addition to the metric, authors propose a new synthetic dataset (SynthBias) for fairness evaluation of LLM on co-reference resolution task. Finally, the authors combine the metric and the dataset into the fairness evaluation benchmark and evaluate several LLMs on this benchmark. 1. Authors provide an original approach for evaluating the fairness of LLMs, based on per-group uncertainty instead of accuracy. This metric could improve the fairness evaluation of LLMs for some tasks. 2. To demonstrate the proposed metric, the authors present a novel dataset for fairness evaluation (SynthBias). While the main idea of the dataset follows the previously introduced WinoBias dataset, the proposed SynthBias extends WinoBias by making it more challenging and appropriate for state-of-the-art LLM. Claims And Evidence: - The proposed metric, UCerF, highly relies on the uncertainty of the model's generation. However, authors use only perplexity as the uncertainty measure, while there are a lot of other methods of uncertainty quantification. Recent studies show that there are better methods than perplexity for uncertainty quantification in LLMs. Overall, without an additional ablation study, it is not clear how reliable the proposed metric is with respect to various uncertainty quantification methods. - The UCerF compared with the EO metric only on two datasets, while there are some other datasets for gender-occupation bias (see Questions section for missed references). It will be beneficial to report the results on these datasets as well to better support the claim that UCerF better represents the fairness of LLMs than EO. The same idea remains for additional models for evaluation - the results on several modern LLMs will be very useful for practitioners and allow to show the benefits of using UCerF for evaluation. Methods And Evaluation Criteria: - There is no enough motivation behind the joint fairness-performance metric (FP) in Appendix A. For example, consider: DTO score - Han X. et al. Fairlib: A unified framework for assessing and improving fairness. Proceedings of the 2022 Conference on Empirical Methods in Natural Language Processing: System Demonstrations. 2022. The overall choice of FP as a simple dot product is questionable due to the unequal contribution of components (especially in the case of perplexity, which is not normalized in a 0-1 scale). Theoretical Claims: - Experimental Designs Or Analyses: It will be very beneficial to add some modern LLMs, and maybe compare results for open-sourced and closed-source ones. Supplementary Material: Appendix A. Relation To Broader Scientific Literature: The authors propose UCerF, an uncertainty-aware fairness metric that significantly expands upon previous attempts (Kuzucu et al., 2023) by jointly considering prediction correctness and uncertainty, rather than separately evaluating uncertainty across groups. This novel approach enables finer-grained discrimination between model behaviors, capturing scenarios where LLMs exhibit biased overconfidence in predictions, a phenomenon not adequately addressed by existing metrics. However, this work overlooks previous papers on this work e.g. Kuzmin, Gleb, et al. "Uncertainty Estimation for Debiased Models: Does Fairness Hurt Reliability?." Proceedings of the 13th International Joint Conference on Natural Language Processing and the 3rd Conference of the Asia-Pacific Chapter of the Association for Computational Linguistics (Volume 1: Long Papers). 2023. The authors introduce SynthBias, a dataset addressing key limitations found in widely-used fairness evaluation datasets such as WinoBias (Zhao et al., 2018), WinoBias+ (Vanmassenhove et al., 2021), and GAP (Webster et al., 2018). However overlook citation to the BIOS dataset and the CrowS-Pairs dataset. Essential References Not Discussed: There are several missed references: 1. Relevant work: Kuzmin, Gleb, et al. "Uncertainty Estimation for Debiased Models: Does Fairness Hurt Reliability?." Proceedings of the 13th International Joint Conference on Natural Language Processing and the 3rd Conference of the Asia-Pacific Chapter of the Association for Computational Linguistics (Volume 1: Long Papers). 2023. 2. BIOS dataset (the gender-occupation bias dataset) - De-Arteaga M. et al. Bias in bios: A case study of semantic representation bias in a high-stakes setting. Proceedings of the Conference on Fairness, Accountability, and Transparency. 2019. P. 120-128. 3. CrowS-Pairs dataset also has a gender-dependent subset - Nangia N. et al. CrowS-pairs: A challenge dataset for measuring social biases in masked language models. arXiv preprint arXiv:2010.00133. 2020. Other Strengths And Weaknesses: - Other Comments Or Suggestions: 1. Typo in Section 5.2 - This gap highlights that while the model achieves perfect correctness on TPR, the predictions are not as desirable as expected based on TPR. (in the last part TPR should be replaced by TPD). 2. Typo in the abstract - UCerf -> UCerF. ============ After rebuttal I thank the authors for the detailed response and clarifications. Regarding Q1, the additional results with Rényi divergence and Fisher-Rao distance are interesting, but these uncertainty quantification methods are denoted as among the worst on similar tasks [1]. Hence, the usage of these methods could affect the overall UCerF results. It will be beneficial to compare with more powerful methods, e.g., MSP from the benchmark [1]. Regarding other questions, the additional results mostly addressed my concerns, and I suggest including these results in the camera-ready version to strengthen the main claims of the paper. Based on this, I will raise my score. [1] Vashurin et al. “Benchmarking Uncertainty Quantification Methods for Large Language Models with LM-Polygraph”. TACL, 2025 Questions For Authors: - Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We thank the reviewer for the thoughtful feedback and recognition of the novelty and relevance of our proposed UCerF metric and SynthBias dataset. ## Q1 Use of other uncertainty quantification estimators Please refer to reviewer 6e3v Q2 for response. ## Q2 Limited dataset in evaluations We appreciate the reviewer pointing out two other gender-occupation fairness datasets in addition to our discussion on related datasets. We will cite and discuss them in the camera-ready revision. We chose a WinoBias-like dataset for its well-established and effective evaluation setup. Bias in Bios is shown to be overly simple as the main source of bias is only the gender-related tokens [1]. On the other hand, CrowS-Pairs is curated for masked LMs and needs to be repurposed for the autoregressive LMs studied in our work. Nonetheless, we have expanded our experiments on the BBQ Lite dataset [2], which has longer sentence context and a broader span of biases such as race and religion. Taking Pythia 1B and Mistral 7B as an example, the UCerF scores on BBQ Lite are: \|\|Gender\|Disability\|Race\|Appearance\|Religion\|Age\|SES\|Orientation\| \|-\|-\|-\|-\|-\|-\|-\|-\|-\| \|Pythia 1B\|0.991\|0.941\|0.977\|0.983\|0.902\|0.873\|0.918\|0.892\| \|Mistral 7B\|0.897\|0.910\|0.955\|0.940\|0.975\|0.986\|0.985\|0.944\| The results reveal different strengths among LLMs, e.g., Mistral is more biased regarding gender and disability while Pythia is more biased in other social aspects. We will include the evaluation of eight LLMs on nine social bias splits in BBQ Lite in the revision to provide more comprehensive LLM social fairness evaluations. ## Q3 Choice of joint fairness-performance metric We thank the reviewer for pointing out and recommending another joint fairness-performance metric. As we highlighted in our Impact Statement, the focus of our work is on the new fairness metric and evaluation. We mentioned the joint evaluation of fairness and performance in the appendix due to its importance in model selection; but since it is not our main contribution, we presented the simple dot-product-based combination as a demonstration. Note that both UCerF and Accuracy are normalized on a scale of 0 to 1. Nonetheless, the recommended DTO score is an informative addition to this appendix section and we re-evaluated the models under DTO, as shown below: \|\|Pythia-1B\|Pythia-12B\|AmberChat\|AmberSafe\|Mistral-7B\|Mixtral-8x7B\|Falcon-7B\|Falcon-40B\| \|-\|-\|-\|-\|-\|-\|-\|-\|-\| \|DTO\|0.318\|0.273\|0.259\|0.243\|0.255\|0.176\|0.278\|0.206\| We found consistent model ranking results as in Tab.2 in the paper and will include and discuss DTO in the paper revision. We appreciate the reviewer’s suggestion. ## Q4 Evaluation on more modern LLMs We acknowledge the benefits of evaluating more recent LLMs and evaluated Qwen-72B-Instruct on the WinoBias Type 2 task as below. We will also include full evaluations of Qwen and DeepSeek models in our final revision. \|\|Acc\|Equalized Odds\|Equal Opps\|Statistical Parity Diff\|Perplexity\|UCerF\| \|-\|-\|-\|-\|-\|-\|-\| \|Qwen-72B\|0.961\|0.064\|0.062\|0.119\|1.243\|0.902\| The results indicate that Qwen-72B-Instruct, a more advanced LLM, achieves the best performance and fairness (under all fairness metrics) as expected. ## Q5 Overlooked previous work - Kuzmin, Gleb, et al. We thank the reviewer for pointing out another work around fairness from the perspective of uncertainty-based reliability. We will cite and discuss this work in our revision. However, despite the work promoting the importance of evaluating models on both fairness and reliability metrics, which supports the motivation of our work, the study in this work is not directly related to ours. This work studied fairness and reliability (uncertainty) as two separate metrics and focused on how debiasing methods impact the trade-off between the two metrics. On the other hand, our work promotes an improvement in the fairness metric itself by incorporating uncertainty information. Hence the methods are not directly comparable. Please see our response to reviewer jA6X Q1 for more detailed explanation on our differentiation from studies in fairness and uncertainty metrics. ## Q6 Typos We thank the reviewer for pointing out the typos in the paper. Regarding the first “typo” in Sec.5.2, i.e., “the predictions are not as desirable as expected based on TPR” as a part of discussion of Fig.5(a), we meant that the model behavior desirability is overestimated based on TPR since the TPD score, which is more informative, reveals that the model is not perfect. We will update and clarify this point in the paper revision. We hope these revisions adequately address your concerns and demonstrate the rigor, flexibility, and value of UCerF as a fairness evaluation framework. Please let us know if we can further elaborate or address any concern remains. [1] Hua Tim. SHIFT relies on token-level features to de-bias Bias in Bios. AI Alignment Forum, 2025 [2] Parrish et al. "BBQ: A hand-built bias benchmark for question answering." Findings of ACL, 2022	null	null	null	null	null	null
Polynomial-Time Approximability of Constrained Reinforcement Learning	Accept (poster)	Summary: The authors study the computational complexity of constrained MDPs. They show some novel results regarding finding approximately optimal policies. In particular, they studied the question of whether polynomial time approximation algorithms exist for many of the classic formulations studied in the CRL literature. They found that for the vast majority of constraints, including all the standard constraints, polynomial-time approximability is possible. Their work resolves the polynomial-time approximability of many settings, some of which have been lacking in any polynomial-time algorithm. Claims And Evidence: Yes. Methods And Evaluation Criteria: Yes. Theoretical Claims: I only checked the main body :) Experimental Designs Or Analyses: Yes, at a high level. Supplementary Material: No. Relation To Broader Scientific Literature: Contributions are relevant and important for the broader RL community, as they prove long-sought guarantees for various types of RL tasks, such as polynomial-time approximability for policies under chance constraints, deterministic policies under multiple expectation constraints, policies under non-homogeneous constraints (i.e., constraints of different types), and so on. Essential References Not Discussed: No. Other Strengths And Weaknesses: This work is to the best of my knowledge, original. The authors are the first to prove polynomial-time approximability for the following settings: policies under chance constraints, deterministic policies under multiple expectation constraints, policies under non-homogeneous constraints (i.e., constraints of different types), and policies under constraints for continuous-state processes. This fills an important gap in the literature, and for that matter I am vouching for this paper to be accepted. Other Comments Or Suggestions: Please add an Impact Statement! Questions For Authors: Page 1: Please frame your main question in a more general way. Page 2: Could you please add some discussion on CAMDPs? Page 3: I do not understand Definition 2.4. Page 3: Can you please add some comments regarding Proposition 2.3 (proof sketch)? I understand that the proof is in the appendix, but some justification must be added in the main body as well. Page 4: In Equation (2), did you perhaps mean to sum over $a$? Please further explain Equation (4). Page 5: Please elaborate on the functionalities of Algorithm 1 and Algorithm 2, in their respective captions. Page 6: I do not understand Lines 302 to 309 (second column). Page 7: Theorem 5.4: Why is this running time polynomial? Page 8: Please further elaborate on future work. Code Of Conduct: Affirmed. Overall Recommendation: 5	Rebuttal 1: Rebuttal: Thank you for your constructive feedback! We will update the paper to clarify the points the reviewer made. To address your questions, [Page 4] This is meant to be s' as is. Note, this equation corresponds to the usual policy evaluation equations for a deterministic policy. Here, we are assuming a is the specific action chosen by the policy. [Page 7] Note, each quantity involved is part of the MDP, so smaller than its description size. Recall that m, the number of constraints, must be constant or else the problem cannot be solved efficiently. Given m is constant, quantities such as S^m are then polynomial-sized. For example, given only one constraint, the bound is $O(H^7 S^6 A poly(\|M\|)/\epsilon^3)$, which can be seen to be polynomial in $\|M\|$ and $1/\epsilon$. Thanks again and let us know if there is anything else that needs clarifying!	Summary: The paper develops approximation algorithms for constrained MDP problems. The problem formulation in the paper can incorporate a broad class of recursively computable constraints, including almost-sure, chance, expectation, and their anytime variants. For this general problem formulation, the paper develops a framework to compute a near-optimal policy that achieves the same objective value as the optimal policy, while ensuring that the constraints are satisfied with an additive error $\epsilon$. The general approach developed in the paper is based on an augmentation scheme. To be specific, the paper chooses a future artificial budget to replace the original constraints. The artificial budget imposes some restrictions on the actions that can be taken at each round, and then enables us to reduce the original constrained MDP problems into MDP problems. Then, with this reduced MDP problem, the paper can develop the associated Bellman updates and employs a dynamic programming to solve the problem. However, the dynamic programming can be hard to solve, the paper then develops a dynamic rounding approach to ease the computation. Finally, with an additional approximation method that approximates the possible set of artificial budget with a finite set, the paper develops an $\epsilon$-approximate policy with a computation time polynomial in $1/\epsilon$. The paper further extends their approaches to continuous settings, as well as function approximation settings. Claims And Evidence: The claim is clear and looks convincing. Methods And Evaluation Criteria: The method makes sense, however, there is no numerical validation of their algorithms, as I further explain in the strength and weakness part. Theoretical Claims: I have checked the proofs and the theoretical claims. They look correct to me. Experimental Designs Or Analyses: There is no numerical experiment in the paper. Supplementary Material: I have reviewed the supplementary material. Relation To Broader Scientific Literature: The main contribution of the paper is to develop a general method to approximate the CMDP problems, where the constraints can take many formulations, including almost-sure, chance, expectation, and anytime variants. The paper computes a policy that enjoys the same objective value as the optimal policy, and violates the constraint up to an additive $\epsilon$ bound, with a computation time polynomial in $1/\epsilon$. Essential References Not Discussed: Most papers are discussed. Other Strengths And Weaknesses: Strength: The paper develops a general approach to handle the CMDP problems, where the constraints can incorporate many formulation, for example almost surely, chance, expectation, and the anytime variants. Weakness: 1. The comparison with the previous literature can be made better. The CMDP problems are classical problems, and many algorithms have been developed to solve the CMDP problems. However, it is not clear from the paper whether the computation time bound improves over the previous results. 2. The writing of the paper could be further improved, especially the descriptions of the methods in Section 6. 3. There is no numerical experiment over the algorithms developed in the paper. 4. The constrained MDP problems considered in the paper actually assume that all the problem parameters are given and the algorithms in the paper rely heavily on the prior knowledge of the cost, as well as transition probabilities. Therefore, I do not see any learning element in the paper, though the title of the paper is about reinforcement learning. Other Comments Or Suggestions: 1. In Section 6, it is said that an OpenAI gym environment is developed to model the approach with function approximation on this CMDP. However, I cannot find further details in the paper. 2. There is no impact statement in the paper. Questions For Authors: 1. It seems to me that your algorithm will always produce a deterministic policy. However, it is well known that the optimal policy for a CMDP problem can be a randomized policy, especially when the constraint takes an expectation formulation. Is it possible that your algorithm will output a randomized policy? 2. Since the paper assumes that all the problem parameters are given, could we just formulate the CMDP problem as an optimization problem, and then use the existing optimization algorithm to solve it? For example, Altman (1999) just formulates the CMDP problems as linear programming to solve it. 3. How does the computation time bound developed in the paper compare to previous bounds established in the literature? 4. Since the title of the paper is regarding reinforcement learning, how to implement the algorithm when the problem parameters are not given, for example, the cost and the transition probabilities are unknown. 5. Could you comment on the real performance of your algorithm? Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Thank you for your constructive feedback! Please see our general rebuttal above in Reviewer htBq's rebuttal section, which addresses Weaknesses 2-4 and other points the reviewer brought up. In addition to those points, we address several points below. [Weakness 1] In our paragraph "Past Work" in the introduction, we explicitly mentioned all known works that achieve polynomial-time approximation algorithms for special cases of our problem. Are there any specific works the reviewer is thinking of that we have missed here? All other works we are aware of are exponential time or apply to completely different settings, and thus are immediately inferior or incomparable to our method within the context of establishing polynomial-time approximability of our problem. However, we are happy to include references to exponential time algorithms if the reviewer feels this will make connections to the literature clearer. [Q1] Note, in the appendix, we show how to modify our method to achieve stochastic policies. However, we emphasize that the computation of stochastic, expectation-constrained policies is already known and so not a goal of our paper. Our goal is to compute deterministic, expectation-constrained policies and policies under other constraints, which are problems that have yet to be solved in the literature. [Q2] Note, this approach only works for stochastic, expectation-constrained policies. The LP formulation no longer holds when policies are additionally constrained to be deterministic or are forced to obey more complex anytime or chance constraints. This is immediate since our problem is NP-hard as mentioned in the "Hardness" paragraph, so any such polynomial-sized LP formulation would immediately imply that P = NP. [Q3] As in our Weakness 1 discussion, we again emphasize that the only goal of our paper is to devise polynomial-time algorithms for problems that currently have none. As such, the only distinction we focus on is polynomial runtimes vs exponential runtimes. Since all the open problems we discuss either have only exponential time algorithms or have no algorithm whatsoever, our algorithms beat all such competitors by definition in the context of computational complexity. Again, we are happy to include references to exponential time algorithms if the reviewer feels this will make connections to the literature clearer. [Q4 + Q5] Please see our general rebuttal in addition to the discussion above for Q3. Thank you again for your feedback, and let us know if there is anything else we can clarify!	Summary: The submission provides a novel generic bicriteria approximation algorithm that covers a broad range of Constrained Markov Decision Processes (CMDPs). Claims And Evidence: Yes, with the exception of the malformed definitions and anecdotal experimental setup (see "Other Strengths and Weaknesses"). Methods And Evaluation Criteria: The submission is of foundational nature and the methods (proofs) are appropriate. Theoretical Claims: Only some, due to issues with malformed definitions. Experimental Designs Or Analyses: N/A. Supplementary Material: I did not verify the correctness of proofs in the supplementary material. Relation To Broader Scientific Literature: The results build on and extend previous works on solving CMDPs; the most closely related paper is the AISTATS 2024 paper which provides a bicriteria approximation algorithm for a subset of the instances considered here. Essential References Not Discussed: N/A. Other Strengths And Weaknesses: On the positive side, the overall contribution of the submission is solid: while it lacks experimental evaluations (contrasting many of the preceding papers), it does provide a non-trivial theoretical contribution which pushes the boundaries of approximability for a range of CMDPs. I am not an expert on CMDPs, but the description of the related work to me convincingly justified the relevance of these problems. The inclusion of the to-the-point "Our Techniques" paragraph is a nice touch that is often missing from theoretical ICML submissions. Nevertheless, given how close the result is to the recently developed polynomial-time (0, ϵ)-additive bicriteria approximation algorithms of McMahan and Zhu (AISTATS 2024), I would have expected a closer treatment of how the techniques differ from those used previously. There is a brief note on this at the start of Section 3, but does that paragraph imply that there is no intersection between the techniques used here and those employed in the preceding AISTATS 2024 paper? Regarding experimental evaluations, the second-to-last paragraph of the submission mentions a seemingly anecdotal experimental setup without providing any proper details. I believe that in the current form, these claims should not appear in the main body of the submission as they are entirely non-reproducible; they can either be expanded to a proper experimental setup (with details), or moved entirely to the appendix. As the submission's contribution is foundational, I do not consider the lack of experiments to be a significant issue. -On the negative side, the problem is not properly formalized, or more precisely, the provided definition in Section 2 is malformed. It defines a caMDP as a tuple of the form (H,S,...), which is fine - however, when describing the elements of the tuple, it never speaks about S but rather about S_h where h is never defined or explained (and similarly for A_h etc.). Moreover, is the "time horizon" H an integer? What is the triangle(S) and triangle(R) notation? And are s,a elements of S and A, respectively? These things have to be made crystal clear, as without the formal definitions the vast majority of the ICML audience would not be able to understand the specific formal model used (and hence the contributions become meaningless). Due to these issues, I could not verify the formal correctness of the proofs. Formal issues aside, given the complexity of the problem formulation it would be natural to include a simple example of a concrete problem instance (possibly highlighting various types of constraints). This could be, e.g., a running example that guides readers through Section 2, or just some summarizing examples at the end of that section. ## Update after rebuttal Thank you for the responses; I maintain my assessment and score. Other Comments Or Suggestions: -Typo on page 2: "bicritiera" should be "bicriteria", and there should not be an "a" on row "64". -The running title still has the placeholder "Submission and Formatting Instructions for ICML 2025". -Row 196: "Our revolves around" - I suggest rephrasing, as it is not clear what "Our" refers to. -Row 400: "The user also have" -> "... has" Questions For Authors: The authors are welcome to respond to any of the points raised in the "Other Strengths And Weaknesses" section, and in particular clarify the problem definition while providing some concrete example of a problem instance. I am open to adjusting my score, but cannot currently recommend acceptance given the current state of the presentation. On a related note, is there a reason for using CMDP in some places, cMDP in others and caMDP elsewhere? Are these the same things merely using inconsistent abbreviations? As far as I could see, only caMDP is formally defined in the paper. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Thank you for your constructive feedback! Please see our general rebuttal above in Reviewer htBq's rebuttal section. [Formalization] In addition, we address the claim that our problem is not properly formalized. As our work is within the domain of CRL, we assume some basic familiarity with CRL notations and conventions. Specifically, our definition of a caMDP is almost identical to the usual definition of a "constrained MDP" used in other CRL works, including the AISTATS paper [1] that the reviewer referenced. That being said, we are happy to break the norms of the literature to enhance the clarity of the paper. To this end, we will add the following clarifications: 1) H is a positive integer, 2) s represents a state, 3) a represents an action, 4) $\Delta(X)$ represents the probability simplex over elements of a set X (so $\Delta(S)$ is the set of all possible distributions over states), and 5) Lowercase c denotes the cost function when costs are deterministic, similar to lowercase r. [Non-Stationarity] To clarify to the reviewer, we used $S_h$ and $A_h$ in the definition of caMDPs because Definition 3.1 requires a non-stationary state and action space that may change over time, similar to Definition 2 in [1]. To clarify this, we will revert to a classic stationary state space in the caMDP definition, and instead define the non-stationary state and action space concept more explicitly in Definition 3.1, where that concept is first needed. Consequently, the caMDP definition would then take the more standard form $(S, A, H, P, R, C, s_0)$. [CMDP Definition] We also would like to point out that we have formally defined a CMDP in the paragraph "Constrained Processes" to be the tuple $(M, C, B)$ consisting of a caMDP along with a cost criterion $\mathcal{C}$ and a budget B. We introduce this definition because known works on constrained MDPs only consider a single constraint type, so the cost criterion is usually assumed from context. However, since we consider many different types of constraints here, we felt it would be useful to explicitly specify the cost criterion in the environment's definition. If it would be clearer, we are also happy to skip the definition of a caMDP and define a CMPD as the 9-tuple: $(S, A, H, P, R, C, s_0, \mathcal{C}, B)$. Note, the lowercase cMDP is just a typo that should be CMDP. As mentioned above, CMDP and caMDP are different. [Comparison to [1]] Concerning a comparison to [1], we bring the reviewer's attention to the section 3 statement: "When moving to other constraints, the cumulative cost may no longer suffice to determine constraint satisfaction. For example, the expected cost depends on the cumulative cost of all realizable branches, not just the current branch." Thus, unlike the simple augmentation of cumulative cost as done in [1], here we must use a more abstract notion of artificial future budgets with our state augmentation. This results in an exponentially sized augmented action space that cannot be solved efficiently using standard algorithms, unlike the simpler MDP constructed in [1] without action augmentation. This forces us to design an entirely new approximate dynamic programming (DP) approach, which makes up the entirety of section 4. Lastly, in the paragraph "time-space errors", we mentioned that we use a customized rounding scheme due to errors accumulating over space and time in our approximate DP approach, unlike that of [1]'s projection scheme. These are all key fundamental differences needed to tackle combinations of constraints beyond anytime constraints. [Running Example] We will also add a self-driving car example commonly used in CRL. Specifically, we wish to construct a route that minimizes time for the car to reach its destination while obeying 1) an anytime constraint on its gas consumption so that it does not run out of fuel, 2) an expectation constraint on its CO2 consumption to minimize damage to the Earth, and 3) a chance constraint ensuring the car has a low probability of sustaining damage on the route. Please let us know if there are any other items we can clarify, and thank you again for your feedback! --- Rebuttal Comment 1.1: Comment: Regarding the sentence "As our work is within the domain of CRL, we assume some basic familiarity with CRL notations and conventions.", I think this is a bit of an unfortunate approach that, if adopted more widely, would completely defeat the purpose of ICML as a broad conference connecting distinct communities working on ML. For instance, when writing ICML papers, researchers working more on the complexity-theoretic side of things do introduce basic tools (such as the exponential time hypothesis or treewidth) even if these are well-known by everyone in their research community. The same holds for submissions that provide new contributions to Bayesian networks, constraint satisfaction, teaching dimension and so forth; a submission to ICML would generally focus much more on approachability than a submission to a specialized venue. Nevertheless, if the authors are willing to expand on the definitions to avoid assuming "familiarity with CRL notations and conventions", add an example and remove the informal references to experiments (as per their response to Reviewer htBq), I will not push for rejection and have updated my score accordingly.	Summary: In this paper, they study polynomial algorithm for a generalized constrained MDP (CMDP). In particular, they formulate a class of CMDPs whose constraints have generalized Bellman-recursive structures, and construct polynomial algorithms for it via state/action augmentation and budget/state discretization. Moreover, they extend their method by replacing the augmented component with function approximation. Finally, they show an application of the proposed method as a fast, approximate solver for knapsack problem. Claims And Evidence: Reinforcement learning is a subfield of machine learning, which I believe involves some form of inference from finite sample. However, the presented results assume the complete knowledge of CMDP. Therefore I think the title is more accurate with something like "Polynomial-Time Solvability of Constrained Markov Decision Process". Methods And Evaluation Criteria: The presentation of Knapsack Example could be more detailed in a quantitative aspect. Theoretical Claims: The idea behind the proof is easy to follow. Experimental Designs Or Analyses: The presentation of Knapsack Example could be more detailed in a quantitative aspect. Supplementary Material: No. Relation To Broader Scientific Literature: I am not an expert in constrained MDP literature, so not sure how significant its contributions are. On one side, the proposed framework is of great generality, which is nice, yet on the other side, the theoretical analysis seems rather straightforward and the authors indicate no particular use of the widened applicability beyond the good old knapsack problem. Essential References Not Discussed: None that I am aware of. Other Strengths And Weaknesses: None. Other Comments Or Suggestions: * L074 left: "SR" appears here for the first time without explanation. * L097 left (and more): decide which one to use: cMDP or CMDP? * L099 right: Give the total description size of caMDP explicitly. * L133 left: $t$ starting from 1, but the initial time step is 0. * L155 left: "finite extension of $f$" is ambiguous. I personally prefer explanations with mathematical expression, like $f_{t=1}^T x_t:=f(f(\cdots f(f(x_1, x_2), x_3), \cdots, x_{T-1}), x_T)$. * L145 right: what is the truncated-horizon process? * L196 left: Our method(?) revolves ... * L262 left: Define $\bar{C}_h^\pi(s,b)$ * L316 left: $\kappa_\ell$ * L321 left: $g(P_h(s'\|s,a),b_{s'}))$ Questions For Authors: None. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Thank you for your constructive feedback! We intend to revise the paper with your notational suggestions in mind. Please see our general rebuttal below, which addresses your concerns about our title, the significance of our results, and the role of our knapsack example: --- General Rebuttal --- "We address the common concerns of the reviewers, particularly those who may not be experts in the Constrained Reinforcement Learning (CRL) domain. These concerns include using the term "Reinforcement Learning" (RL) in our title and the significance of our contributions to the CRL literature. We also clarify the intention behind the final section's knapsack example, given the theoretical nature of our work. 1. [Title] First, it is a common convention in the RL literature to use "RL" to reference both planning (full MDP knowledge) and learning settings, as seen in many of the past CRL works cited in our paper, such as [1,2,3]. Moreover, planning algorithms can directly translate into learning algorithms through model-based learning approaches. However, we understand this might be misleading to some reviewers, given our paper's focus on computational complexity. We are open to changing the title if the reviewers believe this would be beneficial. 2. [Contributions] Second, we would like to try to convey the significance of our contributions even to non-experts in CRL through their foundational nature. Specifically, we note that the entire objective of CRL is to compute a value-maximizing policy that satisfies constraints. From a computational perspective, the fundamental question is whether such an (approximately) optimal policy is computable in polynomial time. We not only make progress on this question for nearly all constraints studied by the CRL literature, but also derive algorithms that achieve the provably best approximation guarantees possible under $P \neq NP$. Thus, our work is the first to establish polynomial-time approximability for each setting mentioned in the abstract and introduction, including the natural heterogeneous and chance constraint [3] settings. Before our work, all of these settings lacked sub-exponential time algorithms, or any algorithm, since their first introductions over 25 years ago. In fact, a significant paper appearing in Neurips 2024 [2] achieved similar results to ours, but only for the special case of problems with exactly one constraint and excluding chance constraints. 3. [Knapsack Example] Lastly, we emphasize that our paper is theoretical work with the singular focus of addressing: "Can general CMDPs be approximated in polynomial time?" Since this is a question about the worst-case computational complexity of an optimization problem, this question can only be answered using a mathematical proof. In particular, numerical experiments cannot establish computational complexity bounds and thus do not serve our primary objective. Consequently, our final section on function approximation was only intended to highlight the flexibility of our approach rather than stand as an experimental section. We see now this may have been confusing, and are happy to remove that section if it distracts from the paper's main message on the computational complexity of CRL. References: [1] "Anytime-Constrained Reinforcement Learning", Jeremy McMahan and Xiaojin Zhou. AISTATS 2024. [2] "Deterministic Policies for Constrained Reinforcement Learning in Polynomial Time", Jeremy McMahan. NeurIPS 2024. [3] "Risk-Constrained Reinforcement Learning with Percentile Risk Criteria", Yinlam Chow, Mohammad Ghavamzadeh, Lucas Janson, and Marco Pavone. JMLR 2017 --- End of general rebuttal --- In addition to those points, we would like to address the reviewer's statement about the straightforwardness of the results. We note that many works have attempted to develop polynomial-time algorithms for our settings since they were first studied over 25 years ago, yet we are the first to achieve this feat. We believe this fact alone implies our approach is not insignificant. Moreover, if our approach were straightforward, we would argue this is an additional benefit. Specifically, this would mean that our method is not only provably exponentially faster than past approaches but also achieves optimal approximation guarantees without relying on complicated machinery such as large MILPs and exhaustive searches. Thank you once again for your valuable feedback! We hope our responses address your concerns and clarify the contributions of our work.	null	null	null	null	null	null
Regularized Langevin Dynamics for Combinatorial Optimization	Accept (poster)	Summary: The paper introduces Regularized Langevin Dynamics, a novel sampling-based method for improving solutions to CO problems through LD. RLD incorporates regularization to control the distance of solution updates, enhancing traditional heuristics and neural network models by mitigating the issue of local optima. This approach outperforms SOTA baselines in solving large-scale graph-based CO problems, showing improved efficiency and adaptability across various settings. Claims And Evidence: - One fundamental motivation behind this paper is 'the difference in local optima between continuous optimization and combinatorial optimization.' However, it seems to lack theoretical evidence, and it remains unclear whether this difference is specific to certain function landscapes or applies to continuous/combinatorial optimization problems in general. - Although QUBO is a fairly general formulation for CO problems, it appears to be much less effective for a prominent and extensive subset of CO problems involving global constraints, such as the TSP. The authors are encouraged to thoroughly discuss the method's limitations and scope. Methods And Evaluation Criteria: N/A Theoretical Claims: N/A Experimental Designs Or Analyses: I have some concerns regarding the experimental designs: - How do you initialize the solutions? - The authors seem to address a fundamental problem in optimization, i.e., the trade-off between exploration and exploitation. Regularizing the update distance to a fixed scalar seems overly simplified to serve as a generic solution to this issue. I noticed that, in Tables 4 and 5, the hyperparameters are extensively tuned across problems and problem scales. Is it possible that your methods, under certain sets of hyperparameters, overfit the benchmark datasets? How do you ensure a fair comparison with the baseline methods, especially the ablation baseline (e.g., vanilla SA)? Did you also search the hyperparameters within the same ranges? - It seems that some baselines are not directly competitive with your methods. Methods such as DIMES and DIFUSCO learn to initialize the solutions, while your sampling-based method learns to update them. Could you please elaborate on the rationale behind the choice of baselines? Is it possible to leverage the best of both worlds? - It seems reasonable to compare your method against other approaches designed to escape local optima during solution improvements. Are there any feasible alternatives you considered for comparison? - Is the high efficiency of your method due to the ability to use a very large batch size, given that your method is lightweight in terms of computation and memory consumption? Comparing per-instance solution duration, as discussed in many benchmarking and criticism papers, seems reasonable. Supplementary Material: Mostly A and C. Relation To Broader Scientific Literature: This paper contributes to two threads of literature, as discussed in the Related Work section. Essential References Not Discussed: Section 5.1 lacks an adequate discussion of recent RL-based methods [1]; the most recent work cited was published in 2022. [1] RL4CO: an Extensive Reinforcement Learning for Combinatorial Optimization Benchmark. Other Strengths And Weaknesses: I enjoyed reading this paper. This paper is very well-written and introduces a simple and effective method. I encourage the authors to address my concerns raised above. Other Comments Or Suggestions: Typos: - "thes"; line 82 - "difference in local optimal between continuous optimization and continuous optimization", line 415 Questions For Authors: - Although you annotate both DIMES and RLNN as RL-type methods, can I consider them distinct types of approaches? DIMES appears to learn how to generate a solution in one step, whereas your RLNN learns to iteratively update the solution based on RLD. Furthermore, can I consider them not necessarily competitive or mutually exclusive, since you could initialize your solution with DIMES or DIFUSCO and then refine it using RLNN? - Is it possible to adaptively regularize the solution updates? - Is it possible to apply regularization to the solution updates only when detecting local optima? Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: > However, it seems to lack theoretical evidence >Is it possible to apply regularization to the solution updates only when detecting local optima? Thank you for your insightful question. Given the short time period, here we simply outline some perspective for the theoretical analysis. When not at the local optimum, RLD could accelerate the convergence. The main assumption here is that the graph is sparse (which is very common in CO), so it is unlikely for $d$ variables to be adjacent to each other and the gradient remains accurate after the change. In terms of the ability to escape optimum, we would like to point out the connection between RLD and path-auxiliary proposal [1], whose first-order version, PAFS, is also the fundamental algorithm behind iSCO. RLD could be treated as a generalized version of PAFS in terms of updating in expectation $d$ coordinates at each step, so it also satisfies Theorem 3 in that paper. Based on this generalization form, we propose a more efficient (parallel) sampling strategy to avoid the sequential sampling in PAFS, thus accelerating the search and significantly outperforming iSCO. [1] Sun, et al. Path Auxiliary Proposal for MCMC in Discrete Space. ICLR 2022. > How do you initialize the solutions? The initialization is a Bernoulli distribution of probability 0.5 for each variable. > the hyperparameters are extensively tuned across problems and problem scales We would like to clarify that all our hyperparameters are tuned via random search (see section A.1) rather than grid search. The hyperparameters in Tables 4 and 5 reflect this randomness rather than an extensive tuning process. Moreover, only the initial temperature $\tau_0$ and the regularization target $d$ would impact performance and were carefully tuned in our experiments. We believe that tuning just two parameters is far from overfitting the dataset. > How do you ensure a fair comparison with the baseline methods, especially the ablation baseline (e.g., vanilla SA) For our ablation baseline, $K$, $T$, $\beta$ and $\tau_0$ are kept the same as the ones used in our method. Another parameter $\alpha$ is searched over {0.001,0.01,0.1}$ as presented in Figure 1. > Methods such as DIMES and DIFUSCO learn to initialize the solutions … Could you please elaborate on the rationale behind the choice of baselines? We would like to clarify that our method also initializes the solution since it does not guarantee the feasibility. We use the greedy decoding to transform the searched initialization to a feasible solution. For DIMES and DIFUSCO, they also have the greedy decoding variant. But given their poor performance, we only report the best variant with a sampling-based decoding. > Is the high efficiency of your method due to the ability to use a very large batch size … Comparing per-instance solution duration … We test all instances sequentially in our experiment, so the per-instance solution duration is simply total_time/(# instances). RLSA only needs <0.2s per instance except on ER-[9000-11000] (around 6s per instance). > it appears to be much less effective for a prominent and extensive subset of CO problems involving global constraints This is an insightful question but we want like to mention that tackling global constraints typically need strong inductive biases and this is a common challenge for all energy-based models (EBMs). Here we refer to some recent EBM-based CO solvers that also face this dilemma and exclude the evaluation on the problems with global constraints such as TSP. [1] Haoran Sun et al., ‘Revisiting Sampling for Combinatorial Optimization’, ICML 2023. [2] Dinghuai Zhang et al., "Let the Flows Tell: Solving Graph Combinatorial Optimization Problems with GFlowNets", NeurIPS 2023 spotlight. [3] Sebastian Sanokowski et al., A Diffusion Model Framework for Unsupervised Neural Combinatorial Optimization. ICML 2024. The reason behind is because the global constraints are highly structured, while EBMs are general solvers, whose formulation itself prevents a better performance than heuristics with a strong inductive bias such as k-OPT. > It seems reasonable to compare your method against other approaches designed to escape local optima during solution improvements. Are there any feasible alternatives you considered for comparison? Note that SA itself is a strategy to escape the local optimum and we have already included the SOTA baseline iSCO. We have also experimented with the restarting strategy on top of our ablation baseline but find no clear advantage. Another method is semidefinite programming, as we included in Table 2. However, this method is in general very slow compared to SA methods. >Is it possible to adaptively regularize the solution updates? We have tried but found no clear gain. Note that RLD itself should be counted as an adaptive strategy on the MCMC proposal (with an adaptive $\alpha$ in Equation 8).	Summary: Regularized Langevin Dynamics for Combinatorial Optimization proposes Regularized Langevin Dynamics (RLD), a sampling framework for combinatorial optimization (CO). The authors note that discrete Langevin dynamics (LD) has limitations in exploration when applied to CO. RLD addresses this by enforcing an expected distance between sampled and current solutions, avoiding local minima. Two CO solvers are developed based on RLD: Regularized Langevin Simulated Annealing (RLSA) and Regularized Langevin Neural Network (RLNN). RLSA is a simple yet effective algorithm that often outperforms previous state - of - the - art (SOTA) SA methods. For example, it reduces the running time of the previous SOTA SA method by up to 80% while achieving equal or better performance. RLNN, partially based on reinforcement learning, can be trained efficiently with a local objective. Empirical results on three classical CO problems (Maximum Independent Set, Maximum Clique, and Max Cut) show that both RLSA and RLNN can achieve comparable or better performance than previous SOTA SA and NN - based solvers. Ablation studies verify the effectiveness of the regularization in RLD. Overall, RLD offers a promising framework for enhancing traditional heuristics and NN models to solve CO problems, though its effectiveness on non - binary data and theoretical understanding remain areas for future research. Claims And Evidence: The paper claims that regularization could mitigate the local optima during the optimization process. It then explains this claim using an MIS problem as an example as well as experiments. It could be better if provide more theoretical analysis. Methods And Evaluation Criteria: The method and evaluation make sense in general. Theoretical Claims: The paper does not give theoretical claims. Experimental Designs Or Analyses: I checked the experimental results, the ablation study and the curve of primal gap, which gives convincing results to back up the proposed method. Supplementary Material: I go through the experimental details in the appendix. Relation To Broader Scientific Literature: The paper is related to combinatorial optimization and gradient-guided generative algorithms. Essential References Not Discussed: The paper does not contain missed references as far as I know. Other Strengths And Weaknesses: Advantage: - The proposed RLSA and RLNN achives better decision quality with lower inference time. The ablation study validates the effectiveness of proposed regularization. - The proposed regularization contributions to the discrete sampling algorithm for addressing the local optimal problem during optimization. Disadvantage: - It would be better if the paper could give a theoretical analysis of the proposed regularization. Other Comments Or Suggestions: None Questions For Authors: Questions: - Is there any advantage of RLNN compared to RLSA? It seems it falls behind of RLSA on both decision quatlity and inference time. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We sincerely thank you for your positive feedback, here are the response to your concerns. >Is there any advantage of RLNN compared to RLSA? It seems it falls behind of RLSA on both decision quality and inference time. Recall that our RLNN is designed to address a limitation of RLSA, i.e., its reliance on closed-form formulation of the gradient (as mentioned in the first sentence of Section 3.3). In other words, RLSA requires additional knowledge for making it works; when such knowledge is not available, RLNN is a better alternative. And it should not be surprising that RLSA performs better since it has more prior knowledge. > It would be better if the paper could give a theoretical analysis of the proposed regularization. Thank you for your suggestion. Given the short time period, here we simply outline some perspective for the theoretical analysis. When not at the local optimum, RLD could accelerate the convergence. The main assumption here is that the graph is sparse, so it is unlikely for $d$ variables to be adjacent to each other and the gradient remains accurate after the change. In terms of the ability to escape optimum, we would like to point out the connection between RLD and path-auxiliary proposal [1], whose first-order version, PAFS, is also the fundamental algorithm behind iSCO. RLD could be treated as a generalized version of PAFS in terms of updating in expectation $d$ coordinates at each step, so it also satisfies Theorem 3 in that paper. Based on this generalization form, we propose a more efficient (parallel) sampling strategy to avoid the sequential sampling in PAFS, thus accelerating the search and significantly outperforming iSCO. [1] Sun, et al. Path Auxiliary Proposal for MCMC in Discrete Space. ICLR 2022.	Summary: This paper introduces Regularized Langevin Dynamics (RLD), an approach inspired by normalized gradient descent to enhance combinatorial optimization (CO) methods. The authors develop two specific algorithms: Regularized Langevin Simulated Annealing (RLSA), which incorporates simulated annealing, and Regularized Langevin Neural Network (RLNN), which integrates neural networks. Through empirical evaluations on Maximum Independent Set (MIS), Maximum Clique (MCl), and Max Cut (MCut) problems, the authors demonstrate that their regularization technique improves performance over unregularized counterparts. While RLNN provides moderate improvements over certain learning-based methods, RLSA achieves performance comparable to the current state-of-the-art heuristic, iSCO, in CO problems. The authors further conduct ablation studies to validate the efficacy of the regularization. ## update after rebuttal I increase my score to 3, but the writing should be further improved. Claims And Evidence: While the paper presents strong empirical evidence to support its claims, concerns remain regarding the fairness of experimental comparisons. Specifically, the evaluation methodology for iSCO may not be entirely consistent, as discussed in the weaknesses section. Methods And Evaluation Criteria: The proposed methods and evaluation criteria are generally appropriate for CO problems. However, the choice of evaluation metrics for MIS could be improved. Metrics such as average performance drop (Drop) or approximation ratio (ApR), as used in prior works (e.g., Qiu et al., 2022; Ichikawa & Arai, 2024), might provide a more comprehensive assessment of performance. Reference Qiu R, Sun Z, Yang Y. DIMES: A Differentiable Meta Solver for Combinatorial Optimization Problems. NeurIPS, 2022. Ichikawa Y, Arai Y. Optimization by Parallel Quasi-Quantum Annealing with Gradient-Based Sampling. arXiv preprint arXiv:2409.02135, 2024. Theoretical Claims: The theoretical claims appear correct, and I did not find any issues in the proofs presented. The mathematical formulations align with previous works on Langevin dynamics and simulated annealing. Experimental Designs Or Analyses: There are concerns regarding experimental fairness, particularly in the comparison of iSCO and RLSA, as discussed in the weaknesses section. A more rigorous comparison based on computational time rather than fixed iterations would be preferable. Additionally, the omission of Parallel Quasi-Quantum Annealing (PQQA) as a baseline is a notable limitation. Reference Ichikawa Y, Arai Y. Optimization by Parallel Quasi-Quantum Annealing with Gradient-Based Sampling. arXiv preprint arXiv:2409.02135, 2024. Supplementary Material: I reviewed sections A.1 (Hyperparameters), A.2 (Training), A.3 (Postprocessing), and B (Comparison with Longer Running Steps). These supplementary materials provide details regarding the experimental setup and hyperparameter choices. Relation To Broader Scientific Literature: The paper is related to gradient-based sampling and combinatorial optimization. Essential References Not Discussed: There are no critical omissions in terms of references. Other Strengths And Weaknesses: Strengths: 1. The concept of regularization in Langevin dynamics is well-motivated and empirically validated. 2. The implementation is simple yet effective, making it accessible for further research and applications. Weaknesses: 1. Experimental Fairness: The experimental section in the iSCO paper reports DIMES achieving a size of 42.06 on ER-[700–800] in 12.01 minutes and 332.80 on ER-[9000–11000] in 12.51 minutes, which aligns with previously reported results. However, the iSCO results in this paper do not consistently reflect this. Additionally, the claim that “For a fair comparison, we run iSCO with the same number of steps and trials as we did for RLSA” is questionable. A more appropriate fairness criterion would be to impose the same computational time limit. For instance, iSCO (using fewer steps) reaches a size of 44.77 in 1.38 minutes, whereas RLNN takes 1.37 minutes to reach a size of 43.34. A time-based comparison would be fairer. 2. Experimental Performance: In heuristic methods, iSCO outperforms RLSA in both the fewer-step scenario (size = 44.77) and the more-steps scenario (size = 45.15) compared to RLSA’s result (size = 44.10). In neural network approaches, DiffUCO achieves a size of 38.87 in 4.95 minutes on RB-[800–1200], whereas RLNN takes 6.24 minutes to reach a size of 38.46, indicating that RLNN is weaker than DiffUCO. Also, there are too many missing values (“-”) in the experimental tables, making cross-comparison difficult. 3. Significance of the Neural Network Approach: Since RLSA consistently outperforms RLNN across test cases, the contribution of the neural network method appears to be limited. 4. Presentation Issues: The presentation needs to be improved, and the paper contains an excessive number of typographical errors. Reference Sun H, Goshvadi K, Nova A, et al. Revisiting Sampling for Combinatorial Optimization. ICML, 2023. Other Comments Or Suggestions: Below is a refined list of typos and minor textual issues: 1. Line 82 (Left Column): Change "thes" to "the." 2. Line 150 (Left Column): Change "an" to "a." 3. Line 178 (Right Column): Change "coefficiednt" to "coefficient." 4. Line 219 (Left Column): Change "mean-filed" to "mean-field." 5. Line 227 (Right Column): Change "Barabasi-Albert" to "Barabási-Albert." 6. Line 263 (Right Column): Change "mean-filed" to "mean-field." 7. Line 724: Capitalize "On." 8. Equation (13): Replace "$-c^{T}x_{i}$" with "$-c^{T}x$" for consistency. 9. Line 703: Correct the summation notation: "$D_{ii} = \sum j=1^N \hat{A}{i,j}$" should be "$D{ii} = \sum_{j=1}^N \hat{A}_{i,j}$". Questions For Authors: 1. Evaluation Criteria Consistency: Shouldn’t the evaluation criteria be aligned across all experiments to ensure fairness, given that Sun et al. (2023) reports consistent DIMES results when comparing with iSCO? 2. Iteration Step Size Justification: Wouldn’t comparing performance at multiple time budgets rather than fixing iteration steps arbitrarily be a more rigorous approach, given that iSCO can reach better solutions within shorter execution times? Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: > There are concerns regarding experimental fairness, particularly in the comparison of iSCO and RLSA… The experimental section in the iSCO paper reports DIMES achieving a size of 42.06 on ER-[700–800] in 12.01 minutes and 332.80 on ER-[9000–11000] in 12.51 minutes, which aligns with previously reported results. However, the iSCO results in this paper do not consistently reflect this… We sincerely appreciate your question and want to offer an important clarification on a confounding issue. That is, in the iSCO paper (Sun et al. 2023), they reported the average running time per instance for iSCO, while they reported the total running time for all other methods (DIMES included). This mis-alignment in time measurements makes iSCO look 16 or 128 times better than the reality (given the test-set size is 16 and 100 for ER graphs). We have contacted the authors of that paper, and they confirmed that it was indeed an error on their behalf. (if needed and possible, we could attach their relevant material) To fix such a confounding issue, we reported the total running time for all the methods in our results tables. This is why our numbers look inconsistent to that in the iSCO paper, but for a good reason. We will revise related sentences about those tables, to make the point more transparent. We fully understand that the mistake in Sun et al. 2023 caused the confusion in your review. If the above clarification sufficiently addressed this issue, would you kindly adjust your score accordingly? > Since RLSA consistently outperforms RLNN across test cases, the contribution of the neural network method appears to be limited. Recall that our RLNN is designed to address a limitation of RLSA, i.e., its reliance on closed-form formulation of the gradient (as mentioned in the first sentence of Section 3.3). In other words, RLSA requires additional knowledge for making it works; when such knowledge is not available, RLNN is a better alternative. And it should not be surprising that RLSA performs better since it has more prior knowledge. > RLNN is weaker than DiffUCO In fact, RLNN has comparable performance to DiffUCO, based on the results in Tables 1 and 2 (RLNN outperforms DiffUCO in 4 out of 6 datasets). More importantly, the training of RLNN is much more efficient than that of DiffUCO because RLNN only needs to be trained locally while DiffUCO relies on a sequential training loss. For example, the training time is 1 hour for RLNN and 2 days plus 2 hours for DiffUCO (reported in section C.6, Sanokowski, et al. 2024) on RB-200. > typos & metrics We want to apologize for the presentation issues, and we would fix them in our future version.	Summary: This paper proposes improvements to existing diffusion-based amortized neural samplers and discrete Langevin dynamics samplers for combinatorial optimization, introducing simple regularization techniques aimed at mitigating issues with local minima in discrete spaces. The key claim is that avoiding local minima in discrete optimization is inherently more challenging than in continuous optimization, necessitating additional regularization methods. While the idea is intuitive and the proposed methods (Regularized Langevin Simulated Annealing and Regularized Langevin Neural Network) are straightforward and well-presented, the novelty appears somewhat incremental—essentially amounting to relatively simple adjustments to existing techniques. Empirical evaluations on standard combinatorial optimization benchmarks do demonstrate improved performance and computational efficiency; however, the overall methodological innovation is limited, as it mainly builds upon existing discrete Langevin dynamics frameworks with slight modifications. Claims And Evidence: The main claim of the paper—that avoiding local minima in discrete optimization is inherently more challenging compared to continuous optimization and thus necessitates more sophisticated regularization techniques—is reasonable and well-motivated. The authors provide clear empirical evidence demonstrating that their proposed regularization approach significantly improves performance compared to standard discrete Langevin dynamics. Specifically, their experiments convincingly show faster convergence and better-quality solutions on multiple combinatorial optimization benchmarks. However, the theoretical justification for why their specific form of regularization effectively escapes local minima remains somewhat intuitive rather than rigorously proven. Although the experimental results support their main claims, further theoretical analysis would strengthen their argument regarding the superiority of the proposed regularization method over existing approaches. Methods And Evaluation Criteria: The authors' choice of benchmarks is reasonable and aligns well with common evaluation practices in combinatorial optimization. They use standard problems (e.g., maximum independent set, max clique, and max cut), which primarily involve local constraints. However, previous diffusion-based sampling methods have also demonstrated applicability to problems with global constraints, such as vehicle routing or scheduling tasks. Given that these tasks require satisfying complex global constraints—significantly more challenging than local constraints like those present in the current benchmarks—it remains an open question whether the proposed regularization method would generalize well to such problems. Specifically, it would be insightful to see whether the method can effectively handle combinatorial optimization tasks involving intricate global constraint matching, which is known to pose substantial difficulties for sampling-based methods. Exploring applications such as vehicle routing or scheduling would further clarify the strengths and limitations of the proposed framework. Theoretical Claims: No theory here. Experimental Designs Or Analyses: Already noted in Methods And Evaluation Criteria. Supplementary Material: The paper clearly describes its proposed methods and provides detailed implementation information, which is helpful. Relation To Broader Scientific Literature: This discrete sampling method can potentially applied to impactful combinatorial tasks such as LLM reasoning (EBM style) and molecular dynamics simulation. Essential References Not Discussed: They have to includes some diffusion sampler works, amortized inference works and RL for vehicle routing works. Missed critical paper: [1] Dinghuai Zhang et al., "Let the Flows Tell: Solving Graph Combinatorial Optimization Problems with GFlowNets", NeurIPS 2023 spotlight. Other Strengths And Weaknesses: No. Other Comments Or Suggestions: No. Questions For Authors: 1. The proposed sampler demonstrates good performance on medium-scale combinatorial optimization benchmarks. Have you evaluated its performance on larger-scale problems (e.g., tens of thousands of nodes)? If so, how does scalability and performance stability compare to baseline methods at those larger scales? 2. Considering that your evaluations mainly focus on combinatorial problems with relatively simple (local) constraints, have you investigated how well your method performs on problems with stronger global constraints, such as the Traveling Salesman Problem (TSP)? I'm particularly curious whether your regularization approach can effectively handle the global constraints inherent to routing or scheduling problems. Code Of Conduct: Affirmed. Overall Recommendation: 2	Rebuttal 1: Rebuttal: We sincerely appreciate the reviewer's thoughtful comments and constructive suggestions. > the novelty appears somewhat incremental—essentially amounting to relatively simple adjustments to existing techniques We see your point but would like to highlight that our approach addresses a fundamental limitation of the previous method (discrete Langevin-like sampling in Zhang et al., 2022, and iSCO in Sun et al. 2023) in solving CO problems, with SOTA performance on benchmarks and significantly reduced computational costs. Which should be informative for the research community, we hope. > However, the theoretical justification for why their specific form of regularization effectively escapes local minima remains somewhat intuitive rather than rigorously proven. Thank you for your insightful question. Given the short time period, here we simply outline some perspective for the theoretical analysis. When not at the local optimum, RLD could accelerate the convergence. The main assumption here is that the graph is sparse, so it is unlikely for d variables to be adjacent to each other and the gradient remains accurate after the change. In terms of the ability to escape optimum, we would like to point out the connection between RLD and path-auxiliary proposal [1], whose first-order version, PAFS, is also the fundamental algorithm behind iSCO. RLD could be treated as a generalized version of PAFS in terms of updating in expectation $d$ coordinates at each step, so it also satisfies Theorem 3 in that paper. Based on this generalization form, we propose a more efficient (parallel) sampling strategy to avoid the sequential sampling in PAFS, thus accelerating the search and significantly outperforming iSCO. [1] Sun, et al. Path Auxiliary Proposal for MCMC in Discrete Space. ICLR 2022. > Have you evaluated its performance on larger-scale problems (e.g., tens of thousands of nodes)? Please notice our results on ER-[9000-11000] in Table 1: RLSA outperforms iSCO using only 2.5% running time. Also, RLNN takes a similar amount of time as DIMES but delivers significantly better results. All these results provide strong evidence for the advantage of our approach on larger-scale problems. > However, previous diffusion-based sampling methods have also demonstrated applicability to problems with global constraints, such as vehicle routing or scheduling tasks. > Considering that your evaluations mainly focus on combinatorial problems with relatively simple (local) constraints, have you investigated how well your method performs on problems with stronger global constraints, such as the Traveling Salesman Problem (TSP)? This is an insightful question but we would like to clarify that tackling global constraints typically need strong inductive biases and this is a common challenge for all energy-based models (EBMs). Here we refer to some recent EBM-based CO solvers that also face this dilemma and exclude the evaluation on TSP. [1] Haoran Sun et al., ‘Revisiting Sampling for Combinatorial Optimization’, ICML 2023. [2] Dinghuai Zhang et al., "Let the Flows Tell: Solving Graph Combinatorial Optimization Problems with GFlowNets", NeurIPS 2023 spotlight. [3] Sebastian Sanokowski et al., A Diffusion Model Framework for Unsupervised Neural Combinatorial Optimization. ICML 2024. The reason behind is because global constraints are highly structured, while EBMs are general solvers, whose formulation itself prevents a better performance than heuristics with a strong inductive bias such as k-OPT. Besides, we would like to mention that diffusion models themselves cannot handle global constraints, whose success heavily relies on (i) the supervision, which smooths the landscape (ii) decoding heuristics (2-OPT, MCTS or permutation), which is the key to handle the global constraint.	null	null	null	null	null	null
Flexible, Efficient, and Stable Adversarial Attacks on Machine Unlearning	Accept (poster)	Summary: The paper presents the Dynamic Delayed Poisoning Attack (DDPA), a novel adversarial framework for machine unlearning (MU) that overcomes three key limitations of existing MU attacks: inflexibility due to predefined targets, inefficiency in handling multiple requests, and instability from non-convex loss functions. DDPA allows attackers to specify arbitrary targets post-training, enhancing flexibility. It improves efficiency by using a single poisoned dataset for multiple attacks, reducing computational costs. Stability is achieved through convex polyhedral approximation, which replaces non-convex loss functions with convex ones for more predictable optimization. Inspired by thrust vector control, DDPA manipulates model parameters via simplex geometry to maximize parameter space coverage, enabling precise attack control and better generalization across MU algorithms. Experiments on CIFAR-100, Tiny ImageNet, and SST-2 demonstrate DDPA's higher attack success rate (ASR) compared to existing methods, while maintaining stealth and efficiency. The results underscore DDPA's ability to degrade MU performance, emphasizing the need for stronger MU defenses. ## update after rebuttal All my concerns are addressed. Thus, I maintain my score. Claims And Evidence: The paper’s claims are largely supported by theoretical analysis and empirical results. Mathematical formulations (e.g., convex polyhedral approximation, simplex geometry) justify the attack’s stability and flexibility, while experiments on CIFAR-100, Tiny ImageNet, and SST-2 validate DDPA’s higher attack success rates (ASR) and efficiency compared to existing methods. However, some claims need further rigor: 1. Scalability & Generalization: Testing on larger-scale or real-world MU applications would strengthen the claim that DDPA is a general solution. 2. Computational Efficiency: Direct runtime comparisons with all baselines, beyond aggregated figures, would better support the efficiency claim. 3. Target-Agnostic Adaptability: Additional experiments in black-box or limited-access settings would further validate DDPA’s real-world applicability. Overall, the evidence is strong but could benefit from broader experiments and more realistic constraints. Methods And Evaluation Criteria: The methods and evaluation criteria are well-suited to MU attacks. The DDPA attack is logically structured, leveraging convex polyhedral approximation for stability and simplex geometry for flexibility. Experiments on CIFAR-100, Tiny ImageNet, and SST-2 with VGG16, ResNet-18, and LLaMA-3B provide relevant benchmarks. 1. Strengths: Strong theoretical basis, relevant datasets/models, and comprehensive metrics (ASR, BA, runtime). 2. Weaknesses: Limited MU methods tested, lacks large-scale dataset evaluation, and assumes full model knowledge (black-box testing needed). Overall, the approach is solid, but broader MU methods, datasets, and black-box evaluations would improve generalizability. Theoretical Claims: The paper presents several theoretical claims, primarily around convex polyhedral approximation for stability and simplex geometry for flexible attack control. The key results include: 1. Convex Polyhedral Approximation (Theorem 3.5) – Ensures stability by approximating non-convex loss functions. 2. Simplex Geometry (Theorems 3.1–3.4) – Establishes the use of regular simplices for optimal parameter space coverage. The proofs follow standard mathematical principles (e.g., John’s theorem, Carathéodory’s theorem) and appear logically sound. However: 1. Some derivations, like the proportion of effective parameter space occupied by the simplex (Theorem 3.4), could use more intuitive explanation for clarity. 2. The convex approximation approach is not always differentiable, which may affect optimization feasibility in practice. Overall, the theoretical claims seem correct and well-supported, though further clarification in some areas could improve accessibility. Experimental Designs Or Analyses: The experimental design is generally sound, evaluating DDPA across CIFAR-100, Tiny ImageNet, and SST-2 using VGG16, ResNet-18, and LLaMA-3B. The attack success rate (ASR), test accuracy (BA), and runtime are appropriate metrics for assessing attack effectiveness and efficiency. Strengths: 1. Comprehensive comparisons with 9 baselines across 5 MU methods. 2. Multiple attack settings (targeted, untargeted, varying unlearning ratios). 3. Ablation studies on key components (simplex vs. convex approximation). Weaknesses: 1. Scalability not fully tested (lacks large-scale datasets like ImageNet-1K). 2. Assumes white-box access, limiting real-world applicability. 3. Efficiency claims lack per-step breakdown (more fine-grained runtime comparisons needed). Overall, the design is well-structured and relevant, but testing on larger datasets and black-box settings would improve robustness. Supplementary Material: Yes, I reviewed the Appendix, focusing on: 1. Appendix C – Proofs of Theorems 3.1–3.4, which formalize the simplex geometry and convex polyhedral approximation. The derivations appear correct but could benefit from more intuitive explanations. 2. Appendix D – Algorithm 1 (DDPA Pseudocode) provides a clear step-by-step breakdown of the attack but lacks a complexity analysis. 3. Appendix F – Experimental details, including hyperparameters and dataset/model descriptions, are well-documented, but runtime breakdowns per step would strengthen efficiency claims. Overall, the appendix is comprehensive and supports the main paper well, though some areas could use better clarity and additional insights. Relation To Broader Scientific Literature: N.A. Essential References Not Discussed: N.A. Other Strengths And Weaknesses: Other Strengths: 1. Originality – The paper introduces a novel target-agnostic MU attack using simplex geometry and convex polyhedral approximation, which is a creative combination of optimization and adversarial attack strategies. 2. Significance – Highlights critical vulnerabilities in MU systems, emphasizing the need for robust defenses. 3. Clarity – Well-structured with clear problem motivation, methodology, and experimental setup. Other Weaknesses: 1. Limited real-world applicability – Assumes white-box access; testing in black-box or federated learning settings would improve practicality. 2. Complexity concerns – The convex approximation approach may not always be computationally feasible in large-scale applications. 3. Presentation – Some theoretical derivations could be explained more intuitively for better readability. Overall, the paper is innovative and impactful, but addressing practical constraints and clarity in theory would further strengthen it. Other Comments Or Suggestions: 1. line 203-204, typo, $K$ should be $n$. 2. line 252, we propose we propose. Questions For Authors: See comments above. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We would like to thank the reviewer for the helpful and constructive comments. We have tried our best to address your concerns. We will include all the analyses, duscussions, and experimental results in this rebuttal into the submission. Due to the limit of 5000 characters, if anything remains unclear, post-rebuttal comments are appreciated. 1. Scalability not fully tested (lacks large-scale datasets like ImageNet-1K). As shown in Table 1 [ https://anonymous.4open.science/r/sup_materials ], we evaluate all methods on ResNet-18 with ImageNet-1K. Our method achieves the highest unlearning ASR (82.11 ± 1.42) with competitive runtime (22,561 seconds), demonstrating both effectiveness and scalability in large-scale settings. 2. Computational Efficiency (Claims And Evidence) We break down the total runtime into poisoning, training, and unlearning stages for clarity. As shown in Table 2 [ https://anonymous.4open.science/r/sup_materials/timing_comparison_table.pdf ], DDPA consistently incurs lower cost across all three stages. This is because DDPA generates a single poisoned dataset that supports multiple attack targets, while baselines must create a new poisoned dataset for each target. As the number of requests increases, their cumulative training time grows rapidly, whereas DDPA remains low and stable. 3. Target-Agnostic Adaptability (Claims And Evidence) We extend our DDPA method to the setting of federated learning (FL). As shown in Table 5 [ https://anonymous.4open.science/r/sup_materials/fed_comparison_table.pdf ], even in the FL environment, DDPA can still achieve very high attack performance. We will include these results in the submission. In black-box settings, attackers can train a surrogate model using input-output pairs from public APIs. Once the surrogate mimics the target model, DDPA computes thrust vectors and crafts poisoned data. Since our approach guides model updates via data removal rather than relying on direct gradient manipulation, the poisoning strategy can transfer from the surrogate to the target model, making the attack applicable in black-box settings. 4. Intuitive explanation for some derivations (Theoretical Claims) We include a concrete example to illustrate Theorems 3.1--3.4. Using a 2D regular simplex with centroid at the origin, we compute the inscribed radius as $r = \frac{\sqrt{3}}{6} \approx 0.2887$, with tangency points satisfying the barycentric condition (Theorem 3.1). The area from Theorem 3.2 yields $3\sqrt{3} \approx 5.196$, and the regularity measure in Theorem 3.3 evaluates to 1. In Theorem 3.4, equal edge lengths and centroid alignment yield an effective proportion $\rho = 0.866$. This example grounds the abstract results in a clear geometric case. See [ https://anonymous.4open.science/r/sup_materials/Numerical%20Example.pdf ] for visualization. For a more detailed explanation, please refer to our response to Reviewer X4cj Q3. 5. The convex approximation approach is not always differentiable (Theoretical Claims) The goal of our DDPA method is not to directly perform gradient-based optimization on the convex polyhedral envelope itself, but rather to identify thrust points (group centers) that lie in regions where the original non-convex loss is close to its convex approximation. Specifically, we optimize the objective in Eq.(17), which minimizes the maximum deviation between the original loss and its convex approximation over the convex polyhedron defined by the group centers. Since this objective involves selecting points rather than differentiating through the envelope, non-differentiability does not hinder the optimization in practice. Once the group centers are selected, the subsequent unlearning process operates directly on the original model and loss function, without relying on the convex envelope. 6. Algorithm 1 lacks a complexity analysis (Supplementary Material) The complexity of Algorithm 1 comes from two stages: optimizing the group centers $V = \{v_1, \dots, v_n\}$ by minimizing $L_t + L_s$, and generating poisoned data. As defined in Eq. (17), computing $L_t$ involves solving a constrained optimization (Eq. 16) for each $x \in G$, with cost $\mathcal{O}(g p d)$ per iteration. The structural loss $L_s$ (Eq. 12) includes $\phi(V)$ (Eq. 10), pairwise distances, and the centroid term. These are computed in a subspace of dimension $\mathcal{O}(\log n / \varepsilon^2)$ using a Johnson--Lindenstrauss projection, with per-iteration cost $\mathcal{O}(n \log n / \varepsilon^2)$. Sampling $k$ points from $\mathcal{N}(v_i, \sigma^2)$ for each $v_i \in V$ costs $\mathcal{O}(n k d)$. The overall complexity is $\mathcal{O}(T g p d + T n \log n / \varepsilon^2 + n k d).$ The procedure is efficient in practice, as $n$ is small, optimization is one-time, and all structural terms are computed in a low-dimensional subspace. --- Rebuttal Comment 1.1: Comment: All my concerns are addressed. Thus, I maintain my score.	Summary: This work addresses adversarial attacks on machine unlearning (MU), focusing on target-agnostic attacks that can target arbitrary parameters upon request. It allows quick responses to multiple MU attack requests after deployment, while maintaining attack stability. First, the authors use a convex polyhedral approximation to identify points in the loss landscape where convexity approximately holds, ensuring stable attack performance. Second, a regular simplex detection technique is developed to maximize coverage of the parameter space, enhancing attack flexibility and efficiency. The algorithm adjusts one or more thrust vectors to move parameters in any direction, responding promptly to MU attack requests as long as data removal stays within the MU budget, while ensuring attack stability through convex approximation and optimization. ## update after rebuttal This paper investigates an interesting problem of target-agnostic attack. The method is novel, and thoroughly examined in the experiments. Thus, I keep my original rating of "accept". Claims And Evidence: Yes. The paper is well-written with a clear algorithm workflow, thorough theoretical analysis, and extensive experiments show that the proposed method addresses three key issues: inflexibility, inefficiency, and instability. Methods And Evaluation Criteria: The method is novel, and thoroughly examined in the experiments. The experimental criteria, including datasets, baselines, and metrics, are well-chosen. Theoretical Claims: Theoretical analysis in this work seems to be complete and correct, including the solution of convex polyhedral approximation, the regularity property of the maximum regular simplex, and the coverage of the simplex to the parameter space. Experimental Designs Or Analyses: The experimental criteria are reasonable, including datasets, baselines, and metrics. The paper evaluates different variants of the method and most of them achieve better results than baselines. The experiments in the paper are extensive and convincing. The ablation experiments show the efficacy of the new method. Supplementary Material: Yes. The Appendix provides thorough literature review, detailed theoretical analyses and proofs, and comprehensive experiments. Relation To Broader Scientific Literature: This work enhances the performance of adversarial attacks on machine unlearning, by tackling three open critical challenges of flexibility, efficiency, and stability. Essential References Not Discussed: No Other Strengths And Weaknesses: Strengths 1.The paper focuses on an emerging topic of adversarial attacks on machine unlearning, which is importance in many privacy-sensitive applications. 2.The idea of the thrust vector control in aerospace engineering is interesting. 3.Both theoretical analysis and experimental results are shown to justify the effectiveness of the proposed method. Weaknesses 1.My major concern is the benchmark comparison. Authors claim it is the first algorithm to address the inflexibility and inefficiency issues in adversarial attacks on machine unlearning. I saw the efficiency experiments regarding the runtime of multiple attack requests. It would be nice to provide additional empirical results about flexibility. 2.Some parameter settings/choices in implementation can be better explained, for example, the group center and the unlearning rate. 3.In the Appendix, lines 2282 and 2283 overlap with each other. I suggest the authors to update the paper layout to get more clear presentation. One minor presentation issue: In the experiment figures, the font size in the legend decreases the paper readability, e.g., Figures 2-5. Other Comments Or Suggestions: There are some careless expression errors. For example, “It ensuring the stability of MU attacks based on convex approximation and optimization” in line 130. Also, the algorithm name is ambiguous. The paper uses two versions of DDPA and FESA in different places. Questions For Authors: Please refer to the above weaknesses. Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: We would like to thank the reviewer for the helpful and constructive comments. We have tried our best to address your concerns. We will include all the analyses, duscussions, and experimental results in this rebuttal into the submission. Due to the limit of 5000 characters, if anything remains unclear, post-rebuttal comments are appreciated. 1. Empirical results about flexibility (Other Strengths And Weaknesses) We have included the flexibility test in Figure 5 in Page 8 in the main paper. We compare DDPA with all baselines under a target-agnostic setting (unknown attack target during poisoning). While other methods suffer significant ASR drops as the number of potential targets increases, DDPA maintains consistently high ASR. For example, DDPA achieves the highest ASR $91.6\%$, whereas the baselines obtain the ASR $6.3\%$. These results clearly demonstrate DDPA's flexibility in adapting to different attack targets during unlearning. 2. Parameter settings/choices (Other Strengths And Weaknesses) Based on our observations, increasing the number of group centers (from 5 to 25) leads to higher ASR across all datasets, as it allows for more fine-grained control over parameter manipulation. Longer training epochs (e.g., from 30 to 150) significantly improve ASR, since models trained for more epochs become more sensitive to unlearning. For image classification tasks, higher learning rates help the model converge to exploitable optima more quickly, resulting in increased ASR. However, in large-scale models such as LLaMA-3b, overly high learning rates can destabilize optimization and reduce ASR. Higher unlearning rates also tend to improve ASR by amplifying the model’s sensitivity to data removal, though excessive rates may negatively affect accuracy. Similarly, increasing the unlearning ratio (e.g., from 5\% to 20\%) intensifies parameter disturbance, leading to further gains in ASR. The parameter settings are detailed in our response to Reviewer X4cj Q4. 3. Overlap with each other, font size, and careless expression errors (Other Strengths And Weaknesses) (Other Comments Or Suggestions:) We will correct the overlapping lines in the appendix, unify terminology for algorithm names, increase font size, fix expression errors, and improve figure readability and formatting for clarity. 4. real-word scenarios This work focuses on exploring the vulnerability of machine unlearning (MU) models under adversarial attacks, rather than using MU techniques to attack standard machine learning (ML) models. In line with modern privacy regulations such as the EU’s GDPR and California’s CCPA, MU allows data holders to remove the influence of specific data points from a trained ML model. For example, Stable Diffusion 3.0 allows artists to remove their artwork in the training data, responding to the 'Right to be Forgotten' legislation by GDPR and attempting to respect artists' works [1]. However, recent studies [2–10] have shown that MU is vulnerable to malicious unlearning requests in adversarial settings. In such attacks, the adversary first injects carefully crafted samples that help maintain the model’s performance and remain indistinguishable from clean data. Once the model is trained, the attacker submits an MU request to remove those specific samples, which degrades the model’s performance only after unlearning. The goal of our attack is to preserve the performance of the original ML model while impairing the MU model after the unlearning process. This objective is fundamentally different from that of traditional backdoor attacks. [1] Stability AI will let artists opt out of Stable Diffusion 3.0 training. Ars Technica. [2] Static and Sequential Malicious Attacks in the Context of Selective Forgetting. NeurIPS 2023. [3] Releasing Malevolence from Benevolence: The Menace of Benign Data on Machine Unlearning. CoRR 2024. [4] Hidden Poison: Machine Unlearning Enables Camouflaged Poisoning Attacks, NeurIPS 2023. [5] Backdoor attacks via machine unlearning, AAAI 2024. [6] Exploiting machine unlearning for backdoor attacks in deep learning system, arxiv 2023. [7] UBA-Inf: Unlearning activated backdoor attack with Influence-Driven camouflage, USENIX 2024. [8] Unlearn to relearn backdoors: Deferred backdoor functionality attacks on deep learning models, arxiv 2024. [9] Rethinking adversarial robustness in the context of the right to be forgotten, ICML 2024. [10] A duty to forget, a right to be assured? exposing vulnerabilities in machine unlearning services, arxiv 2024. --- Rebuttal Comment 1.1: Comment: Thanks for the response and additional results. They answered my questions. I am happy to recommend the acceptance. --- Reply to Comment 1.1.1: Comment: We sincerely thank the reviewer for the thoughtful feedback and for recommending acceptance. We're glad that our additional results and clarifications addressed your concerns. We appreciate the opportunity to highlight our contribution of a novel, target-agnostic attack framework that achieves flexible, efficient, and stable adversarial attacks on machine unlearning systems.	Summary: This paper proposes a novel adversarial attack framework for machine unlearning (MU) called Dynamic Delayed Poisoning Attack (DDPA). The key contributions include: 1. Target-agnostic attack flexibility: By leveraging thrust vector control (from aerospace engineering) and simplex geometry, DDPA dynamically manipulates model parameters to handle arbitrary attack targets during unlearning. 2. Stability via convex polyhedral approximation: A convex approximation method is introduced to stabilize parameter updates in non-convex loss landscapes. 3. Efficiency in multi-target attacks: A regular simplex detection technique maximizes parameter space coverage, enabling efficient handling of sequential unlearning requests. Claims And Evidence: - Claim 1: DDPA supports target-agnostic attacks. - Evidence: Figure 5 shows DDPA maintains high ASR (91.6% untargeted) even when attack targets are unknown during poisoning, while baselines degrade with increasing target classes. - Issue: The claim assumes attackers can freely manipulate unlearning requests post-deployment, but real-world scenarios (e.g., audit mechanisms) are not discussed. - Claim 2: Convex polyhedral approximation mitigates instability. - Evidence: Ablation studies (Figure 4) show DDPA outperforms DDPA-C/S variants in ASR and BA. - Issue: No direct comparison of optimization trajectories (e.g., loss landscape visualization) is provided to validate stability improvements. - Claim 3: Simplex coverage maximizes attack efficiency. - Evidence: Theorem 3.4 derives the parameter space coverage ratio. - Issue: The Gaussian assumption for parameter space is not empirically validated (e.g., via distribution tests). Methods And Evaluation Criteria: - Methods: - Strength: The integration of thrust vector control and simplex geometry is novel, enabling dynamic parameter manipulation. - Weakness: The simplex detection process (Equation 11-12) lacks algorithmic complexity analysis, raising scalability concerns for high-dimensional models. - Evaluation Criteria: - Strength: ASR, TA (targeted accuracy), and BA (benign accuracy) are standard metrics for poisoning attacks. - Weakness: No evaluation of attack stealthiness (e.g., trigger invisibility) or computational cost (e.g., training time vs. baselines). Theoretical Claims: - Theorem 3.4 (Simplex coverage ratio): - The proof assumes parameters follow a Gaussian distribution. While common in ML, this is not empirically verified for the tested models (e.g., VGG16/ResNet-18). - Critical Issue: The edge length $ l $ in Equation 13 is undefined in practice. How $ l $ is estimated for real models remains unclear. - Theorem 3.1-3.3 (John ellipsoid properties): - Proofs in Appendix C rely on standard convex geometry but lack direct connection to MU-specific dynamics (e.g., how MU gradients interact with simplex vertices). Experimental Designs Or Analyses: - Strengths: - Cross-dataset validation (images + NLP) and comparison with nine SOTA methods (e.g., AwoP, MUECPA) enhance credibility. - Ablation studies (DDPA-C/S) effectively isolate contributions of simplex and convex approximation modules. - Weaknesses: - Hyperparameter Sensitivity: Training details (e.g., learning rates, epochs) are listed in Appendix F but lack justification. Supplementary Material: - Reviewed Sections: - Appendix C: Proofs of Theorems 3.1-3.4 are technically sound but overly abstract (e.g., no numerical examples). - Appendix F: Experimental settings are detailed but lack reproducibility scripts or code links. - Algorithm 1: Poisoned dataset generation lacks pseudo-code for simplex detection optimization. Relation To Broader Scientific Literature: - The thrust vector control analogy is novel but under-explored; connections to control theory (e.g., Lyapunov stability) could deepen theoretical grounding. Essential References Not Discussed: Defensive Unlearning with Adversarial Training for Robust Concept Erasure in Diffusion Models: [Zhang et al., NeurIPS 2024] introduced defenses against unlearning attacks, critical for evaluating DDPA’s practicality. Other Strengths And Weaknesses: - Originality: The thrust vector control analogy is creative, though theoretical novelty is limited to combining existing geometric tools. - Significance: Highlights critical vulnerabilities in MU systems, urging the community to prioritize robustness. - Clarity: The John ellipsoid discussion (Section 3.2) is overly technical and distracts from the core contribution. Other Comments Or Suggestions: - Typos: - Page 3: “stPS” → “steps”. - Table 1: Column headers misaligned. - Writing: The threat model (Section 3.1) should explicitly state whether attackers can modify retained data $ D_r $. Questions For Authors: 1. How does DDPA’s training time (for poisoned dataset generation) compare to baselines like AwoP or MUECPA? If slower, does the multi-attack efficiency justify the overhead? 2. How valid is the Gaussian assumption (Theorem 3.4) for deep models? Did you test parameter distributions (e.g., via KL divergence) on trained VGG16/ResNet-18? 3. How does DDPA perform against MU systems with gradient masking or anomaly detection? Code Of Conduct: Affirmed. Overall Recommendation: 5	Rebuttal 1: Rebuttal: We would like to thank the reviewer for the helpful and constructive comments. We have tried our best to address your concerns. We will include all the analyses, duscussions, and experimental results in this rebuttal into the submission. Due to the limit of 5000 characters, if anything remains unclear, post-rebuttal comments are appreciated. 1. Loss landscape visualization (Claims And Evidence) In DDPA, thrust vector control is achieved by selecting group centers near locally convex regions of the non-convex loss, identified via a convex polyhedral approximation that minimizes the gap to the original loss. Figure 1 (https://anonymous.4open.science/r/sup_materials/landscape.pdf) visualizes the loss landscape using a shared 2D projection. The region around the selected anchor is visibly smoother and more stable, showing that DDPA effectively locates well-conditioned areas for stable thrust vector updates. 2. Gaussian assumption for parameter space (Claims And Evidence) We validate the Gaussian assumption using the Shapiro–Wilk, D’Agostino’s $K^2$, and Anderson–Darling tests. For VGG16 on CIFAR-100, the $p$-values are 0.55669 (Shapiro–Wilk) and 0.30275 ($K^2$), with an Anderson–Darling statistic of 0.24373. For ResNet18 on Tiny ImageNet, the values are 0.67146, 0.35562, and 0.35510, respectively. All results fall within standard thresholds for normality: $p > 0.05$ and Anderson–Darling statistic < 0.787. These consistent results across models and datasets support the Gaussian assumption. 3. No evaluation of attack stealthiness (Methods And Evaluation Criteria) and Essentail References Zhang et al. focus on preventing recovery after unlearning, which is orthogonal to our setting. To assess stealthiness, we report anomaly indices from three standard detectors: Neural Cleanse (NC), Perceptual-Based (PB), and AEVA. These methods assign class-wise anomaly scores, with values below –2.0 commonly indicating a backdoor. As shown in Table 3 (https://anonymous.4open.science/r/sup_materials/stealthiness_evaluation_table.pdf), our method achieves scores of 0.322 (NC), 0.29 (PB), and 0.59 (AEVA), all above the detection threshold and generally higher than those of other methods. This indicates that our attack does not leave strong or easily detectable backdoor signatures. 4. No evaluation of computational cost (Methods And Evaluation Criteria) We provide a detailed efficiency comparison of DDPA and all baselines, including AwoP and MUECPA, in Figure 2 (main paper) and Figures 6, 8, and 10 (Appendix F.1). DDPA significantly reduces total training time by generating a single poisoned dataset that supports multiple attack targets. In contrast, baselines such as AwoP and MUECPA require regenerating a new poisoned dataset for each target, leading to much higher cumulative cost. Additional timing details for the poisoning, training, and unlearning stages are discussed in our response to Reviewer twWJ Q2. 5. The edge length in Equation 13 (Theoretical Claims) In practice, we estimate the edge length $l$ of the simplex by computing the average Euclidean distance between all pairs of group centers: $l = \frac{2}{n(n-1)}\sum_{1 \leq i < j \leq n}\\|v_i - v_j\\|_2,$ where $\\\\\\{v_1, v_2, \ldots, v_n\\\\\\}$ are the $n$ group centers used in the simplex construction. This provides a natural measure of the simplex’s spatial scale in the parameter space and is easy to compute. 6. MU gradients interact with simplex vertices (Theoretical Claims) As detailed in Section 3.2 (lines 240–295), we sample group centers from clean data and use a convex polyhedral approximation to identify locally convex regions. Centers aligning with this structure are selected as thrust points and mapped to thrust vectors via a conjugate algorithm, forming a regular simplex in parameter space. During unlearning, removal gradients move the model along these simplex directions, enabling controlled updates and ensuring explicit interaction between MU gradients and the simplex. 7. Attackers can modify retained data (Other Comments Or Suggestions) Our threat model only assume the attacker can inject malicious samples with no ability to alter retained training data. 8. Response to Concerns on Attack Assumptions, Algorithmic Complexity, Numerical Examples and Hyperparameter Sensitivity Regarding the assumption that attackers can manipulate unlearning requests post-deployment, Algorithmic Complexity, Numerical Examples and Hyperparameter Sensitivity please see our detailed response to Reviewer X4cj Q2,Q4 and twWJ Q4, Q6 and Reviewer TAX8 Q4 respectively. 9. Reproducibility Due to the link restrictions imposed by the ICML rebuttal policy (only figures and tables), we will release our code on GitHub along with a project page and full documentation once the paper is accepted.	Summary: This paper introduces a new adversarial attack framework specifically designed for machine unlearning systems. The central contribution is the Dynamic Delayed Poisoning Attack (DDPA) method, which addresses the limitations of previous approaches by being target-agnostic, enabling efficient handling of multiple attack requests, and exhibiting robustness in the face of non-convex loss landscapes. The method leverages convex polyhedral approximation together with simplex geometry to create “thrust vectors” that effectively guide model parameters toward any desired target. Extensive empirical evaluations across several datasets validate the effectiveness of the proposed attack. Claims And Evidence: The authors assert that DDPA achieves superior attack success rates, offers enhanced flexibility due to its target-agnostic design, and improves computational efficiency when compared to existing methods. While the experimental results - featuring comparisons with nine baseline techniques- largely support these claims, the evidence would be more convincing if additional ablation studies were provided to clearly isolate the contributions of the convex approximation and simplex components. Methods And Evaluation Criteria: A key question raised is the necessity of the unlearning process in the attack. Specifically, if the goal is to poison the model, one might simply insert backdoor examples directly. The paper should clarify why incorporating the unlearning step provides additional benefits over conventional poisoning techniques. It is also strange to inject data in the middle of the training. This will be easy to detect. Theoretical Claims: The paper presents several complex theoretical results concerning the properties of regular simplices and the behavior of the convex polyhedral approximation. Due to the intricate nature of these proofs and my limited grasp of some of the details, I am currently unable to fully assess the correctness of these theoretical contributions. Experimental Designs Or Analyses: The experimental analysis would benefit from a more detailed description of the hyperparameter settings, training procedures, and statistical significance measures (for example, error bars). Such additional details would strengthen the overall robustness and reproducibility of the experimental conclusions. Supplementary Material: NA Relation To Broader Scientific Literature: The paper is well-situated within the existing body of research on machine unlearning and adversarial attacks. It builds upon and extends prior work in these areas, effectively positioning its contributions within the broader scientific literature. Essential References Not Discussed: Although the literature review is comprehensive, the paper could be further improved by citing more recent studies on adaptive adversarial attacks, which would provide additional context and support for its contributions. Other Strengths And Weaknesses: Strengths: Presents an innovative blend of methods from convex analysis, simplex geometry, and control theory. Weaknesses: 1. Some of the theoretical proofs and derivations are overly detailed in the main text, which may obscure the central contributions. 2. The approach appears to depend on certain assumptions regarding the behavior of the loss function, potentially limiting its applicability across different domains. Other Comments Or Suggestions: None. Questions For Authors: None. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We would like to thank the reviewer for the helpful and constructive comments. We have tried our best to address your concerns. We will include all the analyses, duscussions, and experimental results in this rebuttal into the submission. Due to the limit of 5000 characters, if anything remains unclear, post-rebuttal comments are appreciated. 1. Ablation studies (Claims And Evidence) We have included the ablation study in Figure 4 in Page 8 in the main paper and Tables 3-19 in Appendix F. DDPA-S utilizes only the simplex method to maximize and generate an effective operational space. DDPA-C employs only Convex Polyhedral Approximation to ensure stability in constructing thrust vectors (group centers). DDPA operates with the full support of both simplex method and convex polyhedral approximation. We have observed that the full DDPA method achieves the lowest BA and the highest ASR and TA in most experiments, consistently outperforming other versions and highlighting the advantages of simplex method and convex polyhedral approximation. 2. Necessity of the unlearning process in the attack (Methods And Evaluation Criteria) This work focuses on exploring the vulnerability of machine unlearning (MU) models under adversarial attacks, rather than using MU techniques to attack standard machine learning (ML) models. The goal is to preserve the model's performance before MU while degrading its performance after MU, which is quite different from traditional backdoor attacks. Traditional backdoor attacks require control over the training process and predefine the attack target, making them inflexible and inefficient. In contrast, our method exploits MU vulnerabilities without access to training and operates at the unlearning stage. The attack target can be determined or modified after training or during unlearning. Injecting data during training is common in real-world settings such as online learning [1] and continual learning [2], where models are incrementally updated. For practical examples, please refer to our response to Reviewer TAX8 Q4. As noted in our response to Reviewer qxUp Q3, our attack remains stealthy and effective under strong detection defenses, underscoring its practical impact. [1] Online learning: A comprehensive survey, ACM, 2021. [2] A comprehensive survey of continual learning: Theory, method and application, 2024. 3. Unable to fully assess the correctness of theoretical contributions (Theoretical Claims) We have explained the physical meaning of these theorems in lines 179-192 in page 4 and lines 282-295 in page 6 in the submission. In addition, we have included the detailed proof of all theorems in pages 17-26 in Appendix C. 4. More detailed description of the hyperparameter settings, training procedures, and statistical significance measures. (Experimental Designs Or Analyses) We have included the hyperparameter setting, implementation details, and training procedures in lines 306-317 on page 5 in the submission and in lines 1,442-1,480 and Table 2 in Appendix F. In addition, we have provided the details of poisoned dataset generation in Appendix D. For further information, please refer to our response to TAX8 Q2. 5. Recent studies on adaptive adversarial attacks (Essential References Not Discussed) Adaptive adversarial attacks refer to attacks that are specifically designed to counteract or bypass known defense mechanisms [3,4]. Compared with standard adversarial attacks, adaptive adversarial attacks provide a more rigorous and realistic evaluation of defense methods, as they are crafted with knowledge of the defense and specifically designed to exploit its weaknesses. We will include the recent related works into the submission. [3] On Adaptive Attacks to Adversarial Example Defenses. NeurIPS 2020. [4] Adversarial examples are not bugs, they are features. NeurIPS, 2019. 6. Assumptions regarding the behavior of the loss function (Other Strengths And Weaknesses) Our method does not rely on strong or global assumptions about the loss function. While our convex polyhedral approximation (Section 3.3) utilizes local properties of the loss surface, we do not assume that the entire loss function is convex. Instead, our approach identifies regions where the loss can be locally approximated by a convex function, and places group centers (thrust vectors) in those areas. This is achieved through the optimization objective in Eq.(17), which selects data samples whose loss behavior deviates minimally from convexity, ensuring stability during the MU. Moreover, our experiments span multiple domains, including image and text classification, demonstrating that the method remains effective across a variety of non-convex loss functions in practice. We would be glad to discuss extensions of our approach to even more complex domains in future work.	null	null	null	null	null	null
Tensor-Var: Efficient Four-Dimensional Variational Data Assimilation	Accept (poster)	Summary: The paper introduces Tensor-Var, a novel framework for variational data assimilation, which integrates kernel conditional mean embedding (CME) with four-dimensional variational assimilation (4D-Var). Traditional 4D-Var methods are computationally expensive and struggle with nonlinear dynamics and imperfect state-observation mappings. Tensor-Var addresses these challenges by linearizing nonlinear dynamics in a learned feature space, making the optimization convex while ensuring theoretical guarantees for consistent assimilation results. To enhance scalability, the framework incorporates deep features (DFs) learned via neural networks, allowing it to handle large-scale problems efficiently. Experiments on chaotic systems and global weather prediction demonstrate that Tensor-Var significantly outperforms conventional and deep learning (DL)-based 4D-Var methods in accuracy while achieving a 10- to 20-fold speedup. 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: NA Essential References Not Discussed: NA Other Strengths And Weaknesses: NA Other Comments Or Suggestions: NA Questions For Authors: 1. How sensitive is the performance of Tensor-Var to the choice of the kernel function in the conditional mean embedding (CME)? Have you tested different kernels, and how do they impact generalization across different dynamical systems? 2. While Tensor-Var achieves a 10- to 20-fold speedup, how does its computational complexity scale with increasing data dimensions and observation frequencies? Are there potential bottlenecks in large-scale real-world applications? Ethical Review Concerns: NA Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We sincerely thank reviewer wFvT for these insightful questions. Below, we address each point in detail. - Choice of kernel functions Thank you for raising the question about choices of kernel functions in Tensor-Var. We would like to clarify that we have included an ablation study in Section 4.4 Table 3 on the Lorenz96 systems with $n_s=40$ and $n_s=80$. To further address the reviewer's comments, we also tested other kernel features, including Matern-1.5 and Matern-2.5. The results are provided in the following Table: Table: Comparison of different features with NRMSE (%) as the metric for state estimation accuracy. \| Features/Experiments \| Lorenz-96 $n_s=40$ \| Lorenz-96 $n_s=80$\| \|-----------------------\|----------------------\|----------------------\| \| $d_s=20$ \| 16.7±2.1 \| 17.3±2.6 \| \| $d_s=40$ \| 14.1±1.3 \| 16.8±2.2 \| \| $d_s=60$ \| 8.3±0.9 \| 11.4±0.9 \| \| $d_s=120$ \| 9.7±0.7 \| 9.0±0.9 \| \| Gaussian Kernel \| 8.4±0.5 \| 14.3±1.4 \| \| Matern-1.5 \| 9.6±0.8 \| 13.2±1.1 \| \| Matern-2.5 \| 7.2±0.2 \| 9.7±0.7 \| In a low dimensional system ($n_s=40$), Matern-2.5 achieves the lowest mean and standard deviation. In the higher-dimensional setting ($n_s=80$), the deep feature with $d_s=120$ outperforms the other approaches, albeit with a slightly higher standard deviation compared to Matern-2.5. In general, the results suggest that fixed kernel features may be more reliable at lower dimensions, but deep features become advantageous as dimensionality increases. For high-dimensional weather forecasting problems, fixed kernel features tend to be poorly scaled and are inadequate for processing structured data. Thus, we propose deep features to address scalability challenges and extend Tensor-Var for broad applications. - Computational Complexity and Scalability We thank the reviewer for their insightful question regarding the scalability of Tensor-Var. The computational complexity of Tensor-Var primarily depends on the feature dimension rather than the system dimension, as DA optimisation is performed within the feature space. As shown in Table 1 (Section 4.1), the evaluation time exhibits only a slight increase with the increasing system dimension. Moreover, the experiments presented in Section 4.2 and Section 4.3 differ in spatial resolution, with Section 4.3 using a resolution of $240121$, approximately 14 times higher than that of Section 4.2. Nonetheless, the computation time does not increase substantially. One potential bottleneck arises from solving the least square problems to compute the two CME operators in high-dimensional feature spaces during training. Incorporating more efficient solvers, such as the Krylov subspace method [Liesen et al. (2013)], could address this challenge in future work. We hope these responses adequately address the reviewer’s concerns, and we look forward to any further comments you may have. References* - Liesen, Jörg, and Zdenek Strakos. Krylov subspace methods: principles and analysis. Numerical Mathematics and Scie, 2013.	Summary: This paper discusses Four-Dimensional Variational Data Assimilation (4D-Var), which is widely used in weather forecasting and dynamic system state estimation. Traditional methods struggle to properly model the nonlinear relationships between observational data and numerical models. The authors propose a novel approach that leverages Kernel Conditional Mean Embedding (CME) to linearize 4D-Var, transforming the nonlinear optimization problem into a convex optimization problem, thereby reducing the computational cost of optimization. Additionally, by incorporating past observational data, the proposed method enables robust estimation even in missing observations. Furthermore, the use of Deep Features (DFs) enhances scalability. Through experiments on two benchmark systems, as well as data assimilation experiments using global Numerical Weather Prediction (NWP) data and satellite observational data, the authors demonstrate that the proposed method achieves lower computational cost and reduced error compared to conventional 4D-Var methods. ## update after rebuttal Thank you for the detailed response. I find the integration with AI-based forecasting models particularly interesting. I also appreciate the addition of the comparison method. Overall, I believe the contribution is significant, so I will keep my evaluation as it is. I mistakenly posted my comment in the Official Comment section. My apologies. Claims And Evidence: The authors propose, for the first time, a method that utilizes Kernel Conditional Mean Embedding (CME) to address the high computational cost and inability to properly handle nonlinear relationships in 4D-Var. Furthermore, by leveraging DFs, they achieve a practically feasible computational cost. This idea is highly logical and well-founded. Additionally, the effectiveness of the proposed method is properly demonstrated through extensive experimental data. Methods And Evaluation Criteria: The proposed method is compared against conventional 3D-Var, 4D-Var, and ML-based 4D-Var (Frerix et al., 2021). These are appropriate baseline methods for demonstrating the advancements of the proposed approach. Additionally, the datasets used for evaluation include chaotic nonlinear systems, making them suitable for assessing the advantages of the proposed method. Theoretical Claims: The specific theoretical framework, including the estimation of error covariance matrices using kernel covariance matrices, is detailed in the Supplementary Material. A broad review of the content confirms that the key points are well covered. Experimental Designs Or Analyses: As mentioned in Methods and Evaluation Criteria, appropriate comparison methods are used, and the datasets chosen for evaluation are also suitable. Supplementary Material: I have broadly reviewed the supplementary material. It includes the detailed formulation of 4D-Var, explanations of conventional methods, theoretical proofs of the theorems, concrete algorithms, and detailed evaluation results, all of which contribute to a deeper overall understanding. Relation To Broader Scientific Literature: The proposed method has broad applicability in modeling large-scale spatiotemporal data. In addition to the weather and satellite observation data evaluated in this paper, it can also be applied to various domains, such as spatiotemporal estimation of air pollution levels, probabilistic forecasting of earthquakes, time series prediction of stock prices and exchange rates, and estimation of biosignals (e.g., EEG and ECG). This approach has the potential to drive significant breakthroughs across a wide range of scientific fields. Essential References Not Discussed: To the best of my knowledge, prior studies related to 4D-Var, including the well-known GraphCast, have been appropriately cited. Other Strengths And Weaknesses: As mentioned above, this paper has the potential to be widely applied to large-scale spatiotemporal data modeling and could lead to significant breakthroughs in this field. Regarding weaknesses, while recent machine learning-based methods, such as GraphCast and GNN-based approaches, are cited, there is little direct comparison with machine learning-based methods. This may be due to the high computational cost of directly learning nonlinear relationships, making comparisons difficult. However, providing at least some level of comparison or an explanation of the challenges in conducting such comparisons could enhance the credibility of the study. Other Comments Or Suggestions: I have no additional comments. Questions For Authors: Could you explain the lack of comparison with recent machine learning-based methods, such as GraphCast and GNN-based approaches? Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We greatly appreciate reviewer's constructive feedback and recognition of the strengths of our work. Below, we address each of the questions in detail. - Compare with sota ML-based DA methods. We thank reviewer for raising the questions regarding the comparison with recent ML-based methods. - Most existing ML-based methods, such as GraphCast [Lam et al. (2023)], primarily focus on weather forecasting rather than data assimilation. Therefore, direct comparisons between our DA framework and these forecasting methods are not straightforward. - Nevertheless, our proposed DA framework can be seamlessly integrated with advanced AI-based weather forecasting models. By incorporating real-time observations, our approach consistently corrects the AI-based weather forecasting models, providing a more reliable starting point for subsequent forecasts. Furthermore, GNN-based approaches can be directly integrated into our proposed DA framework as kernel features, enabling the effective assimilation of spatially irregular data. This integration would further improve the model's ability to handle complex spatial information within the DA context. - We recognise the importance of comparing our method with state-of-the-art ML-based DA approaches, as also highlighted by Reviewer dYtv. To address this concern, our revised manuscript has added the new results from a state-of-the-art machine learning-based data assimilation method, FengWu 4D-Var [Xiao et al. (2023)]. The results and comparison details are provided in our response to Reviewer dYtv under the question Compare with sota ML-based DA methods & Baseline selections and are also presented in the accessible [anonymous Google Slides](https://docs.google.com/presentation/d/1SWXKhJL_4mAKVQlY4HAxQTl_79C94m-2TwgtkYIvuNw/edit?usp=sharing). We believe this addition improves the credibility of our study and provides a more comprehensive evaluation. We hope this response adequately addresses the reviewer’s concerns. We sincerely appreciate the reviewer’s invested time and effort in carefully reviewing our work and providing valuable, constructive feedback. References - Lam, Remi, et al. "Learning skillful medium-range global weather forecasting." Science 382.6677 (2023): 1416-1421. - Xiao, Yi, et al. "Fengwu-4dvar: Coupling the data-driven weather forecasting model with 4d variational assimilation." arXiv preprint arXiv:2312.12455 (2023).	Summary: This paper proposes Tensor-Var, a framework combining kernel conditional mean embedding (CME) with 4D-Var to linearize nonlinear dynamics and enable convex optimization in a learned feature space. It addresses the high computational costs and theoretical limitations of traditional 4D-Var and deep learning hybrids. Tensor-Var incorporates deep features (DFs) for scalability and provides theoretical guarantees for consistent assimilation. Experiments on chaotic systems and global weather prediction show Tensor-Var achieves higher accuracy and a 10- to 20-fold speedup over conventional and DL hybrid 4D-Var methods, offering an efficient and theoretically sound approach for data assimilation. ## Update after rebuttal I appreciate the authors' thorough efforts in addressing my feedback. The explanations and revisions have resolved my concerns, and I maintain my current evaluation of weak accept. Claims And Evidence: Claim 1: Efficiency and Accuracy Improvements: The paper asserts that Tensor-Var outperforms conventional and ML-hybrid variational DA baselines in both accuracy and computational efficiency. This claim is supported by experimental results on chaotic systems and global NWP applications, showing significant improvements in accuracy and a notable reduction in computational cost. However, the comparison with state-of-the-art ML-based DA methods (e.g., FengWu-4DVar) is not provided, which could strengthen the claim of superiority. Claim 2: Handling Incomplete Observations: The authors claim that Tensor-Var improves robustness and accuracy by deriving an inverse observation operator that incorporates historical data to infer system states. While this is a promising approach, the evidence for its effectiveness is limited to the presented experiments. Broader validation on diverse datasets with varying levels of observation incompleteness would strengthen this claim. Claim 3: Scalability via Deep Features (DFs): The paper addresses scalability by learning adaptive DFs to map data into a fixed-dimensional feature space. While this is demonstrated on the 64×32 ERA5 dataset in the experiments, the scalability of the approach for even larger-scale problems (e.g., higher-resolution data) is not thoroughly explored, leaving room for further validation. [1] FengWu-4DVar: Coupling the Data-driven Weather Forecasting Model with 4D Variational Assimilation Methods And Evaluation Criteria: Yes, the methods and evaluation criteria make sense. Tensor-Var uses kernel embedding and deep features to linearize nonlinear dynamics, addressing computational and non-convex challenges in 4D-Var. Experiments on chaotic systems and global NWP applications demonstrate improved accuracy and efficiency compared to conventional and ML-hybrid baselines Theoretical Claims: Yes, the theoretical seems correct. Experimental Designs Or Analyses: Evaluation Setup: All metrics are evaluated 20 times with different initial conditions. However, 20 initial fields are insufficient for data assimilation tasks, as it is common to evaluate over an entire year to ensure robustness and reliability. Baseline Selection: The choice of baselines could be more diverse. For example, DABench [1] provides a comprehensive set of advanced AI-based and numerical assimilation ensemble methods that could serve as stronger baselines for comparison. Evaluation Metrics: The evaluation relies solely on NRMSE. Including additional metrics, such as latitude-weighted RMSE and ACC, would provide a more comprehensive comparison with state-of-the-art DA methods and offer readers better insights into the performance. Prediction Model Details: The details of the prediction model used in the assimilation process are not provided. A clear description of the model's architecture, training, and implementation is necessary for reproducibility and thorough evaluation. [1] DABench: A Benchmark Dataset for Data-Driven Weather Data Assimilation Supplementary Material: Yes, I reviewed the supplementary material, specifically Section D.3. Global NWP. One question I have is regarding Figure 10: Are the RMSE values based on normalized data or the original value range? A 15-day temperature prediction with an RMSE below 0.8 degrees seems unlikely, and this also applies to other variables. Clarifying whether the RMSE is normalized or in the original scale would help ensure the validity and interpretability of the results. Relation To Broader Scientific Literature: The Tensor-Var framework advances the broader scientific literature by integrating kernel embeddings and deep features to linearize nonlinear dynamics in variational data assimilation (DA), addressing challenges like non-convex optimization and scalability. It builds on prior work in ML-enhanced DA but introduces theoretical guarantees and scalable deep features, achieving significant improvements in efficiency (10- to 20-fold speedup) and accuracy. This bridges gaps in traditional and ML-hybrid DA methods, offering a robust solution for real-time applications like numerical weather prediction. Essential References Not Discussed: [1] Verma, Y., Heinonen, M., & Garg, V. (2024). ClimODE: Climate and weather forecasting with physics-informed neural ODEs. arXiv preprint arXiv:2404.10024. [2] Vaughan, A., Markou, S., Tebbutt, W., Requeima, J., Bruinsma, W. P., Andersson, T. R., ... & Turner, R. E. (2024). Aardvark weather: end-to-end data-driven weather forecasting. arXiv preprint arXiv:2404.00411. [3] Han, Tao, et al. "Fengwu-ghr: Learning the kilometer-scale medium-range global weather forecasting." arXiv preprint arXiv:2402.00059 (2024). Other Strengths And Weaknesses: Lack of Stability Testing: The authors do not conduct stability tests for the assimilation and forecasting cycle over extended periods. For example, it is unclear whether the proposed DA method can achieve stable predictions in a year-long rolling forecast scenario. This is a critical gap, as long-term stability is essential for operational DA systems. Lowe Resolution Limitations: All experiments are conducted at a 32x64 resolution, and it is unclear whether the conclusions scale to higher resolutions. Adding experiments at higher resolutions (e.g., 0.25°) would make the study more solid and practically applicable, as higher resolutions are critical for capturing fine-scale weather phenomena and operational forecasting. Other Comments Or Suggestions: See each part above. Questions For Authors: Higher-Resolution Experiments: Can Tensor-Var's performance be validated at higher resolutions (e.g., 0.25°)? Successful high-resolution results would strengthen practical relevance and increase my score. Stability Testing for Rolling Forecasts: Can the authors demonstrate Tensor-Var's stability in year-long rolling forecasts? Evidence of long-term stability would address a critical limitation and improve my evaluation. Comparison with State-of-the-Art Methods: Can Tensor-Var be compared to state-of-the-art methods like FengWu-4DVar? Superior or comparable performance would validate the method's significance and increase my score. Addressing these points would significantly enhance the paper's contributions, and I would like to rise my score. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We greatly appreciate valuable and constructive suggestions from Reviewer dYtv. Your efforts have significantly contributed to improving the quality of our paper. Below, we provide detailed responses to each of your comments. - Higher-resolution experiment We would like to clarify that the experiments in Section 4.3 are conducted at a resolution of 240×121, which is roughly 14 times higher than the 64×32 resolution used in Section 4.2. - Compare with sota ML-based DA methods & Baseline selections We understand the reviewer’s concern about comparing with state-of-the-art ML-based DA methods, particularly FengWu-4DVar. To address this, we conducted additional evaluations of FengWu-4DVar in two weather data assimilation experiments. We used the official implementation from the [GitHub repository](https://github.com/OpenEarthLab/FengWu-4DVar). Training and evaluation settings follow our implementation as described in Sections 4.2 and 4.3. - We have summarized the updated results for Figure 2 (page 7) for Section 4.2 into the following table for clarity. - For the experiment with higher resolution, we have also added the additional results of FengWu-4DVar into Figure 3 (page 7). Both updated figures (2 and 3) are available in the [anonymous Google Slides](https://docs.google.com/presentation/d/1SWXKhJL_4mAKVQlY4HAxQTl_79C94m-2TwgtkYIvuNw/edit?usp=sharing), providing a clearer demonstration of the results. Table: Assimilation NRMSE (%) across variables and evaluation time (s). \| Method\|z500\| t850\| q700\| u850\| v850\| Evaluation Time \| \|-\|-\|-\|-\|-\|-\|-\| \|Latent 3D-Var\|3.10±0.28\|3.83±0.28\|11.4±0.65\|6.40±0.38\|6.36±0.36\|1.84±0.06\| \|Latent 4D-Var\|3.02±1.12\|3.89±1.29\|13.79±3.17\|6.57±1.07\|6.31±0.83\|4.90±0.26\| \|FengWu 4D-Var\|2.80±0.23\|2.88±0.16\|5.00±0.43\|5.51±0.19\|5.40±0.24\|1.81±0.11\| \|Tensor-Var\|1.79±0.11\|1.94±0.09\|4.77±0.19\|3.19±0.14\|3.47±0.15\|0.83±0.02\| The results demonstrate that Tensor-Var outperforms FengWu-4DVar in terms of both accuracy and computational efficiency. Similar results are observed in higher resolution experiments. We provide result figures along with detailed discussions in the shared Google Slides for the reviewer's potential interest. - Prediction Model Details In Tensor-Var, predictions are made using the fitted linear operator $\mathcal{C}_{S^+\|S}$ without the need for additional learnable models. To improve clarity, we have included a demonstrative figure of the fitting procedure in the revised manuscript's Appendix C and made it available in the Google Slides. - Stability Test We thank reviewer for highlighting the importance of long-term stability. In response, we added a long-term rollout stability test with the following key settings: - Spatial Resolution: 240×121. - Meteorological Variables: z500, t850, q700, u850, v850. - Time Step: 6 hours per step. - Assimilation Window Length: 5 steps. - Test Horizon: One year (January 1, 2018 - December 31, 2018). - Leading Time: 7 days. - others: Training and evaluation settings follow Section 4.3. The result figures can be found in the Google Slides. These results demonstrate that Tensor-Var consistently controls the estimation error over one-year horizon. To benchmark performance, we also include the results of FengWu 4D-Var. Our experiments show that Tensor-Var achieves better error control with DA compared to FengWu 4D-Var. However, Tensor-Var rollouts unstablely after 800 steps, where FengWu demonstrates more stable long-term rollouts. Tensor-Var’s long-term instability likely stems from linear dynamics, which only capture short-term evolution accurately. In contrast, transformer model in FengWu better handles long-term evolution. We value the reviewer’s insight and will work on improvng Tensor-Var’s stability while maintaining DA efficiency and accuracy. - Different metrics We thank reviewer for suggesting using different metrics. To address this, we evaluated FengWu 4D-Var (considered cutting-edge) and Tensor-Var using the anomaly correlation coefficient (ACC) at a resolution of $240121$. Other settings follow Section 4.3 Figure 3. The results demonstrate that Tensor-Var outperforms FengWu 4D-Var in ACC* as well. The corresponding figures can be found in the shared Google Slides. - Clarification of Figure 10 We thank reviewer for carefully reviewing our manuscript. The reported metric is normalized RMSE (NRMSE), and we have clarified this in the revised manuscript in Appendix D.3. - Suggested References We thank for the suggested references. After careful review, we have properly cited them in the revised manuscript and discussed their relevance. In the end, we would like to thank reviewer dYtv again for the valuable feedback and invested efforts. We believe that the revisions address your concerns and improve the overall confidence to our work.	Summary: This paper introduces 4d Tensor-Var, a framework for performing data assimilation with learnable features. Building upon CME to parameterize the state space model, the authors propose two versions of constructing the features space. Claims And Evidence: I would recommend reorganizing the presentation: currently, the method section is a mix of literature review and modification based on past works. This format creates a barrier to accessing the method. A diagram or an algorithm block (like the ones in Appendix C with more clarification) would be ideal to present the method. Notations are also confusing: For example, the authors defined the CME (conditional mean embedding) as a mapping from the observation space ($\mathcal{O}$) to latent space ($\mathcal{S}$) on page 3, but later on, when they introduced state feature, the notation they adopted seem to indicate that the CME embedding is from one-step forward feature space $\mathcal{S}^{+}$ to $\mathcal{S}$. This inconsistency without explanation greatly impacts the presentation quality. Another example we could find is regarding the definition of feature space $z_t$, and the feature mapping function $\phi_{\theta_{\mathcal{S}}}$ which maps from $\mathbb{R}^{n_s}$ to $\mathbb{R}^{d_s}$. The authors did not discuss at all what $n_s$ and $d_s$ mean, and the feature $z_t$ is not introduced and suddenly applied to the loss function in Eqn. 5. Methods And Evaluation Criteria: The dataset looks good to me: The authors conducted experiments on chaotic PDE data (KS, Lorenz systems) as well as real weather data (ERA5). Moreover, I would be curious to see how the training time compares between different methods. Theoretical Claims: Yes, I've checked their theoretical claims. However, because of the ambiguity in the method, I am not sure if I am capable of fully accessing their theoretical claims. Experimental Designs Or Analyses: I do like the empirical studies they perform, as well as the intuitive diagram they provided in Figure 1. Besides the current results, I am curious about the comparison between Algorithms 1 and 2: how do fixed kernel features compare to deep features? Supplementary Material: Yes, I've checked part C and briefly read part D. The algorithm blocks in part C helped me understand the method better. But the notations are once again inconsistent, for example, I believe it should be $\phi_{S_{\theta}}$ for algorithm 2. Relation To Broader Scientific Literature: I think the field of research is important. Essential References Not Discussed: I will recommend adding a discussion with the following literature: KalmanNet: Neural Network Aided Kalman Filtering for Partially Known Dynamics (https://ieeexplore.ieee.org/document/9733186) Data Assimilation with Machine Learning Surrogate Models: A Case Study with FourCastNet (https://arxiv.org/abs/2405.13180) Other Strengths And Weaknesses: N/A Other Comments Or Suggestions: N/A Questions For Authors: Please check the "claims" part. I do think improving the clarity of this draft is important. Ethical Review Concerns: N/A Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: We sincerely thank reviewer Qu2S for your thoughtful review and constructive feedback on our manuscript. Your comments have been invaluable in improving the clarity and presentation of our work. Below, we address each of your comments. - Reorganize the method section Thanks reviewer’s suggestion, we have improved clarity in the methods section as follows: - Added a dedicated Related Work section to clearly distinguish the literature review from our methodological contributions. - Included a diagram illustrating the training procedure for CME opeartor $\mathcal{C}_{S^+\|S}$ (can be accessed in the [anonymous Google Slides](https://docs.google.com/presentation/d/1SWXKhJL_4mAKVQlY4HAxQTl_79C94m-2TwgtkYIvuNw/edit?usp=sharing)) - Moved the algorithm (previously Algorithm 1) to the main text (end of Section 3.1), revising it to highlight key steps. - Clarification of Notations Thank you for carefully reviewing our manuscript. We would like to clarify the following: - We do not state the CME operator as a mapping from the observation space $\mathcal{O}$ to latent space $\mathcal{S}$. Instead, we defined it as $\mathcal{C}_{S\|O}\colon\mathbb{H}_O\rightarrow\mathbb{H}_S$, where $\mathbb{H}$ with subscript denotes the corresponding feature (latent) spaces. The forward CME operator is consistently expressed as $\mathbb{H}_{S^+}\rightarrow\mathbb{H}_{S}$ later in the manuscript. - Algorithm 2 (Appendix C) focuses on Tensor-Var with predetermined kernel features, without learnable parameters $\theta$ as in deep features. - We realize the notations in our manuscript may be unclear. To improve clarity, we have added a dedicated table in the Appendix of the updated manuscript. You can also find it in the shared Google Slides above. - Predetermined kernel features compare to deep features We would like to clarify that we conducted an ablation study to compare different feature dimensions and the Gaussian kernel (Section 4.4, Table 3). Details are in Appendix D.5. Additionally, we tested other kernel features, including Matern-1.5 and Matern-2.5. Table: Comparison of features using NRMSE (%) for state estimation accuracy. \| Features/Experiments \| Lorenz-96 $n_s=40$ \| Lorenz-96 $n_s=80$\| \|-----------------------\|----------------------\|----------------------\| \| $d_s=20$ \| 16.7±2.1 \| 17.3±2.6 \| \| $d_s=40$ \| 14.1±1.3 \| 16.8±2.2 \| \| $d_s=60$ \| 8.3±0.9 \| 11.4±0.9 \| \| $d_s=120$ \| 9.7±0.7 \| 9.0±0.9 \| \| Gaussian Kernel \| 8.4±0.5 \| 14.3±1.4 \| \| Matern-1.5 \| 9.6±0.8 \| 13.2±1.1 \| \| Matern-2.5 \| 7.2±0.2 \| 9.7±0.7 \| In $n_s=40$, Matern-2.5 shows the lowest mean and standard deviation (std). In $n_s=80$, the deep feature with $d_s=120$ outperforms other methods, despite a slightly higher std than Matern-2.5. These results indicate fixed kernels are more reliable at low dimensions, while deep features excel as dimensionality increases. For high-dimensional weather forecasting, fixed kernel features often scale poorly and struggle with structured data. Thus, we propose deep features to extend Tensor-Var for broader applications. - Comparing Training Time Across Methods We thank reviewer for the interest in training time. To address this, we measured the training time (per epoch) under identical configurations (NVIDIA RTX 4090) for the experiments in Section 4.2. These results are summarised in the following table and are included in the revised manuscript (Appendix D). \|Methods\|Latent 3D-Var\|Latent 4D-Var\|FengWu 4D-Var\|Tensor-Var\| \|-\|-\|-\|-\|-\| \|Training time (min)\|0.75±0.06\|0.88±0.41\|11.05±1.65\|5.32±1.07 (forward), 4.17±0.31 (inverse)\| Latent 3D and 4D-Var are computationally efficient as they only consist of convolutional and fully connected layers, requiring only one forward pass in training. FengWu 4D-Var, with its transformer-based encoder-decoder, is more time-consuming due to self-attention operations. Tensor-Var’s forward and inverse models are slower than latent DA due to solving least square problems in feature spaces, while the inverse model is faster as no decoding process. - Suggested References We appreciate suggested references. After careful review, we agree that they are relevant to our study. We have properly cited them in the updated manuscript. We thank reviewer Qu2S again for invested efforts and constructive feedback, which helped improve the manuscript. We have carefully addressed all concerns and made substantial revisions to improve clarity. We look forward to any further feedback.	null	null	null	null	null	null
A Machine Learning Approach to Duality in Statistical Physics	Accept (poster)	Summary: This paper show cases a machine learning approach to find dual models in statistical physics. The authors outline a training procedure to find an ML model that can match the observables estimated from two statistical physics systems. If such a match is found for two different Hamiltonians then that points to the existence of a duality transform between these two models. The authors discuss a variance reduction technique to improve the convergence of their learning algorithm. They test their method on the 2D Ising model and an Ising model with plaqueete interactions. They rediscover the duality of the 2D Ising model and draw some interesting conclusions about the plaquette model. Claims And Evidence: The claims made in the paper are supported by limited evidence. The main claim of the paper is that duality transforms can be discovered by an ML algorithm. This is only demonstrated for the 2D Ising model, which is possibly the simplest example one can demonstrate this on. Methods And Evaluation Criteria: Yes they do make sense. But a larger suite of experiments would have been ideal Theoretical Claims: There are no major theoretical claims here to check. Experimental Designs Or Analyses: See questions/suggestions Supplementary Material: Did not review Relation To Broader Scientific Literature: Duality is an important notion that used to study models in statistical physics. The notions of duality used in this paper are derived from existing works in the filed (eg. https://journals.aps.org/rmp/pdf/10.1103/RevModPhys.52.453) I am not aware of papers that try to learn duality transformations explicitly from data. Essential References Not Discussed: N/A Other Strengths And Weaknesses: Strengths: This is a well written paper which deals with a very interesting problem in statistical physics. The results are very encouraging and the authors are very straight forward with their findings and future directions. Weaknesses: The main weakness of this work is limited experiments. The only experiment that shows that such a duality transform can be learned is done for the 2D Ising model. This is the simplest case with a known answer. For the plaquette model, the method seems to find some sort of approximate duality in the ordered phase, but the evidence for this is weak. Also, there must be a set "testing" experiments that show that the learned dual model reproduces the essential physics of the original model. Other Comments Or Suggestions: The paper can be improved by: > More experiments that show that this works in non-trivial settings. > Better figure captions and may be even a different approach to presenting the results visually. For instance, figure 6 is very hard to parse. It would be better if it is split up into smaller figures that support specific conclusions in the text. > Overall this is a good idea but might be better suited for a physics journal. The ML approaches used here are fairly simple and they do not have wide scale applicability beyond studying stat. phys. models. Questions For Authors: > For Fig.6 the learned points actually seem to deviate from the \beta + \kappa line. What is the cause of this error? Code Of Conduct: Affirmed. Overall Recommendation: 2	Rebuttal 1: Rebuttal: ## Stronger evidence of approximate duality We thank the reviewer for the suggestion and agree that additional evidence strengthens our claims. We now provide such evidence, showing that a broad set of moments—including correlation length—is accurately matched across approximate duals. This close agreement suggests that the essential physics is preserved, a novel result to our knowledge. To assess generalization, we compare feature statistics between approximate duals (both found from our experiments in the paper and from the hypothesized line $\beta + \kappa = const$) and the corresponding theoretic duals. Importantly, - We evaluate various features not included in the training loss - We compute these features on larger $24 \times 24$ lattices, beyond the training regime - We include approximate duals along the hypothesized line for comparison Due to computational constraints, training directly on large lattices like $24 \times 24$ is infeasible. Instead, we apply the learned mappings $G_{\theta}$ from $8\times8$ lattices to estimate features on larger systems without retraining. In all the plots, the top panel shows average feature values across all approximate duals for $\beta_0 \in \\{0.2, 0.25, 0.3\\}$ —the original-frame $\beta$ values that yielded these approximate duals, and the lower panels show individual approximate duals (marked by x). Squares mark the features corresponding to theoretical dual configurations. We consider three categories of features. For each category, we present two plots: (Framework) one based on approximate duals found by our framework, and (Hypothesized) another based on duals inferred from the hypothesized line $\beta + \kappa = const$, where the constant is chosen to intersect the known dual point $\beta_{\text{dual}}$. All links point to an anonymous repository hosting the plots. - Product of consecutive links in a linear chain in a lattice of size 24x24: There are 24 such features. (not used in the training loss) - Framework (https://bit.ly/4hQnMJH) - Hyopthesized (https://bit.ly/4jhTOj7) - Both sets of approximate duals closely match theoretical expectations - 13 features constructed from link products used in the training loss: - Framework (https://bit.ly/4lq2vtw) - Hyopthesized (https://bit.ly/41TzC16) - These features match well across both sets of approximate duals, despite being trained on smaller 8x8 lattices. - 101 Features constructed from all possible (up to gauge equivalence) link products in a $3\times3$ grid: (not used in the training loss) - Framework (https://bit.ly/4lt5Tnx) - Hyopthesized (https://bit.ly/42rEtGM) - Even this exhaustive set of features shows strong alignment with the theoretical dual, reinforcing the robustness of our approach. Regarding Figure 6, we appreciate the suggestion and will revise the caption to provide a clearer explanation, helping readers better interpret the figure. ## Simplicity of ML methods Although the ML methods are indeed simple, they certainly involve new important ideas; we did not find anywhere in the literature the task of learning both parameters in a Hamiltonian and an observable. We also thought that the application of these methods to statistical physics models was sufficiently broad, since it is one of the major branches of theoretical physics. We could however have further emphasised the broader applicability of these methods; one such is Hamiltonian truncation, where the task is to compute the spectrum of some truncated hamiltonian to gain insights into the behaviour of the physical systems; it is routinely applied to the study of QFT phenomena, such as duality. RG flows, etc. Our methods could for instance be used in this context to discover accidental dualities like Chang duality (https://journals.aps.org/prd/abstract/10.1103/PhysRevD.93.065014), which have so far received no systematic explanation. More precisely, the task in this context would be to fit parameters in a truncated hamiltonian such that the distance between the eigenvalues of the hamiltonian, or the eigenvalues of some related observable of different models are minimised. This is precisely the type of task discussed in this paper. ## Deviation from the hypothesized $\beta + \kappa$ line We believe this happens because the idea that the physics is completely determined by $\beta + \kappa$ (as explained on p6, where this determines the single spin-flip probability) is an approximation; in practice there is always a finite probability for two spins to flip together, and in this case the observables will depend on \beta and \kappa individually. We believe this is the reason for systematic movement off of the $\beta + \kappa$ line. We stress there is also likely a statistical reason for the movement off the line; not all runs find equally good minima of the loss due to random initializations etc. There is scope for improvement of this through engineering improvements.	Summary: A methodology is developed for automatically finding duality transformations on lattice gauge theory models (actually simple 2D Ising models are considered in this paper as a proof of concept). This duality transformation is an important tool in physics as it can allows one to access physical properties of systems in the so-called non-perturbative regime, i.e. when the coupling constant are too strong to perform any perturbative expansions analysis which is otherwise intractable. Claims And Evidence: The paper constitutes mainly a methodological proof of concept based on experimental observations. It is shown for instance that on the 2d Ising model, dual couplings and dual variables on the dual lattice are properly recovered numerically over some range of temperature. Methods And Evaluation Criteria: The method is based on moment matching with MCMC sampling and a property of duality that relates primal and dual moments, involving nearest neighbour variables. A certain number of well (manually) chosen link product of these variables are estimated by sampling both the primal model and a candidate dual model parameterized by a neural network. The optimization stops when primal and candidate dual moments coincide. The methodology makes sense for the problem at hand, and gives in principle more precise information than previous methods cited in the paper. Theoretical Claims: There are no theoretical claims. Experimental Designs Or Analyses: The NN parameterizing the dual model is a simple Boolean vector function using Gumbel soft-max to enforce sparse solution for the weights, taking as input as set of candidate binary links values (+-1) and returning a moment value. The set of compound moments which are used to define the loss are not given, neither the code. I believe the experiments are correctly done, but these are not easy to reproduce with the information provided in the paper. Supplementary Material: I had a look at the supplementary material, it contains some background about duality which makes the paper self-contained and some additional experimental plots like learning curves. Relation To Broader Scientific Literature: There are few references on the subject, the main one seems to be Betzler,Krippendorf which basically motivates the problem and propose unsupervised methods to find duality relations. It is cited but not much discussed, in particular comparative merits with respect to the overall motivation is not detailed. Essential References Not Discussed: I did not find that an important reference was missing. Other Strengths And Weaknesses: The proposed method is sound, the interpretation of the results shown is quite clear but the experimental test is very limited. The question addressed in this work is interesting but it looks to me as a preliminary work as the method is tested on elementary example (the 2D Ising one), and a less elementary one, namely 2D Ising + plaquette four spin interactions. But on this last example no duality transformation is to be found in general and leads experiments to output kind of spurious results . More generally I am a bit perplex about the overall practical interest of this study, which appears to me as being mostly at the level of a curiosity without practical use. Usually duality transformation are used to address the strong coupling regime in order be able to compute n-points correlations. Other Comments Or Suggestions: no additional comments Questions For Authors: I would like to ask more on the general scope of the paper. Most of, if not all (would you agree? ) duality transform correspond to a Fourier transform over some compound primal degrees of freedom (see e.g. Cardy, "Scaling and Renormalization in Statistical Physics"). Do the authors expect to unveil new kind of dual transformations with this method? Ultimately what kind of models would that be of interest to learn new physics? is it realistic considering the fact that the method requires to sample at least once a model in the strong coupling regime? In complement to this, here the method requires to sample both the primal and all candidate dual models, so that I would expect that the relevant setting corresponds to the primal being strongly coupled, so that we can hope to be able to sample easily all the dual candidates. Then How is it that the most convincing experiment displayed corresponds the (wrong?) setting, i.e. when the primal model is weakly coupled (high temperature). Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: ## Code Availability & Moments & Reproducibility We would like to kindly remind the referee that a full working code was provided in the supplementary material. Feature computation is handled by `src.utils_ising.generate_masks` (which generates 13 link product masks) and `src.utils_ising.feature_samplewise`. We will also open-source the code and experimentation scripts to ensure full reproducibility. Training Features We use a specific set of link product moments in the training loss. These are visually illustrated in this plot (https://anonymous.4open.science/r/temp_rebuttal_repository-0225/images/features.png), where the red highlights indicate the link products averaged across the lattice and samples to form statistical features. ## How is our work different from Betzler,Krippendorf ? Betzler-Krippendorf has a somewhat different focus, which includes an investigation of the advantage of a variety of different known dual representations. The part of this paper with the most overlap with ours is Section 3.3. The key differences are the following: (1) the input into the duality mapping is spin configurations sampled in the original frame, after which a second step of sampling is done: this is not the usual setup for duality in physics, where one usually just samples once (importantly, in a dual frame) and then performs a deterministic mapping, as in our work. (2) It seems that the loss function used in that work cannot be formulated unless the duality mapping of temperatures is known already, and thus that this work cannot be used to find new dualities, which our formalism in principle allows. We will include this discussion in the updated version of our manuscript. ## Practical use case of our work We have a somewhat broader perspective on duality transformations: we do not think that they are used only to compute n-point functions. Rather they provide an important perspective on the structure of the underlying physics. In particular, Kramers-Wannier duality is important not for calculations because it is the simplest example of an order/disorder duality. The discovery of a genuinely new duality – based on novel principles – would have a huge impact on physics in general. In addition to the above orientational remarks, we would like to provide two more concrete directions that we hope to explore with this technology on a short time scale. 1. Much recent work (summarized in https://arxiv.org/abs/2308.00747) has focused on points in parameter space which are self-dual, in which there is a new symmetry of an exotic “non-invertible” type. Little is known on how these symmetries work in more general theories (such as the plaquette Ising model) – for example we do not know whether the symmetry exists on the phase-transition line away from \kappa = 0. Understanding whether or not a self-duality can exist at all away from \kappa = 0 is an important first step in understanding the symmetry. 2. There exist models with interesting phase transitions (e.g. the simple case of bond percolation, reviewed in https://arxiv.org/abs/math-ph/0103018) that are not described by any known local model. It is very interesting to ask whether there can be a (perhaps complicated) local model that describes them. In both of these cases, we anticipate learning about deeper questions from the existence of a duality. In our eyes this is the true value of our work. ## Do Dualities Reduce to Fourier Transforms? In our opinion, many dualities go beyond Fourier transformations (a well-known example is AdS/CFT, which has no simple Fourier interpretation at all). As described above, our hope indeed is that other kinds of dualities – based on fundamentally new ideas – could be unveiled using these methods. One concrete example is Chang duality in \phi^4 theory (https://journals.aps.org/prd/abstract/10.1103/PhysRevD.93.065014). As we comment in the rebuttal to referee 3, our methods could realistically be applied to the discovery of such dualities, which are under intense investigation in the hep-th community. Let us also note that our approximate dualities are already quite interesting and novel! ## Sampling in the strong coupling regime For these models the difficulty of sampling using MCMC in both the strong and weakly coupled regime is basically the same. (Difficulties arise close to the critical point where critical-slowing down causes familiar but surmountable problems). Obtaining analytic results (e.g. Feynman diagrams etc.) is of course hard at strong coupling, but – very importantly – our formalism does not require this at all. ## Phase Dependence of the Method’s Performance For statistical physics model this strong-weak paradigm is not really relevant; we should stress that it is equally easy to sample in both phases. The reasons why our methods work best in one phase seem more subtle and related to well-known difficulties encountered in the inverse Ising problem.	Summary: This paper develops a machine learning method to find dualities in statistical physics models. The authors turn duality discovery into an optimization problem by using neural networks to map between original and dual models. They create a loss function that matches correlation functions between the two descriptions. The method successfully finds the known Kramers-Wannier duality for the 2D Ising model, getting both the temperature mapping and how observables transform. They also study the plaquette Ising model, showing it likely doesn't have simple self-dualities, though they find interesting "approximate dualities" in ordered phases. The work carefully analyzes optimization problems and uses variance reduction to make training work better. Claims And Evidence: The main claims are supported by numerical results. The rediscovery of Kramers-Wannier duality seems convincing. Their negative result about the plaquette model's self-dualities is also supported by extensive testing. The explanation of why certain parameter combinations give similar results in ordered phases seems insightful. Methods And Evaluation Criteria: The methods make physical sense. Using neural networks to map observables gives enough flexibility while keeping physical meaning. Their loss function based on correlations is reasonable for comparing physical systems. Theoretical Claims: The theoretical claims are in in general justified. Experimental Designs Or Analyses: The experiments reveal real some physical insights. The method struggles near the critical point and in the ordered phase, which can reflect actual physics rather than just technical problems. Their analysis of how the attention picks out the dual lattice is reasonable. The tests of different lattice sizes show what's practical while being honest about computational limits. Supplementary Material: The supplementary material is in general comprehensive. The mean-field calculation improves understanding of the phase diagram. The training curves and scaling tests also show how well the method really works. The authors are honest about where performance degrade at high temperatures. Relation To Broader Scientific Literature: This work combines statistical physics and machine learning in a novel way. While others have used machine learning for physics problems, turning duality discovery into optimization is novel. It adds to existing analytical methods for finding dualities while potentially letting us find new ones. Essential References Not Discussed: The reference seems comprehensive. Additional discussions on neural networks with symmetries seem relevant. Other Strengths And Weaknesses: The paper's main strength is its reframing of duality discovery as machine learning. The physics interpretations are clear and they're honest about the limitations. The main drawbacks are computational speed and handling more complex models. Additional discussions on what the approximate dualities tell us about ordered phases can be beneficial. Other Comments Or Suggestions: No other comments. Questions For Authors: 1. How would the method work for systems with continuous symmetries where there are many more possible dualities? 2. Is it possible to adapt this to quantum systems by working with transfer matrices? 3. Is it worth exploring other neural networks that might better capture long-range correlations? Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We thank the referee for their careful reading and interesting questions. We believe each of their three questions are interesting starting points for future research, and our more precise responses are below: 1. How would the method work for systems with continuous symmetries where there are many more possible dualities? In principle, the philosophy of the method – matching moments of an appropriate subset of observables – would still work for a system with continuous symmetries (e.g. we see no real reason why we could not obtain particle-vortex duality in 3d systems with a continuous U(1) symmetry, etc.). In practice, it seems conceivable that computationally this would be more onerous, as it would take longer to equilibrate the system when doing MCMC sampling (generally there would be gapless modes associated with Goldstone modes of the continuous symmetry which take longer to thermalize). 2. Is it possible to adapt this to quantum systems by working with transfer matrices? We think that it should be possible to use a similar approach for quantum systems without a sign problem: we would use the usual Trotter approach to reduce the quantum problem to an effective classical problem that could be simulated using very similar techniques. The problem would now be strongly anisotropic (as the time direction is now quite different from the spatial ones) and some thought should be put into the correct form of the neural network that maps observables (presumably it would also be strongly anisotropic) but in our opinion this would be manageable. 3. Is it worth exploring other neural networks that might better capture long-range correlations? Yes: making the neural network for the mapping have a larger spatial extent (i.e. going to “n” hops away on the lattice where n is a small number) is something that we are currently actively investigating as indeed some systems might require the need to capture longer-range correlations. Training becomes more difficult as this mapping is made more and more non-local. In principle there are known examples of duality (AdS/CFT being a particularly dramatic example) where the mapping is completely non-local; we do not think that our approach will reliably be able to find such examples as the space of mappings is simply too large. --- Finally, in response to the question about what the approximate duals reveal about the ordered phase: The approximate duals essentially describe a regime where the physics can be approximated by isolated single-spin flip events; this explanation shows that many different models are expected to flow to this regime, giving an example of the universality of RG (and conversely highlighting the difficulties in pinpointing the original Hamiltonian from data in such a regime) --- Rebuttal Comment 1.1: Comment: Thanks for the detailed rebuttal. I would like to keep my score.	null	null	null	null	null	null	null	null
Constrained Optimization From a Control Perspective via Feedback Linearization	Reject	Summary: The paper studies feedback linearization to solve nonconvex optimization problems in which both the objective function and the constraints are nonconvex. ## update after rebuttal No additional updates Claims And Evidence: The paper lacks in rigorous definition of key mathematical entities and assumptions necessary for a well-posed optimization framework. For example, the functions defining the optimization problem are not properly specified -- are they continuously differentiable? once? twice? Some assumptions are scattered throughout the paper. The structure of the paper does not follow the standard flow of papers in these fields: stating the model and its assumption and only then proceeding with the paper, for example, Assumption 1 which facilitates the approach is only stated in the second column of page 3. The results of the paper rely on restrictive assumptions that are uncommon in practice, and therefore require further justification to be convincing. Methods And Evaluation Criteria: The paper defines a KKT gap evaluation criteria which is common in this type of challenging models. However the results and the criteria itself are given in an elaborate manner that is difficult to assess. Theoretical Claims: I read some of the proofs, but did not fully assessed their correctness. Experimental Designs Or Analyses: I did not see whether the models used in the paper's experiments satisfy the assumptions made in the analysis. If they do not, then these experiments lack meaningful justification -- essentially reducing to running an arbitrary method on an arbitrary problem. When the focus is theoretical, numerical experiments should serve to supplement and complement the theoretical findings, rather than being disconnected from the established assumptions. Supplementary Material: Part of it, mainly those related to the theoretical results. Relation To Broader Scientific Literature: To the best of my understanding, this paper extends the work of Cerone et al. (2024) and provides an alternative perspective on the SQP method. However, I am not fully convinced of the added value of its contributions. That said, as I am not sufficiently familiar with the control approach, particularly feedback linearization, I cannot offer a definitive assessment. Essential References Not Discussed: no Other Strengths And Weaknesses: Strengths: - A new perspective on optimizing with nonlinear constraints - Connection to the well-known SQP method Weaknesses: - Confusing structure that makes it hard to follow the framework and approach, consequently the contribution - Relies on the previous work by Cerone et al. (2024) - Restrictive assumptions that are not sufficiently justified: LICQ does not usually hold in optimization problems, assuming that the Jacobian has full row rank, and other assumptions - Missing motivation in the form of explicit model examples in which the assumptions hold - Advantage over the SQP is not clear Other Comments Or Suggestions: - In line ~89 T(x) is defined as a PD matrix but then you assume boundedness of H(x) which was not defined - Line 129: don't -> do not - The paper claims "global convergence" but what is global convergence? sequence? function value? KKT optimality measure? To the best of my knowledge global convergence usually refers to the sequence, and is very hard to attain in nonconvex optimization without restrictive assumptions or sharpness assumption such as the KL property. - Line 246-247 second column "THe" - Line 269 second column "bounded a solution" - Line 325 "firs" Questions For Authors: none Code Of Conduct: Affirmed. Overall Recommendation: 2	Rebuttal 1: Rebuttal: We sincerely thank the reviewer for the comments and suggestions. We have revised our paper accordingly (see https://anonfile.io/f/wvtpAhSf). Below, we briefly summarize the reviewer's concerns and then address them one by one: 1. Lack of Clarity in Assumptions and Paper Structure: The reviewer noted that key assumptions are not clearly or consistently stated, and that convergence criteria (KKT gap) is given in an elaborative manner. Response: We thank the reviewer for the feedback. Our intention was to present a streamlined development by stating assumptions only when they are required for specific theoretical results, rather than listing all assumptions upfront. This reflects the fact that the algorithm itself applies broadly to differentiable objective and constraint functions, and that many of the stronger assumptions (e.g., LICQ, smoothness) are only invoked for particular convergence guarantees. That said, we recognize that this design choice may have caused confusion. To improve clarity, we will add a brief clarification at the beginning of the theoretical section stating that all functions are assumed to be differentiable, and that additional assumptions will be introduced where needed to support the analysis. To further address the reviewer’s confusion in the convergence criteria, we have moved the definition of KKT-gap earlier into the problem formulation part rather than right before stating the theorem. 2. Restrictive Assumptions: The reviewer found the assumptions underlying the theoretical analysis—such as LICQ and full row-rank Jacobians—too strong or uncommon in practice, and requested better justification and examples where they hold. Response: We thank the reviewer for raising this concern. We emphasize that the assumptions invoked in our analysis—such as LICQ (Assumption 1.1)—are standard in the literature on constrained optimization and SQP (see Appendix A paragraph labeed “SQP”). Further, for the inequality-constrained setting, our main convergence analysis relies on Assumption 2.1, which is strictly weaker than LICQ; we clarify this relationship in the discussion following Assumption 2.1 and formally prove it in Appendix F. We also acknowledge that these assumptions may not hold in all practical scenarios; to this end, we include a discussion in Appendix A to highlight their limitations and the potential for extensions beyond the current setting. We would also like to refer the reviewer to our response to Reviewer 3 (Concern 3), who raised a related point. 3. Experimental Setup and Justification: The reviewer questioned whether the experimental problems satisfy the theoretical assumptions, and found that the connection between the experiments and the theory was not sufficiently clear. Response: We thank the reviewer for this helpful observation. We clarify that the models used in our experiments (including Heterogenous Logistic Regression and ACOPF) are constructed to satisfy the standing assumptions in our analysis. In the revised paper, we explicitly state which assumptions are met in each experimental setting. At the same time, we would like to emphasize that it is often valuable for numerical experiments to test methods beyond the strict confines of theoretical assumptions, as strong empirical performance can indicate the method’s robustness in practice. And indeed, one of the strengths of our approach is that it can be applied without explicitly checking strong conditions. 4. Relation to SQP and Novelty: The reviewer felt that the contribution appears closely tied to prior work such as Cerone et al. (2024) and was not fully convinced of the added value or novelty of the proposed approach over established SQP methods. Response: We thank the reviewer for raising this point. We would like to emphasize several aspects of our contribution that we believe are novel and meaningful. First, in contrast to prior works such as Cerone et al. that provide only local stability guarantees in the nonconvex setting, our analysis establishes non-asymptotic global convergence rates. This represents a nontrivial advancement, particularly given the complexity of constrained, nonconvex dynamics. Secondly, compared with the SQP algorithm, we proposed a novel momentum algorithm, which is different from classical SQP formulations and is able to accelerate convergence in using only first-order information. Additionally, compared with the SQP algorithm, the control-theoretic lens we adopt—particularly through feedback linearization—offers a broader design framework. While our current work targets a specific dynamic, this viewpoint allows the incorporation of more general stabilizing controllers for constraint satisfaction, potentially leading to new classes of algorithms with desirable robustness or geometric properties. We would also like to point the reviewer to our response to Reviewer 3 (Concern 5), who raised a related point. --- Rebuttal Comment 1.1: Comment: Thank you for the clarifications and updates. I was able to briefly survey the new version you provided and it indeed looks better in structure and writing, IMO. However, I cannot provide another review to a revised version of the paper, and so cannot significantly reassess my recommendation based on the the revised version. Considering the rebuttal and the other reviewers comments, and since I am not sufficiently familiar with the field and literature, I am keeping my recommendation as is.	Summary: The manuscript proposes a new perspective on analyzing first-order algorithms in constrained optimization that is rooted in the control-theoretic notion of feedback linearization. The manuscript is overall well written and the main innovation is presented well. There are also interesting numerical examples that span distributed logistic regression and the computation of power flow in well-known standard benchmarks (IEEE standard). The topics are of interest to the ML community. In my view the strength of the work lies in introducing the concept of feedback linearization to the optimization/machine learning community. I do think that the control-theoretic notion of feedback linearization - or more generally, finding nonlinear coordinate transformations resulting in linear dynamics (e.g. Frobenius theorem / differential topology) - could be very valuable for understanding optimization/training dynamics, and is certainly an underrepresented branch of mathematics in the optimization/computer-science/learning community. However, I am not convinced that the article achieves this goal and I also have doubts whether the setting analyzed in the article is appealing/promising. On the one hand, there is a body of already existing work analyzing similar dyanmics and on the other hand, the work considers the feedback linearization of y=h(x(t)), which is only a subset of the relevant dynamics. Specific comments: - There are numerous control-theoretic interpretations for the dynamics in (3), where the dual variable is considered to be a control input, including [1], [2]. The authors could possible further strengthen the narrative of why the "feedback-linearization" prespective is useful/fruitful/novel and adds value to the analysis of gradient-based algorithms. - From an algorithmic perspective the question arises whether the authors can derive new/easier/more genearl results for the resulting discrete-time systems. From a mathematical/technical perspective, deriving precise rates for (discrete-time) algorithms is typically much harder than the continuous their continuous-time approximations. Hence, from a purely technical point of view, the manuscript has limited added value to the optimization/learning community. Is there a way the feedback-linearization perspective could help/facilitate the discrete-time analysis? - The fact that the authors assume a unique solution for the optimization over dual variables in (11) seems strong from an optimization perspective. Can the authors connect the assumption to constraint qualification? Please note that LICQ is restrictive. - Similarly, it would be helpful if the authors could discuss Assumption 2.1 (bounded multiplier) in the context of constraint qualification. Why is the relatively strong assumption that lambda is unique not listed in Assumption 2? - The authors might want to justify why continuous-time rates are meaningful, since in principle, reparametrization of time can be used to speed up convergence. - The authors might want to justify why the analysis is focused on deriving slow 1/sqrt(T) rates to stationary points in a nonconvex setting. Often, deriving precise accelerated/non-accelerated rates, e.g. 1/t, 1/t^2, etc. for the convex setting is much more challenging. This would also provide further insights on whether acceleration is actually achieved when adding momentum. - As a result of the feedback linearization of y=h(x(t)) the work suggests to implement a linear decrease in constraint violation of the type dh(x(t))/dt=- k h(x(t)), where k is constant. Please note that there has been quite a few works that suggested similar approaches, which seem relevant and should possibly be cited, in particular [3], [4], [5] (see also references therein). Most works in the ML community prove discrete-time rates even in the momentum-based setting [5] or consider optimization over manifolds [4] where retractions are challenging to compute. - The claim in the 4th contribution "To the best of our knowledge, both the proposed algorithm and its analysis are novel contributions to the field" needs to be revised in light of the state-of-the art in the literature. Note that [5] provides precise accelerated rates in discrete-time. - The paper could benefit from some polishing and comes across as sloppy. There are colloquial terms such as "don't", the punctuation is not consistent with the standards of mathematical writing, and the typesetting of references is funky (just to name a few typographical things). [1] J. Wang and N. Elia, "A control perspective for centralized and distributed convex optimization," CDC, 2011 [2] A. Allibhoy and N. Cortes, "Control-Barrier-Function-Based Design of Gradient Flows for Constrained Nonlinear Programming," IEEE TAC, 2024 [3] M. Muehlebach and M. I. Jordan, "On Constraints in First-Order Optimization: A View from Non-Smooth Dynamical Systems," JMLR, 2022 [4] P. Ablin and G. Peyre, "Fast and accurate optimization on the orthogonal manifold without retraction," PMLR, 2022 [5] M. Muehlebach and M. I. Jordan, "Accelerated First-Order Optimization under Nonlinear Constraints," arXiv:2302.00316, 2023 Claims And Evidence: see above. Methods And Evaluation Criteria: see above. Theoretical Claims: see above. 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: see above. Other Comments Or Suggestions: see above. Questions For Authors: see above. Code Of Conduct: Affirmed. Overall Recommendation: 2	Rebuttal 1: Rebuttal: We thank the reviewer for the constructive feedback. We have incorporated the suggestions into the revised manuscript (see https://anonfile.io/f/wvtpAhSf). We summarize and address the reviewer’s concerns as follows: 1. Feedback linearization perspective: How does the feedback linearization viewpoint compare to existing methods, such as those in [1] and [2] cited by the reviewer? Response: We thank the reviewer for highlighting the question. For this part, we would like to refer the reviewer to the Response to Reviewer 1 (Concern 1) who raised the same concern, as well as the Response to Concern 5 below. The reviewer also notes that our analysis focuses on the feedback linearization of y=h(x(t)), which only captures a subset of the dynamics. This is precisely why establishing global convergence guarantees is crucial: while feedback linearization ensures constraint satisfaction, it does not in itself imply stability or convergence; thus, developing convergence guarantees serves as one of the key contributions of our paper. 2. Continuous vs. discrete-time analysis: The reviewer questions the value of continuous-time rates and whether the feedback linearization perspective can facilitate discrete-time analysis. Response: We agree that continuous-time analysis has limitations as the reviewer suggested. However, even in continuous time, analyzing the dynamics in nonconvex settings is challenging and meaningful in its own right. Our continuous-time framework serves two purposes: (i) it offers theoretical insight into stability and convergence, and (ii) the discretization of the continuous-time dynamics directly informs discrete-time design. In this paper, we show that forward Euler discretization of the feedback-linearized dynamics yields an update closely related to SQP algorithm in discrete time. Moving forward, we believe it would be highly valuable to further explore the discrete time convergence rate and how different discretization schemes (e.g., higher-order methods) affect convergence both in theory and in practice. 3. Assumption justification: Clarification is requested regarding the necessity of the assumptions, particularly the uniqueness of the dual solution and Assumption 2.1, and its connection to constraint qualification. Response: We thank the reviewer for raising this point. Our analysis relies on Assumption 2.1, which requires the existence of a bounded (not necessarily unique) dual variable; the uniqueness mentioned after Equation (11) is used solely for the ease of demonstration and does not affect the proofs. We have revised the manuscript to clarify our assumptions. Regarding the connection to constraint qualifications: we realize that Assumption 2.1 is closely connected to the MFCQ assumption in [3,5], which is weaker than LICQ, we have revised our discussion of the assumption (highlighted in blue). 4. Acceleration and rate focus: Why does the paper focus on the slower $1/\sqrt{T}$ convergence rate in a nonconvex setting, rather than sharper rates (e.g., $1/T$, $1/T^2$) in convex settings? How does this relate to acceleration? Response: We would like to refer the reviewer to the Response to Reviewer 1 (Concern 2) who raised the same concern. 5. Novelty of the accelerated methods: The reviewer suggests revisiting the claim of novelty in light of recent related works, including [2,3,4,5]. Response: We sincerely thank the reviewer for pointing us to relevant works! Note that [4] primarily focuses on the setting where the constraint is an orthogonal manifold, so the setting is different from ours. While the algorithms in [2,3,5] are admittedly similar in spirit to ours, we would like to highlight a few key differences that underscore our contributions. - In the nonconvex setting, [2,3,5] provide asymptotic convergence guarantees, whereas our work establishes non-asymptotic convergence rates. In particular, our analysis is not a trivial extension. In particular, we construct a Lyapunov function tailored to the dynamics, which is not considered in [2,3]. - We establish a connection of the method to the classical SQP algorithm, a perspective not explored in [2,3,5]. - While [5] and our momentum method share some similarities, both the continuous-time dynamics and the discretization approach differ, resulting in distinct algorithms. In the revised paper, we have updated our claims, acknowledged [5], and added a detailed comparison highlighting both the differences and similarities. Furthermore, we believe feedback linearization provides a more general framework beyond specifying a linear target of the form \dot{y} = -Ky. In principle, this approach allows us to leverage arbitrary stable controllers, such as PI controllers for constraint enforcement, potentially offering new algorithmic behaviors or robustness benefits. We have added corresponding additional results in Remark 2 and Appendix B.2.	Summary: The paper develops the view of optimization methods as (optimal) feedback control of ODEs, which is some ways is the original view in the Soviet literature, but has been rediscovered only in the past decade in the Western machine learning, with the work of Andrew Packard, Bin Hu and others. Among others, it allows for inequalities to be considered in the optimization problem. Claims And Evidence: The main idea is nicely argued, but some parts of the manuscript seem to have been written in a rush. Issues: - line 93 on the right: H(x) never reappears in the paper and it is in the same sentence as T(x), shouldn’t it be T(x) then? - line 97 on the right: is there a lambda missing in the equation \nabla f(x^) + J_h^T(x^) = 0? - line 325 on the right: what does “Note that the only difference in (16) is that we add a momentum step w_t = x_t +\beta(x_t −x_{t−1} )” - - - mean? The only difference as opposed to what? - line 367 on the left: there should be L_1 instead of L_2 - line 356-357 on the right: inconsistency in notation of \lambda and \bar\lambda with respect to the variable (t or x(t)) - Figure 3: the label of the blue line “FL-proximal” is missing Methods And Evaluation Criteria: Isn’t it weird that the blue line on the right of Figure 3 is missing completely? The authors claim that it “nearly overlaps with the FL-momentum curve”, but it seems improbable that we can’t see it at all. Theoretical Claims: - Theorem 1 could be stated more neatly. E.g. “Under Assumption 1, for control gain K that is a diagonal positive definite matrix, i.e., K = diag{k_i} , where k_i > 0, we have that…” >> “Let Assumption 1 hold and let the control gain K be a diagonal positive definite matrix, i.e., K = diag{k_i} , where k_i > 0. Then…” - line 265 on the right: The optimization problem in (11) “lambda = argmin…” is stated on this page and then repeated twice on the same page. Labeling the equations in (11) separately as (11.1) and (11.2) would solve these redundancies. - The assumption 1.2 coincides with 2.2 and the assumption 1.3 coincides with 2.3. Having 1.2 and 1.3 as separate assumptions would solve these redundancies. - In general: inconsistent use of colons before equation terms and full stops after them. E.g., compare line 234-238 on the left and on the right. Experimental Designs Or Analyses: The experiments seem illustrative. Supplementary Material: I had only a cursory glance. Relation To Broader Scientific Literature: There is a good overview of the literature. Essential References Not Discussed: None, afaik. Other Strengths And Weaknesses: Minor issues: - line 96 on the right: it must satisfy >> must satisfy - line 141 on the right: "which is equivalent to Jh (x)Jh (x)^T is invertible" >> "which is equivalent to Jh (x)Jh (x)^T being invertible" - line 219 on the left: “in to Appendix A” >> “to Appendix A” - line 242 on the left: “theses” >> “these” - line 246 on the right: “THe” - line 257 on the right: “complimentary set” wrong spelling, moreover this is redundant as this notation is introduced on page 2 - line 259 on the right: “admits bounded a solution” - line 325 on the left: “an ϵ-firs-order” - lines 363-365 on the left: “three-time differentiable” >> “three-times differentiable; “there exists some constant” >> “there exist some constants” - line 381 on the left: “two positive constant” >> “two positive constants” Other Comments Or Suggestions: A proof-reading would help. Questions For Authors: None. Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: We sincerely thank the reviewer for carefully reading our paper and providing constructive feedback, as well as for their positive assessment of our work and its positioning within the broader literature on optimization and control. We are also grateful for the reviewer’s detailed suggestions on typos and improvements to the phrasing of theorems and statements, which have helped us enhance the clarity of the manuscript. With regard to the reviewer’s comments on typos or notational inconsistencies, if we did not provide a specific response, it means we fully agree with the reviewer’s observation and have corrected the issue accordingly in the revised manuscript (see https://anonfile.io/f/DEcRCSxS). Below, we address the technical questions raised by the reviewer. 1. Elaboration on FL-momentum: "line 325 on the right: what does “Note that the only difference in (16) is that we add a momentum step w_t = x_t +\beta(x_t −x_{t−1} )” - - - mean? The only difference as opposed to what?" Response: We sincerely apologize for the confusion. In this part, we intended to compare Equation (16) (now Equation (18) in the revised version) with Equation (6) (now Equation (8)), where FL-proximal is used without momentum. We have revised the text for clarity as follows: “Note that compared with FL-proximal (8), the difference in (18) is the addition of a momentum step $w_t = x_t + \beta(x_t - x_{t-1})$.” We hope this revision helps clarify the point, and we truly appreciate the reviewer’s feedback. We would be happy to further discuss this if there are any remaining questions. 2. Question about Figure 3: “Isn’t it weird that the blue line on the right of Figure 3 is missing completely? The authors claim that it “nearly overlaps with the FL-momentum curve”, but it seems improbable that we can’t see it at all. ” Response: We sincerely thank the reviewer for carefully examining the details of our numerical experiments. In the IEEE 118-bus example, we observed that the algorithm becomes unstable when the momentum hyperparameter $ \beta $ is set too large. The best-performing value found during hyperparameter tuning was $ \beta = 0.02 $, which results in the FL-proximal and FL-momentum curves appearing nearly identical. We believe this is due to the ill-conditioned optimization landscape of the problem, which limits the benefit of momentum. To clarify this, we have plotted a zoomed-in version of the learning curves (see here https://anonfile.io/f/huBzM42f), where subtle differences between the two methods can be observed. We greatly appreciate the reviewer’s observation and have double-checked the plot to ensure its accuracy.	Summary: The paper develops a theoretical foundation for using feedback linearization (FL) from control theory to address constrained optimization problems, proving global convergence rates, extending FL methods to inequality constraints, relating FL to Sequential Quadratic Programming (SQP), and introducing a novel momentum-accelerated FL algorithm with proven convergence guarantees. Claims And Evidence: In the abstract you mention that > Furthermore, we introduce a momentum accelerated FL algorithm that achieves faster convergence, and provide a rigorous convergence guarantee. This seems misleading to me, since I would expect you show a faster convergence rate, which you didn't. Methods And Evaluation Criteria: My main concern is the method requires matrix inversion and thus belongs to the second-order genre. However, a $O(1/\sqrt{T})$ is given, which could be achieved by common 1st-order methods such as projected gradient descent, or Augmented Lagrangian Methods, which also handle constraints naturally. Nesterov's Accelerated Gradient Descent can achieve $O(1/T^2)$ convergence rate, but this paper doesn't have a rate for their accelerated variant. And do to the need of matrix inversion, the proposed algorithms are hard to scale up. Theoretical Claims: The proofs seem correct to me. However: - The convergence rate is slow for a 2nd-order method. See also my comment in Methods And Evaluation Criteria. - In Theorems 1 and 4, the authors establish convergence rates of $O(1/\sqrt{T})$ for their algorithms. However, they don't explicitly characterize how these rates depend on other important problem parameters like the dimensionality $n$, the number of constraints $m$, condition numbers, or properties of the objective function and constraints (the constants appear in the assumptions). - Assumption 3 (the three-times differentiability for momentum analysis) seems less standard and a bit strong. Experimental Designs Or Analyses: I don't see any explicit analysis or comparison of computational complexity, wall-clock time comparisons or memory requirements in their experimental section. Scalability with problem size should also be analyzed. Supplementary Material: I checked the proofs. Seem correct. Relation To Broader Scientific Literature: This paper aims to bridge control theory, dynamical systems, and optimization by establishing theoretical foundations for feedback linearization in constrained optimization. Essential References Not Discussed: Lack discussions on the convergence rates of common first-order methods. Other Strengths And Weaknesses: See above. Other Comments Or Suggestions: see above. Questions For Authors: see above. Code Of Conduct: Affirmed. Overall Recommendation: 2	Rebuttal 1: Rebuttal: We sincerely thank the reviewer for the comments and suggestions! We have revised our paper (see https://anonfile.io/f/DEcRCSxS) accordingly. We briefly summarize the reviewer’s main concerns as follows and address them one by one: 1. Missing Discussion on First-Order Methods: The reviewer suggested that the paper should include a more explicit comparison with the convergence rates of standard first-order methods, such as primal-dual gradient descent (PDGD), projected gradient descent (PGD), and augmented Lagrangian methods (ALM). Response: We thank the reviewer for raising this point. We would like to point the reviewer to Appendix A for a detailed comparison with existing first order methods, which we briefly summarize as follows: PDGD has been extensively studied (e.g., Kose, 1956; Wang and Elia, 2011; Qu and Li, 2018), but is primarily restricted to convex settings. Several works suggest that PDGD can fail to converge or behave poorly in nonconvex problems. In contrast, our feedback linearization framework remains applicable in nonconvex settings, as supported by our theory and experiments. PGD also becomes unsuitable in nonconvex problems, as projections onto general nonconvex sets are often computationally intractable. While ALM can handle nonconvex constraints, each iteration involves solving a nonconvex subproblem, which may be costly. Moreover, in settings where the constraint dimension is much smaller than the dimension of 𝑥, SQP-based approaches (such as ours) tend to perform better numerically. In the revised paper, we have added corresponding numerical results to compare these methods in Appendix B.1. We thank the reviewer for helping improve the clarity and reliability of our presentation. 2. Claim About Acceleration and Convergence Rate: The reviewer found the abstract potentially misleading, as it mentions acceleration without demonstrating an improved convergence rate over the baseline method. Response: We thank the reviewer for this helpful observation and apologize for the ambiguity in the current phrasing. As noted in our response to Concern 1, a key strength of the feedback linearization (FL) framework is its applicability to nonconvex problems. In such settings, even momentum-accelerated methods are only known to achieve a convergence rate of $O(1/\sqrt{T})$, which is the rate we aim to establish in this work. Although convex optimization is not the focus of the paper, we note that our accelerated algorithm can be connected to momentum-accelerated projected gradient descent in the convex setting (see Appendix E.1). This connection allows us to leverage existing convergence results for projected accelerated methods, providing theoretical justification for the observed acceleration of our algorithm in the convex regime. We have revised the claim in our paper to clarify the confusion (Remark 5). 3. Second-Order Nature and Scalability: The reviewer noted that the algorithm requires matrix inversion, placing it closer to second-order methods, and raised concerns about its scalability to high-dimensional problems. Response: We thank the reviewer for raising this point. First, we would like to clarify that although our methods (FL-proximal and FL-momentum) involve matrix inversion, they are not second-order methods, as they only require first-order information—specifically, the gradient of $f$ and the Jacobian of $h$; no Hessians or second-order derivatives are used. Second, regarding scalability: the matrix inversion arises in a subspace defined by the constraints. In many practical settings, e.g. safe RL, the number of constraints is significantly smaller than the dimension of $x$. In such cases, the inversion is computationally inexpensive and can be performed efficiently. We will clarify this in the revision and emphasize that the cost of inversion depends on the number of constraints, not the ambient dimension. We appreciate the reviewer’s comment on scalability, and we have incorporated the above discussion in the revised manuscript (Remark 1). 4. Lack of Computational Complexity Analysis Response: We thank the reviewer for this observation and have added Remark 1 to discuss computational complexity in the revised manuscript. 5. Convergence Rate Dependencies: The reviewer observed that the convergence rates established in Theorems 1 and 4 do not explicitly characterize dependencies on key problem parameters, such as dimensionality, number of constraints, or condition numbers. Response: We appreciate the reviewer’s comment on this point. The convergence rates depend not directly on the dimensionality or number of constraints, but on parameters such as M and D (from Assumption 1), and the condition number of the matrix T(x). (See e.g. the detailed convergence rate formula in Statement 4 within Theorem 1 and 4). Once again, we appreciate the reviewer’s feedback and are open to further discussions.	null	null	null	null	null	null
TimePoint: Accelerated Time Series Alignment via Self-Supervised Keypoint and Descriptor Learning	Accept (poster)	Summary: This paper proposes a keypoint and descriptor detection algorithm, called TimePoint, for time-series alignment. The authors use a deep learning approach to train a model on synthetically-generated data for detecting keypoints and descriptors. The correspondences learned by their model is passed into a DTW algorithm to perform the time-series alignment. Claims And Evidence: The paper claims that their keypoint/descriptor model trained on synthetic data yields more accurate and efficient alignment at a lower computational cost. This is because their model enables a sparser correspondence. In the experiments, they show that their method has better classification performance and runtime in terms of a kNN analysis with various baselines and the proposed method as the distance measure. Methods And Evaluation Criteria: Yes, I believe the methods and evaluation criteria make sense for the problem domain. Theoretical Claims: The paper doesn't have extensive proofs, but the equations in page 6 make sense to me. Experimental Designs Or Analyses: Yes Supplementary Material: No Relation To Broader Scientific Literature: This paper builds on DTW and its extensions (e.g. softDTW, shapeDTW), which propose either different optimization strategies or handcrafted descriptors for correspondence matching. This paper is different in that it uses a deep learning strategy to learn descriptors and keypoints, where the deep learning model is trained on synthetically-generated data. Essential References Not Discussed: N/A Other Strengths And Weaknesses: Strengths: - The paper is well-written - The paper solves a clear problem and motivates their method well. - I think the results indicate that learning data-driven, sparse correspondences leads to improved performance, and this makes sense to me. Weaknesses: - My main weakness is the rather limited scope of this work. It is focused on the problem of time-series alignment which is one task in a specific modality of 1-d time series, and may not be sufficiently broad enough for an ICML audience. I wonder if the authors might consider applying this sparse correspondence approach to other tasks or modalities? Other Comments Or Suggestions: I'm curious why the authors approach the problem from a synthetic-generation standpoint. I'm not sure if it was mentioned (at least I could not find it) for why this approach was used, as opposed to, e.g. training on real data with augmentations. I feel like this approach would be more aligned with real data and learn correspondences that might be more transferable to real-world applications. Could the authors please elaborate on this design choice, and perhaps motivate this more in their paper? Questions For Authors: N/A Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We thank the reviewer for their kind words and suggestions. # Q1 - The scope of the proposed method We appreciate the reviewer's concern regarding the scope of the proposed method. Time Series Alignment (TSA) has been a key research topic of time series analysis and machine learning in general. Machine Learning conferences such as ICML and NeurIPS publish several TSA papers at each conference. The original DTW paper has approx. 10K citations. Some key examples for papers on this topic include: * SoftDTW (Cuturi & Blondel, ICML 2017) * Drop-DTW (Neurips 2017) * Autowarp (NeurIPS 2018) * Diffeomorphic Temporal Alignments Nets (Neurips 2019) * Closed-form Diffeomorphic Transformations for Time Series Alignment (ICML 2022) * Regularization-free Diffeomorphic Temporal Alignment Nets (ICML 2023) We believe the UCR archive, that was used for evaluation and includes more than 100 real-world datasets, is diverse enough in terms of modalities (ECG, motion sensor, shape outlines, and more). Thus, the concern that the training on synthetic data won't suffice for obtaining good results on real-world datasets is unwarranted: as we showed in the paper, the approach yielded SOTA results on real-world datasets. RE: other tasks - TP could potentially be extended to other tasks such as time series classification, clustering, anomaly detection, and more. However, properly addressing these tasks is beyond the scope of the current paper. These are indeed interesting research directions that are left for future works. # Q2 - Synthetic data training vs real-world data An excellent point. We discuss this issue in lines: 065-073. We agree with the notion that training and/or fine-tuning TP on real-world data could further improve the proposed method. The reasons we chose to focus solely on synthetic data are: 1. We are not aware of real-world TS datasets with annotated KPs. 2. Using only synthetic data mitigates license-related issues that might arise. We will make this point clearer in the revised manuscript. That being said, we have conducted more experiments on real-world datasets. Specifically, as per your inquiry and other reviewers' requests, we perform a fine tuning experiment where TP is pre-trained on synthetic data and then fine-tuned on real-world data. Due to space limitations, they appear in our answers to other reviewers: Please see the additional experiments: 1. Robustness to Noise experiment - Reviewer zrdP 2. Fine Tune on Real World Data - Reviewer QUAf	Summary: The paper presents TimePoint, a self-supervised method for accelerating Dynamic Time Warping (DTW) in time series alignment by leveraging keypoint detection and descriptor learning from synthetic data. The main findings demonstrate that TimePoint significantly outperforms traditional DTW in terms of speed and accuracy, effectively addressing computational challenges and noise sensitivity in time series analysis. Claims And Evidence: The claims made in the submission regarding TimePoint's capability to enhance the speed and accuracy of Dynamic Time Warping (DTW) are well supported by extensive experimental results demonstrating significant improvements over traditional DTW methods. However, while the authors provide convincing evidence of TimePoint's performance on synthetic data, further clarification on its generalization to a wider range of real-world datasets with varying conditions may strengthen the submission's robustness. Methods And Evaluation Criteria: The proposed method, TimePoint, effectively addresses the challenges of time series alignment by utilizing a self-supervised learning approach that incorporates keypoint detection and descriptor generation, making it suitable for handling large and varied datasets. Additionally, the evaluation criteria, including extensive testing on benchmark datasets like the UCR Time Series Archive, demonstrate its robust performance and contextual relevance to real-world applications in time series analysis. Theoretical Claims: I reviewed the theoretical claims presented in the paper, particularly focusing on the proofs related to the efficiency of the TimePoint framework and its alignment accuracy. Experimental Designs Or Analyses: The experimental designs and analyses appear to be sound, particularly the ablation study which effectively demonstrates the performance improvements of the TimePoint framework across various datasets. However, further clarification on the selection criteria for datasets and the impact of synthetic data generation on real-world performance would enhance the validity of the findings. Supplementary Material: Yes Relation To Broader Scientific Literature: The key contributions of the paper, particularly the introduction of TimePoint for efficient time-series alignment, relate closely to existing literature in several ways: 1) Dynamic Time Warping (DTW): The paper builds on the foundational work of DTW, which has been widely used for time-series alignment due to its ability to handle elastic shifts in the temporal axis. However, it addresses DTW's limitations, such as its quadratic time complexity and sensitivity to noise, which have been noted in prior studies. 2) Keypoint Detection and Description: TimePoint adapts concepts from 2D keypoint detection methods, like SuperPoint, to the 1D time-series domain. This adaptation is significant as it addresses the unique challenges of time-series data, such as nonlinear distortions and amplitude variations, which have not been thoroughly explored in previous works. 3) Synthetic Data Generation: The introduction of SynthAlign, a synthetic dataset designed for training keypoint detection and descriptor learning, is a novel contribution. Previous research has often focused on real-world datasets, while this paper emphasizes the importance of synthetic data for self-supervised learning, a concept that has been underutilized in time-series analysis. 4) Continuous Piecewise Affine Based (CPAB) Transformations: The use of CPAB transformations to model nonlinear temporal warping is a significant advancement. While prior works have explored diffeomorphic transformations, they often lacked practical implementations for keypoint detection and descriptor extraction, which TimePoint successfully integrates. 5) Efficiency and Scalability: The paper demonstrates that applying DTW to a sparse set of keypoints and descriptors leads to substantial computational speedups and improved alignment accuracy. This finding aligns with the ongoing research in machine learning and time-series analysis that seeks to enhance efficiency without sacrificing performance, as seen in methods like FastDTW and SoftDTW. Overall, the contributions of this paper not only advance the state of the art in time-series alignment but also provide a framework that can inspire further research in both theoretical and applied contexts within the broader scientific literature. Essential References Not Discussed: No Other Strengths And Weaknesses: The paper introduces TimePoint, a novel self-supervised framework for keypoint detection and descriptor learning specifically tailored for time series data. This adaptation from 2D keypoint detection methods to 1D signals is a significant innovation, addressing a gap in existing literature. Other Comments Or Suggestions: None Questions For Authors: 1. How does TimePoint's performance compare to other state-of-the-art time series alignment methods in terms of robustness against noise and temporal distortions in real-world datasets? 2. What specific metrics or criteria were used to evaluate the generalization capability of TimePoint when applied to diverse real-world time series data, beyond the synthetic datasets used for training? 3. Can you elaborate on the potential limitations or challenges of using synthetic data for training TimePoint, particularly in terms of its applicability to highly variable real-world time series signals? Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: We thank the reviewer for their kind words and comprehensive response and suggestions. # Q1 - TP vs. SOTA time series alignment: robustness to noise and temporal distortions. TP was evaluated on 100+ datasets of the UCR archive. These datasets significantly vary in terms of noise and temporal distortion. In Section A. in the appendix, page 12, we show the model’s KPs and descriptors on three datasets that vary in length, frequency, domain, and distortion. Additionally, we believe the comparisons in Figure 7 and Table 1 provide a strong indication of TP robustness compared to state-of-the-art DTW-based method. While we test TP+DTW and TP+SoftDTW (Table 1), other alignment algorithms could also benefit from TP’s descriptors and KPs. Finally, we have performed a "Robustness to noise" experiment on real-world data, detailed below. # Robustness to Noise (Additional Experiment) We conducted a robustness analysis to Gaussian Blur where $\sigma\in\[0.1, 0.2\]$ and Additive Gaussian Noise (a.k.a, Jitter) where $\sigma\in\[0.1, 0.2\]$. Due to the random sampling of noise, we repeat the experiment 3 times. Due to the large number of experiments per dataset (noise types X noise rates X method = 2 X 4 X 3) we use a subset of 30 UCR datasets. The results are presented below: \| \| no_noise \| Blur ($\sigma=0.1$) \| Blur ($\sigma=0.2$) \| Jitter ($\sigma=0.1$) \| jitter ($\sigma=0.2$) \| \|------------------\|----------\|--------------\|--------------\|---------\|---------\| \| DTW \| 0.844 \| 0.843 \| 0.838 \| 0.801 \| 0.744 \| \| TimePoint(kp=0.1)\| 0.867 \| 0.866 \| 0.853 \| 0.804 \| 0.760 \| \| TimePoint(kp=0.2)\| 0.881 \| 0.873 \| 0.873 \| 0.828 \| 0.791 \| # Q2 - What specific metrics or criteria were used to evaluate generalization? We have used the Nearest Neighbor classifier with DTW as distance measure (DTW-NN) to evaluate TP on real-world data. It is the customary benchmark for evaluating alignment algorithms (e.g., see the SoftDTW paper [Cuturi & Blondel, ICML ‘17]). In more detail, DTW is performed between each test and train sample. The test data is labeled according to its closest neighbor label in the train set. Higher classification accuracy indicates that the similarity measure (DTW, TP-DTW, SoftDTW, etc.) is better. Given that the similarity measure is fixed (DTW) compared with competing methods, the quality of the KPs and descriptors is the main variable measured for evaluation. We will clarify this point in the revised manuscript. # Q3 - Limitations using synthetic data when generalizing to real-world data Yes. As we mentioned in the limitations section (Sec. 5, Line 344), a key limitation is when the real-world data significantly differ from the synthetic data for SynthAlign. An example for such data is speech recordings. While the UCR holds some data that relates to speech recognition (see Appendix. A.1, Line 652 -Phoneme dataset), speech alignment and/or recognition is left for further research, as it requires special care (perhaps a combination of SynthAlign and text-to-speech generative model). To further answer this question, we have conducted an experiment where we fine-tune TP on real world data. Please see our answer to Reviewer QUAf: Fine Tune on Real World Data.	Summary: This paper introduces TimePoint, a self-supervised framework for accelerating DTW-based time series alignment by learning keypoints and descriptors. TimePoint leverages 1D diffeomorphisms to model nonlinear temporal distortions, combined with fully convolutional and wavelet-based architectures to extract multi-scale features. Experiments demonstrate that TimePoint consistently achieves faster and more accurate alignments than standard DTW, making it a scalable solution for time-series analysis. 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: Not mentioned. Essential References Not Discussed: No. Other Strengths And Weaknesses: Strengths: 1. The paper introduces an efficient time-series alignment framework which addresses the scalability limitation of traditional methods like DTW. 2. Experimentally, the proposed TP is a robust and efficient method. Weakness: 1. Since SynthAlign relies on predefined waveforms (e.g., sine, RBF), its performance on real-world data with complex patterns (e.g., high-frequency noise, non-stationary trends) is unclear. It is recommended to conduct experiments under the real-world dataset like PTB [1]. [1] Goldberger, Ary L., et al. "PhysioBank, PhysioToolkit, and PhysioNet: components of a new research resource for complex physiologic signals." circulation 101.23 (2000): e215-e220. 2. In Figure 8, when using the full signal (L = 100%), the runtimes for DTW and TP+DTW are almost identical. This observation warrants further analysis and discussion of the results. Other Comments Or Suggestions: See Weakness. Questions For Authors: See Weakness. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We thank the reviewer for their kind words and suggestions. # Q1 - It is recommended to conduct experiments under the real-world dataset like PTB [1] Agreed, but this was already done in the paper. Please note that while TP was trained on synthetic data, all of the reported experiments were conducted on real world datasets of the UCR time series classification archive (i.e., section 6.2 Classification on Real-World Data and the results from Figures 7-8, and Tables 1-2). We evaluated TP on more than 100 datasets of various data types, such as ECG, sensors, motions (action recognition for Wii remote, smart devices), Human activity recognition (HAR) and more. The datasets were contributed by different authors. Specifically, the original dataset for "ECG5000", which is one those 100+ UCR datasets, is a 20-hour long ECG downloaded from Physionet (under the name “BIDMC Congestive Heart Failure Database”, see: https://www.timeseriesclassification.com/description.php?Dataset=ECG5000 ); i.e., the very dataset the reviewer mentioned. The UCR archive is considered a gold standard for time series alignment and is widely used for evaluating alignment algorithms such as DTW. We will make sure this is clearer in the revised manuscript. Since PhysioNet contains dozens of datasets, not all are applicable for TS alignment, we were unable to evaluate TP on further datasets (besides ECG5000) from this benchmark. ### Please also see the additional experiments on real world data: 1. Robustness to Noise experiment - Reviewer zrdP 2. Fine Tune on Real World Data - Reviewer QUAf # Q2 - Runtime (Figure 8) You are correct. The runtime for DTW and TP+DTW using 100% of KPS (the entire length of the time series) are almost identical. This is due to the low-overhead of TPs forward pass, which means that the runtime is almost entirely dominated by the time it takes to compute DTW. We will make this point clearer in the revised manuscript. Thank you for pointing it out.	Summary: This paper proposes a self-supervised method that dramatically accelerates DTW-based alignment while typically improving alignment accuracy by learning keypoints and descriptors from synthetic data. Claims And Evidence: The claims are clear and convincing except one concern. While CPA is an effective method for modeling nonlinear temporal distortions and generating correspondences between time series signals, I am concerned that CPAB may not be sufficiently comprehensive to model all types of time series distortions, particularly those exhibiting high complexity and variability. For instance, in the case of non-stationary time series, the parameter $\theta$ in the CPAB transformation might evolve over time. I recommend that the authors conduct further studies to enhance their proposed method and ensure it can fully address all challenges posed by real-world problems. Methods And Evaluation Criteria: The paper introduces a synthetic time series dataset with known KPs and applies CPAB warps to generate training pairs with ground-truth correspondences. It further proposes a self-supervised framework, TimePoint, for detecting and describing keypoints in time series data. However, the model's performance could potentially be enhanced by fine-tuning it on real-world datasets. As noted by the authors in Section 5, TimePoint's performance may be suboptimal if the signals deviate significantly from the synthetic distribution. Therefore, I strongly recommend incorporating a fine-tuning step on real-world data to ensure robust performance and adaptability to practical scenarios. Theoretical Claims: The proofs for theoretical claims are correct. Experimental Designs Or Analyses: I recommend that the authors conduct a robustness analysis of their proposed methods. The paper utilizes CPAB warps to generate training pairs with ground-truth correspondences. However, in real-world scenarios, some pairs may be incomplete. Introducing a study where certain points are removed from the pairs and evaluating the model's performance on incomplete data could enhance its robustness to various practical scenarios. Supplementary Material: Yes, all. Relation To Broader Scientific Literature: The efficient and scalable alignment of time series is a critical research topic within the time series community. This study introduces a self-supervised method that significantly accelerates DTW-based alignment, offering key advancements and valuable insights to the field. Essential References Not Discussed: No Other Strengths And Weaknesses: While CPA is an effective method for modeling nonlinear temporal distortions and generating correspondences between time series signals, I am concerned that CPAB may not be sufficiently comprehensive to model all types of time series distortions, particularly those exhibiting high complexity and variability. For instance, in the case of non-stationary time series, the parameter $\theta$ in the CPAB transformation might evolve over time. I recommend that the authors conduct further studies to enhance their proposed method and ensure it can fully address all challenges posed by real-world problems. Other Comments Or Suggestions: In Section 4.2, KPs are selected by either applying a pre-defined threshold or choosing the top-K timesteps with the highest probability. -> In the experiments, please elaborate how sensitive the threshold to the model's performance. Questions For Authors: While CPA is an effective method for modeling nonlinear temporal distortions and generating correspondences between time series signals, I am concerned that CPAB may not be sufficiently comprehensive to model all types of time series distortions, particularly those exhibiting high complexity and variability. For instance, in the case of non-stationary time series, the parameter $\theta$ in the CPAB transformation might evolve over time. I recommend that the authors conduct further studies to enhance their proposed method and ensure it can fully address all challenges posed by real-world problems. The paper introduces a synthetic time series dataset with known KPs and applies CPAB warps to generate training pairs with ground-truth correspondences. It further proposes a self-supervised framework, TimePoint, for detecting and describing keypoints in time series data. However, the model's performance could potentially be enhanced by fine-tuning it on real-world datasets. As noted by the authors in Section 5, TimePoint's performance may be suboptimal if the signals deviate significantly from the synthetic distribution. Therefore, I strongly recommend incorporating a fine-tuning step on real-world data to ensure robust performance and adaptability to practical scenarios. I recommend that the authors conduct a robustness analysis of their proposed methods. The paper utilizes CPAB warps to generate training pairs with ground-truth correspondences. However, in real-world scenarios, some pairs may be incomplete. Introducing a study where certain points are removed from the pairs and evaluating the model's performance on incomplete data could enhance its robustness to various practical scenarios. n Section 4.2, KPs are selected by either applying a pre-defined threshold or choosing the top-K timesteps with the highest probability. -> In the experiments, please elaborate how sensitive the threshold to the model's performance. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We thank the reviewer for their kind words and comprehensive response and suggestions. # Q1 - Non-stationary time series (NSTS) This is an excellent point. A single CPAB warp implies a stationary velocity field, while the CPAB prior restricts the warps to avoid unrealistic distortions. Three factors affect the alignment quality: 1. KP detection is unaffected by NSTS as it is performed independently for each TS. 2. Descriptors are also computed independently. Since each descriptor's receptive field is quite large, it might be affected by NSTS. 3. The matching is computed using DTW on TP’s features at KPs locations. DTW is not restricted to a specific type of misalignment between TS, and in TP’s case only relies on the features' similarity. Empirically, the UCR archive consists of more than a 100 of real-world datasets, including several NSTS datasets. E.g., “ECGFiveDays” dataset holds ECGs that were recorded five days apart. TP reaches 94.2% test accuracy while the best competitor achieves 92% (see Tables E2 and E3 at our appendix). As an aside, one can compose CPAB warps, and, partially because CPAB warps are not closed under composition, this has the effect of integrating a non-stationary velocity field. However, in 1D, this effect can be well approximated by taking a finer tessellation. Either way, we haven't noticed an empirical need to do so. # Q2 - Fine-tuning on real-world data True, the performance could potentially be enhanced by fine-tuning the model on real-world data. The reasons we chose to focus the training on synthetic data (as opposed to the test, that was done on real-world data) are: 1. We are unaware of real-world TS dataset with enough annotated KPs. 2. Using synthetic data bypasses any license-related issues that might arise. That said, and in accordance with the reviewers' suggestions, here in the rebuttal we include additional results, obtained after fine-tuning TP on real-world data (see below). # Fine-Tune on Real-World Data We thank all reviewers for their suggestions and inquiries regarding fine-tuning TP on real-world data. The experiment details are as follows: * We used the same method to compute KP as we did for SynthAlign (local minima/maxima, etc.). * We fine-tuned TP after it was first trained on SynthAlign. * The training data contained virtually the entire UCR archive (a few datasets were omitted due to technical reasons). * We created pairs with known correspondences by applying two CPAB warps to each input signal (i.e., each signal is augmented twice, and those augmented views are the input for TP and loss functions). * Training for 2K epochs Below we report results for 10%/20%/50% of the length (the experiment with 100\% didn't finish in time for the rebuttal, but we'll include it in the revised manuscripts). Results \| Method \| Baseline (DTW) \| 10% \| 20% \| 50% \| \|--------------------------\|----------------\|-------\|-------\|-------\| \| TP (Synth) \| 0.706 \| 0.707 \| 0.721 \| 0.710 \| \| TP (Synth + Fine Tune) \| 0.706 \| 0.777 \| 0.790 \| 0.769 \| The results show that fine-tuning TP on real-world datasets yields a significant improvement in performance across all KPs percentages. The table follows Table 1 from the paper, where the results in the first row are taken from the paper and the second row from this fine-tune experiment. The runtime remains the same as in Table 1. We thank the reviewers for suggesting this experiment. Fine-tuning TP on real-world data, using our proposed training scheme, is a useful addition to the overall method. We will incorporate this experiment in the revised manuscript. # Q3 - Robustness with missing KPs Re missing data, we agree such analysis can be benficial. That said, we are unsure exactly what the reviewer meant: “[...] where certain points are removed from the pairs and evaluating on incomplete data“. Since during inference KPs are computed automatically by TP, the scenario where points are removed never occurs in our current setting. We have conducted a “Robustness to Noise” experiment using Blurring and Jitter. (please see our answer to zrdP). # Q4 - Sensitivity to the threshold. The choice of threshold is critical for TP’s performance. To that end, Table 1 shows the performance for 10\%, 20\%, 50\%, 100\% of KPs. Effectively, each value corresponds to a different threshold (the reported runtime includes sorting KPs by their probability, so the overhead is minimal). Since the evaluation was conducted on 100+ datasets, choosing a fixed threshold for all dataset will be sub-optimal. Thus, we believe this adaptive strategy is a good heuristic when working with a large number of datasets. When working on a specific dataset, cross-validation may also be used for choosing the value. We will elaborate on the model’s sensitivity to the choice of threshold in the revised manuscript.	null	null	null	null	null	null
InfoSEM: A Deep Generative Model with Informative Priors for Gene Regulatory Network Inference	Accept (poster)	Summary: This paper emphasizes the reason why unsupervised gene regulatory network inference lags in supervised ones is that it did not well utilize the prior knowledge. They followed the framework proposed by DeepSEM and proposed infoSEM to involve prior knowledge provided by BioBERT and logit probability. In addition, the paper argued that the previous benchmarks suffer from robustness and imbalanced classes. They improved it by making sure that genes in test sets are not in training sets. The effectiveness of InfoSEM is verified on real-world datasets with Ground-Truth provided by ENCODE and ChIP-Atlas. Claims And Evidence: This paper relies on an important assumption that genes, which are similar in function, prefer to have similar causal relationships. I think this claim needs evidence to support it. I do not know if it is reasonable in biology. Methods And Evaluation Criteria: I agree with that Chip-seq is used as ground truth to evaluate the performance. But ENCODE and ChIP-Atlas usually have limited records, how do you evaluate the output gene regulatory network? 1. How can we guarantee that the prior knowledge from BioBERT is reliable? 2. For gene regulatory network inference, if you train a model for different cells, how do you guarantee that the output network is suitable for all cells, as the expressed genes are different among different cells? 3. If you consider the data generation process following e.q. (3), how to identify the direction of genes if there is a latent variable affecting them? Theoretical Claims: There are no theoretical claims Experimental Designs Or Analyses: Yes. I am curious about how to align the splitting of test sets and the ground truth in evaluation, as if you randomly split the training and test sets, some genes may not be reported by Chip-seq. Usually the sc-RNA seq datasets have around 5000 genes, why the dataset you choose all is around 1000 genes. Supplementary Material: Yes. All the parts. Relation To Broader Scientific Literature: Providing a way to involve prior knowledge for unsupervised learning. Essential References Not Discussed: No Other Strengths And Weaknesses: How to guarantee the asymmetry of gene regulatory network, especially, considering the confounding effect provided by latent variables? Other Comments Or Suggestions: No Questions For Authors: No Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We appreciate the reviewer’s insightful comments. Below, we address their questions. 1. Do Functionally Similar Genes Share Causal Relationships?: The assumption that functionally similar genes share causal relationships is well supported by biological literature. Evolutionary principles suggest that genes used for related functions often maintain similar regulatory architectures [1,2]. Mendelian randomization studies show that genes affecting related traits frequently share causal variants in lipid metabolism and coronary heart disease [3,4]. Pleiotropy analyses further demonstrate that cell-type-specific genes influence multiple neuropsychiatric traits via overlapping pathways, reinforcing the notion of shared causal roles among functionally related genes [5]. We will include this discussion and relevant citations in the camera-ready version. 2. Evaluation of the Output GRN: We use the established BEELINE GRN evaluation dataset [7], which only evaluates interactions with recorded ground-truth labels, consistent with previous works [8,9]. 3. Reliability of BioBERT-Derived Prior: BioBERT has been shown to enhance scRNA-seq information for GRN inference in prior work [10]. In our InfoSEM framework, we treat BioBERT embeddings as an additional prior, with their influence adjustable through a cross-validated hyperparameter that allows the model to reduce their importance if deemed unreliable. Still, to further validate the reliability of BioBERT embeddings in response to the reviewer's question, we performed Gene Ontology enrichment analysis on gene clusters derived from hierarchical clustering of the similarity matrix of BioBERT embeddings, controlling for false discovery rate (FDR). Analysis of 908 genes revealed several significant functional enrichments post-FDR correction (FDR < 0.05), notably in lipid transport (FDR=6.80e-12), DNA replication initiation (FDR=6.95e-07), and RNA polymerase II transcription (FDR=3.49e-07). The enrichment patterns displayed clear biological specificity; for instance, one cluster included APOA1, APOA2, APOA4, and APOB, enriched for cholesterol efflux (FDR=4.12e-14), while another cluster encompassed multiple MED genes related to transcription regulation. These robust enrichments strongly suggest that BioBERT embeddings capture meaningful biological relationships between genes. 4. Training Single Model for Different Cell Types: This appears to be a misunderstanding. We do not train a single model for multiple cell types. Like DeepSEM [8] and other baselines, we train separate models for each cell type to capture cell-type-specific regulatory interactions instead of assuming a universal gene regulatory network. 5. Handling Latent Variables & Network Asymmetry: The impact of latent variables on inferred direction of GRNs is an important research area, as shown in studies like [6]. We will include a discussion of this in our paper and cite [6]/other relevant works. However, our study relies on established datasets with experimentally validated interactions from prior works [7], which we believe minimizes the impact of latent confounders. Addressing confounders comprehensively will be a non-trivial task that warrants a separate paper, beyond the scope of our work. 6. Alignment of Test Set Split and ChIP-seq Ground Truth: Like question 2's response, we adhere to established literature by considering only known interactions from ChIP-seq databases [7,8,9] and splitting them into training and test sets. 7. Choice of 1000 Genes Instead of 5000: We follow BEELINE's established preprocessing method [7], selecting the top 1000 highly expressed genes to enhance the quality of inferred networks and ensure comparability with prior methods [8,9]. In light of additional experiments & clarifications provided in response to reviewer's comments, we kindly request consideration on raising the score. We believe these clarifications address all the comments! #### Reference [1] Evaluating the potential role of pleiotropy in Mendelian randomization studies, 2018 [2] Inferring causality and functional significance of human coding DNA variants, 2012 [3] Diagnostics for Pleiotropy in Mendelian Randomization Studies: Global and Individual Tests for Direct Effects, 2018 [4] Pleiotropy-robust Mendelian randomization, 2018 [5] Selecting causal genes from genome-wide association studies via functionally-coherent subnetworks, 2016 [6] Gene Regulatory Network Inference in the Presence of Selection Bias and Latent Confounders, 2025 [7] Benchmarking algorithms for gene regulatory network inference from single-cell transcriptomic data, 2020 \ [8] Modeling gene regulatory networks using neural network architectures, 2021 \ [9] Graph attention network for link prediction of gene regulations from single-cell RNA-sequencing data, 2022 \ [10] scGREAT: Transformer-based deep-language model for gene regulatory network inference from single-cell transcriptomics, 2024 --- Rebuttal Comment 1.1: Comment: Thanks for the author's response! Re:1: If this assumption is common or can be a principle to follow if only supported by some cases, I think it is not enough. Another concern is whether the similarity in the embedding of BioBert can accurately represent functional consistency instead of only similarities. Re4 and 6 Differential gene expression is a well-established concept in biology. Based on this phenomenon, it is commonly assumed that gene regulatory networks (GRNs) are context-specific—meaning that different cell lines may have distinct underlying regulatory mechanisms. You mentioned using ChIP-seq data as a reference; however, I believe it is challenging to ensure consistency due to the limited availability and coverage of ChIP-seq records. So I still have concerns about the ground truth. Could you introduce more about which ChIP-seq data you use, and how consistence between the ChIP-seq data and ScRNA-seq data? --- Reply to Comment 1.1.1: Comment: Thank you! We provide additional clarifications below. ## Functionally Similar Genes Share Causal Relationships We reiterate that functionally similar genes sharing causal relationships is not a hypothesis, but rather a well-established biological fact supported by extensive literature with insights from statistical genetics and evolutionary principles. In our rebuttal, we cited five papers [1-5] supporting this and here we add two more works further reinforcing this fact [11-12]. We will include them in related works section in paper. We believe the reviewer's claim that this fact is "only supported by some cases" overlooks the substantial evidence we have cited, which consistently demonstrates these relationships across numerous independent studies. Given the scientific evidence, we see no reason to dispute the validity of this fact and believe our expanded references clarify it sufficiently. ## Similarity in BioBERT embedding accurately represents functional consistency As mentioned in our rebuttal, firstly our method utilizes BioBERT gene embeddings as a flexible prior while learning the appropriate weights to assign to this prior and hence can automatically down-weight their contribution, if deemed unreliable. Secondly, in our rebuttal we already provided further evidence of BioBERT embeddings' effectiveness in representing functional consistency via gene-set enrichment analysis, a well-established technique in biology cited over 50,000 times [13]. Conducting Gene Ontology enrichment on gene clusters from BioBERT embeddings revealed strong functional enrichments in processes such as lipid transport, DNA replication initiation, and RNA polymerase II transcription, demonstrating clear biological specificity in clusters derived from BioBERT gene embeddings and consistent functional relationships among similar genes. Importantly, our main contribution lies not in the use of BioBERT embeddings as prior, but rather in InfoSEM, a variational Bayes framework for GRN inference that can incorporate any informative gene embedding to enhance performance. We showed that other effective priors, such as GenePT embeddings (in main text) and Gene Ontology knowledge graph embeddings (in our rebuttal to Reviewer bvmZ), also improve GRN inference with our method. Therefore, if other gene embeddings are identified to be more reliable, they can be seamlessly integrated in place of BioBERT embeddings, as evidenced by our experiments. ## GRNs are context-specific—different cell lines may have distinct underlying regulatory mechanisms We fully agree with reviewer on the importance of cell-type specificity and this is precisely why we train separate models for different cell types, a practice also adopted by others in the field. The cell-type specificity of GRN is demonstrated through our cell-type-specific target experiments in Table 2 in paper already. We are not aware of any instance in the paper or rebuttal that contradicts this point. ## More about ChIP-seq data/consistency between ChIP-seq and scRNA-seq We use scRNA-seq and ChIP-seq data from BEELINE project [7] (Pratapa et al., Nature Methods, 2020), which collected and preprocessed scRNA-seq data from five different cell lines (two human, three mouse) with corresponding ChIP-seq data from the same or similar cell types for each scRNA-seq dataset, sourced from ENCODE, ChIP-Atlas, and ESCAPE databases. For detailed information, refer to "Datasets" section of BEELINE paper (Nature Methods version). The datasets have been widely recognized for cell-type specific GRN inference, as evidenced by their use in literature [8-9, 14] and highlighted in three more works by Reviewer TUBJ [15-17]. Notably, BEELINE paper and its associated datasets have been cited over 680 times, reflecting their quality and reliability. While acquiring more comprehensive ChIP-seq datasets for multiple cell lines is valuable, it is beyond the scope of our ML-focused paper, which utilizes existing public datasets to propose new ML models. We believe this addresses all questions and we request the reviewer to consider raising their score in light of these clarifications! ## References: References [1-10] mentioned in original rebuttal \ [11] Shared associations identify causal relationships between gene expression & immune cell phenotypes, 2021 \ [12] Shared genetic architecture and causal relationship between frailty & schizophrenia, 2025 \ [13] Gene set enrichment analysis: a knowledge-based approach for interpreting genome-wide expression profiles, 2005 \ [14] DeepDRIM: a deep neural network to reconstruct cell-type-specific GRN using scRNA-Seq data, 2021 \ [15] Boosting single-cell GRN reconstruction via bulk-cell transcriptomic data, 2022 \ [16] GRN Inference from Pre-trained Single-Cell Transcriptomics Transformer with Joint Graph Learning, 2024 \ [17] STGRNS: an interpretable transformer-based method for inferring GRNs from single-cell transcriptomic data, 2023	Summary: This paper introduces a method that incorporates gene embeddings from pretrained language models or known gene-gene relationships into the existing DeepSEM framework, resulting in two models: InfoSEM-B and InfoSEM-BC. The authors provide a detailed discussion on how to integrate the interaction matrix $Y$ and adjacency matrix $A$ when introducing gene relationships. Additionally, they propose a new benchmark approach for evaluating gene regulatory network model performance, where not only are interactions absent from the training set, but transcription factors are also excluded from the training set. Claims And Evidence: Yes, the authors support their claims through comparisons with baselines and through precise ablation experiments and relevant analyses. Methods And Evaluation Criteria: Yes, AUPRC and Hit@1% appear to be reasonable metrics for evaluating the accuracy of gene regulatory network predictions. Theoretical Claims: I have examined the author's explanations regarding the variational inference proofs in the main text and did not find any issues. Experimental Designs Or Analyses: I have reviewed the performance comparison tables with baselines and the ablation experiment tables. The analysis results demonstrate the effectiveness of the author's proposed method and the effectiveness of using gene embeddings. Supplementary Material: I focused on examining Appendix B regarding dataset details and Appendix E showing experimental results on the unseen gene set. Relation To Broader Scientific Literature: The authors' proposed method is a direct extension of the DeepSEM[1] method published in 2021. [1] Modeling gene regulatory networks using neural network architectures Essential References Not Discussed: See the Familiarity With Literature and Questions For Authors sections. Other Strengths And Weaknesses: This paper appears to be an incremental improvement on DeepSEM. Nonetheless, I personally believe that the work of integrating external gene knowledge and gene relationships is quite important. The authors' experimental conclusions demonstrate the effectiveness of these biological priors in improving gene regulatory network prediction performance, which I think may inspire more work in this direction. Other Comments Or Suggestions: See Questions For Authors. Questions For Authors: 1. In Section 2.2, do the mentioned external priors specifically refer to the gene embeddings and gene relationships mentioned later? Could you provide a brief explanation here? 2. Would the authors have time to add a comparison with the SCENIC method? 3. How does the authors' proposed model generalize to the $D_\text{unseen}$ set? Is it through gene embeddings and gene interactions? 4. Why did you prioritize trying gene embeddings from pretrained language models? How effective would gene embeddings from RNA foundation models (such as scGPT, scFoundation, etc.) be? 5. Did the authors consider the impact of data leakage when integrating external priors? Were any validation measures taken? Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: We thank the reviewer for their thoughtful and constructive comments. We appreciate the recognition of our new benchmark and the value of integrating external priors for GRN inference. We address the reviewer’s questions below and will include them in the camera-ready version. 1. External Priors in Section 2.2: Yes, the external priors refer to gene embeddings and gene relationships. These priors can be derived from various sources, including textual embeddings (e.g., BioBERT), knowledge graphs (e.g., Gene Ontology), or known gene interactions, all of which original DeepSEM cannot use directly. 2. Comparison with SCENIC: We have now included a comparison with SCENIC, which demonstrates similar performance as GRNBoost2. Our InfoSEM-B and InfoSEM-BC outperform SCENIC across all cell lines for AUPRC and across all but hHEP for Hit@1% metric for the cell-type specific datasets. \| Method\| hESC AUPRC \| hESC Hit@1% \| hHEP AUPRC \| hHEP Hit@1% \| mDC AUPRC \| mDC Hit@1% \| mESC AUPRC \| mESC Hit@1% \| \|-------\|----------- \|-------------\|------------\|-------------\|-----------\|------------\|------------\|-------------\| \| SCENIC\| .210(.020)\| .200(.037)\| .465(.020)\| .568(.047)\| .227(.014)\| .219(.062)\| .346(.024)\| .393(.045)\| \| InfoSEM-B (Ours)\| .331(.055)\| .547(.091)\| .498(.020)\| .533(.048)\| .298(.028)\| .472(.076)\| .388(.023)\| .522(.047)\| \| InfoSEM-BC (Ours)\| .331(.056)\| .585(.094)\| .499(.020)\|.550(.053)\| .322(.032)\| .498(.069)\| .408(.020)\| .575(.045)\| 3. Reason for InfoSEM generalization to D_{unseen}: InfoSEM's main training objective is the gene expression reconstruction rather than the interaction prediction used in the supervised learning framework. This encourages the model to learn the gene-gene relationships from the gene expression data, instead of utilizing the gene-specific bias from the labels, hence contributing to its ability to generalize to the unseen gene set, D_{unseen}. Additionally, using gene embeddings as priors aids our model's generalization to the unseen gene set by leveraging those priors to learn gene relationships. 4. Use of Gene Embeddings from Single-cell Foundation Models: We initially focused on gene embeddings from pretrained language models like BioBERT due to their effectiveness in providing semantic context for various models and tasks (see [1,2]). Furthermore, BioBERT is easier to use; it requires only the gene names already available, unlike single-cell models that necessitate specific preprocessing of scRNA-Seq data. Following the reviewer's suggestion, we experimented with embeddings from scBERT [3], a foundation model designed for single-cell RNA data, but did not observe significant improvements in performance over InfoSEM-B working with a one-hot baseline instead. We hypothesize that this may result from scBERT's binning of scRNA-Seq data, which could lead to a loss of important information. Additionally, scBERT's embeddings, derived from binned scRNA-Seq data, are similar to those used in InfoSEM already and may not provide complementary insights for the adjacency matrix compared to embeddings like Gene Ontology or BioBERT, which are derived independent of scRNA-Seq data. We believe, though, that exploring other scRNA-Seq foundation model derived gene embeddings presents an interesting avenue for future exploration. In response to a similar query from reviewer bvmZ regarding the use of external priors from knowledge graphs, we conducted additional experiments using Gene Ontology (GO) embeddings as priors. The AUPRC results, shown below on the unseen-genes benchmark, demonstrate that this further enhances our InfoSEM results on human cell lines, reinforcing the importance of incorporating external priors from independent sources. \| Method \| hESC AUPRC \| hHEP AUPRC\| \|---------\|------\|------\| \| DeepSEM\| .265(.032)\| .435(.019)\| \| Our InfoSEM-B (onehot) \| .270(.038)\| .447(.027)\| \| Our InfoSEM-B (BioBERT) \| .332(.055)\| .498(.020)\| \| Our InfoSEM-B (GO) \| .345(.057)\|.524(.034)\| \| Our InfoSEM-B (scBERT) \| .272(.029)\| .442(.027)\| 5. Data Leakage and Validation Measures: Thank you for the important remark! Unlike seen-gene benchmarks, we ensured there was no data leakage between training and test sets in our proposed unseen benchmarking setup, as the genes between training and testing are different. We hope our clarifications and additional experiments answer all your valuable comments. In light of the additional experiments and results presented, we kindly ask if the reviewer would consider raising their score. Thank you! #### References [1] scGREAT: Transformer-based deep-language model for gene regulatory network inference from single-cell transcriptomics, 2024 \ [2] GenePT: A Simple But Effective Foundation Model for Genes and Cells Built From ChatGPT, 2024 \ [3] scBERT as a large-scale pretrained deep language model for cell type annotation of single-cell RNA-seq data, 2022 --- Rebuttal Comment 1.1: Comment: Thank you for your detailed and thoughtful response. Your clarifications and additional experiments have addressed my concerns thoroughly. Based on your response and the updated results, I have raised my score accordingly.	Summary: Summary This study proposes infoSEM, a deep generative model with informative priors for gene regulatory network (GRN) inference. By integrating text-based gene embeddings as biological priors, it addresses the critical challenge of GRN reconstruction without ground-truth interaction labels. The authors also introduce a novel benchmarking framework to evaluate predictions for unseen gene relationships. Main findings: 1. Leveraging textual gene embeddings as informative priors enhances GRN inference when interaction labels are unavailable. 2. Further integrate available interaction labels as additional priors to reduce bias and improve performance. Main Results: 1. Evaluated the performance of existing supervised and unsupervised methods under established benchmarks, analyzing why simple methods like one-hot logistic regression (LR) perform remarkably well. 2. Supervised models (e.g., scGREAT and GENELink) showed significant performance degradation in predicting interactions between unseen genes, while unsupervised methods (especially DeepSEM) outperformed supervised methods across three datasets. 3. The InfoSEM-B model improves GRN inference by 25% and 52% on average over DeepSEM when gene interactions are unknown. The InfoSEM-BC variant, which incorporates known interaction information, achieves the best AUPRC performance across all datasets. 4. The study also demonstrates that BioBERT embeddings enhance GRN inference. Main algorithmic ideas: Built upon the DeepSEM framework, integrating BioBERT embeddings and gene interaction embeddings as prior knowledge. Claims And Evidence: 1. Under existing benchmarks, the performance of current supervised and unsupervised methods is significantly inferior to the one-hot logistic regression (LR) approach. The minimal differences in AUPRC also were observed on the new benchmark dataset. A question arises: Would replacing one-hot encoding with BioBERT embeddings in LR yield improved performance on the new benchmark? 2. InfoSEM-B and InfoSEM-BC were only evaluated on the new benchmark, with no assessment conducted on original benchmarks. Methods And Evaluation Criteria: 1. The proposed method demonstrates limited technical improvements compared to DeepSEM, primarily consisting of additional embedding incorporation. 2. The newly proposed benchmark represents a significant advancement for GRN inference research, particularly in addressing the critical challenge of generalizability to unseen gene relationships. Theoretical Claims: 1. The work provides detailed theoretical derivations and mathematical formulations, enabling readers to easily comprehend the mathematical principles and logical foundations underlying the model. 2. Existing methodologies are thoroughly described and systematically categorized. Experimental Designs Or Analyses: The experimental design (unseen gene) is reasonable. Experimental analysis: 1. InfoSEM-B and InfoSEM-BC only evaluate the results on the new benchmark, not the results on the original benchmark. 2. Ablation studies should be supplemented, such as BioBert's dembedding + LR, ... Supplementary Material: I have reviewed all the content in the supplementary material. Relation To Broader Scientific Literature: This work built upon the DeepSEM framework, integrating BioBERT embeddings and gene interaction embeddings as prior knowledge. Essential References Not Discussed: The paper adequately cites and discusses foundational works relevant to GRN inference, including: 1. Supervised approaches(scGREAT, GENELink) 2. Unsupervised variational approaches (DeepSEM, GRNBoost2) While the core references are sufficient, expanding the discussion to include: 1. Gene Regulatory Network Inference from Pre-trained Single-Cell Transcriptomics Transformer with Joint Graph Learning. ICML 2024 AI for Science workshop 2. Boosting single-cell gene regulatory network reconstruction via bulk-cell transcriptomic data. Briefings in Bioinformatics, 23(5):bbac389, 2022. 3. STGRNS: an interpretable transformer-based method for inferring gene regulatory networks from single-cell transcriptomic data. Bioinformatics 2023 Other Strengths And Weaknesses: Strengths: 1. Conducts systematic evaluation of supervised vs unsupervised methods across legacy and novel benchmarks 2. Empirically demonstrates BioBERT's effectiveness as biological priors for GRN inference. Weaknesses: 1. The proposed method shows limited architectural innovation over DeepSEM (primarily embedding additions) 2. InfoSEM variants lack ablation studies Other Comments Or Suggestions: None Questions For Authors: 1. The proposed method demonstrates limited technical improvements compared to DeepSEM, primarily consisting of additional embedding incorporation. 2. Under existing benchmarks, the performance of current supervised and unsupervised methods is significantly inferior to the one-hot logistic regression (LR) approach. The minimal differences in AUPRC also were observed on the new benchmark dataset. A question arises: Would replacing one-hot encoding with BioBERT embeddings in LR yield improved performance on the new benchmark? 3. InfoSEM-B and InfoSEM-BC were only evaluated on the new benchmark, with no assessment conducted on original benchmarks. 4. Ablation studies should be supplemented, such as different loss (VAE -> AE), and more other variants. 5. While the core references are sufficient, expanding the discussion to include: [1] Gene Regulatory Network Inference from Pre-trained Single-Cell Transcriptomics Transformer with Joint Graph Learning. ICML 2024 AI for Science workshop [2] Boosting single-cell gene regulatory network reconstruction via bulk-cell transcriptomic data. Briefings in Bioinformatics, 23(5):bbac389, 2022. [3] STGRNS: an interpretable transformer-based method for inferring gene regulatory networks from single-cell transcriptomic data. Bioinformatics 2023 Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We appreciate the reviewer’s feedback and acknowledgment of our real-world benchmark as a key advancement in GRN inference, along with their praise for our theoretical clarity. Below, we address their questions and provide additional results, which we will include in the camera-ready version. 1. Ablation studies (BioBERT embeddings+LR, AE loss): Thank you for the suggestion! We have now tested BioBERT embeddings in LR on unseen genes benchmark. Results below show that BioBERT+LR performs similarly or slightly better than the 1-hot LR baseline in paper. This is expected, as in the unseen-gene setting, both LR baselines (with 1-hot or BioBERT) can't leverage gene-specific biases for GRN inference. The slight improvement with BioBERT embeddings highlights the informativeness of the embeddings over 1-hot encoding. However, both these baselines perform considerably worse compared to our InfoSEM-B/InfoSEM-BC models, underscoring the benefits of our proposed framework as a whole beyond simply incorporating BioBERT as prior. We explored the AE loss function (DeepSEM-AE) suggested by the reviewer, but it performed significantly worse than DeepSEM and our InfoSEM-B and InfoSEM-BC models due to DeepSEM's assumption of a Gaussian distribution for Z [1, 2], which requires regularization in the variational Bayes loss. Our InfoSEM-B and InfoSEM-BC naturally serve as ablation studies on the baseline DeepSEM. InfoSEM-B serves as an ablation study by replacing DeepSEM's Laplace prior over A with our informative prior, while InfoSEM-BC adds Aˡ and its informative prior to InfoSEM-B. We are open to any further ablation studies if the reviewer suggests. \|Method\|hESC AUPRC\|hESC Hit@1%\|hHEP AUPRC\|hHEP Hit@1%\|mDC AUPRC\|mDC Hit@1%\|mESC AUPRC\|mESC Hit@1%\| \|------------\|------------\|-------------\|------------\|-------------\|-----------\|------------\|------------\|-------------\| \| 1-hot LR \|.210(.018)\| .205(.041)\| .395(.016)\| .345(.056)\| .247(.019)\| .225(.004)\| .329(.026)\| .397(.036)\| \| BioBERT+LR\|.212(.019)\| .227(.050)\| .423(.023)\| .450(.076)\| .230(.020)\| .151(.050)\| .347(.021)\| .397(.088)\| \| DeepSEM-AE\|.203(.016)\| .183(.033)\| .400(.018)\| .483(.054)\| .211(.009)\| .143(.022)\| .321(.021)\| .311(.031)\| \| DeepSEM\| .265(.032)\| .419(.059)\| .435(.019)\| .517(.043)\| .277(.014)\| .292(.095)\| .343(.024)\| .369(.048)\| \| InfoSEM-B (Ours)\|.331(.055)\| .547(.091)\| .498(.020)\| .533(.048)\| .298(.028)\| .472(.076)\| .388(.023)\| .522(.047)\| \| InfoSEM-BC (Ours)\|.331(.056)\| .585(.094)\| .499(.020)\| .550(.053)\| .322(.032)\| .498(.069)\| .408(.020)\| .575(.045)\| 2. Evaluation on Original Benchmarks: Thank you for your comment! We have now included InfoSEM on the original seen-gene benchmarks in our response to reviewer bvmZ, with results presented in the accompanying table. Our results show that for traditional seen-gene benchmarks, simple supervised models (One-hot LR & MatComp) perform best by leveraging gene-specific biases without using scRNA-seq data, a fact which our work highlights for the first time and is a key contribution of our work. Even in this context, InfoSEM-BC maintains a competitive balance, avoiding overfitting gene-specific biases while performing better than unsupervised baselines. However, the key takeaway is that for seen-gene benchmarks, simpler models that exploit gene-specific biases are sufficient, and hence, we propose to evaluate advanced machine learning models on unseen-gene benchmarks. 3. Limited architectural innovation over DeepSEM: We emphasize that our contribution is not on architectural innovation over DeepSEM, but in extending it within a principled variational Bayes framework to leverage informative priors (e.g., gene embeddings from language models) or available ground truth information without overfitting to gene-specific biases, an aspect not explored so far. Additionally, we show for the first time that existing supervised learning models tend to leverage gene-specific biases in the dataset, and hence, we introduce a new unseen genes benchmark to provide a reliable testbed for evaluating generalizability of GRN inference methods. As the reviewer themselves noted, our benchmark for evaluating generalizability to unseen gene relationships is a crucial advancement for GRN inference, and we are happy that it has been well received. 4. Including citations to proposed references: We thank the reviewer for additional references. We have already cited the first and third references in the paper and will include the second one in the camera-ready version too. These citations will enhance the discussion and provide further context to our work. We hope that our clarifications and additional results address your concerns! We kindly request the reviewer to consider raising their score, taking these into account. #### References [1] DAG Structure Learning with Graph Neural Networks, 2019 \ [2] Modeling gene regulatory networks using neural network architectures, 2021	Summary: The paper introduces InfoSEM, an unsupervised generative model for Gene Regulatory Network (GRN) inference that leverages textual gene embeddings as informative priors. The model can also integrate ground truth (GT) labels when available, avoiding biases and enhancing performance. The authors propose a new benchmarking framework that evaluates interactions between unseen genes, better aligning with real-world applications like biomarker discovery. The paper also highlights limitations in existing supervised learning benchmarks, showing that supervised models may exploit dataset biases rather than capturing true biological mechanisms. Claims And Evidence: The authors claim that current GRN inference benchmarks fail to generalize well because they are trained and evaluated on the same set of genes, leading to an overestimation of model performance. This claim is supported by experiments where supervised models show significant performance drops when evaluated on unseen genes. However, a major limitation is that the proposed method is only evaluated on the new unseen-gene benchmark, and it does not compare performance in the traditional setting where models infer unseen regulatory interactions among known genes (seen-gene sets). Given that many real-world biological applications prioritize discovering novel interactions among well-studied genes, the broader impact of InfoSEM’s approach may be limited. Methods And Evaluation Criteria: The evaluation methodology is well-structured, incorporating multiple datasets from the BEELINE suite and relevant baselines (e.g., DeepSEM). However, the paper only evaluates InfoSEM on the new unseen-gene benchmark and does not compare its performance in the traditional seen-gene setting. This omission raises concerns about whether InfoSEM is broadly applicable to all GRN inference tasks. The rationale for selecting BioBERT embeddings as informative priors is reasonable, but it would be helpful to compare against other gene representation techniques (e.g., knowledge graph embeddings). Theoretical Claims: The variational Bayes framework for InfoSEM appears mathematically sound. The decomposition of the adjacency matrix (Ae and Al) into effect size and interaction probability is novel, but the paper does not provide strong theoretical justification for why this decomposition improves GRN inference. Experimental Designs Or Analyses: The experiments convincingly demonstrate that supervised models overfit seen genes and fail to generalize to unseen genes. However, the paper does not compare InfoSEM’s performance for discovering unseen interactions among seen genes, which is a key limitation. In many real-world settings, researchers seek to uncover new regulatory interactions within well-characterized gene networks, rather than predicting interactions for entirely unseen genes. Computational efficiency is not addressed, which is critical for scaling deep generative models to larger genomic datasets. Supplementary Material: The supplementary material includes detailed derivations of the ELBO for InfoSEM-B and InfoSEM-BC, as well as additional experimental results and hyperparameter settings. These details enhance the reproducibility of the study and provide further evidence supporting the claims made in the paper. Relation To Broader Scientific Literature: The paper is well-positioned in the GRN inference and single-cell genomics literature and aligns with recent efforts to develop interpretable AI models for biology. However, the focus on unseen-gene inference is not well contextualized within broader biological research, where many studies aim to infer novel regulatory interactions among well-characterized genes. Essential References Not Discussed: The paper should discuss related work in knowledge graph-based GRN inference, as BioBERT embeddings are not the only way to encode biological prior knowledge. Other Strengths And Weaknesses: Strengths: Novel use of BioBERT embeddings as informative priors for GRN inference. Insightful critique of dataset biases in supervised GRN benchmarks. Demonstrates strong performance on the new unseen-gene benchmark. Weakness: Does not evaluate InfoSEM in the traditional seen-gene setting, limiting its applicability to broader GRN inference tasks. Computational efficiency is not addressed, which is important for scalability. Lack of theoretical justification for the adjacency matrix decomposition (Ae and Al). Other Comments Or Suggestions: The authors should evaluate InfoSEM’s performance in the seen-gene setting to determine whether it is broadly applicable. A runtime comparison of InfoSEM vs. baselines would improve understanding of its computational feasibility. A more explicit discussion of the real-world implications of predicting interactions among unseen genes vs. seen genes would strengthen the paper. Questions For Authors: 1. Why is InfoSEM not evaluated in the traditional seen-gene setting? This is a crucial benchmark for real-world GRN inference. 2. How does InfoSEM compare computationally to other deep generative models for GRN inference? 3. Would using alternative gene embeddings (e.g., knowledge graph embeddings) affect performance? Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We appreciate the reviewer’s valuable feedback and acknowledgment of our work’s novelty and rigor. We are happy that our analysis of biases in supervised GRN benchmarks and InfoSEM’s performance on the unseen-gene benchmark were well received. Below, we address the reviewer’s questions and provide additional results, which we will include in the camera-ready version of the paper. 1.Evaluation in Traditional Seen-Gene Setting: Thank you for the important point! We now show InfoSEM's performance in this setting below for all datasets (cell-type-specific ChIP-seq targets). \| Method \| hESC AUPRC \| hESC Hit@1% \| hESC AUPRC \| hESC Hit@1% \| mDC AUPRC \| mDC Hit@1% \| mESC AUPRC \| mESC Hit@1% \| \|------------\|------------\|-------------\|------------\|-------------\|-----------\|------------\|------------\|-------------\| \| One-hot LR \| .600(.028) \| .932(.039) \| .835(.005) \| 1.(.003) \| .176(.006) \| .250(.024) \| .844(.009) \| .991(.004)\| \| MatComp \| .638(.026) \| .913(.037) \| .840(.006) \| 1.(.006) \| .351(.013) \| .419(.034) \| .860(.007) \| .974(.008) \| \| DeepSEM \| .216(.010) \| .318(.016) \| .424(.011) \| .509(.028) \| .118(.006) \| .165(.033) \| .340(.013) \| .431(.023) \| \| InfoSEM-B \| .374(.027) \| .752(.067) \| .467(.011) \| .538(.020) \| .130(.010) \| .174(.048) \| .401(.012) \| .562(.016) \| \| InfoSEM-BC \| .553(.028) \| .913(.053) \| .702(.007) \| .865(.023) \| .285(.016) \| .555(.063) \| .672(.010) \| .918(.026) \| The results show that for traditional seen-gene benchmarks, simple supervised models (One-hot LR, MatComp) without utilizing scRNA-seq perform best by leveraging gene-specific dataset biases, a fact which our work highlights for the first time and is a key contribution of our work. Even in this context, InfoSEM-BC maintains a competitive balance, avoiding overfitting to the gene-specific biases while performing better across multiple datasets compared to other unsupervised methods (GRNBoost2, DeepSEM). However, we again emphasize that the key takeaway is for seen genes benchmark, simple supervised models (One-hot LR, MatComp) that exploit gene-specific biases from known interactions are sufficient even without scRNA-seq. Hence, we propose to evaluate more advanced machine learning models on unseen-gene benchmarks where simple models entirely fail as shown in paper. 2.Gene embeddings from knowledge graphs: Thank you for the suggestion! Our flexible framework can incorporate embeddings from other sources, such as knowledge graphs. To showcase this, we now did additional experiments using Gene Ontology (GO) knowledge graph embeddings as priors (AUPRC shown below on unseen-genes benchmark), which improve our InfoSEM-B (BioBERT) results even further on human cell lines but lag behind our original InfoSEM-B (BioBERT) on mouse cell lines. This is because GO knowledge graph used is specific to human cells. Unlike BioBERT, which is more generic, knowledge graphs have to be chosen carefully depending on the context. \| Method \| hESC \| hHEP\| mDC \| mESC \| \|---------\|------\|------\|------\|------\| \| DeepSEM \| .265(.032) \| .435(.019)\| .277(.014)\| .343(.024)\| \| Our InfoSEM-B (one-hot)\| .270(.038) \| .447(.027)\| .224(.012)\| .338(.022)\| \| Our InfoSEM-B (BioBERT)\| .332(.055) \| .498(.020)\| .298(.028)\| .388(.023)\| \| Our InfoSEM-B (GO)\| .345(.057) \| .524(.034)\| .275(.011)\| .359(.024)\| 3.Compute Efficiency: We have now included comparison of run times (in seconds) for different configurations of (num_cell, num_gene) for InfoSEM and other baselines. Our results demonstrate that InfoSEM is faster than popular supervised learning baselines and only slightly slower than DeepSEM, while consistently outperforming them in terms of performance in unseen genes benchmark. \| Model \|(454, 844) \| (758, 844) \| (758, 1291) \| \|-----------\|-----------\|------------\|-------------\| \| scGREAT\| 236.30 \| 239.96\| 357.52 \| \| GENELink\| 177.25 \| 172.72 \| 258.91\| \| SCENIC\| 80.81 \| 97.74\| 142.51\| \| GRNBoost2 \| 9.27 \| 10.81\| 13.74\| \| DeepSEM \| 91.88 \| 112.55\| 116.01\| \| InfoSEM-B \| 118.00 \| 134.11\| 206.86\| \| InfoSEM-BC\| 125.91 \| 164.16\| 211.37\| 4.Rationale for Aᵉ and Aˡ splitting of interaction matrix: By splitting the interaction matrix into two components—Aᵉ for the magnitude and Aˡ for the logit—we create a setup where both components can incorporate prior biological knowledge independently so that any possible misspecification of one prior will not affect the other. The prior on Aᵉ, informed by embeddings, acts as a starting point, but the model can adjust its MAP estimate based on data. Similarly, the prior on Aˡ allows for a probabilistic treatment of known interactions, but leaves room for learning from the data where these interactions might not be fully observed. We hope these clarifications and new results address the reviewer’s concerns and enhance our paper's contributions. We kindly request consideration for a score increase based on this. We are happy to address any further suggestions!	null	null	null	null	null	null
Pixel2Feature Attack (P2FA): Rethinking the Perturbed Space to Enhance Adversarial Transferability	Accept (poster)	Summary: This paper introduces Pixel2Feature Attack (P2FA), a novel approach aimed at enhancing the transferability of adversarial examples in black-box attacks. The main point of the paper is to address the inefficiency of existing feature-level attacks, which tend to perturb features multiple times in pixel space, leading to limited transferability. 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: /NA Essential References Not Discussed: /NA Other Strengths And Weaknesses: ## Strengths The theoretical identification of the principle underlying feature-level attacks, which reveals the inefficiency of existing methods in disrupting important features. The proposal of P2FA, which shifts perturbations from pixel space to feature space, improving the efficiency and transferability of adversarial examples. ## Weaknesses While the paper mentions using different feature importance assessment methods in the ablation study, it does not provide sufficient details on how these methods are implemented or how they differ from each other. This paper not compare the performance of VIT backbone. Other Comments Or Suggestions: /NA Questions For Authors: /NA Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We are grateful to the reviewer for their valuable feedback, and we will address the following issues in our response. (If the latex formula is not rendered, please refresh the page.) # Q1: Explanation of Feature Importance Assessment Methods In Sec. A.1 of the appendix, we provided a brief introduction to the feature importance assessment methods used in different feature-level attacks. However, we did not offer sufficient details regarding the implementation of these methods or the distinctions between them. Next, I will provide a detailed explanation. - FIA: In FIA, feature importance $W$ can be expressed as $$ W = -\bar{\Delta} _ k^x = -\frac{\sum _ {n=1}^N \Delta _ k^{\mathcal{T} _ n(x)}}{\|\| \sum _ {n=1}^N \Delta _ k^{\mathcal{T} _ n(x)} \|\| _ 2}, ~~ \mathcal{T} _ n(x) = x \odot M _ {p _ d}^n, ~~ M _ {p _ d}^n \sim Bernoulli(1 - p _ d), $$ where $\bar{\Delta} _ k^x$ denotes the aggregate gradient, $\Delta_k^x = \frac{\partial l(x, y)}{\partial f_k(x)}$, $l(\cdot, y)$ denotes the logits output concerning the ground-truth label $y$, and $M_{p_d}^n$ is a binary matrix that satisfies the $Bernoulli(1 - p_d)$ distribution, where $p_d$ represents the random pixel dropping rate. Therefore, the aggregated gradient $\bar{\Delta}_k^x$ can be summarized as performing a batch of random pixel-dropping transformations on the original image and then unitizing the gradient sum of the feature maps of the transformed images. - RPA: The difference between RPA and FIA lies only in the different transformation $\mathcal{T}$, which results in different feature importance $W$. Specifically, FIA applies random pixel-dropping transformations to the image, while RPA first generates a mask $M$ of the same size as $x$, which is a matrix with all elements of 1. Then, $M$ is divided into regular, non-overlapping patches $P$, with each patch size being $n^2$. Next, we randomly select a subset of patches with the probability of $P_m$: $P_{p_m}=Rand(P,p_m)$ and modify them to follow a uniform distribution: $P_m \sim U[0,1)$. Therefore, the transformation $\mathcal{T}$ of RPA can be expressed as $\mathcal{T}_n(x) = x \odot M$. - NAA: In NAA, the feature importance $W$ can be expressed as follows: $$ W = -\frac{\sum_{m=1}^n \frac{\partial F(x_m, y)}{\partial f_k(x_m)}}{\|\| \sum_{m=1}^n \frac{\partial F(x_m, y)}{\partial f_k(x_m)} \|\|_2} $$ where $F(\cdot, y)$ denotes the softmax output of the true label $y$, $x_m = (1 - \frac{m}{n})x' + \frac{m}{n} x$ and $x'$ denotes a baseline image. Therefore, the feature importance $W$ of NAA can be understood as taking $n$ points along the linear path from the baseline image $x'$ to the input image, calculating the unitized result of the gradient sum of the feature map of these $n$ points, and finally adding a negative sign. - DANAA: The difference between DANAA and NAA lies only in that the paths used to compute $x_m$, which results in different feature importance $W$. DANAA uses a non-linear path instead of the linear path. Specifically, $x^m = x^0 + \sum_{k=0}^{m-1} \Delta x^k$, where $\Delta x^k = lr \cdot \text{sign}\left( \frac{\partial F(x^k)}{\partial x^k_i} \right) + N(0, \sigma)$, $\frac{\partial F}{\partial x^k_i}(\cdot)$ is the partial derivative of $F$ to the $i$-th pixel, $lr$ denotes learning rate and $N(0,\sigma)$ denotes Gaussian noise. - SFVA: In SFVA, the feature importance $W$ can be expressed as follows: $$ W = -\hat{W}^=-\frac{1}{c} \sum_{i=1}^{N}\frac{\partial F(x'_i)}{\partial f_k(x'_i)} $$ where $\hat{W}^$ denotes the optimal feature weights, $x'_i=Scale(Mask(x)+\gamma_i)$. Specifically, we sequentially perform random mask, random addition of noise, and scale transformation on the original image $N$ times, and then compute the unitized result of the gradient sum of the feature map of the transformed images. - BFA: In BFA, feature importance $W$ can be expressed as follows: $$ W =I = \frac{1}{N}{\sum_{m=1}^N \frac{\partial F(x_m^{IF}, y)}{\partial f_k(x_m^{IF})}} $$ where $x_m^{IF}$ denotes the fitted image at the $mth$ iteration. Specifically, we compute the average of the fitted gradients of the fitted images with different degrees of fit to represent the feature importance $W$. # Q2: Lack of Transformer-based models The target models we selected, while classic, may not be sufficiently advanced and are exclusively CNN-based. We have additionally included four Transformer-based models, i.e., PiT-S, CaiT-S, DeiT-B, and Swin-B, as target models. The experimental results are presented in the response to Reviewer ASTV’s Q3 and Reviewer Li9f’s Q1. These results demonstrate that our proposed P2FA continues to exhibit higher transferability, further substantiating the effectiveness of our approach. Finally, we express our gratitude for your valuable feedback, which will greatly contribute to improving the quality of our manuscript. We look forward to your response.	Summary: This paper theoretically analyzes that existing multi-feature-based attack methods are essentially equivalent to perturbing features once. Correspondingly, a P2FA is proposed to perturb the feature spaces multiple times, by shiting the perturb space from pixel to feature. Extensive experiments were conducted to demonstrate the effectiveness of the proposed method. Overall, this paper proposes the P2FA from a novel and interesting point with sufficiently theoretical analysis. I think this finding can enhance most feature-based adversarial attacks. Claims And Evidence: Most claims are supported by its experiments and analysis. Methods And Evaluation Criteria: Yes. Theoretical Claims: Yes. Experimental Designs Or Analyses: Yes. Supplementary Material: No supplementary material was provided. Relation To Broader Scientific Literature: This paper contributes to the trustworthiness AI. Essential References Not Discussed: Yes. Other Strengths And Weaknesses: This paper demonstrates good originality in terms of the integrated analysis of existing feature-level attacks. Also, there is sufficient derivation and experimental evidence to validate the correctness of their conclusion. The insightful conclusion drawn in this paper may offer valuable inspiration for future research endeavors. However, the target classification models chosen, though classic, are not sufficiently advanced. Also, they are all CNN-based. Most of models are built upon Transformer nowadays, so people may want to know the performance of your attack on more advanced Transformer models. Another weakness is that the proposed attack method lacks innovation, since it is largely based on previous works. Other Comments Or Suggestions: In your derived conclusion “is effectively equivalent to perturbing the features only once along the direction of feature importance in the feature space”, I am not sure “once” refers to one step or updating in one direction only. If you mean perturbing in only one direction, is there a clearer way to express it instead of “once”? Questions For Authors: No. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: # Q1: Lack of Transformer-based models You rightly pointed out that Transformer-based models dominate contemporary research, and there is a legitimate interest in understanding how our proposed attack performs against these more advanced architectures. In response to your comment, we have followed your suggestion and expanded our experimental evaluation to include four Transformer-based models: Swin Transformer (Swin-B)[1], Data-efficient Image Transformer (DeiT-B)[2], Pooling-based Vision Transformer (PiT-S)[3], and Class-Attention in Image Transformers (CaiT-S)[4]. These Transformer-based models were used as target models by the recent work RPA[5]. The preliminary results are shown in Table 1 (more experimental results can be found in Reviewer ASTV's Q3), demonstrating that our attack method remains effective against these models and outperforms the current SOTA feature importance-based attack, BFA. Detailed results and analysis will be incorporated into the revised manuscript. Table 1. Attack Success Rates of P2FA(Ours), BFA, and their Combinations with Input Transformations on Transformer-based Models, Using Inception-v3 as the Surrogate Model \| Model \| Attack \| Swin-B \| DeiT-B \| PiT-S \| CaiT-S \| Avg. \| \| :-: \| :-: \| :-: \| :-: \| :-: \| :-: \| :-: \| \| Inc-v3 \| BFA \| 42.0 \| 52.8 \| 68.8 \| 52.8 \| 54.1 \| \| Inc-v3 \| P2FA(Ours) \| 43.4 \| 55.7 \| 70.7 \| 53.3 \| 55.8 \| \| Inc-v3 \| PIDI-BFA \| 46.2 \| 59.6 \| 73.4 \| 59.3 \| 59.6 \| \| Inc-v3 \| PIDI-P2FA(Ours) \| 60.3 \| 75.9 \| 85.2 \| 73.0 \| 73.6 \| We believe this extension not only addresses the limitation you identified but also enhances the practical relevance of our findings to the current research landscape. We will include a discussion of this limitation, the newly added experimental results, and our planned follow-up experiments in the revised manuscript to reflect your suggestion adequately. [1] Liu Z, Lin Y, Cao Y, et al. Swin transformer: Hierarchical vision transformer using shifted windows[C]//Proceedings of the IEEE/CVF international conference on computer vision. 2021: 10012-10022. [2] Touvron H, Cord M, Douze M, et al. Training data-efficient image transformers & distillation through attention[C]//International conference on machine learning. PMLR, 2021: 10347-10357. [3] Heo B, Yun S, Han D, et al. Rethinking spatial dimensions of vision transformers[C]//Proceedings of the IEEE/CVF international conference on computer vision. 2021: 11936-11945. [4] Touvron H, Cord M, Sablayrolles A, et al. Going deeper with image transformers[C]//Proceedings of the IEEE/CVF international conference on computer vision. 2021: 32-42. [5] Zhang Y, Tan Y, Chen T, et al. Enhancing the Transferability of Adversarial Examples with Random Patch[C]//IJCAI. 2022, 8: 13. # Q2: Clarification of innovations Regarding innovation concerns, this paper offers two key contributions. - Innovation 1: Discover the inefficiency of existing feature importance-based attacks through mathematical proofs. We would like to highlight that our work stems from a comprehensive analysis of existing feature importance-based attacks. Through mathematical proofs (the latest proof see Reviewer ASTV's Q1) and experimental validation, we reveal that existing feature importance-based attacks, relying on multiple pixel-space perturbations, equate to just one step in the feature space along feature importance. Therefore, the perturbation efficiency of existing feature importance-based attacks is inefficient, which also motivates the proposed P2FA to apply feature-space perturbations directly to improve the perturbation efficiency. - Innovation 2: A new paradigm for transforming perturbed space from pixel to feature space. Based on the above proof and experiments, P2FA shifts perturbation from pixel to feature space, applying multiple efficient perturbations to critical features, boosting transferability across models. This redefines feature importance-based attack paradigms, and we will clarify these innovations in the revised introduction and methodology sections. We are grateful for your feedback, which has prompted us to refine our exposition. In the revised manuscript, we will expand the discussion in the introduction and methodology sections to clearly articulate this innovation and underscore our contributions. # Q3: Poorly expressed We thank you for noting ambiguity in our phrasing: “is effectively equivalent to perturbing the features only once along the direction of feature importance in the feature space.” We meant one perturbation step in the feature space matches the effect of multiple pixel-space perturbations. To avoid confusion, we will revise it to: “is effectively equivalent to perturbing the features in one step along the direction of feature importance in the feature space.” This clarification will improve readability in the updated manuscript.	Summary: In this paper, the authors propose Pixel2Feature Attack (P2FA) to enhance the transferability of feature-based attack across different DNN models. To enhance the efficiency, the proposed P2FA shifts the disturbance space from the pixel space to the feature space. Specifically, P2FA perturbs feature maps within the feature space by following the direction of dynamically updated feature importance, and then generate adversarial samples through feature inversion. Experiments using the ImageNet benchmark dataset demonstrate that the proposed P2FA method achieves the better attack transferability compared to state-of-the-art approaches. Moreover, ablation study is conducted to analyze the impact of training factors on the attack success rate. ## update after rebuttal Thank you to the author for addressing the raised questions. However, several critical concerns remain unresolved. The rebuttal provides derivations suggesting that Eq. 11 serves as an upper bound for Eq. 8. However, there is no explicit connection established between the solutions of Eq. 8 and Eq. 11. Therefore, the conclusion that perturbing features once is equivalent to perturbing pixels multiple times remains questionable. Moreover, the methodology heavily relies on the feature importance computed by the BFA method, resulting in interactions between the input pixel space and the feature space during perturbation training. As a result, the specific contribution of perturbing the feature space remains unclear. For these reasons, I have decided to maintain my original score of “Weak Reject”. Claims And Evidence: 1. The claim that perturbing multiple times in the pixel space is equivalent to perturbing once in the feature space lacks rigorous theoretical support. 2. Regarding the efficiency of feature attacks, this paper focuses solely on the attack success rate but lacks an analysis of efficiency itself, such as computational time cost. 3. The feature importance $W_t$ is updated using the fitted image obtained from the input space in each iteration. However, this approach does not effectively address the previously stated inefficiency issues. Methods And Evaluation Criteria: Yes, the proposed methods and evaluation criteria are relevant and appropriate for addressing the problem. Theoretical Claims: In Section 3.2, it is unclear how the conclusion that “perturbing multiple times in pixel space” equals “perturbing once along the direction of feature importance in feature space” was derived from Eq.11. To be specific, Eq.11 does not have a closed-form solution; Eq.11 should be a constrained optimization problem, rather than the simplified representation shown in Figure 2. Experimental Designs Or Analyses: 1. The input transformation methods (e.g., PIM and DIM) considered are not the most up-to-date. 2. In Table 4, only two defended CNN models are used as target models. To ensure a more comprehensive evaluation, additional models should be included, refer to the experimental settings used in FIA and RPA. 3. In Section 4.1, the rationale behind choosing a large step size in the feature space for the experiments is unclear. Additionally, no clear justification is provided for defining the number of perturbations as 3. Supplementary Material: Sections A.1-A.4 have been reviewed. Relation To Broader Scientific Literature: This paper focuses on the literature of feature-based attacks, leveraging feature importance from the BFA method to generate adversarial samples. Essential References Not Discussed: This paper discusses both feature-based attacks and input transformation attacks. However, the cited input transformation attacks are not up-to-date, as recent methods such as SIA [1] and BSR [2] are not included in the discussion. [1] Structure Invariant Transformation for better Adversarial Transferability. ICCV 2023. [2] Boosting Adversarial Transferability by Block Shuffle and Rotation. CVPR 2024. Other Strengths And Weaknesses: 1. Eq.12 does not clearly explain how the cross-entropy loss is defined between $f_k$ and $y$. 2. The experiment demonstrates that the proposed method enhances attack transferability; however, there is no clear evidence indicating an improvement in efficiency. Other Comments Or Suggestions: In line 214, the parameter $s$ is introduced, but its role is not clearly explained in this context. Questions For Authors: 1. Could the authors provide further clarification on why perturbing the feature only in the feature space can achieve the optimal solution of Eq.11 under the L-infinity constraint? 2. As the feature importance $W_t$ is iteratively updated from the input space, this additional computation raises concerns regarding the algorithm's time efficiency. Could the authors provide a comparison of P2FA’s efficiency against state-of-the-art methods? 3. Could the authors clarify why PIM and DIM were integrated with feature-based attacks while recent input transformation methods, such as SIA and BSR, were not considered? 4. Could the authors clarify why this optimization algorithm requires a large step size to update the feature map in the latent feature space? Additionally, in Fig.3, why is the attack performance not sensitive to the hyperparameter, particularly when the step size exceeds $10^3$? Code Of Conduct: Affirmed. Overall Recommendation: 2	Rebuttal 1: Rebuttal: We thank the reviewer for their valuable feedback, which we address below. (If the latex formula is not rendered, please refresh the page.) # Q1: Theoretical Proof We appreciate the reviewer spotting an error in Eq. (11). We omitted the constraint on $x^{adv}$. Next, we will focus on rigorously proving that multiple pixel-space perturbations in Eq. (8) equal a single feature-space perturbation along feature importance $W$. First, we equivalently rewrite Eq. (8) as: $$ \underset{x^{adv}}{\arg \max} \langle W, f_k(x^{adv}) - f_k(x) \rangle,~ s.t.~\|\|x^{adv} - x \|\|_p \leq \epsilon. $$ Then, using the Cauchy–Schwarz inequality ($\langle u, v \rangle \leq \|\|u\|\|_2\|\|v\|\|_2$, equality when $u = s \cdot v, s \geq 0$), the following inequality still holds: $$ \left \langle W, f_k(x^{adv}) - f_k(x) \right \rangle \leq \|\|W\|\|_2 \|\| f_k(x^{adv}) - f_k(x) \|\|_2 $$ with equality holding when $f_k(x^{adv}) = f_k(x) + s \cdot W (s \geq 0)$ and $\|\|x^{adv} - x\|\|_p \leq \epsilon$, also achieving the optimum. The role of $s$ is to ensure that the adversarial example obtained through feature inversion satisfies $\|\|x^{adv} - x\|\|_p \leq \epsilon$. In practice, we additionally add a clip function to ensure this. In other words, we only need a single feature-space perturbation $s \cdot W$ and satisfy the $\epsilon$-ball to achieve the optimum of Eq. (8). Experiments in Sec. 3.2 also validates the correctness of the claimed conclusion. We’ll update the manuscript with a more detailed version of this proof and revise Fig. 2. # Q2: Efficiency We clarify that efficiency in the submitted manuscript refers to fewer perturbation iterations ($T=3$ for P2FA vs. $T=10$ for baseline). As you rightly noted, efficiency also includes time efficiency. To fairly compare time efficiency, we tuned BFA’s hyperparameters ($T$, $N$) to match P2FA’s success rate on ImageNet-NIPS with Inception-v3 on an RTX 4090. P2FA ($T=3, N=30$) achieves 84.1% average success in 0.616s/example, while BFA ($T=50, N=200$) reaches 83.9% but in 1.577s/example. BFA is 2.5x slower than P2FA. We’ll add detailed data to the revised manuscript. # Q3: SIA and BSR SIA and BSR are two highly commendable works. In response to your feedback, we have conducted additional experiments integrating P2FA with SIA and BSR. Partial experimental results are presented in the table below. \| Attacks \| Inc-v3* \| IncRes-v2 \| Res-152 \| Vgg-16 \| Swin-B \| DeiT-B \| PiT-S \| CaiT-s \| Avg. \| \| --- \| --- \| --- \| --- \| --- \| --- \| --- \| --- \| --- \| --- \| \| BFA+BSR \| 100.0 \| 89.1 \| 85.7 \| 92.0 \| 34.3 \| 45.8 \| 62.6 \| 46.5 \| 69.5 \| \| P2FA+BSR \| 100.0 \| 96.2 \| 96.2 \| 97.3 \| 56.6 \| 73.6 \| 83.1 \| 69.1 \| 84.0 \| \| BFA+SIA \| 100.0 \| 93.4 \| 92.6 \| 95.9 \| 47.1 \| 66.0 \| 76.8 \| 64.0 \| 79.5 \| \| P2FA+SIA \| 100.0 \| 98.9 \| 98.7 \| 99.4 \| 68.1 \| 81.8 \| 91.5 \| 80.8 \| 89.9 \| Results show P2FA+SIA and P2FA+BSR achieve higher transferability than SOTA BFA with SIA and BSR. Full results will be added to the revision. # Q4: Step Size ## Q4.1: Large Step Size P2FA requires a large step size for effective perturbations due to small $W_t$ values (the average order of magnitude is between $10^{-6}$ and $10^{-5}$) relative to the intermediate layer’s feature $f_{k,t}$ (the average order of magnitude is $10^{-1}$). ## Q4.2: Low Sensitivity Beyond $10^3$ Clipping within the $\epsilon$-ball limits the feature-space perturbation range when $s > 10^3$, reducing sensitivity. The average values of pre- and post-clip features confirm this. \| $s$ \| Pre-clip$(t=0/1/2)$ \| Pose-clip$(t=0/1/2)$ \| \| --- \| --- \| --- \| \| $1$ \| 0.674/0.675/0.678 \| 0.675/0.677/0.678 \| \| $10$ \| 0.679/0.680/0.683 \| 0.675/0.677/0.678 \| \| $10^2$ \| 0.726/0.732/0.739 \| 0.675/0.679/0.682 \| \| $10^3$ \| 1.410/1.509/1.566 \| 0.697/0.731/0.757 \| \| $10^4$ \| 10.930/11.316/11.544 \| 0.766/0.820/0.848 \| \| $10^5$ \| 108.424/110.887/112.908 \| 0.788/0.837/0.860 \| \| $10^6$ \| 1075.449/1096.937/1114.703 \| 0.790/0.838/0.861 \| ## Q4.3: Meaning of $s$ $s$ is the scaling factor from the Cauchy–Schwarz inequality, acting as the step size along $W$. We’ll clarify this in the revision. # Q5: Defense Models Regrettably, we were unable to find PyTorch versions of Ens3-Inc-v3, Ens4-Inc-v3, and Adv-IncRes-v2, but tested P2FA on PiT-S, CaiT-S, DeiT-B, and Swin-B from RPA, showing higher transferability (see Reviewer Li9f’s Q1). Lastly, if you could kindly provide a solution for utilizing above defense models in PyTorch, we would be delighted to conduct further validation of our proposed method. # Q6: Eq. (12) In gradient-based attacks, cross-entropy $J(x, y) = -\mathbb{1}_y \cdot \log \text{softmax}(f(x))$ is used to update the input image $x$. We shift it to $J(f_k, y) = -\mathbb{1}_y \cdot \log \text{softmax}(f_k^{post}(f_k))$ for feature updates, where $f_k^{post}$ is the post-$k$-th-layer model part. We’ll add this explanation to the revision. --- We sincerely thank you for enhancing our manuscript’s quality.	null	null	null	null	null	null	null	null
In-Context Deep Learning via Transformer Models	Accept (poster)	Summary: This paper studies the representation power of the transformer model in performing in-context learning (ICL). In particular, this paper focuses on the implementation of in-context gradient descent with respect a general deep neural network. The proposed construction is flexible that it can either use a ReLU attention or the more common softmax attention, and it is efficient that it uses $O(N)$ for each gradient update step of a $N$-layer network. In my opinion, the contributions of this paper is significant because it works for an arbitrary depth neural network and can be implemented using a softmax attention. The later point is especially valuable because much of the literature on ICL cannot handle the softmax activation. Claims And Evidence: Although this work is a substantial addition to the literature, it is plagued by very poor readability. I believe that some major restructuring would be necessary before publication. 1. Several parts of the Appendix absolutely should be in the main body. The paper in its current form does not have a self-contained main body. The definition of transformer and attention have to be part of the intro. The results on softmax attention should also be discussed in the main text because this is in my opinion the most interesting result of the paper. And some of the experiments need to be in the main body because they are mentioned in the abstract. My understanding is that the readers are expected to understand the key arguments of the paper without checking the appendix, and this paper currently falls short. 2. The paper is overly verbose and many of the details are disruptive to the flow without contributing much to the exposition. For example, "Problem 1" and "Problem 2" are basically the same thing. Definition 1 is just an over-complicated description of a MLP. And the "proof sketch" in Section 3.3 don't need this level of precision for a general audience -- they are simply too dense to parse. I think the details of Section 3.3 (especially those constant) can be striped down and moved to the appendix. 3. I think an illustration would be very helpful. For example, one can make a diagram marking all of the partial derivatives in back-propagation of the neural network and then highlight which layer of the transformer model implements each of these partial derivatives. Given the amount of "fat" in this paper, I think my proposed changes can fit into the page limit without too much efforts. And some more technical concerns: 1. While my first impression is that the proposed construction is for a standard transformer architecture, this is actually not the case. The authors introduced a piecewise multiplication layer," which is fine because it can be implemented efficiently in code. Also, the attention and MLP layers are not stacked in alternating orders. The authors should highlight these differences rather burying them under a wall of texts. 2. In Lemmas 2-4, the constants for ReLU approximations are not explicitly instantiated. I think it would be very helpful if the author could gives the values of these parameters for a simple example such as ReLU network with quadratic loss. Lastly, I really like that Appendix B.3 clearly discussed the limitations of this paper. I appreciate the authors' honesty. In light of these observations, I do not* recommend acceptance of this paper as-is. However, I do think the overall ideas in this paper can be valuable to the community and I hope the authors can take account of my feedback to improve this paper. In particular, I want to see concrete plans from the authors on how to address my concerns so the revised paper is more accessible, but I fully understand that I am asking for a lot of changes and it is okay if the author do not have enough time during the rebuttal period to finish the revision. I am happy to raise my score if my concerns are adequately addressed. Methods And Evaluation Criteria: n/a Theoretical Claims: The theoretical derivations of the paper seem to be precise and the authors devoted significant efforts into tracking the various algebraic blobs. So I have confidence that the results do not have any fatal flaws. I have one question: in the second point Section B.2 seems to imply that the intermediate computations on the partial derivatives are passed down through the forward pass of the transformer layers, but Section 2.i implies that the tokens' embedding dimension is only of order $\Theta(d)$. Can you clarify the differences and if possible, clearly state those values in the revision? Furthermore, it would be useful to discuss what values were written into the rows containing $q_i$'s, where are initialized to be 0. Experimental Designs Or Analyses: The experiments are clear and validates the main theoretical claims of this paper. I have no complaints about them. Supplementary Material: I read Appendices A-C, a bit of F and took a quick look at G and H. Relation To Broader Scientific Literature: see above Essential References Not Discussed: The citations in this paper is sufficiently comprehensive. Other Strengths And Weaknesses: see above Other Comments Or Suggestions: see above Questions For Authors: see above Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Thanks for your detailed review. We have revised our draft (changes marked in BLUE) in this [anonymous Dropbox folder](https://www.dropbox.com/scl/fo/cv5unyj4vew76op0xjftj/ALWvpjkaQ-_83Je7h0APsgs?rlkey=z80f15tgc59a3zl2m7owaklbe&st=05cr7uzt&dl=0). > C1: Reconstruction of the Manuscript. Response Thank you for the suggestions. We agree with this. In response, we have made the following modifications in the revised version: * We have moved the definitions of transformers and attention into the introduction while keeping the full standard definition in Appendix D due to space constraints. * The results on softmax attention and the experimental results have been incorporated into the main body—softmax results in Section 3.4 and experimental results in Section 4. * To improve clarity, we simplify Problem 2 and clearly state that it describes an MLP with $N$ layers. * The proof sketches in Section 3.3 have been moved to Appendix D, just before the detailed proof of the lemmas. * The complex constants in Lemma 6 have been shifted to Appendix D to improve readability. * While we acknowledge that Definition 1 may appear verbose, it establishes the notation used throughout the paper, particularly in the proofs, ensuring precision and consistency. Therefore, we have retained it as is. Additionally, we appreciate the suggestion to include a visualization of the backpropagation process. We have included it in Appendix A.2 of the revised version. We also redisplay it [anonymous figure](https://imgur.com/a/jfsYTQI). > C2: Difference with Standard Transformer Response Thank you for your suggestions. We have added this to the last point of limitations (`line 749-754`) and restate it here: There are two minor differences between the transformer used in the theoretical analysis and a standard transformer: (i) The transformer used in the theoretical analysis incorporates an element-wise multiplication layer, a specialized variant of self-attention that retains only the diagonal score and allows efficient implementation. (ii) It does not alternate self-attention and MLP layers. We emphasize that this also qualifies as a standard transformer because we view either an attention or an MLP layer as equivalent to an attention plus MLP layer due to the residual connections. > C3 Example of Explicit Construction of ReLU Response Thank you for your insightful comments. Here, we provide clarifications on why the constants can be explicitly instantiated and illustrate this using a simple example. The key reason is that the function approximated by the sum of ReLUs is relatively simple in our context, such as the Sigmoid activation function. For such simple functions, it is straightforward to derive an explicit construction. Here, we take the Sigmoid activation function as an example and propose one explicit construction method. Let $r(z)$ denote the Sigmoid function. 1. Segment the input domain. For example, divide the domain $[-10, 10]$ smaller intervals such as $[-10, -9], [-9, -8], \dots, [9, 10]$. 2. Approximate each segment locally using a linear function via linear interpolation. For instance, in the domain $[9,10]$, approximate $r(z)$ using a linear function $a_1 z + c_1$, where $a_1$ and $c_1$ are calculated as follows: (i) $a_1 = (r(10)-r(9)) / (10-9)$. (ii) $c_1 = r(9) - a_1 * 9$. 3. Approximate linear function $a_1 z + c_1 (z \in [9,10])$ using a sum of ReLU terms. This step involves two substeps, which are straightforward to implement: (i) Approximate the indicator function for $z \in [9,10]$ using a sum of ReLU terms. (ii) Approximate the constant $c_1$ using the sum of ReLU. This is because bias terms are not included in the sum of ReLU terms in Definition 4. The bias term $c_1$ must be approximated using an additional sum of ReLU terms. 4. Combine all the sum of ReLU approximators across all segments. Finally, integrate the approximations for all segments to construct the complete approximation. 5. Estimation of the parameters in Definition 4. $\epsilon_{approx} = 0.625$, $R=10$, $H=80$, and $C=25$. Furthermore, to achieve higher precision in the approximation, it is sufficient to use finer segmentations. > Q1: Difference of Dimensions Response Thank you for your question. We apologize for any confusion caused. Here are some clarifications: * In Section 2.(i), the value of $D$ is derived from prior research on in-context learning (ICL) for functions, indicated as $D=\Theta(d)$. This basis does not pertain to our focus on models, such as an $N$-layer neural network. We have removed these parts in the revised version to make things easier to read. * Regarding the zero values in the rows of q_i, these primarily consist of intermediate terms such as $\bar{p}_i(j), \bar{r}^{‘}_i(j), \bar{s}_t(j)$, which are essential for calculating partial derivatives and contain gradient information. These rows are initially set to zero. --- Rebuttal Comment 1.1: Comment: I thank the author for their responses. While the revision are a little minimalist in my opinion, it addressed most of my key concerns. I will upgrade my score from 2 to 3 and encourage the authors to further improve their manuscript for the camera-ready version. Also, I like your example of approximating sigmoid with ReLU, can you add this to the appendix? --- Reply to Comment 1.1.1: Comment: Thank you for your thorough review and for the improvement in the score. We are pleased to have addressed many of your concerns and truly value your feedback. We are committed to further refining our manuscript for the camera-ready version. We have updated our draft to include the example of approximating the sigmoid function with ReLU in the "Further Discussion" section (Appendix B.3). You can find the revised version, with changes highlighted in blue in [anonymous Dropbox folder](https://www.dropbox.com/scl/fo/ukjkfsqtpqmrjeq2rrpmn/AAskqgf9U5Q_pMEE2KoDVIE?rlkey=e9ywy926mlhizbfhi0t9zyta9&st=s8wrdbek&dl=0).	Summary: This paper shows that one can construct weights of a ReLU-activation transformer that can simulate L steps of gradient descent on an N-layer ReLU network using in-context examples. ## update after rebuttal While I have concerns with clarity and usefulness of the construction, I appreciate the author's honesty and thus will stick to my raised score of 2. Claims And Evidence: The theory appears sound but the empirics are lacking. > Experiments. We support our theory with numerical validations in Appendix G As far as I can tell, the experiments in Appendix G have nothing to do with constructing a transformer? Instead, they follow the more classical setup (of e.g., Garg et al) in seeing if a transformer can infer the function f in context. No analogy is drawn to whether or not the solution found by the transformer is similar to the construction shown in the main text, beyond the fact that on certain evaluation data the performance matches doing GD on a ReLU network (but this could also just be performance being "good" rather than the "same"). Methods And Evaluation Criteria: See above. Theoretical Claims: See above. Experimental Designs Or Analyses: See above. Supplementary Material: Appendix G Relation To Broader Scientific Literature: The paper appears to cite relevant literature. I'm not sure how relevant the finding is/if such a construction is actually of interest to the broader community. Essential References Not Discussed: Not to my knowledge. Other Strengths And Weaknesses: I think the paper suffers a lot from reduced clarity. It seems that most of the content of the paper is in the appendix, including empirical comparisons as well as discussion, which to me makes for a less clear read. I would suggest the authors re-write the main body of text to include more intuitions and takeaways (e.g. when some assumptions may hold in practice rather than just in theory). Other Comments Or Suggestions: N/A Questions For Authors: Do trained transformers actually achieve the construction? Code Of Conduct: Affirmed. Overall Recommendation: 2	Rebuttal 1: Rebuttal: Thanks for your detailed review. We have revised our draft and addressed all concerns. The revised version (changes marked in BLUE) is available in this [anonymous Dropbox folder](https://www.dropbox.com/scl/fo/cv5unyj4vew76op0xjftj/ALWvpjkaQ-_83Je7h0APsgs?rlkey=z80f15tgc59a3zl2m7owaklbe&st=05cr7uzt&dl=0). > Q1: Do trained transformers actually achieve the construction? Response: Thank you for the question. The trained transformers do not always achieve the construction. We apologize for any confusion caused, and acknowledge the limitation you mentioned. However, this limitation does not affect the primary contributions of our work. Here are some clarifications. The main contribution of this paper is to provide an explicit construction demonstrating the existence of a transformer capable of simulating gradient descent (GD) for $N$-layer neural networks via in-context learning (ICL). The experimental design empirically validates that the trained transformer can indeed simulate GD steps for $N$-layer neural networks, supporting our theoretical results on the existence of such a transformer. Although there is a discrepancy between the theoretically constructed transformer and the empirically used one, this difference does not weaken the central point of our work, which is establishing the theoretical existence of such a transformer. We acknowledge the limitation you mentioned and have incorporated it into the revised version: `line 744-748`. > C1: I think the paper suffers a lot from reduced clarity. It seems that most of the content of the paper is in the appendix, including empirical comparisons as well as discussion, which to me makes for a less clear read. I would suggest the authors rewrite the main body of text to include more intuitions and takeaways (e.g. when some assumptions may hold in practice rather than just in theory). Response: Thank you for your thoughtful suggestions. We agree that the main text can be better organized to improve readability and self-containment. In response, we have made the following modifications in the revised version: * The results on softmax attention and the experimental results have been incorporated into the main body—softmax results in Section 3.4 and experimental results in Section 4. * The proof sketches have been moved to Appendix D, just before the detailed proof of the lemmas. * We include a remark concerning the practicality of our assumptions (Remark 4: `line 1577-1579`). Our assumptions remain modest. For example, we require that the loss function $l$, the activation function $r$, and its derivative be $C^4$-smooth. This condition is met by numerous network architectures, including those using the sigmoid activation function $r$ and the squared loss function $l$. --- We hope our responses address your concerns and look forward to further feedback. --- Rebuttal Comment 1.1: Comment: I appreciate the authors' honesty. I've increased my score to a 2, assuming that the authors will factor in the clarity suggestions and will be correspondingly upfront in their paper: Specifically, > The trained transformers do not always achieve the construction. this comment should appear in the intro and main text of the paper, not just the appendix. When providing theoretical constructions as the paper focuses on, it's important to be clear about how they differ from practice so as to not add noise -- for example, the results show that while a construction exists, it isn't typically found through training (i.e., the outer loop if ICL is viewed as the inner loop). --- Reply to Comment 1.1.1: Comment: Thank you for your careful consideration of the responses and for increasing the score. We really appreciate your thorough evaluation. We have revised our draft by adding comments to ``line 056-058 column 2`` and ``line 408-410 column 2``. The revised version (changes marked in BLUE) is available in this [anonymous Dropbox folder](https://www.dropbox.com/scl/fo/cv5unyj4vew76op0xjftj/ALWvpjkaQ-_83Je7h0APsgs?rlkey=z80f15tgc59a3zl2m7owaklbe&st=05cr7uzt&dl=0). Thanks very much!	Summary: The paper introduces an approach that harnesses the transformer's ability to emulate the in-context learning for training process of deep models. Its key contribution is the demonstration of a practical instance where a transformer is used to simulate the training process of a deep neural network. Furthermore, the paper appears to extend the work presented in "Transformers as Statisticians: Provable In-Context Learning with In-Context Algorithm Selection," which provides a solid theoretical analysis. Claims And Evidence: The paper poses the question, "Is it possible to train one deep model using the in-context learning (ICL) capability of another foundation model?" and answers it affirmatively. The paper offers theoretical guarantees for achieving approximation within any desired error margin and for the convergence of ICL-based gradient descent. The analysis centers on a practical setting involving Softmax-based transformers. The method is evaluated on synthetic datasets for 3-layer, 4-layer, and 6-layer neural networks, with results showing that ICL performance is on par with that of direct training. Methods And Evaluation Criteria: The method was primarily motivated by theoretical considerations. The authors systematically formulate in-context learning (ICL), carefully defining the neural network's mathematical model. Their approach relies on a recursive application of the chain rule, approximating derivatives sequentially. The authors suggest optimizing a transformer to mimic in-context gradient descent across different configurations. Theoretical Claims: The paper's contribution mainly lies in its mathematical formulation and theoretical analysis. The ultimate goal is to demonstrate that bounds can be established for the approximation. Experimental Designs Or Analyses: The experiments primarily aim to validate the correctness of the theorems. Although they are not conducted on large neural networks, they are sufficient in my view. Supplementary Material: I reviewed the experimental sections but did not go through the theoretical proofs in all the details. Relation To Broader Scientific Literature: N/A Essential References Not Discussed: From my perspective the paper provides adequate citations. Other Strengths And Weaknesses: Overall, the paper is clearly written and easy to follow. The proposed method has been validated through both theoretical analysis and experimental results. Other Comments Or Suggestions: Same as previous comments. Questions For Authors: N/A Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: Thank you for your review! We greatly appreciate your attention to detail and recognition of our theoretical and experimental contributions! Your constructive comments and encouraging words are also highly appreciated!	Summary: This paper studies the expressive power of transformer models to simulate gradient descent on other architectures like N layer feedforward networks using in-context learning. The authors corroborate their study with experiments on synthetic datasets that show that the in-context learning performance of Transformers matches direct training of deep networks. Claims And Evidence: The authors show clean theoretical claims to show expressivity of transformer models. The authors extensively discuss the proof strategies for each theoretical claim. Furthermore, they conduct experiments in the appendix to support their theoretical claims. Methods And Evaluation Criteria: The experiments in appendix have been conducted on toy datasets to corroborate their theoretical claims. Theoretical Claims: I glanced through the proofs of each theoretical claim. Even though I didn't go through specific details, the theoretical proofs and statements are reasonable. Furthermore, the authors clearly corroborate their theoretical observations with clean empirical experiments. Experimental Designs Or Analyses: The experiments in appendix have been conducted on toy datasets to corroborate their theoretical claims. Supplementary Material: I checked the empirical results in the supplementary material and simply glanced over the proofs of the theoretical statements. Relation To Broader Scientific Literature: The paper is relevant to the current interests of the scientific community. Exploring the strengths of in-context learning of transformer models has been a topic of interest for the last few years and this paper takes an important step towards this direction. Essential References Not Discussed: The authors have extensively discussed the important references. Other Strengths And Weaknesses: The main strength of this paper lies in its motivation to study the strengths of in-context learning abilities of real world transformer models. The paper first discusses the pros and cons of existing studies on similar topics and attempts to specialize the framework to understand expressive power for simulating multi-step gradient descent of N-layer feedforward networks. Other Comments Or Suggestions: I don't see any typos. Questions For Authors: Please find my questions below. - In corollary 1.1, the error bound is exponential in the number of steps L. How would the bound vary if the transformer's size is allowed to increase beyond (2N+4)L? Can it be made polynomial, by making the transformer size grow exponential? - Theorem 1 requires Element-wise Multiplication Layers (EWMLs) to approximate Hadamard products. Can some form of approximate self-attention or MLP layers be used in their place? How would the size of the constructed model vary then? Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: > Q1: How would the bound vary if the transformer's size is allowed to increase beyond (2N+4)L? Can it be made polynomial, by making the transformer size grow exponential? Response: Thank you for your question. The bound does not change if the transformer's size exceeds $(2N+4)L$, and the error cannot be reduced to a polynomial level. Here are some clarifications: * Each $(2N+4)$-layer transformer simulates one gradient descent (GD) step, and we stack such transformers $L$ times. * In non-convex optimization, each step’s trajectory depends on the previous steps. This dependency causes the exponential accumulation of the error. > Q2: Can some form of approximate self-attention or MLP layers be used in their place? How would the size of the constructed model vary then? Response: Thank you for your insightful question. The answer is No. Here are some clarifications. * Explicit construction of transformer: We aim to provide an explicit transformer construction that simulates $L$ gradient descent steps. Although self-attention or MLP layers can approximate Hadamard products through their universal approximation capabilities, such approximations would result in non-explicit constructions. * Specialized variant of self-attention: EWML can be viewed as a specialized variant of self-attention that retains only the diagonal scores. --- We hope our responses address your concerns and look forward to further feedback.	null	null	null	null	null	null
Thoughts Are All Over the Place: On the Underthinking of o1-Like LLMs	Reject	Summary: The paper propose an interesting phenomenon termed "underthinking" for LLM reasoning -- models frequently switch between different reasoning strategies without sufficiently exploring promising paths, leading to inadequate reasoning depth. Authors introduce a novel metric to quantify underthinking by measuring token efficiency in incorrect answers and propose a decoding strategy with a thought switching penalty to encourage deeper exploration of each reasoning path. Experimental results show that this strategy improves accuracy across challenging datasets without requiring model fine-tuning. Claims And Evidence: Yes, most claims supported by experiments. Methods And Evaluation Criteria: Not quite reliable. A key step in evaluating underthinking is identifying whether early thoughts lead to the correct answer. However, the method used here leverages LLMs to assess whether each thought leads to a correct answer using a prompt. This approach is highly dependent on the capabilities of the chosen model and is significantly influenced by the prompt itself, potentially introducing bias. To ensure the objectivity of evaluation and analysis, the reliability of using LLMs to assess whether each thought leads to a correct answer needs further validation. Theoretical Claims: No theoretical part in this paper. Experimental Designs Or Analyses: Yes. I believe the reliability of the authors' utilization of the Llama-3.3-70B model to automatically segment a response into reasoning thoughts needs further justification. Since many reasoning thoughts originate from more powerful reasoning models and tend to be very lengthy, the validity and quality of Llama's segmentation of reasoning thoughts should be discussed. Supplementary Material: No, there's no supplementary material. Relation To Broader Scientific Literature: The key contributions of the paper are closely related to the broader scientific literature on large language models and their reasoning capabilities. It addresses the underexplored issue of underthinking. Essential References Not Discussed: There are no essential references missing from the paper. Other Strengths And Weaknesses: Strength Good analysis on the phenomenon underthinking of LLMs, especially reasoning models. Weaknesses: The proposed Thought Switching Penalty method is heuristic and somewhat arbitrary. To encourage the model to explore its current thoughts more thoroughly before switching, the authors introduce a penalty on tokens associated with thought transitions, such as "alternatively." However, the impact of specific words varies across different models, which may make the effectiveness of this approach difficult to ensure. Moreover, there is insufficient exploration and analysis of how different words influence the results. Other Comments Or Suggestions: None. Questions For Authors: What's the set of tokens for TIP? What's the influence of TIP on inference time cost, i.e.,response length? Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: > Q1: Reliability of using LLMs to assess the correctness of intermediate reasoning steps. A1: We fully understand your concerns about the reliability of using LLMs to assess the correctness of intermediate reasoning steps, particularly the dependency on model capabilities and prompt sensitivity. In fact, we have explicitly addressed this issue in lines 246-258 of our submitted manuscript. As reported: "Our assessment approach achieves accuracies of 82.9% for correct examples and 81.8% for incorrect examples, demonstrating its effectiveness." These results offer quantitative validation of our evaluation method, although we agree further validation and model-independent analysis are valuable future work directions. --- > Q2: Reliability of using Llama-3.3-70B to automatically segment a response into reasoning thoughts. A2: Thank you very much for your insightful suggestion. We selected Llama-3.3-70B because, at the time of our ICML submission deadline, it was one of the strongest and most widely adopted open-source models available. To further validate our segmentation approach, we followed your recommendation and performed a manual evaluation on 100 randomly selected thought segments generated by DeepSeek-R1 on the AIME 2024 dataset. This manual check yielded an accuracy of 86%, further supporting the validity and effectiveness of our automated thought segmentation approach. We will explicitly report this additional validation result in the revised manuscript. Once again, we appreciate your valuable feedback. --- > Q3: Effectiveness of the proposed TIP method. A3: We have carefully addressed your points by conducting additional experiments to demonstrate the effectivenss and universality of the proposed TIP method. Below, we summarize our improvements with respect to your main comments: To further clarify the effectiveness of TIP, we conducted analyses on key reasoning metrics, specifically examining: - the average number of thought-switching tokens; - the length of intervals between thought switches. To examine TIP's generality explicitly, we reused hyperparameters tuned initially on the QwQ-32B-Preview model directly for the subsequent models — R1-Distill-Qwen-32B and DeepSeek-R1— without additional tuning. Our analysis across multiple benchmarks consistently showed that TIP significantly reduces the overall number of thought-switching tokens while increasing the average intervals between them. This suggests the models become more committed to exploring individual reasoning threads thoroughly before pivoting to alternatives, aligning with our design intent of addressing underthinking explicitly. In addition, TIP consistently and effectively enhanced reasoning performance across different models (R1-Distill-Qwen-32B, DeepSeek-R1) even without model-specific hyperparameter tuning. These results demonstrate both the universality and the empirical robustness of TIP. \| Model\|Pass@1\|Pass@4\|Pass@8\|Pass@16\|Thought Number\|Thought Interval\|Weighted UT Score (↓) \| \|-\|-\|-\|-\|-\|-\|-\|-\| \|MATH500-Hard(Lv5)\|\|\|\|\|\|\|\| \|QwQ-32B-Preview\|83.1\|92.4\|94.4\|95.8\|12.6\|445.6\|11.7±20.5\| \|+TIP\|83.7\|93.2\|95.3\|96.4\|5.7\|517.6\|11.0±19.5\| \|GPQA Diamond\|\|\|\|\|\|\|\| \|QwQ-32B-Preview\|57.6\|78.5\|85.3\|90.3\|21.1\|356.8\|25.1±23.9\| \|+TIP\|59.1\|78.9\|85.8\|91.2\|7.3\|432.5\|23.2±23.2\| \|AIME2024\|\|\|\|\|\|\|\| \|QwQ-32B-Preview\|38.3\|53.7\|58.5\|62.7\|16.1\|459.7\|40.6±28.4\| \|+TIP\|44.1\|61.6\|68.3\|74.0\|13.9\|515.7\|35.8±27.8\| \|R1-Distill-Qwen-32B\|61.4\|75.9\|79.1\|81.7\|8.2\|819.5\|19.6±20.6\| \|+TIP\|64.1\|79.0\|81.7\|83.0\|4.5\|1018.0\|17.7±20.6\| \|DeepSeek-R1\|73.8\|86.2\|88.8\|89.8\|13.8\|580.1\|14.6±19.1\| \|+TIP\|74.8\|86.4\|88.8\|89.8\|5.7\|941.6\|13.0±18.0\| To thoroughly assess the robustness and generality of our TIP approach, we combined it with best-of-N sampling methods, and the results confirm that our method remains consistently effective under these conditions. \|Models\|Acc.(↑)\|UT(↓)\| \|---\|:---:\|:---:\| \|QwQ+Self-Consistency\|43.7\|35.4\| \|+TIP\|51.4\|26.6\| \|R1-Distill-Qwen+Self-Consistency\|67.0\|13.4\| \|+TIP\|69.9\|12.5\| \|R1+Self-Consistency\|79.3\|10.1\| \|+TIP\|81.3\|7.5\| --- Rebuttal Comment 1.1: Comment: Thanks for addressing my concerns, I have updated my score.	Summary: This paper introduces a novel investigation into the phenomenon of 'underthinking' in large language models (LLMs), specifically those designed for complex reasoning tasks, such as the 'o1-like' models. The authors define underthinking as the premature abandonment of promising reasoning paths, leading to suboptimal solutions. This is a significant contribution as it highlights a limitation in current models that has not been extensively studied. The core of their methodology involves identifying and segmenting 'thoughts' within the model's response, which they define as distinct reasoning steps, and then evaluating the correctness of each thought. To quantify underthinking, they propose a novel metric that measures token efficiency in incorrect responses, essentially assessing how many tokens are generated before a correct line of reasoning is abandoned. This metric provides a quantitative way to assess the efficiency of reasoning processes in LLMs, complementing traditional accuracy metrics. Furthermore, the authors introduce a decoding strategy called Thought Switching Penalty (TIP) to mitigate underthinking. TIP penalizes the model for switching between thoughts, encouraging it to explore each reasoning path more thoroughly before considering alternatives. --- ## After Rebuttal Score 2.0 -> 2.5 Claims And Evidence: The paper must provide more direct evidence of changes in the quality of reasoning, beyond just a reduction in thought switching. While the paper demonstrates improved accuracy, it's crucial to analyze whether this improvement stems from a genuine increase in the depth and detail of individual thoughts, as theoretically proposed, or merely from a decrease in the frequency of less productive thought shifts. Further analysis is needed to directly link the observed performance gains to the intended theoretical mechanism of promoting deeper, more sustained reasoning. Methods And Evaluation Criteria: To enhance the practical applicability and ease of use of the TSP method, the current reliance on manual hyperparameter tuning needs to be addressed. While the paper provides a grid search example, a more systematic and robust approach to hyperparameter selection is required. Theoretical Claims: None. Experimental Designs Or Analyses: In my opinion, the supporting evidence from the experiments in this paper remains insufficient. The paper primarily focuses on the performance of the QwQ-32B-Preview model and three math and science tasks. While the paper demonstrates improved accuracy and reduced thought switching, it is imperative to ascertain whether the remaining thoughts are genuinely deeper and more detailed, or if the improvement is solely a result of reduced switching frequency. Further analysis, including metrics on thought length, complexity, and reasoning steps per thought, is necessary to confidently claim that TSP promotes deeper thinking and not just less frequent thought switching. Supplementary Material: None. Relation To Broader Scientific Literature: Good! Essential References Not Discussed: None. Other Strengths And Weaknesses: This paper offers several noteworthy contributions to the field of large language models, particularly concerning complex reasoning. Firstly, the introduction of "underthinking" is a concept that I found to be quite insightful and genuinely novel. By pinpointing this tendency of LLMs to prematurely abandon potentially fruitful reasoning paths, the authors, I think, effectively highlight a key limitation in the current generation of these models. This isn't just about efficiency; it clearly impacts, and perhaps significantly, the accuracy of these models on really challenging problem-solving tasks. The formal definition and characterization of underthinking, especially with the empirical backing they provide, strikes me as a meaningful step towards a better understanding of how these models actually work internally. The development of a quantitative metric for assessing underthinking is in my opinion, a valuable tool for researchers in this area. This proposed metric, measuring token efficiency in incorrect responses, provides a concrete way to delve deeper into a model's reasoning process beyond just simple accuracy scores. I think it allows for a more nuanced evaluation of model performance. The authors effectively demonstrate the utility of this metric by showing its correlation with the effectiveness of their proposed TSP method, which is a convincing demonstration. Other Comments Or Suggestions: Honestly, for this work to truly reach its potential and make the broad impact I believe it can, you absolutely must consider expanding the experimental scope beyond just math and science problems. While the current findings are valuable, limiting ourselves here means we are potentially missing out on understanding if "underthinking" and TSP are relevant – and helpful – in other critical areas. Think about logical reasoning, everyday common sense, even creative tasks! Exploring these diverse areas isn't just about ticking boxes; it's about showing the real power and universal value of your insights to the whole research community. From a truly responsible research perspective, we have to be cautious and explore the boundaries of TSP. While it's brilliant for addressing underthinking, I sincerely worry about scenarios where frequent thought switching might actually be a good thing – even necessary! We need to be able to honestly say when TSP is the right tool and when it might actually get in the way. Designing experiments to test this isn't just about being critical; it’s about being thorough and providing really useful guidance to anyone who wants to use TSP. Questions For Authors: How does the proposed underthinking metric perform on tasks that require creative or divergent thinking, where the notion of a single "correct" answer may not be well-defined? Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: > Q1: More experimental results & analyses. A1: Thank you for your insightful feedback and constructive suggestions. We have carefully addressed your points in the revised manuscript and conducted additional experiments to substantiate our claims. Below, we summarize our improvements with respect to your main comments: To further clarify the effectiveness of TIP, we conducted analyses on key reasoning metrics, specifically examining: - the average number of thought-switching tokens; - the length of intervals between thought switches. To examine TIP's generality explicitly, we reused hyperparameters tuned initially on the QwQ-32B-Preview model directly for the subsequent models — R1-Distill-Qwen-32B and DeepSeek-R1— without additional tuning. Our analysis across multiple benchmarks consistently showed that TIP significantly reduces the overall number of thought-switching tokens while increasing the average intervals between them. This suggests the models become more committed to exploring individual reasoning threads thoroughly before pivoting to alternatives, aligning with our design intent of addressing underthinking explicitly. In addition, TIP consistently and effectively enhanced reasoning performance across different models (R1-Distill-Qwen-32B, DeepSeek-R1) even without model-specific hyperparameter tuning. These results demonstrate both the universality and the empirical robustness of TIP. \| Model\|Pass@1\|Pass@4\|Pass@8\|Pass@16\|Thought Number\|Thought Interval\|Weighted UT Score (↓) \| \|-\|-\|-\|-\|-\|-\|-\|-\| \|MATH500-Hard(Lv5)\|\|\|\|\|\|\|\| \|QwQ-32B-Preview\|83.1\|92.4\|94.4\|95.8\|12.6\|445.6\|11.7±20.5\| \|+TIP\|83.7\|93.2\|95.3\|96.4\|5.7\|517.6\|11.0±19.5\| \|GPQA Diamond\|\|\|\|\|\|\|\| \|QwQ-32B-Preview\|57.6\|78.5\|85.3\|90.3\|21.1\|356.8\|25.1±23.9\| \|+TIP\|59.1\|78.9\|85.8\|91.2\|7.3\|432.5\|23.2±23.2\| \|AIME2024\|\|\|\|\|\|\|\| \|QwQ-32B-Preview\|38.3\|53.7\|58.5\|62.7\|16.1\|459.7\|40.6±28.4\| \|+TIP\|44.1\|61.6\|68.3\|74.0\|13.9\|515.7\|35.8±27.8\| \|R1-Distill-Qwen-32B\|61.4\|75.9\|79.1\|81.7\|8.2\|819.5\|19.6±20.6\| \|+TIP\|64.1\|79.0\|81.7\|83.0\|4.5\|1018.0\|17.7±20.6\| \|DeepSeek-R1\|73.8\|86.2\|88.8\|89.8\|13.8\|580.1\|14.6±19.1\| \|+TIP\|74.8\|86.4\|88.8\|89.8\|5.7\|941.6\|13.0±18.0\| To thoroughly assess the robustness and generality of our TIP approach, we combined it with best-of-N sampling methods, and the results confirm that our method remains consistently effective under these conditions. \|Models\|Acc.(↑)\|UT(↓)\| \|---\|:---:\|:---:\| \|QwQ+Self-Consistency\|43.7\|35.4\| \|+TIP\|51.4\|26.6\| \|R1-Distill-Qwen+Self-Consistency\|67.0\|13.4\| \|+TIP\|69.9\|12.5\| \|R1+Self-Consistency\|79.3\|10.1\| \|+TIP\|81.3\|7.5\| --- > Q2: How does the proposed underthinking metric perform on tasks that require creative or divergent thinking, where the notion of a single "correct" answer may not be well-defined? A2: We fully acknowledge the importance and potential value of broadening our evaluations beyond purely math and science tasks. Your thoughtful comment highlights critical considerations regarding the broader relevance of the underthinking concept and the TIP method. In this work, closely following the technical approach in the DeepSeek-R1 study [1], we concentrated primarily on reasoning-intensive quantitative/formal knowledge tasks, as these tasks are directly aligned with clearly defined correctness criteria and enable systematic measurement and analysis of underthinking behaviors in a reproducible manner. We recognize that exploring more diverse reasoning tasks, such as logical reasoning and common-sense scenarios, could amplify our method's scope and impact. While tasks requiring creative or open-ended thinking represent valuable but challenging new directions (due to ambiguous evaluation criteria and limitations in large-scale reinforcement learning methods), we aim to pursue these avenues in follow-up studies. Carefully investigating these scenarios will indeed help establish clearer boundaries regarding when TIP is beneficial, when frequent thought switching might be advantageous, and under which conditions it might even be necessary. We will explicitly discuss this direction as an important avenue for future work in the revised manuscript. For now, the current scope is clearly declared and motivated as an initial, controlled investigation into the robustness and effectiveness of addressing underthinking in reproducibly measurable tasks. [1] DeepSeek. "Deepseek-r1: Incentivizing reasoning capability in llms via reinforcement learning." arXiv preprint arXiv:2501.12948 (2025). --- Rebuttal Comment 1.1: Comment: Thank you for your reply, which has solved my problem to some extent! If other reviewers are willing to accept this paper, then I will not object. In my mind, the rating of this paper is at the borderline, which is 2.5.	Summary: This paper investigates strategies to leverage decoding-time interventions for improving reasoning depth and accuracy in o1-like LLMs. The authors propose a thought switching penalty TIP decoding strategy that discourages frequent and premature switching between reasoning paths to mitigate underthinking; then, they evaluate TIP across multiple complex reasoning benchmarks using two o1-like LLMs. They find significant gains in task accuracy and reasoning depth compared to baseline greedy decoding and standard sampling methods. Claims And Evidence: The authors' claim that TIP improves reasoning depth and accuracy is generally supported by experimental results that show consistent performance gains over baseline decoding. However, the paper does not provide a deeper analysis of why TIP works across different types of reasoning tasks and whether it may negatively affect tasks requiring flexible thought switching. Methods And Evaluation Criteria: The workflow is well-structured, as it combines a novel underthinking metric with decoding adjustments to make the intervention measurable and actionable. This approach quantifies the problem of underthinking in a transparent way and further provides a practical solution that operates entirely at inference time, making it broadly applicable to existing o1-like LLMs. Theoretical Claims: The paper does not present much formal theoretical proofs. It mainly relies on an empirical definition of underthinking and the proposed TIP mechanism. I find the explanation of underthinking and thought switching intuitive and reasonable, but I believe a formal analysis of how TIP quantitatively relates to reasoning depth would strengthen the theoretical grounding of the method. Experimental Designs Or Analyses: The experiments are extensive, with detailed analysis of the results. These experiments validate the effectiveness of TIP in improving reasoning quality and task accuracy and demonstrate the robustness and scalability of the method across different sizes and complexities of benchmarks. Supplementary Material: / Relation To Broader Scientific Literature: The idea of improving LLM reasoning depth through decoding-time interventions to address underthinking is novel and timely. Most existing work focuses on model fine-tuning or prompting strategies to improve reasoning, but these approaches cannot control reasoning behavior at inference time, limiting their flexibility and applicability to fixed models. This paper introduces a method that applies a thought switching penalty during decoding to encourage deeper exploration within each line of thought, as well as significantly improves reasoning accuracy and coherence without requiring model retraining. Essential References Not Discussed: I find the related work discussion comprehensive, and I do not see essential references missing that would significantly impact the contributions Other Strengths And Weaknesses: The paper proposes TIP as a decoding strategy to improve reasoning quality and shows its empirical effectiveness. However, the authors do not provide a theoretical discussion on how TIP relates to reasoning depth. My understanding is that TIP is designed based on the intuition that reducing thought switching encourages deeper reasoning. If the authors could offer a formal justification, quantitative analysis, or even case studies to support this design choice, it would significantly strengthen the credibility of the method. Other Comments Or Suggestions: I suggest the authors include a case study or a clearer explanation and analysis of Figure 2 to better illustrate how TIP affects reasoning depth and thought switching in practice. Questions For Authors: I wonder how TIP balances preventing shallow jumps with avoiding overly rigid reasoning. How is the generality of TIP across different tasks, especially those that require flexible or multi-path reasoning? Does it have potential downsides, such as limiting model adaptability? Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: > Q1: More insights about how TIP works and the generality of TIP. A1: Thank you for your insightful questions and constructive feedback. We fully agree that more in-depth insights into why TIP enhances models' reasoning depth and accuracy would significantly reinforce our method. To further clarify the effectiveness of TIP, we conducted analyses on key reasoning metrics, specifically examining: - the average number of thought-switching tokens; - the length of intervals between thought switches. To examine TIP's generality explicitly, we reused hyperparameters tuned initially on the QwQ-32B-Preview model directly for the subsequent models — R1-Distill-Qwen-32B and DeepSeek-R1— without additional tuning. Our analysis across multiple benchmarks consistently showed that TIP significantly reduces the overall number of thought-switching tokens while increasing the average intervals between them. This suggests the models become more committed to exploring individual reasoning threads thoroughly before pivoting to alternatives, aligning with our design intent of addressing underthinking explicitly. In addition, TIP consistently and effectively enhanced reasoning performance across different models (R1-Distill-Qwen-32B, DeepSeek-R1) even without model-specific hyperparameter tuning. These results demonstrate both the universality and the empirical robustness of TIP. \| Model\|Pass@1\|Pass@4\|Pass@8\|Pass@16\|Thought Number\|Thought Interval\|Weighted UT Score (↓) \| \|-\|-\|-\|-\|-\|-\|-\|-\| \|MATH500-Hard(Lv5)\|\|\|\|\|\|\|\| \|QwQ-32B-Preview\|83.1\|92.4\|94.4\|95.8\|12.6\|445.6\|11.7±20.5\| \|+TIP\|83.7\|93.2\|95.3\|96.4\|5.7\|517.6\|11.0±19.5\| \|GPQA Diamond\|\|\|\|\|\|\|\| \|QwQ-32B-Preview\|57.6\|78.5\|85.3\|90.3\|21.1\|356.8\|25.1±23.9\| \|+TIP\|59.1\|78.9\|85.8\|91.2\|7.3\|432.5\|23.2±23.2\| \|AIME2024\|\|\|\|\|\|\|\| \|QwQ-32B-Preview\|38.3\|53.7\|58.5\|62.7\|16.1\|459.7\|40.6±28.4\| \|+TIP\|44.1\|61.6\|68.3\|74.0\|13.9\|515.7\|35.8±27.8\| \|R1-Distill-Qwen-32B\|61.4\|75.9\|79.1\|81.7\|8.2\|819.5\|19.6±20.6\| \|+TIP\|64.1\|79.0\|81.7\|83.0\|4.5\|1018.0\|17.7±20.6\| \|DeepSeek-R1\|73.8\|86.2\|88.8\|89.8\|13.8\|580.1\|14.6±19.1\| \|+TIP\|74.8\|86.4\|88.8\|89.8\|5.7\|941.6\|13.0±18.0\| --- > Q2: I suggest the authors include a case study or a clearer explanation and analysis of Figure 2 to better illustrate how TIP affects reasoning depth and thought switching in practice. A2: Thank you for this valuable suggestion. Due to length constraints, we did not include the complete response within the paper nor clearly specified whether each thought was promising. In the revised manuscript, we will provide the full response in an appendix and enhance the clarity and interpretability of Figure 2 accordingly.	Summary: This paper introduces and investigates the phenomenon of "underthinking" in advanced "o1-like" large language models, characterized by their tendency to frequently switch between reasoning thoughts without sufficiently exploring promising paths, particularly on complex problems. The authors empirically demonstrate that this behavior correlates with incorrect responses, which often exhibit higher thought counts and token usage compared to correct ones. # update after rebuttal Since most of my concerns remain and significant revisions are still needed, I strongly suggest another round of revision. Thanks. Claims And Evidence: Fine Methods And Evaluation Criteria: Fine Theoretical Claims: Fine Experimental Designs Or Analyses: Fine Supplementary Material: Fine Relation To Broader Scientific Literature: Fine Essential References Not Discussed: Fine Other Strengths And Weaknesses: Hope the feedback is valuable for the authors and helps improve the quality in the revision or camera ready. I am happy to update my score after rebuttal if necessary. Thanks! Pros: 1. Clearly defines and names "underthinking" as a distinct reasoning inefficiency in advanced LLMs, contrasting it with potential overthinking. 2. Addresses a critical aspect of state-of-the-art reasoning models (o1-like capabilities) and their practical limitations. 3. Provides quantitative analysis (token/thought counts, correlations) across multiple challenging datasets (MATH, GPQA, AIME) and relevant models (Qwen, DeepSeek variants). 4. The Underthinking (UT) score offers a novel, quantitative way to measure a specific type of reasoning inefficiency in incorrect responses. Cons: 1. It is suggested that the authors provide the code for reproduction. 2. The term "o1-like" relies heavily on community understanding and specific named replicas. While practical, briefly defining the key characteristics being emulated (e.g., explicit iterative thought generation, test-time compute scaling structure) beyond just "deep reasoning" would strengthen the paper's foundation and clarify the scope. 3. It is not very clear how the authors set the hyperparameters such as temperatures. It suggested that the authors provide more details about all the experiment setting. 4. It is not very clear about the impact of hyperparameters such as temperatures on the "Underthinking" issues. It is suggested that the authors conduct a more detailed analysis on the sensitivity of the hyperparameters. 5. There is no formal definition of the "Underthinking" issue. It is suggested the authors provide a formal definition of the "Overthinking" issue. Otherwise, it is not very clear. The current description "where o1-like LLMs frequently switch between different reasoning thoughts without sufficiently exploring promising paths to reach a correct solution." is kind of vague. What do "different reasoning thoughts" and "promising paths" refer to? 6. It is not very clear how often the "Underthinking" issue happens. What is the percentage of the "Underthinking" issue in all the wrong responses? A more quantitive analysis is desired. 7. Figure 2 needs more explanations. Is there any thought is "promising"? It the final answer correct or not? 8. The insight is limited and the overall observations are superficial. Why Some LLMs have the "Underthinking" issues? Do all reasoning LLMs have the "Underthinking" issues? What are the fundamental cause of the "Underthinking" issues? Does the proposed method solve the fundamental cause of the "Underthinking" issues? 9. It is suggested that the authors provide more example to how whether the proposed method really mitigate the "Underthinking" issue. Otherwise, it may be not convincing enough. Other Comments Or Suggestions: N/A Questions For Authors: See Weaknesses Code Of Conduct: Affirmed. Overall Recommendation: 1	Rebuttal 1: Rebuttal: Thank you for the valuable suggestions, which helped clarify and strengthen the paper. > Q1: Provide the code for reproduction. A1: We will make our code publicly available soon. --- > Q2: The term "o1-like models" isn't precisely defined. A2: Thank you for pointing this out. We acknowledge that our original description of “o1-like” models lacks precision. A clearer term would be “Long Reasoning Models”, which refers to models that generate detailed CoT reasoning by iteratively producing intermediate reasoning steps and sequentially refining solutions until reaching a final conclusion. --- > Q3: More details about the temperatures. A3: In our experiments, we set the temperature to 0.7 and the top-p value to 0.95. We followed your suggestion and conducted a more detailed analysis regarding the impact of temperature settings. The table below summarizes the results of QwQ-32B-Preview evaluated on the Math Level 1 and 5. Clearly, the temperature hyperparameter has only a marginal effect on the number of generated thoughts, further confirming our assertion that "underthinking" is a fundamental behavior inherent to these models. \|Level\|Temperature\|Thoughts\| \|---\|---\|---\| \|1\|0\|3.7\| \|1\|0.3\|4.6\| \|1\|0.5\|3.8\| \|1\|0.7\|4.1\| \|1\|1\|3.7\| \|\|\|\| \|5\|0\|10.9\| \|5\|0.3\|11.1\| \|5\|0.5\|11.6\| \|5\|0.7\|10.8\| \|5\|1\|10.7\| --- > Q4: There is no formal definition of the "Underthinking" issue. A4: We recognize the terminology requires clarity. We clarify definitions explicitly: - Underthinking (formal definition): Defined in Section 2.3 as: "Underthinking occurs when models generate potentially correct intermediate reasoning thoughts initially, but prematurely shift away without thoroughly exploring and continuing these promising reasoning paths, eventually yielding incorrect answers." - Different Reasoning Thoughts: Defined explicitly in Section 2.1 as: "Individual cognitive steps within a model’s reasoning strategy. These transitions often explicitly indicated through terms like "alternatively"." - Promising Paths: Defined in Section 2.2 as: Reasoning trajectories identified as promising based on intermediate correctness evaluations. We describe our detailed implementation and assessment strategies for thought correctness clearly in that section. --- > Q5: The percentage of underthinking issue in all the wrong responses. A5: We presented in Table 1 the quantitative results of the underthinking score, which focuses the token efficiency specifically on the wrong responses. The results show that all Long Reasoning Models suffer from significant underthinking issues. --- > Q6: Figure 2 needs more explanations. A6: The final correct answer for the case in Figure 2 is 23. Thoughts #1,3,4,5 are promising and can lead to the correct answer if explored sufficiently. --- > Q7: The insight is limited and the overall observations are superficial. A7: In this pioneering work, our main contributions include: - Clearly defining and evaluating underthinking in long reasoning models. - Introducing quantitative evaluation measures. - Proposing a simple yet effective decoding approach that significantly mitigates underthinking on multiple reasoning benchmarks such as Math500, GPQA Diamond, and AIME2024. At this stage, we acknowledge that the existing community lacks complete open-source reproductions of large-scale long reasoning models, making it prohibitively expensive to empirically investigate training-related foundational causes. Therefore, we do not claim contributions toward understanding the training mechanism behind underthinking. However, clearly defining the issue and presenting empirical mitigation techniques is a valuable foundational step that future studies can further build upon toward fundamental analyses. --- > Q8: More convinced analyses. A8: We conducted extensive experiments across multiple models on the AIME24 benchmark. The results demonstrate that our proposed approach significantly reduces both the average number of thoughts generated and the average length of each thought, underscoring the broad effectiveness of our method. \|Models\|Pass@1\|Number\|Interval\| \|------\|------\|------\|--------\| \|QwQ-32B-Preview\|38.3\|16.1\|459.7\| \|+TIP\|44.1\|13.9\|515.7\| \|R1-Distill-Qwen-32B\|61.4\|8.2\|819.5\| \|+TIP\|64.1\|4.5\|1018.0\| \|DeepSeek-R1\|73.8\|13.8\|580.1\| \|+TIP\|74.8\|5.7\|941.6\| To thoroughly assess the robustness and generality of our TIP approach, we combined it with best-of-N sampling methods, and the results confirm that our method remains consistently effective under these conditions. \|Models\|Acc.(↑)\|UT(↓)\| \|---\|:---:\|:---:\| \|QwQ+Self-Consistency\|43.7\|35.4\| \|+TIP\|51.4\|26.6\| \|R1-Distill-Qwen+Self-Consistency\|67.0\|13.4\| \|+TIP\|69.9\|12.5\| \|R1+Self-Consistency\|79.3\|10.1\| \|+TIP\|81.3\|7.5\|	null	null	null	null	null	null
Function-to-Style Guidance of LLMs for Code Translation	Accept (poster)	Summary: This paper studies code translation. Different from previous settings where researchers only care about the functional correctness of translated codes, the authors in this paper also care the functional consistency. They propose a method to handle this by splitting it into a two-stage training framework, function learning and style learning. Besides existing benchmarks, the authors also propose a more up-to-date benchmark for code translation. Experimental results demonstrate the effectiveness of their proposed ;earning framework and extensive ablation studies explore the impact of different design choices. Claims And Evidence: Yes. Experimental results demonstrate that style learning benefits code translation. Methods And Evaluation Criteria: In style learning, the authors use a list-wise loss function to train LLMs to favor style-consistent target codes. The motivation of using such a loss function is not clear. This preference could also be learned through reinforcement learning (e.g DPO). The authors should study the impact of replacing the list-wise loss function with RL algorithms in their ablation studies. At least for me, the performance of list-wise loss doe not have to be better than DPO. This is because I consider these loss functions as designing variations of the framework. In the future, there may be more advanced loss functions to achieve even better performance. Theoretical Claims: There are no theoretical claims in this paper. Experimental Designs Or Analyses: There are other benchmarks that could be used for code translation, other than CodeNet, though not specifically designed for code translation. For example, the Multiple-E [1]. The author should also apply their framework on such benchmarks. [1] Multi-Programming Language Evaluation of Large Language Models of Code Supplementary Material: There are mainly prompting templates, a detailed description of some techniques in their paper, and some additional experimental results. Relation To Broader Scientific Literature: This work is specifically designed for code translation. Essential References Not Discussed: N.A Other Strengths And Weaknesses: N.A Other Comments Or Suggestions: N.A Questions For Authors: See my comments above. Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: We greatly appreciate the reviewer's insightful and constructive feedback, and we have carefully addressed each point in our response to resolve your concerns. If our response has satisfactorily addressed your questions, we kindly request your consideration of raising the score (currently Rating: 3: Weak Accept). Should any further issues remain, please feel free to share your additional comments, and we will continue actively responding to your comments and improving our submission. >Q1: Comparison between DPO and list-wise loss function. A1: The list-wise loss function is designed to improve the generation of positive translations by learning from one positive example and multiple negative examples. This approach differs significantly from DPO, which optimizes models based on pairwise comparisons between a single positive and a single negative sample. To evaluate the effectiveness of these two methods, we conduct experiments on the CodeNet and F2STrans benchmarks, with the results presented in Figure 8 of Appendix E in our paper. The average performance across three training runs is summarized in the following table, from which we can observe that our list-wise loss function is more effective. For more details on the experimental setup and additional analyses, please refer to Figure 8 of Appendix E in our paper. \|Dataset\|Our Models\|DPO\|List-wise Loss\|Delta\| \|-\|-\|-\|-\|-\| \|CodeNet\|Qwen-0.5B\|78.2\|78.9\|+0.7\| \|\|StarCoder-3B\|85.5\|86.7\|+1.2\| \|F2STrans\|Qwen-0.5B\|61.1\|62.1\|+1.0\| \|\|StarCoder-3B\|71.4\|72.9\|+1.5\| --- >Q2: In addition to the CodeNet and F2STrans benchmarks, the paper should evaluate performance on a broader range of benchmarks, such as Multiple-E. A2: We fully recognize the importance of comprehensive testing benchmarks. Therefore, Table 5 of Appendix D in our paper demonstrates the model's performance on the xCodeEval and CodeScope benchmarks. The average translation results for various source languages are as follows: \|xCodeEval\|C\|C++\|Go\|Java\|Py\|Avg.\| \|-\|-\|-\|-\|-\|-\|-\| \|Direct (Qwen-32B)\|72.9\|65.5\|76.1\|68.0\|70.3\|70.5\| \|CoT (Qwen-32B)\|71.9\|66.2\|76.4\|67.1\|73.0\|70.9\| \|RAG (Qwen-32B)\|75.8\|68.8\|78.1\|72.6\|75.6\|74.2\| \|Self-debug (Qwen-32B)\|76.7\|70.9\|79.5\|73.8\|76.9\|75.5\| \|Direct (GPT4)\|79.0\|75.9\|86.1\|73.9\|70.8\|77.1\| \|CoT (GPT4)\|78.8\|75.8\|86.8\|74.2\|74.3\|78.0\| \|RAG (GPT4)\|81.8\|77.6\|86.8\|77.6\|77.9\|80.3\| \|Self-debug (GPT4)\|83.1\|79.9\|89.0\|80.7\|77.4\|82.0\| \|Ours (Qwen-0.5B)\|84.2\|78.2\|82.7\|77.4\|66.8\|77.9\| \|Ours (Qwen-1.5B)\|88.8\|84.8\|88.8\|85.2\|78.8\|85.3\| \|Ours (Qwen-3B)\|90.4\|87.0\|90.3\|87.1\|82.2\|87.4\| \|Ours (Qwen-7B)\|91.4\|88.8\|91.8\|89.3\|84.1\|89.1\| \|Ours (StarCoder-3B)\|90.2\|86.8\|89.8\|86.6\|80.9\|86.9\| \|CodeScope\|C\|C++\|Go\|Java\|Py\|Avg. \|-\|-\|-\|-\|-\|-\|- \|Direct (Qwen-32B)\|59.4\|56.0\|67.4\|60.7\|48.6\|58.4 \|CoT (Qwen-32B)\|67.6\|53.5\|65.3\|60.1\|52.8\|59.9 \|RAG (Qwen-32B)\|75.4\|58.8\|65.7\|67.8\|59.7\|65.5 \|Self-debug (Qwen-32B)\|75.3\|61.4\|71.8\|67.9\|60.7\|67.4 \|Direct (GPT4)\|69.3\|64.4\|77.8\|62.1\|49.3\|64.6 \|CoT (GPT4)\|74.6\|65.6\|75.9\|68.2\|55.0\|67.9 \|RAG (GPT4)\|80.1\|68.2\|77.4\|73.5\|59.8\|71.8 \|Self-debug (GPT4)\|80.8\|70.5\|81.8\|74.8\|61.2\|73.8 \|Ours (Qwen-0.5B)\|75.4\|69.4\|75.8\|67.9\|45.7\|66.8 \|Ours (Qwen-1.5B)\|84.5\|71.9\|78.2\|76.8\|58.2\|73.9 \|Ours (Qwen-3B)\|88.6\|75.3\|80.7\|82.5\|65.5\|78.5 \|Ours (Qwen-7B)\|92.8\|86.6\|82.6\|85.3\|68.5\|83.2\| \|Ours (StarCoder-3B)\|87.3\|78.1\|83.2\|78.9\|62.5\|78.0 In response to your suggestion, we have conducted additional tests on the Multiple-E and CodeTransOcean benchmarks. For Multiple-E, since it does not include C code, we focus on evaluating its performance across other languages. For CodeTransOcean, we adopt the CodeBLEU metric, consistent with the standard practice described in the CodeTransOcean paper. For other benchmarks, we continue to use the Computational Accuracy metric as outlined in our paper. \|Multiple-E\|C++\|Go\|Java\|Py\|Avg. \|-\|-\|-\|-\|-\|- \|Direct (Qwen-32B)\|58.6\|64.8\|72.0\|44.3\|59.9 \|CoT (Qwen-32B)\|61.8\|65.8\|77.0\|47.3\|63.0 \|RAG (Qwen-32B)\|62.9\|69.4\|77.5\|49.1\|64.7 \|Direct (GPT4)\|71.2\|75.9\|78.4\|46.5\|68.0 \|CoT (GPT4)\|71.6\|77.6\|79.1\|48.8\|69.3 \|Self-debug (GPT4)\|73.5\|77.2\|81.6\|52.3\|71.1 \|Ours (Qwen-0.5B)\|71.7\|71.9\|81.7\|40.0\|66.3 \|Ours (Qwen-1.5B)\|79.3\|77.9\|89.5\|50.0\|74.2 \|Ours (Qwen-3B)\|82.6\|80.6\|92.4\|54.7\|77.6 \|Ours (Qwen-7B)\|84.6\|83.6\|93.3\|58.2\|79.9\| \|Ours (StarCoder-3B)\|82.3\|80.9\|92.1\|52.9\|77.1 \|CodeTransOcean\|C\|C++\|Go\|Java\|Py\|Avg. \|-\|-\|-\|-\|-\|-\|- \|Direct (Qwen-32B)\|27.6\|27.0\|27.1\|31.6\|24.1\|27.5 \|CoT (Qwen-32B)\|27.3\|26.5\|27.5\|32.1\|25.2\|27.7 \|RAG (Qwen-32B)\|28.2\|27.4\|28.1\|32.4\|24.7\|28.2 \|Direct (GPT4)\|29.1\|29.0\|28.4\|32.9\|25.7\|29.0 \|CoT (GPT4)\|29.2\|29.3\|28.6\|32.2\|26.2\|29.1 \|Ours (Qwen-0.5B)\|30.3\|29.0\|28.4\|30.8\|25.7\|28.9 \|Ours (Qwen-1.5B)\|30.8\|29.7\|29.8\|32.3\|25.8\|29.7 \|Ours (Qwen-3B)\|31.2\|29.9\|30.9\|33.2\|26.7\|30.4 \|Ours (Qwen-7B)\|31.2\|30.6\|30.4\|34.3\|27.1\|30.7 \|Ours (StarCoder-3B)\|30.8\|29.8\|30.0\|32.8\|26.6\|30.0 --- Rebuttal Comment 1.1: Comment: I thank the authors for their rebuttal. All my concerns are well addressed. Thus, I will raise my score to 4. Please make sure that all of the content during the rebuttal will appear in the camera-ready version. --- Reply to Comment 1.1.1: Comment: Thank you very much for your thoughtful feedback and for raising your score to 4! We deeply appreciate the time and effort you have invested in carefully reviewing our work and providing such constructive suggestions. Your insights have been invaluable in helping us strengthen our paper and address key concerns more comprehensively. We will make sure to incorporate the additional results and discussions into the camera-ready version, as you suggested. Your feedback has not only improved the quality of our work but also deepened our understanding of the methods and their implications. Once again, thank you for your support and for recognizing our efforts. We hope that our work can contribute meaningfully to the field.	Summary: This paper proposes F2STrans, an approach for improving code-to-code translation by optimizing large language models (LLMs). The main idea of this paper is to provide fine-tuning processes that instruct knowledge on good code and bad code in terms of two criteria: Functional Learning and Style Learning. For functional learning, which requires LLM to generate translated code with a high level of functional correctness, this approach designs a paradigm called Function-oriented Guidance by two steps: Function-consistent Data Construction using code embedding and ranking candidate code using LLMs and Functional Learning, which uses Instruction Fine-tuning to return the optimized LLM for code translation. For Style learning, this approach uses strong LLMs to generate positive translation examples with stylistic similarity scores to find the best example and the same process to find negative translation examples. Next, it uses a lit-wise loss function to instruct LLM to generate code with better style. In the experiment, this work uses CodeNet and their proposed benchmark called F2STrans for evaluation. Their results show that F2STrans can provide better Computational Accuracy and stylistic accuracy compared to state-of-the-art LLMs like GPT-4 and Qwen-32B. Claims And Evidence: The claims made in the submission are clear and convincing. Methods And Evaluation Criteria: The evaluation criteria are clear and convincing, with the benchmark constructed and the evaluation metrics. For the proposed method, It is good to know the correctness of Judge LLM used in Function Learning and how it can impact the accuracy of code translation. In Table 3, the authors reported the accuracy without LLM Judge and it underperforming the default configuration. However, the authors need to analyze the case when the judge returns bad results. Other parts of the Methods are clear and convincing. Theoretical Claims: This paper proofs that the existing dataset for evaluating LLM-based code translation like CodeNet is somehow outdated. They claim that their proposed dataset can capture better the complexity and nature of LLM-based code translation. Through the experiment, they successfully proved that claim since the accuracy of multiple configurations of their tool for code translation tends to be lower with their constructed benchmark. Experimental Designs Or Analyses: Experiment designs and analysis are sound and valid. Supplementary Material: No, I could not get time to review it. Relation To Broader Scientific Literature: This paper proposed a new direction of improving LLM-based code translation with a focus on important aspects of translated code as functional correctness and stylistic information. Their results show that with proper improvement, simple open LLMs can still outperform large scale open LLM and closed LLMs. They also contributed to the science community a dataset that will be helpful in evaluating code translation. Essential References Not Discussed: I suggest the authors explain why they chose stylistic and functional correctness as two aspects for improvement. They should add papers about studies on code preferences (CodeUltraFeedback: An LLM-as-a-Judge Dataset for Aligning Large Language Models to Coding Preferences - Wessay et al.) to describe the potential/ challenges of applying new aspects to their approach. Other Strengths And Weaknesses: Strength: - This paper is well-written and has a good structure to follow. - The strategy of providing better samples for the fine-tuning process is a good direction. - The selections of loss functions for functional learning and style-oriented learning were based on well-known prior works. - The result has an acceptable level of outperformance compared to existing works. - Integrating manually annotated ground-truth translation. Weakness: - Unclear motivation example: Can you define which part of the translated code should include the code for I/O optimization? - For Function-consistent Data Construction, there is a risk that the LLM Judge can provide incorrect output. Further study is needed to analyze the case when LLM judges provide low-quality output. - While human annotation for ground-truth dataset creation is important, there is are lack of description of this process in the current version of this paper. Other Comments Or Suggestions: Lack of comparison with non-LLM approaches. Authors can consider comparing their work with transformer-based approaches such as CodeRosetta (CodeRosetta: Pushing the Boundaries of Unsupervised Code Translation for Parallel Programming). Questions For Authors: 1. The scale of the manual ground-truth translation creation (mentioned in section 3.1). How many people are required to do this process? How do authors ensure that human responses were correct? 2.Code Pair embedding. Did authors try other well-known code embedding methods, such as UniXcoder (Guo et al. - UniXcoder: Unified Cross-Modal Pre-training for Code Representation)? Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: We thank the reviewer for the insightful and valuable comments. >Q1: Further study is needed to analyze the case when LLM judges provide low-quality output. A1: We observe that LLM Judge is prone to errors when evaluating source code that is either lengthy or contains numerous built-in APIs, e.g., "map", "lambda", etc., in Python. To evaluate its performance in assessing translation quality, we introduce an LLM Judge benchmark. This benchmark comprises source code and human-annotated translation from our F2STrans benchmark, along with translations generated by Qwen-32B and GPT-3.5. We measure the performance of a Qwen-7B-based LLM Judge by its success rate in identifying the human-annotated translation as the best translation for a given source code. The table below summarizes results for source code with varying API counts and token lengths. While performance deteriorates with increased complexity, our analysis indicates that LLM Judge still reliably identifies high-quality translations in most scenarios. #API\|[0,3]\|[4,7]\|[8,11]\|Overall -\|-\|-\|-\|- Results\|83.4\|75.6\|61.3\|77.5 #Token\|[0,250]\|[251,500]\|[501,750]\|[750, $+\infty$]\|Overall -\|-\|-\|-\|-\|- Results\|84.3\|79.6\|64.6\|46.3\|77.5 --- >Q2: Why were style and functional correctness chosen as two aspects for improvement? A2: We focused on style and functional correctness for two main reasons: 1. Fundamental requirements: Functional correctness ensures the translated code maintains the same behavior as the source code—an essential requirement for any translation system. Stylistic correctness enhances readability and maintainability, making the translated code easier to understand and modify. 2. Translation-specific factors: While efficiency, security, and other aspects are certainly important in code development, these factors are largely determined by the source code itself rather than the translation process. We are actively exploring ways to optimize code translation quality from a broader perspective in our ongoing research. --- >Q3: The research on code preferences (CodeUltraFeedback) should be discussed. A3: We agree that the CodeUltraFeedback is highly relevant to our work. It inspires us to explore incorporating user-defined code styles and preferences into our code translation system. Additionally, it illuminates important future challenges beyond our current scope, particularly how to extend our approach to address other crucial non-functional factors like efficiency, security, and maintainability in the translated code. Our paper will incorporate a more detailed discussion of CodeUltraFeedback and its implications for our research. --- >Q4: Clarification on I/O optimization in motivation example. A4: In the C++ code, the lines ```cpp ios::sync_with_stdio(false); cin.tie(0); ``` disable synchronization between C++ I/O streams and untie cin from cout, reducing overhead and accelerating input/output operations. In Python, a comparable optimization would involve using faster input methods, such as ```sys.stdin.readline()``` or reading all input at once via ```sys.stdin.read()```. --- >Q5: The paper lacks a detailed description of the process for manually annotating the ground-truth dataset. A5: Our annotation team consisted of 30 professional software developers with industry experience, 15 graduate students, and 5 doctoral students in computer science. During code translation, each source code was translated by at least 5 different annotators, ensuring multiple candidate translations. Doctoral students then selected the best translation or refined problematic ones. For test case annotation, we maintained a 95% branch coverage rate, prioritizing edge cases and challenging scenarios. The entire annotation process took approximately 5 months. --- >Q6: Lack of comparison with non-LLM approaches, like CodeRosetta. A6: We appreciate the suggestion to compare our work with non-LLM approaches for a more comprehensive evaluation. While CodeRosetta focuses on translations between C++ and CUDA/Fortran (which differs from our scope), we will include a more detailed discussion of it in our paper. Below, we compare our approach with two prominent non-LLM code translation systems, TransCode-ST and TransCode-IR. Codenet Benchmark\|C++↔Go\|C++↔Java\|C++↔Py\|Go↔Java\|Java↔Py -\|-\|-\|-\|-\|- TransCoder-ST\|-\|66.3\|72.7\|-\|71.2 TransCoder-IR\|54.3\|69.4\|-\|50.6\|- Ours (Qwen-0.5B)\|77.9\|84.9\|78.2\|77.3\|80.6 F2STrans Benchmark\|C++↔Go\|C++↔Java\|C++↔Py\|Go↔Java\|Java↔Py -\|-\|-\|-\|-\|- TransCoder-ST\|-\|50.2\|26.3\|-\|32.6 TransCoder-IR\|41.7\|53.2\|-\|54.3\|- Ours (Qwen-0.5B)\|67.0\|72.3\|44.1\|70.6\|53.4 --- >Q7: Did authors try other well-known code embedding methods, like UniXcoder? A7: The training results of Qwen-1.5B using various embedding models are as follows: \| \|Size\|CodeNet\|F2STrans -\|-\|-\|- BGE\|110M\|84.3\|68.8 UniXcoder\|123M\|85.2\|70.1 Jina-embeddings\|161M\|85.1\|69.8 CodeXEmbed\|400M\|85.4\|70.5	Summary: Previous work in code translation has focused on improving the performance of LLM-based code translation by focusing on multilingual training and various test-time inference strategies. In this paper, the authors hypothesize that optimizing for program correctness and program readability can improve the performance of LLMs on code translation tasks. Specifically, the authors mine codeforces to collect a dataset of cross-lingual code pairs that are functionally consistent and present a contrastive learning framework to optimize for coding style. The authors find that (1) evaluating on their curated benchmark reduces mean average score by about 10% highlighting greater complexity (2) ablating the style-consistent training and the functional consistency checks significantly reduce the overall effectiveness of the model, (3) for many tasks, a 0.5B parameter Quen model outperforms GPT4 model. Claims And Evidence: Generally yes. I think the authors have presented reasonable evidence that supports their claims. Specifically, I looked at these claims: - Claim 1: F2STrans is an effective benchmark for code translation. - Evidence 1: The mean average success rate of models drops 10% from CodeNet to F2STrans. Comments: The performance of Python translation drops signficiantly from CodeEval to FS2Trans. The authors mention that this could be because python is an interpreted language but a deeper answer would be useful here. what is the mean average success rate ignoring Python translation tasks? - Claim 2: Functional consistency training is beneficial to code translation. - Evidence 2: An ablation experiment shows that, without functional consistency training, translation success rate drops slightly. - Claim 3: Style-oriented training is beneficial to code translation. - Evidence 3: An ablation showcases that model accuracy suffers without style oriented training. Methods And Evaluation Criteria: This paper is generally missing a comparison with the CodeTransOcean benchmark. Evaluating how the trained methods performed on this dataset would be very informative since the CodeEval seems to be sourcing data from the same underlying data distribution as F2STrans (codeforces). Furthermore, I find it concerning that the data mining algorithm for both the functional consistency and the style-guidance seem to rely heavily on having an LLM as a critic (Quen-7B as the "LLM Judge" and Quen-32B as the "Style Aware LLM") but there was no evaluation done as to how the inherent biases of these models affects the final performance of a model training on the F2STrans benchmark. Theoretical Claims: none. Experimental Designs Or Analyses: For Table 2: > L258R: As shown in Table 2(II), all evaluated models achieve scores that are at least 10 points lower on average in our benchmark compared to CodeNet, highlighting the greater complexity of our proposed benchmark This seems to be the only quantitative evidence in the main paper that argues for whether FS2Trans is a better benchmark than CodeNet. This is a major claim which deserves a finer-grained analysis than the current analysis presented. Some recommendations: - Please present concrete numbers of the mean average success rate delta, ideally by each language category. - It seems that Python translation tasks have an outsized influence on the aggregate number presented. If we remove Python, what does the delta difference look like? > L258R: ... weaker performance on Python... Its pretty interesting that Python translation success rate decreases so much between the datasets. The reasoning presented in the paper is that this is because of the "interpreted nature [of Python]". I'm not sure this argument holds up very well. If this argument were true, CodeEval results should also have been in the 25%-55% range. Yet, on CodeEval, the average performance is between 70%-90%. I think a deeper qualitative analysis would be beneficial here, such as a qualitative analysis of the code and a study of what kinds of failures the models fell into on CodeEval and on F2STrans. __Overall__: For Table 2, I agree that the overall reduction in success rate is interesting. However, there are many other non-trivial insights we can take from this experiment that are not presented. A deeper analysis is required. Additionally, both CodeEval and FS2Trans source their data from codeforces. I do not think the code-writing style on codeforces is a good indicator of how well code translation would work "in the wild." For instance, we generally modularize and structure code in Java around certain object oriented classes while in C we modularize and structure code around shared procedures. I think evaluating and comparing on a code translation dataset that sources it's data from other sources would be very useful here. (eg: CodeTransOcean but the authors might know other ones as well). > While the effectiveness of LLMs ... most models face two critical limitations .. (i) Correctness [and] (ii) Readability Table 2 and related experiments seem to only measure the correctness of the generated code against a dataset. How is code quality improved by the presented approach? How can this be measured quantitatively? Even some qualitative examples of how the code correctness and readability changes before and after training would be beneficial. Supplementary Material: . Relation To Broader Scientific Literature: Just in terms of the benchmark, I don't think the results with the style guidance and functional consistency are particularly surprising. I definitely see this benchmark complementing other preexisting benchmarks but I'm not sure what additional non-trivial insight a user would gain by benchmarking their model on CodeEval as compared to F2STrans, other than the fact that their model will be slightly worse on FS2Trans. I believe this can be solved by improving the presentation of the paper to motivate the hypothesis. a bit more. For instance, by showcasing a non-trivial tasks where function consistency and style-oriented training truly brings a large difference in performance. In terms of the algorithmic insight, the training methodology and loss functions do not seem to be novel contributions. Essential References Not Discussed: . Other Strengths And Weaknesses: - The notation for denoting LLM prompts $\mathcal{P}(\cdot)$ looks very similar to $P(\cdot)$. It might be better to express these as serializations of various variables. e.g: instead of using $\mathcal{P}(src),tgt_{<i}$ to denote the "prompt" for translating source code with the text generated so far, we can instead denote it as $\langle \text{src} \rangle;\langle\text{tgt}_{<I}\rangle$ to denote the serialization of the source code concatenated with the target code generated so far. - > L63: Relying solely on the inherent capabilities of LLMs to overcome these issues is only a short-term solution. - I can agree with this statement but more justification for this statement (in what use cases? Under what constraints?) would be useful. - In the related work section, it would be beneficial to comment on how the proposed pipeline relates to each of the sub-fields mentioned. Other Comments Or Suggestions: Overall, I'm leaning towards Rejection (Weak Rejection). While F2STrans presents an interesting hypothesis (that style consistency and functional consistency are important for code translation), the supporting analysis for the experimental observations is inadequate to support these claims. I'm willing to raise my score after discussion with the authors. ---- After discussions with the Authors, I'm increasing my score to Weak Accept. Questions For Authors: (merged with other sections) Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Thank you for recognizing the contributions of our work and providing valuable feedback. We respond to each comment as follows and sincerely hope that our rebuttal could properly address your concerns. If so, we would deeply appreciate it if you could raise your score (currently Rating: 2: Weak reject). If not, please let us know your concerns, and we will continue actively responding to your comments and improving our submission. Before addressing your specific points, we would like to clarify that the "CodeEval" mentioned in the review likely refers to the "CodeNet" benchmark. >Q1: In addition to the CodeNet and F2STrans benchmarks, the paper should evaluate performance on a broader range of benchmarks, such as CodeTransOcean. A1: Besides the CodeNet and F2STrans benchmarks, we also report results on xCodeEval and CodeScope benchmarks in Table 5 of Appendix D. Here, we show more results on CodeTransOcean and Multiple-E benchmarks. For CodeTransOcean, we adopt the CodeBLEU metric, consistent with the standard practice in the CodeTransOcean paper. \|\|xCodeEval\|CodeScope\|Multiple-E\|CodeTransOcean -\|-\|-\|-\|- Qwen32B\|70.5\|58.4\|59.9\|27.5 GPT4\|77.1\|64.6\|68.0\|29.0 Ours (Qwen1.5B)\|85.3\|73.9\|74.2\|29.7 --- >Q2: The paper lacks evaluation of code quality. A2: In Table 4 of Section 3.5, we assess the stylistic quality of translations based on the CCSim metric. The results are as follows: \|\|CSSim \|-\|:-:\| Qwen32B\|76.4 GPT4\|77.9 Ours (Qwen1.5B)\|82.0 --- >Q3: The paper uses Qwen7B and Qwen32B for LLM Judge and Style Aware LLM Translation, respectively. It does not analyze the impact of inherent biases in these LLMs on the model training. A3: We build training datasets based on different LLMs (Qwen-7B/32B and DeepSeek-6.7B/33B) and show the training results of Qwen1.5B based on F2STrans benchmark: LLMs Used by Judge and Style Aware Translation\|C\|C++\|Go\|Java\|Py\|Avg. -\|:-:\|:-:\|:-:\|:-:\|:-:\|:-:\| Qwen-(7B/32B)\|81.0\|69.2\|75.1\|83.6\|40.0\|69.8 DeepSeek-(6.7B/33B)\|80.4\|67.1\|77.3\|82.2\|43.4\|70.1 Hybrid Mining\|81.3\|70.5\|77.8\|84.1\|43.6\|71.5 We find that the inherent biases of LLMs cause uneven performance across languages. By adopting a Hybrid Mining strategy—using Qwen LLMs for C, C++, and Java, and DeepSeek LLMs for Go and Python—we achieved consistent performance improvements. This demonstrates that assigning tasks according to each model's strengths can alleviate the impact of LLMs’ inherent biases and improve the quality of training data. --- >Q4: Some non-trivial insights into the overall performance decline on the F2STrans benchmark are required. A4: We have identified two main reasons for the overall performance decline: - Number of Test Cases. F2STrans includes 50 human-annotated test cases for each code snippet (see Table 1), whereas CodeNet provides only one. The scarcity of test cases in CodeNet may lead to inflated evaluation results, introducing evaluation errors. To quantify this impact, we conducted 10 code translation evaluations, each using a random test case from F2STrans samples. The results, shown below, reveal that relying on a single test case introduces at least a 2.4% evaluation error. \|\|1 Case\|50 Cases\|Evaluation Error \|-\|:-:\|:-:\|:-:\| Qwen32B\|56.7\|53.9\|3.8 GPT4\|66.0\|63.6\|2.4 Ours (Qwen3B)\|76.1\|73.7\|2.4 - Code Length. As shown below, source code in F2STrans usually contains more tokens than in CodeNet, which makes evaluations more challenging. \|\|C\|C++\|Go\|Java\|Py \|-\|:-:\|:-:\|:-:\|:-:\|:-:\| CodeNet\|298.5\|264.8\|300.6\|256.0\|91.3 F2STrans\|397.3\|368.7\|350.6\|315.2\|216.4 Delta\|98.8\|103.9\|50.0\|59.2\|125.1 --- >Q5: The Python translation performance of various models shows a significant decline in the F2STrans benchmark, yet the paper lacks an analysis. A5: We find that Python code in our F2STrans benchmark is more complex, characterized by longer average length and more frequent use of built-in APIs, such as "map" and "lambda". As a result, models are more prone to generating code with compilation errors when translating these complex examples. For instance, over half of the errors produced by Qwen32B are due to compilation failures, as follows: \|\|CodeNet\|F2STrans -\|:-:\|:-:\| #Token\|91.3\|216.4 #API\|4.3\|7.5 Compilation Error Ratio\|21.4\|51.8 --- >Q6: Presenting concrete numbers for the mean average success rate delta, both with and without Python, can help verify the benchmark advantages of F2STrans. A6: The table below shows the mean average success rate delta for each language between the CodeNet and F2STrans benchmarks. Each model's performance drops by at least 11.7 on F2STrans compared to CodeNet, and by at least 6.0 even without Python. This confirms that our F2STrans benchmark is highly challenging. \|\|C\|C++\|Go\|Java\|Py\|Avg.\|Avg. w/o Py \|-\|:-:\|:-:\|:-:\|:-:\|:-:\|:-:\|:-:\| Qwen32B\|12.9\|26.6\|8.7\|4.0\|42.8\|19.0\|13.0 GPT4\|5.8\|13.6\|2.6\|1.9\|34.4\|11.7\|6.0 Ours (Qwen1.5B)\|6.4\|17.8\|5.9\|1.7\|44.5\|15.3\|8.0 --- Rebuttal Comment 1.1: Comment: Thank you for the additional insights! Apologies about the lack of proofreading on my end. Generally, These additional observations were extremely insightful and I'd recommend adding these to the main paper (if possible). I'm raising my score to Weak Accept. --- Reply to Comment 1.1.1: Comment: Thank you very much for your thoughtful feedback and for raising your score to 3! We deeply appreciate the time and effort you have invested in carefully reviewing our work and providing such constructive suggestions. Your insights have been invaluable in helping us strengthen our paper and address key concerns more comprehensively. We will make sure to incorporate the additional results and discussions into the camera-ready version, as you suggested. Your feedback has not only improved the quality of our work but also deepened our understanding of the methods and their implications. Once again, thank you for your support and for recognizing our efforts. We hope that our work can contribute meaningfully to the field.	Summary: Authors present F2STRANS, a novel function-to-style guiding paradigm that enhances the code translation performance of smaller LLMs by addressing functional correctness and stylistic readability. Authors propose a 2-stage learning approach: 1) The functional learning stage is based on instruction fine tuning(FT) using good quality source-target code pairs collected by authors from online programming platforms (codeforces). This step optimizes for code translation correctness by FT a base LLM. The quality of code pairs is maintained by (a) Qwen-7B as LLM judge (b) testing. 2) The style learning stage improves code readability by training model fine-tuned in stage 1 using constrastive learning (positive and negative style examples). The positive example is generated by Qwen-32B while negative style translations are generated from model fine-tuned in stage 1. Authors present extensive evaluations which shows that F2STRANS significantly improves code translation performance across benchmarks for 4 different prompting approaches based on FT smaller Qwen and starcoder models and comparing these against larger Qwen-32B and GPT-4. Authors also introduces a new larger code translation benchmark F2STRANS. Claims And Evidence: Key technical Innovations claimed include: 1. Relevance-driven code pair selection: (a) Use of Jina code embedding model & LLM judge to assess solution consistency (b) Differential testing ensures code pairs exhibit identical input-output behavior 2. Style consensus selection: a) Leverages CSSim metric to ensure stylistic similarity among candidates translations. 3. New code translation benchmark dataset with 5 programming languages. Main results claimed include: 1. F2STRANS improves translation performance on both the new (fs2trans) and existing benchmarks (codenet). F2STRANS enables smaller Qwen and starcoder models to outperform Qwen32B and GPT-4 on several language pairs. 2. Ablation studies demonstrate that functional and style learning stages contribute substantially to performance gains. F2STRANS shows improved effectiveness in correcting various types of errors in base LLM translations compared to function guidance alone. 3. Evaluation using CCSim metric shows F2STRANS enhances stylistic quality of translated code. 4. Experiments with multilingual training strategies indicate that cross-lingual training enhances the performance of F2STRANS. Methods And Evaluation Criteria: Yes . Authors use (i) a new larger benchmark (ii) CCSim to evaluate the stylistic similarity (iii) Comparison with stronger LLMs QWEN-32B and GPT-4. (iv) Ablation Studies to attribute the contribution of different components of FS2TRANS. (v) Analysis of types of errors corrected by F2STRANS. Theoretical Claims: None Experimental Designs Or Analyses: NIL Supplementary Material: Appendix F. Relation To Broader Scientific Literature: Broadly, this work makes a good contribution in the code translation space, by building upon ideas from literature and contributing a new benchmark. Essential References Not Discussed: NIL Other Strengths And Weaknesses: - Weakness: Heavy dependence on the availability of larger LLMs to judge translations and generate correctly styled translations. Other Comments Or Suggestions: None Questions For Authors: - Could you please explain how the negative-style translations are generated using Mfun in stage 2 along with prompting techniques used. How did you validate that there is sufficient variability/diversity in the generated negative style samples and that they are different from one another. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We thank the reviewer for the insightful and valuable comments. We respond to each comment as follows and sincerely hope that our rebuttal could properly address your concerns. If our response meets your expectations, we would greatly appreciate it if you could consider raising your score (currently Rating: 3: Weak Accept). If further concerns remain, please let us know, and we are committed to addressing them and refining our submission accordingly. >Q1: Heavy dependence on the availability of larger LLMs to judge translations and generate correctly styled translations. A1: Using larger LLMs to build training data can indeed enhance model performance. However, we would like to clarify two key points: (1) While it is important to acknowledge the limitations of this approach, we should not overlook its significant benefits. For instance, our training framework enables Qwen-1.5B to outperform GPT-4 across a wide range of code translation benchmarks. The specific results are as follows: \|\|CodeNet\|F2STrans\|xCodeEval\|CodeScope\| \|-\|:-:\|:-:\|:-:\|:-:\| \|Qwen-32B\| 72.9 \| 53.9 \| 70.5 \| 58.4 \| \|GPT-4\| 75.3 \| 63.6 \| 77.1 \| 64.6 \| \|Ours (Qwen-1.5B)\| 85.1 \| 69.8 \| 85.3 \| 73.9 \| (2) Even when we use LLMs of the same scale as the trained model to construct training data, our two-stage training method remains effective. Here, we trained Qwen-3B exclusively on data constructed entirely by itself. The results are presented in the table below. We find that, without relying on larger LLMs, our framework still enables Qwen-3B to surpass GPT-4 across these code translation benchmarks. \|\|CodeNet\|F2STrans\|xCodeEval\|CodeScope\| \|-\|:-:\|:-:\|:-:\|:-:\| \|Qwen-32B\| 72.9 \| 53.9 \| 70.5 \| 58.4 \| \|GPT-4\| 75.3 \| 63.6 \| 77.1 \| 64.6 \| \|Ours (Judge-Qwen-3B, Positive Translation Generation-Qwen-3B, Model Training-Qwen-3B)\| 85.5 \| 70.3 \| 85.7 \| 75.1 \| --- >Q2: Could you please explain how the negative-style translations are generated using $M_{fun}$ in stage 2 along with prompting techniques used. How did you validate that there is sufficient variability/diversity in the generated negative style samples and that they are different from one another. A2: We set $M_{fun}$'s temperature to 1.5 and perform multiple sampling generations with the prompt described in line 825 of our paper. A translation is retained only if its CCsim score with any prior translation is below 0.9; otherwise, it is discarded. CCSim, as detailed in lines 606 to 633 of the paper, measures stylistic similarity between code snippets, and a threshold of 0.9 ensures that the retained samples are sufficiently distinct from one another. If fewer than the desired number of translations are retained after 20 sampling attempts (a rare scenario), we incrementally increase the temperature to encourage greater diversity in the $M_{fun}$'s outputs. The table below illustrates the average similarity between our constructed negative-style translations, measured using two metrics: CCSim and CodeBLEU. \| \| C \| C++ \| Go \| Java \| Python \| Average \| \|---------\|:------:\|:------:\|:------:\|:------:\|:--------:\|:---------:\| \| CCSim \| 82.4 \| 84.3 \| 77.5 \| 81.7 \| 73.6 \| 79.9 \| \| CodeBLUE\| 78.1 \| 79.7 \| 72.1 \| 76.4 \| 68.7 \| 75.0 \| We further evaluated the performance of the trained Qwen-1.5B model on various benchmarks using different CCsim filtering thresholds. The results shown in the following table indicate that omitting negative translation filtering—disregarding the diversity of negative translations—led to a noticeable decline in performance. Moreover, setting the threshold too low (e.g., 0.8) also impaired performance. This may be because an excessively low threshold introduces some highly diverse but low-quality negative translations. \| Benchmark \| 1.0 (w/o Negative Translation Filtering) \| 0.95 \| 0.9 \| 0.85 \| 0.8 \| \|-----------------\|:------------------------------------:\|:------:\|:------:\|:------:\|:------:\| \| CodeNet \| 84.0 \| 84.5 \| 85.1 \| 85.1 \| 84.9 \| \| F2STrans \| 68.9 \| 69.3 \| 69.8 \| 69.7 \| 69.5 \| \| xCodeEval \| 84.6 \| 84.8 \| 85.3 \| 85.4 \| 85.1 \| \| CodeScope \| 73.1 \| 73.5 \| 73.9 \| 73.7 \| 73.4 \|	null	null	null	null	null	null
Language Models May Verbatim Complete Text They Were Not Explicitly Trained On	Accept (spotlight poster)	Summary: This work shows that current LLMs are able to generalize from their training dataset in a way that completes unseen (measured by n-gram overlap) data samples during inference time, thus challenging the use of n-gram-based metrics for a wide range of fields such as memorization, contamination, poisoning, and dataset inference. The paper approaches this from two angles: (1) it shows that even when removing all sequences of verbatim copying (memorization) from an original dataset, there remain so-called "lingering sequences" that are still reproduced verbatim after full re-training (and likely an artifact of very similar neighboring sequences or natural generalizations which evade filtering) - notably this is still the case for, e.g., 5-gram filters (albeit less and with noticeable trend to generalization). Second, they show that by creating a specific dataset that shares no (n-gram) overlap with a given target sequence, a model can be "forced" to learn the target sequence verbatim (via generalization). For this, the authors test three techniques (and their combinations): chunking, dropout, and case flip. Notably, dropout (and its combinations) highlight that such sequences can be easily forced while evading filters - even after only a few fine-tuning gradient steps. The authors also find that more capable models are more susceptible (likely due to their increased capabilities in generalizing from similar sequences). Overall, the work challenges the notion of membership definitions via n-gram or exact match commonly used in various related fields. ## Update after rebuttal The reviewer stands by their decision at the end of the reviewer rebuttal discussion and is in favor of acceptance. Claims And Evidence: All main claims are backed up by sufficient and strong empirical evidence. In particular: - C: The threshold for n-gram-based membership in LLM training data can be gamed. - C: n-gram definitions have limitations in the context of data membership inference. - C: Removing n-gram members does not have to prevent LLM Verbatim Completion. - C: One can force LLM verbatim completion by adding n-gram non-members. have direct experiments with solid ablations. Methods And Evaluation Criteria: Yes, across experiments and settings, both the datasets and the models are reasonable and provide a solid empirical basis for the claims made. Ablations across various parameters are reasonable and presented in an understandable format. Used models are realistic in size (given resource constraints and evaluations on the dataset itself are thorough enough to be convincing). Theoretical Claims: The work did not contain any theoretical claims of which one could check the soundness. Experimental Designs Or Analyses: The reviewer has read all experimental setups including their additional descriptions in the Appendix. The definitions of algorithms have only been skimmed, but they are straightforward enough not to warrant any questions. Supplementary Material: I read the Appendix fully - no further supplementary material was visible. Relation To Broader Scientific Literature: Overall, the authors of the work have made significant efforts to contextualize their work concerning the surrounding scientific literature. While the reviewer is primarily familiar with Memorization and DI literature, the key notion in many of these fields was that verbatim memorization (of a high enough entropy sequence) is very close to a gold standard of its verbatim containment in the training set. The work starts to challenge this assumption, opening up further discussions about what it means to contain data during training and finding proof of such containment - increasingly relevant topics with larger LLM adoption. Essential References Not Discussed: None Other Strengths And Weaknesses: #### Strengths - Extremely well-written with clear structure, definitions, and presentation. The reviewer thoroughly enjoyed reading the paper. - The main claims of the paper are important and well substantiated with a wide range of sensible experiments showing that existing metrics can be easily circumvented. - Ablations are reasonable and the ablations about finding closest matches and types of lingering examples are appreciated to help the overall understanding. #### Weaknesses - Minor in the context of this work: While the proposed techniques for forcing the memorization of a specific sequence tend to work in the "un-defended" scenario, in a realistic scenario for data poisoning (e.g., 5.6.1), it would likely be caught by a variety of filters and could be interesting follow-up directions. ##### Comments - It might make sense to mention again in the later sections that the case flip results only hold for later normalized text. Other Comments Or Suggestions: - L1340 otheriwse Questions For Authors: - What ways do you see to craft such sequences in a way such that they are not killed by common pre-processing techniques for model training (normalization, high-perplexity filtering)? - Could such memorization-forcing sequences already be included in the pre-training and not only in finetuning - is there anything that would prevent this generalization? Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: We appreciate the reviewer’s positive assessment of our work! We’re glad the reviewer finds the paper enjoyable to read, the experiments well-designed, and the claims important for the community. We hope to address the comments below and would appreciate the reviewer’s consideration. > [Weakness] …in a realistic scenario for data poisoning (e.g., 5.6.1), it would likely be caught by a variety of filters and could be interesting follow-up directions. > [Q1] … craft such sequences in a way such that they are not killed by common pre-processing techniques for model training (normalization, high-perplexity filtering)? We appreciate the reviewer’s insightful question. In principle (recall the beginning of Sec 5), we believe that any noisy transformation of a reasonable noise distribution should work, and there should be transformations that result in “normal looking” text. For example, following Reviewer J1BJ’s suggestion and our response, one could consider: - Shuffling token ordering; - Multi-lingual replacement; - Token replacement within a restricted corpus (e.g. a fixed book, thus the perturbed sequences look like that book). We agree with the reviewer that there can be many interesting follow-up and hope to explore additional noisy transformation strategies. > [Q2] Could such memorization-forcing sequences already be included in the pre-training and not only in finetuning - is there anything that would prevent this generalization? The reviewer raises an interesting question. In Appendix A.3, we performed a costly edit-distance search of a few lingering sequences; judging from the visualizations, one could potentially interpret the near-duplicates and template sequences commonly in webtext as a form of “memorization-forcing sequences” that has no n-gram overlap. Given the vast size of pre-training data and the existence of lingering sequences (Sec 4), we believe that such generalization would happen naturally; however, strong data deduplication techniques that extend beyond n-gram overlap—such as semantic deduplication or MinHash/LSH deduplication that operates on very small values of n-gram—could potentially mitigate this at the pre-training level. > [Comments] It might make sense to mention again in the later sections that the case flip results only hold for later normalized text. Thank you for the suggestion! We will mention it in the updated version. --- Rebuttal Comment 1.1: Comment: I thank the authors for their rebuttal and will keep my score and opinion that the paper should be accepted.	Summary: This paper illustrates numerous challenges with the existing n-gram definition of membership in the LLM privacy community. They show that LLMs can output n-grams even if they have all been removed from the training data. They then show that the n-gram definition can be gamed by constructing training datasets which do not satisfy n-gram notions of membership but still yield the target completions. ## update after rebuttal After the rebuttal, in which I mainly asked the authors to clarify some details in the discussion, I keep my high score. Claims And Evidence: Yes, the claims are supported by the experiments. Methods And Evaluation Criteria: Yes, the methods used are standard in the LLM privacy literature. Theoretical Claims: N/A Experimental Designs Or Analyses: Yes, the experimental setup for all experiments seem rigorous. Supplementary Material: No Relation To Broader Scientific Literature: Much of the existing literature on LLM privacy has relied on notions of n-gram overlap to quantify membership for the training data. However, this submission challenges the validity of this metric by providing numerous experiments that show that n-grams can be reproduced even if all n-grams in the training data are removed. Essential References Not Discussed: N/A Other Strengths And Weaknesses: Strengths: 1. This paper is conceptually important and of broad interest for the LLM privacy and unlearning communities. 2. The paper is very well-written and lots of intuition is provided. 3. The authors do a very solid job of rigorously exploring these "lingering" sequences in the training data and linking them with simple generalizations. I could not find any serious weaknesses. Other Comments Or Suggestions: It might be useful to run the same experiments on an alternative pre-training dataset, or at least include a longer discussion on the choice of it. I think it might also be worthwhile to study how the main results on n-grams change for fine-tuning data. I would imagine that n-grams might be a better metric if the finetuned data is extremely unlikely, i.e. a hash is unlikely to be reconstructed unless it is included in the training data. Questions For Authors: 1. Could the authors include more discussion on alternative definitions and tests for membership? 2. How would the results change in the fine-tuning regime? 3. Could you report CIs on important results, i.e. Table 1 and Figure 3? Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: We thank the reviewer for the positive assessment of our work! We’re glad that the reviewer finds the work rigorous, well-written, and of broad interest to the community. We hope to address comments below, and would appreciate the reviewer’s consideration. > It might be useful to run the same experiments on an alternative pre-training dataset, or at least include a longer discussion on the choice of it. We fully agree with the reviewer. For example, it would be interesting to examine math/code-heavy datasets to observe possible new behaviors in the “lingering sequences”. We chose FineWeb since it is a state-of-the-art, open dataset, and it is sufficiently large to provide high confidence in the generalizability of our findings. Since pre-training experiments are very costly, we were unable to extend our results to other pre-training sets while maintaining a similar degree of comprehensiveness. We will add this discussion in the updated version. > It might also be worthwhile to study how the main results on n-grams change for fine-tuning data … a hash is unlikely to be reconstructed unless it is included in the training data This is an interesting direction. Indeed, one axis we did not fully explore in this work is the spectrum of “entropy” of sequences, and how it relates to completion; hashes (or random character strings) constitute the high entropy end of the spectrum. Our removal experiments (sec 4) partially addresses this: the lingering sequences that persist after applying strong filters (e.g., n-gram=5) are of “lower entropy” (following more predictable patterns) compared to sequences that persist at higher thresholds (e.g., n-gram=50). > [Q1] Could the authors include more discussion on alternative definitions and tests for membership? Thank you for the suggestion! - On definition. A key message of our work is that “membership” in LLMs extends beyond simple set membership of text in the raw dataset (Intro); it includes data neighborhoods (“soft membership”) arising from LLM generalization, data provenance, preprocessing, and other auxiliary information available throughout the training pipeline. We believe that a precise definition may require a standalone framework and supporting experiments, and consider this important future work. - On tests. Our results suggest that the “completion test” seems robust, in that it captures exact n-gram membership, near-duplicates (Sec 4), scattered information about a sequence in the training set (Sec 5), and other generalization behaviors by the LLM. We hope to explore other tests in future work. We will incorporate these discussions in the updated version. > [Q2] How would the results change in the fine-tuning regime? We assume that the reviewer refers to extending the removal experiments (sec 4, the study of “lingering sequences”) to the fine-tuning regime (sec 5). Our intuition is that our paper effectively demonstrates the remarkable ability of LLMs to generalize from “neighboring” text, where the neighborhood spans text space (e.g., Fig 8), token space (e.g., Table 21), and even semantic space. From this angle, we expect “lingering sequences” to also exist in the fine-tuning regime as long as their “neighbors” exist. We hope to explore this in future work and will add this as discussion. > [Q3] Could you report CIs on important results, i.e. Table 1 and Figure 3? We appreciate the reviewer’s suggestion! Since every point in Table 1 / Fig 3 corresponds to a pre-training run from scratch (33B tokens), it was computationally prohibitive to repeat all settings. That said, we report 5 repeated runs for the 1.6B parameter model in Appendix A.9; we find that the error bars are fairly small. --- Rebuttal Comment 1.1: Comment: Thank you for your detailed rebuttal. I keep my score.	Summary: The authors present a study on the ability of LLM to generate and complete verbatim text, which they were not explicitly exposed to during training. They start by challenging the n-gram overlap membership, showing how redacting samples filtered using this criterion does not hinder LLMs' capability to generate these sequences verbatim. They then continue showing how to generate adversarial samples with no n-gram overlaps with a reference sequence that, when used for model training, allows LLMs to complete the reference sequence verbatim. Claims And Evidence: The authors rightly raise concerns about the usage of n-gram membership, as it is associated with high rates of false negatives and fails to consider broader notions of membership. I'm less aligned with the conclusions on machine unlearning and the possibility of generating adversarial examples easily. As reported in the manuscript, the completions and verbatim reproductions are due to the inconsistency of n-gram membership ("near duplicates, sequences with m < n-grams that are not removed or are explained by the model’s generalization capabilities"). Hence, models can reproduce completion verbatim because they interpolate using similar examples that are trivially different from target sequences. Similarly, the generation of the adversarial samples is designed following the definition of n-gram-based membership. This membership definition is faulty and allows for generating slightly perturbed trivial samples that allow, once the model is trained on them, to interpolate "unseen" sequences. Methods And Evaluation Criteria: As stated above, while the experiments on highlighting the limitations of n-gram membership are interesting, the following experiments on generative adversarial examples are somehow not surprising and do not provide additional insights. Theoretical Claims: No theoretical claims or proofs provided. Experimental Designs Or Analyses: As hinted in previous sections on "Claims And Evidence" and "Methods And Evaluation Criteria", the experiments reported in section 5 are designed to prove a point that is somehow already addressed by showing the inconsistency of relying on n-gram membership. Moreover, the strategies proposed to generate adversarial samples (especially case-flipping) expose the model to slightly noisy versions of the sequences that are then tested for verbatim generation. Supplementary Material: Inspected the appendix when the main manuscript referred to parts of it that were supporting statements in the main manuscript. Found particularly useful the section defining the n-gram data filtering formally. Relation To Broader Scientific Literature: Despite the relevance of investigating LLM behavior and concerns/risks linked to the possibility of reconstructing data, the nature of the contribution and the way it is presented have limited impact. Essential References Not Discussed: I'm not aware of any essential related work not referenced. Other Strengths And Weaknesses: Besides what is already highlighted in previous sections, I believe the paper nicely sets the stage for a problem, i.e., the need for better membership definition when considering datasets for LLM training and evaluation, but then misses the opportunity to suggest or propose mitigation strategies or better ways to define membership. Other Comments Or Suggestions: I strongly recommend that the authors reconsider the paper structure and present the work as a perspective/position paper. After raising concerns about n-gram-based membership with the experiments they have already conducted, they could outline and present strategies to overcome such limitations. This contribution can be highly relevant to the scientific community. Questions For Authors: No further questions besides the comments. Code Of Conduct: Affirmed. Overall Recommendation: 2	Rebuttal 1: Rebuttal: We appreciate the reviewer’s time and effort! We understand & address the concerns below and would appreciate the reviewer’s consideration. > [Claims & evidence] less aligned with the conclusions on unlearning We wish to clarify that: - Unlearning serves many goals, one is output suppression [1]. - Our experiments (Sec 4) match the “golden baseline” of unlearning: removing target sequences and re-training from scratch. - Our conclusions on unlearning (Sec 6) directly follow Sec 4.2: even this golden baseline is insufficient for output suppression. The reviewer may be concerned that our data removal wasn’t thorough; in Fig 3 / Sec 4.2 we show that this golden baseline is insufficient even under strong filters that account for many near-duplicates. [1] https://arxiv.org/abs/2412.06966 > [Methods & eval] … generative adversarial examples are somehow not surprising > [Experimental design] Sec 5 experiments repeat points from n-gram membership inconsistency We clarify that our removal (Sec 4) and addition (Sec 5) experiments are complementary in challenging n-gram membership: - The insufficiency of removing n-gram members (Sec 4) illustrates natural “non-member” completions as part of model training (e.g., ineffective data cleaning); - The feasibility of adding n-gram non-members (Sec 5) illustrates adversarial “non-member” completions that exploit this property (e.g. hard-to-detect backdoors by the model developer, or data poison by 3rd party). We provide concrete demonstrations and recipes in Sec 5 in part to make limitations of n-gram membership easier to compare rigorously and reproduce across publications. > [Relation to literature] …the nature of the contribution and the way it is presented have limited impact. We emphasize that the simplicity of our findings does not take away their significance. We defer to: - Reviewer 7JNu: “The work … opens up further discussions … [for] increasingly relevant topics with larger LLM adoption.” - Reviewer J1BJ: “[this work] demonstrates that the community should strengthen the methods they use to determine data membership.”; “The paper … would be important to the community.” - Reviewer aZwA: “Much of the existing literature on LLM privacy has relied on notions of n-gram overlap”; “This paper is conceptually important and of broad interest for the LLM privacy and unlearning communities.” While the limitations of n-gram membership may be folklore knowledge, we provide the first systematic study of its failure modes which we hope is useful for the community. > [Claims & evidence] … (less aligned with) the possibility of generating adversarial examples easily … > [Experimental design] … the strategies … expose the model to slightly noisy versions of the sequences … We appreciate the reviewer’s viewpoint. We first clarify that: - Adversarial sequences are easy to generate. Simple perturbations (in both token-space and text-space) are sufficient (Sec 5). - Adversarial sequences are not “trivially different”. Tables 19, 21 (appendix) illustrate that “trivial” differences in token space can result in vast differences in text space due to BPE tokenization. This is important as such sequences may, e.g., evade human inspection. Note that case-flipping is but one simple, pathological choice we explore that avoids n-gram overlap in token space. In line with Reviewer J1BJ, we imagine many other transformations; e.g., shuffling token ordering, multi-lingual replacement, and token replacement within a restricted corpus. Our key message is that these transformations are easily extensible, allowing room for evolving adversaries and defenses. > [Other strengths and weaknesses] the paper nicely sets the stage … but then misses … mitigation strategies > [Other comments] … they could outline and present strategies to overcome such limitations. We appreciate the reviewer’s positive assessment of our experiments and framing! We hope our work is also judged by how it opens up an important yet underexplored discussion on data membership. We agree with the importance of mitigations. Our paper’s key message is that LLM “membership” extends beyond set membership of text in the raw dataset (Intro)—it also includes data neighborhoods due to generalization, provenance, preprocessing, and other auxiliary information throughout the training. A precise definition (and mitigation) may require a standalone framework and supporting experiments, which we consider as important future work. > [Other comments] Recommendation as a perspective/position paper. We thank the reviewer for the suggestion! We believe that our paper is better suited for main track since: (1) our work emphasizes systematically demonstrating the limitations of n-gram membership, rather than advocating a position; and (2) a position paper emphasizes conceptualization whereas our paper goes beyond and proposes new methodology and empirical experimentation. --- Rebuttal Comment 1.1: Comment: Thank you for the detailed rebuttal. I appreciate the fact that authors reiterated the main points from the paper, but my concerns on the nature of the contribution remain, so I will keep my score. --- Reply to Comment 1.1.1: Comment: Dear Reviewer vJUh, Thank you again for your engagement and feedback. We understand and appreciate your concern. We believe that we responded to your concerns point-by-point logically and faithfully (not just "reiterated the main points from the paper"), and would really appreciate if you could let us know if there’s anything else we could add for your consideration. Thank you!	Summary: This paper demonstrates LLMs may generate verbatim versions of text that is not included in their training data as measured by n-gram membership tests. After demonstrating this, they examine some possible reasons why this may be and show that it is possible to adversarially inject samples into training data in such a way that they are not measured as being included by existing membership tests, but may still be generated by LLMs trained on the data. Claims And Evidence: The main claims are: 1. LLMs can generate text verbatim that n-gram membership tests fail to recognize 2. It is possible to perturb verbatim texts in such a way to obtain this behavior My evaluation is as follows: ## 1. Verbatim generations ## This claim is well shown. The authors demonstrate that it is possible to remove training data from models using n-gram filtering and yet still see verbatim generations of the text when prompting the model with relevant prefixes. Upon investigation they discover that this is not because the model is truly able to generate this without training data, but rather because smaller pieces not detected by the n-gram filter are still present in the training data. This is thoroughly explored across a variety of filter sizes, demonstrating the impact how filtering is done. ## 2. Training data perturbations ## This claim is also well demonstrated. The authors devise a series of perturbations to the training data that allow target texts to still be present in the training data while remaining undetected by n-gram filtering. This includes splitting text across multiple data locations, removing chunks of text, and flipping the case of random characters. They observe models trained on this data can generate verbatim completions of the texts, despite the perturbation. They further explore the impact of how extreme the perturbations are to the LLM ability to generate completions. Methods And Evaluation Criteria: The evaluation methods are reasonable. Though the authors test on a limited set of texts when poisoning datasets, they are able to replicate results across different texts, indicating that it is likely not due to specific qualities of the text. They evaluate commonly used membership tests using different settings as well. Theoretical Claims: N/A Experimental Designs Or Analyses: The experiments appear well designed to me. Membership tests are performed across a variety of n-gram lengths, and multiple examples of completions are observed for non-members. This allows quantification of how choice of n impacts this discrepancy. When testing methods of adversarially adding data to the training set, the perturbations are intuitive and plausible (e.g. a case flipped sample would still be recognized as source text by a human, but not by a language model), demonstrating easy ways that this poisoning could occur. Supplementary Material: I reviewed the examples and visualizations in the supplementary material. Relation To Broader Scientific Literature: This paper relates to privacy, memorization, and unlearning literature for LLMs. It contributes by examining how effective n-gram measures of membership, which are commonly used for testing whether a model has regurgitated training data, actually work. By highlighting settings where these measures fail, it demonstrates that the community should strengthen the methods they use to determine data membership. Essential References Not Discussed: Not that I am aware. Other Strengths And Weaknesses: # Strengths The premise of the paper is well motivated and explored. The experiments detail methods to elicit the behavior as well and provide explanations for why n-gram membership tests fail. The paper is generally clear and well written and would be important to the community. # Weaknesses Only GPT-2 models are considered, due to training feasibility. While understandable, it would be good to see how this applies to other models, particularly those that have been fine-tuned to not generate certain text due to copyright or privacy concerns. Other Comments Or Suggestions: Addressed in other sections. Questions For Authors: 1. How is human detectability measured for the adversarial samples? 2. Do you test shuffling the order of the base text in any experiments? It appears in the perturbations presented that the order is maintained (though dropout or distance is added), which may make the "repair" task of the model easier, but could also be a tool for detection if ordering is important. Code Of Conduct: Affirmed. Overall Recommendation: 5	Rebuttal 1: Rebuttal: We appreciate the reviewer’s positive assessment of our work! We’re glad that the reviewer finds the paper well-motivated, well-written, and important to the community. We address the comments below. > [Weakness 1]: Only GPT-2 models are considered, due to training feasibility. While understandable, it would be good to see how this applies to other models, particularly those that have been fine-tuned to not generate certain text due to copyright or privacy concerns. We appreciate the reviewer’s suggestions! We’d like to note that we also explored Gemma and Qwen models for the adversarial / fine-tuning experiments (Sec 5), and we agree with the reviewer that exploring models other than GPT-2 would be useful for the pre-training experiments (Sec 4) if we had additional compute. Models that are specifically fine-tuned to avoid certain text (e.g. models that were applied post-hoc unlearning) sound interesting; we hope to explore this in future work. > [Q1]: How is human detectability measured for the adversarial samples? The reviewer raises a good question. We interpret “human detectability” as distinguishing original sequences from adversarially perturbed samples (Sec 5). Due to scope limitations, we did not conduct large-scale human studies on detectability; we primarily relied on manual inspection of generated samples (visualized in Tables 18–21), finding examples such as those in Table 21 difficult to discern by us without the original context. We agree with the reviewer that it could be a valuable extension. > [Q2]: Do you test shuffling the order of the base text in any experiments? We appreciate the reviewer’s suggestion! Among all possible noisy transformations (recall the beginning of Sec 5), we explored only the three presented. Shuffling text order is indeed a valid and straightforward strategy that could easily complement our proposed transformations. More broadly, we imagine the class of transformations can be easily expanded upon; for example: - Chunk shuffling; - Multi-lingual replacement (semantic equivalents from other languages); and - Token replacement within a restricted corpus (e.g. a fixed book, thus the perturbed sequences look like this book). Because models get better at completions with scale (Fig 6), we hypothesize that larger models can accommodate even noisier strategies. We hope to explore in future work.	null	null	null	null	null	null
Near-optimal Sketchy Natural Gradients for Physics-Informed Neural Networks	Accept (poster)	Summary: This paper proposes SNGD, a sketched version of natural gradient descent (NGD), for training PINNs. SNGD uses sketching to scale a previous optimizer, ENGD, to larger neural networks for PINN training. The authors evaluate SNGD against Adam, BFGS, and NEGD on several benchmark problems and demonstrate that SNGD outperforms the competition. ## update after rebuttal I thank the authors for responding to my questions and comments on their paper. However, I still believe that my concerns about the experiments have not been adequately addressed. For example, the authors say that they can compare to the results in “Challenges in Training PINNs: A Loss Landscape Perspective”, but this might not be a good comparison due to differences in network architecture, hyperparameters, etc. I am inclined to maintain my score at this time. Claims And Evidence: Bottom of page 3: “the matrix $\mathbf{G}$ should be rank-deficient”. The expression (6) for $\mathbf{G}$ is an integral over the domain and boundary. In this case, why should $\mathbf{G}$ still be rank-deficient? However, I believe that $\mathbf{G}$ should be rank-deficient for the discretized PINN objective, which is what we actually optimize in practice. Figure 1: Does this exponential trend in the eigenvalues of $\mathbf{G}$ hold for other problems? Moreover, which PDE does Figure 1 correspond to. Top of page 5: Why is the asymptotic upper bound of $10^{-16}$ valid? To make $\lambda_{r + 1}$ small, $r$ might have to be large, which could make $C(p, r, e)$ large. I disagree with the authors' claim that CG-type methods can’t be used to solve the linear system. I agree that vanilla CG would struggle due to the lack of preconditioning. However, preconditioned conjugate gradient could greatly accelerate convergence within the linear system step. For example, a low-rank preconditioner could be incredibly helpful due to the spectral decay shown in Figure 1. Please see “Randomized Nystrom Preconditioning” (SIMAX 2023) for an example of such a preconditioner. What are the per-iteration complexity and memory requirements of SNGD? This is important to include so practitioners can understand whether Algorithm 1 will scale to their problem. In what sense is the error in section 4.1 “near-optimal”? How do we know that a different sketching strategy can’t obtain a better error bound? Methods And Evaluation Criteria: The algorithm itself makes sense for PINNs, since several previous works have shown that better optimization algorithms can lead to lower errors in solving PDEs. I’m concerned that the benchmarks in sections 5.1 to 5.3 are too simple. The analytical solutions for these benchmarks do not have high-frequency components, which suggests that they are relatively easy to solve. Perhaps the authors should run their experiments on other challenging settings, such as the wave equation from “On the eigenvector bias of Fourier feature networks: From regression to solving multi-scale PDEs with physics-informed neural networks” (Computer methods in applied mechanics and engineering 2021). Theoretical Claims: I don’t think Lemma 3.1 shows that the eigenvalues decay exponentially. Since the rate of decay is $j^{-4}$, the decay would actually be polynomial. For completeness, I would also recommend the authors provide a proof of Lemma 3.1 in the supplementary material, in addition to the proof sketch they provide in the main paper. Experimental Designs Or Analyses: Is the comparison in Table 2 fair? Table 2 makes it seem like Adam is slower than SNGD in the paper, but Adam is also run for 40 times as many iterations as SNGD. Why is Adam omitted from the experiments in sections 5.2-5.4? I think the authors should also include Adam in these experiments in order to really demonstrate that their method is better than other optimizers for PINNs. I’m concerned by the authors not running L-BFGS in their experiments. L-BFGS is used more often than BFGS for training PINNs, since L-BFGS has a much lower memory requirement than BFGS. For example, “Characterizing possible failure modes in physics-informed neural networks” (NeurIPS 2021) and “Challenges in Training PINNs: A Loss Landscape Perspective” (ICML 2024) both use L-BFGS in their experiments, not BFGS. Without comparisons to L-BFGS, it is hard to say whether SNGD is actually a better method for PINN training. How does single-pass SNGD perform on the transport equation? I would like to know how single-pass SNGD performs in this setting, since single-pass seems to outperform two-pass on the other benchmarks in the paper. Supplementary Material: I skimmed both Appendix A and Appendix B. Appendix B: “There are modifications at the boundary grid points that we will not be careful with here.” Why is it reasonable to leave these modifications out of the analysis? This requires more justification. Appendix B: Why use the ReLU activation? I thought PINNs do not use ReLU activations in practice. Appendix B: What makes the result around line 755 “somewhat unexpected”? Relation To Broader Scientific Literature: To the best of my knowledge, the algorithm proposed in the paper is new. Given that PINNs are challenging to optimize, the algorithm proposed in this paper could be useful to practitioners. Despite my criticisms of the paper, I applaud the authors’ effort in developing a new optimizer for PINNs. Essential References Not Discussed: The paper is missing two key references: “Sketch-Based Empirical Natural Gradient Methods for Deep Learning” (Journal of Scientific Computing 2022) and “Challenges in Training PINNs: A Loss Landscape Perspective” (ICML 2024). The “Sketch-Based” paper introduces SENG, which uses sketching-based techniques to approximate the natural gradient (although the sketching technique they use is different from the one in this submission). The “Challenges” provides an in-depth analysis of optimization challenges in PINNs and also proposes a new optimizer for PINN training, so it should also be discussed in the introduction and/or related work. Other Strengths And Weaknesses: In general, I believe the presentation of the sketching-based approach could be improved. For example, the authors should say what kind of sketching-based technique they are using (I believe it is the randomized SVD, but please correct me if I am wrong). Other Comments Or Suggestions: I would recommend enabling hyperlinks to citations, figures, tables, etc. For example, when I click on a citation in the main text, it should take me to the appropriate location in the references. There should be a period at the end of the second paragraph in the introduction. There should be a space between “Descent” and “(SNGD)” at the top of Algorithm 1. Is there a typo in the single-pass step in Algorithm 1? I believe both $\mathbf{Q}$ and $\mathbf{M}$ have size $\|\theta\| \times (p + r)$, and this would mean that the matrix product $\mathbf{Q} \mathbf{M}$ is invalid. The line search for $\eta^\star$ should use $\theta_i$ instead of $\theta$. Questions For Authors: N/A Code Of Conduct: Affirmed. Overall Recommendation: 1	Rebuttal 1: Rebuttal: We thank the reviewer for the many helpful suggestions, for their careful and detailed comments and for the positive comment about the novelty and utility of the work. Claims And Evidence: - If we understand your comment correctly, we believe that our observation about rank deficiency is completely in line with your observation about discretization. Indeed, the expression for (6) describes the continuous form of the matrix before discretization, while $\mathbf{G}$ refers to the matrix that we get under an appropriate discretization of (6). We use the convention of denoting continuous objects with calligraphic font and their discretized counterparts as bolded objects. We have added a sentence to clarify this notational convention. - At the top of section 3, we state that Figure 1 corresponds to an experiment from section 5.4. This info has been added to the caption. The exponential decay of the eigenvalues of $\mathbf{G}$ is a feature that we observed across all of the experiments presented in the paper. This is briefly mentioned in section 3. Given your comment, we added a sentence stating this at the start of section 3 to clarify this. - The constant $C(p,e,r)$ is polynomial in $r$. Our case has the ideal feature of exponential decay in the eigenvalues, which means that for $r$ sufficiently large, the decay is rapid enough to beat the polynomial growth of $C$. We have added a sentence at the top of page 5 to explain this. - In our setting, $\mathbf{G}$ is dense with $\|\theta\|^2$ entries, and computing its matrix-vector products is prohibitively expensive. These require computing nested auto-diffs of the residual w.r.t. each parameter. This would need to be computed anew in every CG iteration. Therefore, we opt for directly sketching $\mathbf{G}$. In “Randomized Nystrom Preconditioning” the authors explicitly caution that in order for Nystrom preconditioning to be effective, matvecs must be reasonable in terms of computational cost. However, we speculate that a low-rank preconditioner might have, in some ways, a similar effect to the benefits gained by cutting off the smallest eigenvalues via sketching. - We really appreciate this question and thank the reviewer. We will update the manuscript to include this information. The memory requirement for NEGD is $\mathcal{O}(\|\theta\|^3)$ and for SNGD it is $\mathcal{O}(\|\theta\|(p+r))$. Focusing on the computational cost of the solve per iteration, least squares costs $\mathcal{O}(\|\theta\|^3)$ for ENGD, whereas Algorithm 1 has a cost $\mathcal{O}(\|\theta\|(p+r)^2)$ when $\|\theta\|$ is large enough. - The error bound is “near-optimal” in the sense that due to the exponential decay of the eigenvalues of $\mathbf{G}$, we can pick a tolerance that guarantees that the error is close to machine precision. We feel that given the nature of the decay, it is fair to characterize the error in this way. Methods And Evaluation Criteria: We thank the reviewer for this comment and agree with their assessment. We are working on a benchmark for a more challenging problem and appreciate the reviewer’s suggested additional benchmark problem. We will do our best to update the manuscript to include both of these. Theoretical Claims: The decay rate for ReLU is polynomial; however, when using analytic activation functions the decay rate becomes exponential. Please see the discussion near Lemma 3.1. Experimental Designs Or Analyses: - Because ADAM is a first-order optimizer, it cannot achieve the high level of accuracy of SNGD, even when given 40 times more training iterations. Given only 1,000 iterations, it would not reduce the loss or error much. Adam is omitted from sections 5.2-5.4 because PINNs often perform better with the use of second-order optimizers. However, we appreciate the reviewer’s concerns and will add ADAM to 5.2-5.4. - In our experiments, BFGS was more accurate than L-BFGS, so we omitted the latter. We would like to briefly note that although we don’t use L-BFGS in 5.4, we can compare to “Challenges in Training PINNs: A Loss Landscape Perspective”, which uses the same benchmark problem. They report an error of $\mathcal{O}(10^{-1})$ for a PINN using L-BFGS. In our manuscript, both BFGS and SNGD outperform this result. - We agree this should be included and will update the manuscript. We thank the reviewer for their suggestion. Essential References Not Discussed: We thank the reviewer for these helpful suggested references and have added them to the related work section of the paper. Other Strengths And Weaknesses: We agree that the presentation of the sketching-based approach should be improved. We are indeed using classical randomized SVD (in our case, an eigenvalue decomposition). We have clearly stated this in the manuscript and expanded our explanation of the sketching method. Other Comments Or Suggestions: We thank the reviewer for pointing these out. We have fixed each error and enabled hyperlinks.	Summary: This work improves the computational efficiency and estimation accuracy of NEGD by leveraging the structural properties of the Gram matrix and introducing the classical RSVD method. It effectively addresses the high storage and computational costs associated with the Gram matrix while also enhancing the neural network’s ability to learn high-frequency components. ## Update after rebuttal The authors claim their contribution lies in analyzing the matrix structure and linking it to known error bounds from randomized numerical linear algebra, stating this is novel in the context of natural gradients for PINNs. However, from my perspective, the proposed method is essentially a straightforward application of RSVD to NEGD, and the spectral error bounds discussed are drawn from existing literature. Based on both the paper and the authors’ rebuttal, I do not see a clear advantage or new theoretical insight specific to the combination of RSVD and PINNs. Therefore, I find the theoretical contribution to PINNs limited and maintain my original scores. Claims And Evidence: The core argument of this paper is that introducing randomized sketching techniques for PINNs optimization can enhance both the computational efficiency and accuracy of the NEGD method. This claim is validated through extensive numerical experiments, where the proposed method is compared against ADAM, BFGS, and ENGD. However, one concern remains: Sections 5.2–5.4 present experimental results showing that SNGD outperforms BFGS and ENGD in both efficiency and accuracy. Why is there no comparison with the ADAM method in these sections? Methods And Evaluation Criteria: Yes, this work proposes a new method that addresses the computational bottleneck in PINNs and improves estimation accuracy. Theoretical Claims: This paper does not provide novel theoretical results and does not verify any proofs. Experimental Designs Or Analyses: Yes, I have reviewed the experimental content and results in Section 5, and overall, they appear reasonable and effective. However, the following concerns remain: 1. Section 5 demonstrates SNGD's superior performance over NEGD, ADAM, and BFGS across multiple examples. While the paper acknowledges the impact of $tol$, p on algorithm performance, it does not specify their values for each experiment. Providing these parameter values would enhance the reproducibility of the results and strengthen the credibility of the findings. 2. Table 1 shows that both SNGD and ADAM achieve similar accuracy on the 5,000-parameter (A2) and 1,000,000-parameter (A3) networks. However, this does not fully demonstrate SNGD's scalability, as it is unclear whether A2 and A3 use the same p+r. If they differ (e.g., if A3 uses a larger p+r, meaning the sketching matrix M has a higher dimension), this conclusion may lack sufficient credibility. Could you provide a more detailed explanation? Supplementary Material: This paper does not provide supplementary materials. A brief check of Appendices A and B raised no concerns. Relation To Broader Scientific Literature: The paper introduces the advantages and challenges of PINNs, discusses the research progress of commonly used solution algorithms, and analyzes their strengths and weaknesses. Among them, NEGD (Müller & Zeinhofer, 2023) currently achieves the highest estimation accuracy. However, NEGD suffers from high computational complexity. To address this, the authors employ single-pass and two-pass sketching techniques from Saibaba et al. (2016) to improve both the computational efficiency and estimation accuracy of NEGD, proposing a new method called SNGD. Essential References Not Discussed: The paper "Streaming low-rank matrix approximation with an application to scientific simulation" introduces a more efficient single-pass RSVD algorithm than Saibaba et al. (2016), yet this work does not mention it. Given that the study employs RSVD to accelerate NEGD computation, why not adopt the more efficient single-pass RSVD from that work? Could you clarify this choice? Another common approach for accelerating over-parameterized iterative estimation using randomized sketching techniques is RSN (see RSN: Randomized Subspace Newton). Given the iterative estimation structure used in this paper, RSN may have a lower computational complexity than RSVD. In addition to utilizing dense Gaussian matrices, RSN allows the use of sparse or orthogonal sketches, which could offer additional computational benefits. To further strengthen the contributions of the paper, I suggest comparing the RSN method with the RSVD-based approach introduced in this work. A thorough comparison could better illustrate the advantages of using RSVD for gradient descent acceleration and preconditioning, particularly from the perspective of spectral bias analysis. This would enhance the practical significance and applicability of the conclusions presented in the paper. Other Strengths And Weaknesses: Strengths The paper proposes the SNGD method by incorporating randomized sketching techniques, which improve both the computational efficiency and estimation accuracy of NEGD. Weaknesses 1） However, the SNGD approach primarily relies on a direct application of the classical randomized SVD (RSVD) algorithm for low-rank approximation of the Gram matrix. While this method is straightforward, the paper does not fully demonstrate the advantages of integrating RSVD with NEGD compared to other estimation techniques. The methodological innovation appears somewhat limited. Could you provide deeper insights and conclusions about the SNGD method, beyond those merely derived from existing low-rank approximation results? 2） This work does not adopt the more efficient single-pass RSVD from "Streaming low-rank matrix approximation with an application to scientific simulation" to accelerate NEGD computation. Other Comments Or Suggestions: 1. line 68: The first occurrence of NEGD should follow the standard convention of writing the full term followed by the abbreviation in parentheses. 2. line 226: $G^{-1}_{(p+r)}$-> $ \hat G^{\dagger}_{(p+r)}$ 3. lines 298-299: Ensure consistency in the naming of methods in experimental comparisons: In Table 1, update "ONE"-> "SINGLE-PASS" and "TWO" -> "TWO-PASS". 4. line 175: There is an error in Algorithm 1, specifically in the single-pass step. The formula $ (QM)^{-1}$ is incorrect as the dimensions do not match. 5. Please ensure uniform formatting of references, particularly in paper titles, where only the first word should be capitalized, and the rest should be in lowercase. Questions For Authors: 1. Does Equation (7) have an extended version specifically for the two-pass method mentioned in Algorithm 1? Equation (7) cannot be directly used for the two-pass update: $T <- Q^GQ $ 2.The approximation $(\sum^n_{j=r+1}\lambda^2_j)^{1/2}\approx \lambda_{ r+1}$ and the error bound $E\\|G-\hatG_{p+r}\\|\lesssim10^{-16}$ hold only under the assumption that tol is set to 10^{-16}. However, the paper does not provide a theoretical guarantee that tol should be precisely 10^{-16}. Currently, this assumption is only supported by the experimental results in Figure 1, which may not be sufficiently convincing. Could you provide a more detailed explanation of how the threshold tol is determined? A more rigorous justification would strengthen the validity of the two formulas above. 3. Section 5 claims that Section 4.1 explains why the training process is much less sensitive to the oversampling parameter p, but this explanation is unclear. Could you clarify this point more directly? 4. This paper applies randomized SVD to approximate the Gram matrix, improving computational efficiency. Section 5 shows that SNGD, using \hat G, outperforms NEGD with exact G in both efficiency and accuracy. Could you clarify in the main text why randomized SVD enhances NEGD’s estimation accuracy? A stronger explanation would reinforce the experimental conclusions and highlight the paper’s contributions. Code Of Conduct: Affirmed. Overall Recommendation: 2	Rebuttal 1: Rebuttal: We thank the reviewer for their helpful and detailed suggestions and comments and the time and effort they put into reviewing our manuscript. Experimental Designs Or Analyses We will add comparisons with ADAM to 5.2-5.4. At the end of section 5, we specify how $p$ is chosen and set the tolerance to 1E-13 across all experiments. The sketching size changes at each iteration of training adaptively as the rank grows during training as a result of the underlying parameter space, and therefore, we cannot directly compare sketching sizes for different architectures. Essential References Not Discussed Regarding “Streaming …” please see the comment (2) under Weaknesses below. Regarding RSN: We agree with the reviewer that it would be interesting to compare RSN to SNGD, but we believe the computational complexity of SNGD to be either similar or lower than RSN. Both RSN and SNGD require a randomized approximation: RSN requires the Hessian of the loss at every iteration of training, and SNGD requires the matrix $G$ at every iteration of training. The Hessian entails computing the second derivatives w.r.t. the parameters of the loss function, which depends on the PDE residual, and $G$ requires computing the first derivatives w.r.t. the parameters of the PDE residual itself. Moreover, for SNGD, the sketch $GM$ can be computed efficiently via equation (7). Weaknesses 1) The main innovation is that we identify and exploit spectral structure inherent to the matrix $G$ to develop a fast, memory-efficient, and accurate natural gradient method. The structure of $G$ is the best-case scenario for the approximation capacity of RSVD, due to the exponential decay of the eigenvalues, which guarantees error near machine precision. Previously, NEGD was limited to only very small neural networks. Therefore, our work represents a significant advance. We will consider more sophisticated estimation techniques in future work. 2) We don't believe our use case falls into the streaming framework: gradient descent iterations do not follow a known linear update (see more details in the next paragraph). We employ the methods recommended by the same authors in the related paper “Fixed-Rank Approximation of a Positive-Semidefinite Matrix from Streaming Data”, designed specifically for PSD matrices (such as $\mathbf{G}$). On page 3, they state that in the absence of constraints such as streaming, they recommend the general-purpose methods we use. Concretely, to clarify why updates to $G$ do not follow a known linear map, notice that $\mathbf{G}\_{i+1}$ depends on $\left( \partial{\theta\_k} \circ \mathcal{D}\right) \left[ u\_{\theta}(\theta\_{i+1})\right]$ through equation (6). We can write $u\_\theta(\theta\_{i+1}) = u\_\theta\left( \theta\_i - \eta \mathbf{G}^{\dagger}(\theta\_i)\nabla\_{\theta}L(\theta\_i) \right)$. Because $u\_\theta$ is non-linear, the relationship between $\mathbf{G}\_{i+1}$ and $\mathbf{G}\_i$ is non-linear. We are not aware of a way to express $\mathbf{G}\_{i+1}$ as $\mathbf{G}\_{i+1} = \eta\mathbf{G}_i+ \nu \mathbf{H}$. Other Comments Or Suggestions We thank the reviewer and have updated the manuscript to fix each error. Questions For Authors 1. We have fixed a typo in Algorithm 1: $Q \gets Q[:,1:(p+r)]$, so $T = Q^{T} G Q$. 2. Lemma 3.1 shows that for a 1D, 1-layer network with analytic activation functions, the eigenvalues decay exponentially. We agree that the discussion of how to choose the threshold tol should be clarified and tied more directly to the error bounds and Lemma 3.1. Based on the exponential decay supported by Lemma 3.1 and by the empirical evidence, the tolerance is set s.t. $\lambda\_{j+1}$ is close to $10^{-16}$. 3. We agree that this point should be clearer. Because the error in equation 8 is bounded by $C(p,r,e) \lambda\_{r+1}$, it depends on the oversampling parameter only through a polynomial constant. When $r$ is sufficiently large, the exponential decay of the eigenvalues drives the error close to machine epsilon, and the oversampling parameter p does not make much of a difference. We have clarified this point in the main text. 4. We have added some discussion in the last paragraph of section 4. 1. Because the matrix $\mathbf{G}$ is ill-conditioned, computing the pseudo inverse via least squares introduces computational instability that is ameliorated by cutting off small near-zero eigenvalues. 2. In section 5.4, we compare the rank above the cut-off of 1e-13 of two-pass SNGD and the original ENGD and see that SNGD is able to find more directions in parameter space above this cut-off. This suggests that SNGD is finding a better and flatter local minimum, which is a phenomenon that has been observed to be useful for generalization and related to spectral bias. Finally, the randomness introduced by multiplying by a Gaussian matrix at each training iteration and the mixing effect of Guassians contribute to the enhanced performance. --- Rebuttal Comment 1.1: Comment: Thank the authors for the detailed rebuttal. I have the following comments: - There are numerous sketch-based methods available to accelerate iterative algorithms. I suggest that the authors further explain the motivation for applying RSVD specifically to PINNs and elaborate on its advantages in this context. - From my understanding, the proposed method is essentially a direct application of RSVD to NEGD. The spectral error bounds discussed in the paper are derived from existing literature. While the paper demonstrates its applicability, it lacks new theoretical insights specific to PINNs. In particular, it does not present new theoretical results or analyses specific to PINNs, such as error bounds on the estimation of the model parameters $\boldsymbol{\theta} $. This makes the theoretical contribution of the paper somewhat limited. - Regarding the comparison with RSN, I will offer some my perspectives: In the context of RSN, the matrix$ \mathbf{G} $ in this work can be treated directly as the Hessian$\mathbf{H} $. As such, the RSN estimation formula $ \mathbf{S} \left( \mathbf{S}^\top \mathbf{G} \mathbf{S} \right)^\dagger \mathbf{S}^\top $ can be applied without needing to compute the second-order derivatives of the PDE residual with respect to model parameters. Therefore, the concern raised in the rebuttal regarding the computational cost of second-order derivatives may not be an issue. --- Reply to Comment 1.1.1: Comment: We thank the reviewer for taking the time to read our rebuttal and for offering additional comments and perspective. - We thank the reviewer for this suggestion and agree that we should more clearly motivate the use of RSVD, specifically for PINNs. One of the main advantages is the straightforward and well-developed error bounds when using RSVD to estimate matrices that have exponential decay in their eigenvalues. For this kind of matrix, the error bounds on the sketched approximation are near-optimal in the sense that they can be driven to near-machine precision. While there may be benefits to applying other sketching techniques, to the best of our understanding, the error bounds are already as good as possible in a double-precision computing environment. Iterative algorithms are an interesting direction and are a natural direction to explore in our setting, where $G$ scales as $\|\theta\|^2$, and we thank the reviewer for raising this. Here, we note that sketching and preconditioning would need to bring the number of iterations in the iterative scheme to below $(p+r)$. We favorably view the possibility of taking a hybrid approach where we switch to an iterative scheme at some point in training when $r$ is sufficiently large. We again thank the reviewer for this constructive comment and will certainly explore this avenue. - We appreciate the reviewer’s perspective. We believe that our paper provides a novel and useful contribution by studying and uncovering the important properties of the structure of the matrix $G$ and connecting these to error bounds from the randomized numerical linear algebra. To the best of our knowledge, in the context of natural gradients for PINNs, the insights we provide about the structure of $G$ are novel. We agree with the reviewer that the theoretical aspects of this work are somewhat limited in the context of PINNs, where our theoretical contribution that uncovers the spectral structure of $G$ is limited to the case of a one-layer, one-dimensional network. The state of available theory in this young paradigm makes it a bit difficult at the moment to develop decisive additional theoretical insights without making simplifying assumptions. We will, of course, continue to explore to the best of our abilities the theoretical benefits of our approach in the context of PINNs, as we continue to develop our method and apply it in other domains. - We thank the reviewer for offering their perspective. It should indeed be possible to use the estimation formula from RSN with $G$ instead of $H$. From our understanding, the difference between our method and using RSN with $G$ at each training iteration is that in RSN, given a sketching matrix $S$, the gradient is multiplied by $S(S^THS)^{\dagger} S^T$, whereas in our manuscript, we compute $GS$ and then use QR decomposition and eigenvalue decomposition to find the pseudo-inverse. We will need to further understand the benefits in terms of error and computational savings of approximating $ G^\dagger$ by $S(S^THS) ^\dagger S^T$ versus our approach. We thank the reviewer again and will explore this estimation technique.	Summary: The manuscript discusses the application of randomized numerical linear algebra to scale natural gradient methods for the training of physics informed neural networks (PINNs). More precisely, a randomized eigensolver is employed to solve the linear system in the natural gradient algorithm at every step. The authors demonstrate that this can be done efficiently and scalable, i.e., without the need to assemble the Gramian matrix. It is expected that this realization helps the widespread adoption of natural gradient methods for the training of PINNs. ## update after rebuttal I maintain my positive evaluation. Claims And Evidence: The claims made in the manuscript are properly substantiated. The numerical experiments are convincing. Methods And Evaluation Criteria: The setup of the numerical experiments is reasonable. Theoretical Claims: I did not check the theoretical result concerning the low rank of a two layer network. Experimental Designs Or Analyses: I checked the setup of all numerical experiments and they are reasonable. Supplementary Material: I read the Appendix. Relation To Broader Scientific Literature: The relevant literature is appropriately discussed. To the best of my knowledge, no relevant work is omitted from the discussion in the literature. The authors may however consider to discuss https://arxiv.org/pdf/2402.01868, which uses a Nyström method to design a preconditioner for a CG in Newton's method. As ENGD is different than Newton (and typically much more effective) I see no direct implications for the authors work. Essential References Not Discussed: See above. Other Strengths And Weaknesses: Weaknesses: - How does the low-rank structure of the Gramian change with varying sample size? Can the authors provide numerical experiments for this? Strengths: - The numerical results are convincing. It is very nice that a network with a million parameters can be trained in only a handful of minutes. Other Comments Or Suggestions: See below. Questions For Authors: 1. It is common practice to include damping into natural gradient methods, i.e., adding a scaled identity on top of the Gramian matrix. Can this be included in the solution approach? 2. The rank of the Gramian seems to grow with training iterations. Does this require larger sketch sizes in later stages of training? 3. Can the authors comment on the choice of randomized method? Why did you not employ Nyströms method which is taylored for psd matrices? 4. Can the authors provide some loss/error plots including statistics to showcase convergence of the optimizer? Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: We thank the reviewer for taking the time to review our manuscript and for their helpful suggestions, comments and questions. We greatly appreciate their positive assessment of our work. Relation To Broader Scientific Literature: We thank the reviewer for the suggestion and have included a brief discussion of this reference in the manuscript in the “related work” section. Weaknesses: Thank you for the suggestion. We will include some numerical experiments in a new appendix. As a preliminary answer: the low-rank structure of the Gramian relates to the phenomenon of Spectral Bias. Small eigenvalues of the Gramian correspond to high-frequency components that neural networks struggle to learn. The literature on spectral bias suggests that higher-frequency components need more sample points for effective learning than lower-frequency ones and that the spectrum of the Gram matrix may depend on the density of samples near these higher-frequency components. Questions For Authors: 1. Damping can be included in the solution approach, and we thank the reviewer for the suggestion. We will add it to future work. 2. The sketch size at each iteration of training depends on a fixed “over-sketch” parameter $p$ and on the computed rank of the sketched matrix $GM$ at the previous iteration of training. The sketch size is $p+r$ where $r$ is updated at each iteration of training. This means that the sketch size is adaptively growing to incorporate the growing rank of $G$ as training progresses. We thank the reviewer for this question and have added some explanation in the manuscript that makes this clearer and explains how the initial rank is estimated to initialize Algorithm 1. 3. - We agree that Nyström methods are a natural choice for further exploration. We appreciate the comment and hope to explore the benefits of Nyström methods in future work. As an additional comment, for Nyström methods that rely on repeated computation of a matrix-vector product, the computational cost of the nested auto-differentiation in $G$ is a major impediment. See the fourth comment under “Claims and evidence” in the response to reviewer nY1h for a more detailed discussion of this last point. - We elected to use one/two pass results from the classical randomized linear algebra literature for a couple of reasons. (1) First, to the best of our knowledge, error bounds for Nystrom methods are more subtle and depend on how columns are sampled. For our use case where we have a PSD matrix with exponentially decaying eigenvalues, error bounds for one/two-pass eigenvalue approximation show that by controlling the tolerance, we can drive the error close to machine precision. Second, because we can efficiently compute the sketch $ GM $ via equation (7), our manuscript already demonstrates the value of sketching for natural gradients in terms of both accuracy and scalability, with the added advantage of using a method that is easy to understand and implement. 4. We thank the reviewer for the helpful suggestion and have updated the manuscript to provide plots of the loss/errors during training to showcase the convergence. --- Rebuttal Comment 1.1: Comment: Thanks for your answer. I do not understand the following: "As an additional comment, for Nyström methods that rely on repeated computation of a matrix-vector product, the computational cost of the nested auto-differentiation in $G$ is a major impediment." Maybe it helps to clarify what exactly I mean with Nyström. I am referring to, for instance, this paper: https://arxiv.org/abs/2110.02820. Both, the theory and also the way to interact with $G$ seem to be reasonably clear. I don't see how your way of interacting with $G$ could be advantageous over the paper I mentioned. Can you clarify this? Otherwise, I retain my positive evaluation. --- Reply to Comment 1.1.1: Comment: Thank you for the question and for the reference. To the best of our understanding, our method is similar to what is being done in Algorithm 2.1 in the suggested reference. Specifically, what we’ve done is similar to the proposed Nyström sketch and solve. Indeed, we thank the reviewer for the suggestion; we intend to explore if there are advantages to specifically using the Nyström estimation, especially in the context of adding a damping term. For using Nyström PCG, unless we are mistaken, the cost involves first computing the randomized Nyström approximation to $G$ and then computing matrix products with $G$ and $p0$ at each iteration of PCG. The randomized Nystrom approximation, by itself, is similar in cost to our algorithm without the added cost of the additional matvecs in PCG. Considering only the cost of the matvecs, our interaction with $G$ is equivalent to $(p+r)$ matvecs.	Summary: This paper introduces a novel natural gradient descent method based on sketching. Instead of computing the search direction of the natural gradient exactly, the paper uses the sketching technique to compress the large Gram matrix into a smaller one with a random Gaussian matrix. The algorithm is interesting and theoretically sound. The theoretical analysis shows that the accuracy of the sketching approximation depends on the least eigenvalues of the Gram matrices, which typically exhibit eigenvalue decay. Additionally, the paper also conducts comprehensive experiments on comparing the proposed methods with ADAM and BFGS. Overall, this is a very interesting study! ## update after rebuttal I maintain my positive score. Claims And Evidence: Yes Methods And Evaluation Criteria: Yes. The natural gradient descent is not commonly adopted for training PINNs, mainly because of its high computational cost for the search direction (Gram matrices). This paper alternatively computes an approximate natural gradient direction by sketching. This technique, although is not new, should be effective and meaningful. Theoretical Claims: Yes. The proof supports the effectiveness of the sketching technique, under the condition that the eigenvalues of Gram matrices are decaying. Experimental Designs Or Analyses: Yes. Supplementary Material: NA Relation To Broader Scientific Literature: The algorithm proposed is not limited to training PINNs. I think it can be applied to broader deep learning applications. Essential References Not Discussed: NA Other Strengths And Weaknesses: NA Other Comments Or Suggestions: NA Questions For Authors: The algorithm proposed is not limited to training PINNs. I think it can be applied to broader deep learning applications. Do I understand correctly? Because the design of the neural network does not depend on the structures of PDEs or PINNs. So based on this, why does the paper only focus on applying it to PINNs? And also the title of the paper. Why is the method restricted to PINNs? Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: We thank the reviewer for taking the time to carefully review our manuscript and appreciate the positive review of our work. Questions For Authors: The proposed algorithm is, indeed, not limited to training PINNs. We began the paper by focusing specifically on improving the training of PINNs, and thus, all of our experiments are examples of PINNs. Our algorithm’s benefits depend on the matrix $\mathbf{G}$ structure, which exhibits exponential decay. This property is related to the spectral bias of neural networks and not explicitly tied to PINNs or the underlying PDE. However, the structure of PINNs tends to worsen spectral bias in ways that can be related to the underlying PDE [1]. In seeking to understand the performance of our algorithm, we discovered that our method may be more broadly applicable. We hope to explore this in future work. As a simple illustrative example, consider training a standard feed-forward fully connected neural network on a set of features and labels using mean squared error as the loss function. For this example, a different but related Gramian matrix $\mathbf{G}$ can be used to perform a “pre-conditioned” gradient descent (see appendix A for a construction of this matrix in a simple setting.) This matrix should have exponentially decaying eigenvalues for analytic activation functions, and one could use Algorithm 1 for this task. [1] Bonfanti, Andrea, Giuseppe Bruno, and Cristina Cipriani. "The challenges of the nonlinear regime for physics-informed neural networks." Advances in Neural Information Processing Systems 37 (2024): 41852-41881.	null	null	null	null	null	null
Beyond Message Passing: Neural Graph Pattern Machine	Accept (poster)	Summary: ## Update after rebuttal The authors have solved most of my concerns. I decide to maintain my score. Graph neural networks struggle to capture essential substructures, such as triangles in social networks or benzene rings in molecular graphs, due to their reliance on message passing. To address this limitation, the Neural Graph Pattern Machine (GPM) is introduced as a framework that directly learns from graph patterns, efficiently extracting and encoding substructures while identifying those most relevant to downstream tasks. Theoretically, GPM surpasses message passing in expressivity and long-range information modeling. The authours have conducted extensive experiments across multiple graph learning tasks to demonstrate its superiority over state-of-the-art baselines. Claims And Evidence: Yes, the claims made in the submission are supported by clear and convincing evidence. Methods And Evaluation Criteria: Yes Theoretical Claims: Yes, see the weakness. Experimental Designs Or Analyses: See the weakness. Supplementary Material: Yes, the appendix. Relation To Broader Scientific Literature: See the weakness. Essential References Not Discussed: No Other Strengths And Weaknesses: Strengths: Refer to the summary. Weaknesses: 1. The fundamental framework of GPM appears similar to [1]. It is recommended that the authors provide a detailed comparison to clarify the distinctions between their approach and this prior work. 2. Regarding the Pattern Encoder, numerous studies have explored the integration of Random Walk with GNNs/RNNs, including DeepWalk [2], GraphRNA [3], and RAW-GNN [4]. The authors should explicitly highlight the key differences between GPM and these existing methods. 3. In Theorem 3.4, GPM is shown to distinguish non-isomorphic graphs given a sufficient number of graph patterns. However, how is this number determined? Are there theoretical bounds on the required number of patterns? Addressing this would be crucial, as it represents a trade-off between computational complexity and learning sufficiency. [1] Wang Y, Cho K. Non-convolutional graph neural networks[J]. arXiv preprint arXiv:2408.00165, 2024. [2] Perozzi B, Al-Rfou R, Skiena S. Deepwalk: Online learning of social representations[C]//Proceedings of the 20th ACM SIGKDD international conference on Knowledge discovery and data mining. 2014: 701-710. [3] Huang X, Song Q, Li Y, et al. Graph recurrent networks with attributed random walks[C]//Proceedings of the 25th ACM SIGKDD International Conference on Knowledge Discovery & Data Mining. 2019: 732-740. [4] Jin D, Wang R, Ge M, et al. Raw-gnn: Random walk aggregation based graph neural network[J]. arXiv preprint arXiv:2206.13953, 2022. Other Comments Or Suggestions: No. Questions For Authors: See the weaknesses. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Thank you for the thoughtful review. We appreciate your constructive suggestions regarding related work and theoretical clarification, and we address each of these points in detail below. > A detailed comparison to RUM. > Motivation: RUM is designed to jointly address expressiveness, over-smoothing, and over-squashing within a message-passing-motivated framework (see below). In contrast, GPM is motivated by bypassing message passing and learning directly from substructure patterns. Graph Inductive Bias: While both RUM and GPM use semantic paths and anonymous paths to represent individual walks, their modeling approaches diverge significantly. RUM utilizes RNNs (GRUs) to encode these paths, following a philosophy aligned with message passing—where localized information dominates importance. GPM, however, leverages Transformers to encode semantic paths, allowing the model to learn inductive biases directly from data, particularly important in tasks requiring long-range dependency modeling. Pattern Aggregator: GPM employs a Transformer-based aggregator to combine learned graph pattern representations, whereas RUM uses a mean aggregator. This design choice brings several advantages: (1) Scalability: GPM scales effectively to large graphs and large model sizes (as demonstrated in Tables 1–3 and Figure 4). (2) Effectiveness: GPM samples 128 graph patterns per instance during inference (vs. 4 in RUM), and the Transformer allows the model to attend to the most informative patterns, yielding superior performance across benchmarks (Tables 1–4). (3) Interpretability: The attention mechanism in GPM’s Transformer provides natural interpretability, allowing us to identify key substructure patterns (e.g., via attention weights in Figure 5), a feature absent in RUM. Empirical Comparison: The distinctions above enables our GPM consistently outperforms RUM empirically (see Table 1,2,3,4). For example, in large-scale ogbn-product dataset (about 2.5 million nodes), GPM achieves 82.62% accuracy comparing to 78.68% of RUM. > Explicitly highlight the key differences between GPM and DeepWalk, GraphRNA, RAW-GNN. > We thank the reviewer for this request and provide the following comparison. DeepWalk and GraphRNA follow the principle of representing an entire graph as a collection of random walks that capture co-occurrence relationships among nodes. Their differences mainly lie in how walks are generated and encoded. GPM and RAW-GNN, in contrast, adopt the philosophy that random walks represent individual substructures of graph instances (nodes, edges, or entire graphs). The key distinctions between GPM and RAW-GNN are (1) Sampling Strategy: GPM uses unbiased random walks, reducing inductive bias. RAW-GNN employs biased sampling, which may impose structural priors that limit generalizability. (2) Structural Representation: GPM explicitly decouples topology and semantics by representing each walk as semantic and anonymous paths. RAW-GNN does not separate structural and feature encoding in this way. (3) Pattern Aggregation: GPM uses a single Transformer to aggregate all patterns. RAW-GNN uses separate aggregators for low- and high-order patterns, which may prevent modeling interactions across different structural levels. Empirical Comparison: Based on the above limitations, GPM consistently outperforms these methods empirically. We show the comparison results on node classification in the following. \| Dataset \| DeepWalk \| GraphRNA \| RAW-GNN \| GPM (ours) \| \| --- \| --- \| --- \| --- \| --- \| \| Computers \| 88.56 \| 91.06 \| 92.03 \| 92.28 \| \| WikiCS \| 76.34 \| 77.65 \| 79.01 \| 80.19 \| \| Flickr \| 49.70 \| 49.78 \| 49.58 \| 52.22 \| > Theoretical clarification > Theorem 3.4 demonstrates the existence of a sufficient number of graph patterns such that GPM can distinguish any pair of non-isomorphic graphs under its pattern-based encoding. However, this is a non-constructive result—it does not provide an explicit bound on the required number of patterns. Establishing such a bound is challenging due to the combinatorial nature of graph structures and the fact that the number may depend on: (1) Graph size and topological complexity, (2) The specific classes of non-isomorphic graphs (e.g., regular vs. irregular), (3) The expressiveness of the semantic and anonymous path encoders. Despite the theoretical uncertainty, our empirical findings show that sampling 128 random walks per graph is often sufficient to achieve perfect accuracy in distinguishing non-isomorphic graphs (see Table 8). We agree that deriving a tight theoretical bound on the number of necessary patterns is an important direction for future work, and we appreciate the reviewer for highlighting this. --- Rebuttal Comment 1.1: Comment: Thanks for the response from authors. I decide to maintain my score. --- Reply to Comment 1.1.1: Comment: Thank you for your response. Your feedback is genuinely appreciated and helps us continue to improve our work.	Summary: The paper introduces the Neural Graph Pattern Machine (GPM), a framework designed to enhance the expressiveness of graph learning models by directly learning from graph patterns. Traditional Graph Neural Networks (GNNs) rely on message passing to aggregate information from local neighborhoods, which can limit their ability to identify fundamental substructures, such as triangles. GPM addresses this limitation by efficiently extracting and encoding substructures, identifying the most relevant ones for downstream tasks. Empirical evaluations across various tasks, including node classification, link prediction, graph classification, and regression, demonstrate GPM's superiority over state-of-the-art baselines. The paper also highlights GPM's robustness, scalability, and interpretability, offering a comprehensive analysis of its performance. Overall, the paper is well-organized and clearly presented. Claims And Evidence: Yes Methods And Evaluation Criteria: yes Theoretical Claims: yes Experimental Designs Or Analyses: yes In Section 4.3, the authors highlight that traditional message-passing Graph Neural Networks (GNNs), such as the Graph Attention Network (GAT), encounter scalability challenges due to the oversmoothing effect. This phenomenon occurs when node representations become indistinguishable as the number of GNN layers increases, ultimately diminishing model performance. To address this issue, the proposed Neural Graph Pattern Machine (GPM) takes a novel approach by learning directly from graph patterns instead of relying solely on message passing. By efficiently extracting and encoding substructures, GPM strives to preserve distinctive node representations. Therefore, it should have the potential to overcome the oversmoothing problem, (if my understanding is correct). However, further experiments are needed to substantiate this claim. Supplementary Material: yes, all Relation To Broader Scientific Literature: The key contributions of this paper relate to the broader scientific literature as follows: New Approach: The framework, GPM, overcomes the limitations of traditional GNNs like restricted expressiveness and oversquashing, echoing ongoing research efforts in addressing these issues. Scalability: GPM scales better for complex tasks involving large models and graphs, contributing to the field's discussions on handling vast datasets. Interpretability: GPM provides a way to interpret models, which is crucial for applications like social network analysis and drug discovery. This aligns with the growing focus on the interpretability of GNNs in the literature. Essential References Not Discussed: no Other Strengths And Weaknesses: The main shortcomings of this paper lie in its reliance on existing technology. However, the author has provided valuable insights into the rationale behind using this technology, supported by corresponding evidence, and conducted thorough experiments. Including experiments specifically aimed at overcoming the oversmoothing issue would further enhance the paper's contributions. Other Comments Or Suggestions: 1. Strongly recommend the author publicly disclose the code to facilitate reproducibility. 2. Suggest adding experiments on heterogeneous graphs. While the author mentions this in the limitations section, evaluating GPM's classification potential on heterogeneous graphs would be valuable. 3. Recommend increasing experimental comparisons to address oversmoothing. For instance, increasing the number of network layers to evaluate model performance would be beneficial. 4. How does the model perform on large datasets, such as OGB? Including an assessment of GPM's performance on big datasets would strengthen the paper. Questions For Authors: How does the model perform on large datasets, such as OGB? How does the model perform on the heterogeneous graph dataset? Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Thank you for the thoughtful and encouraging review. We’re glad the reviewer appreciated our contributions in expressiveness, scalability, and interpretability. We also appreciate the constructive suggestions regarding additional experiments, and we address each point in detail below. > GPM has the potential to overcome over-smoothing. Need more experiments. > Absolutely — we also believe that GPM naturally mitigates the over-smoothing problem. In traditional message-passing GNNs, deeper networks tend to aggregate node features from increasingly distant neighbors, often leading to over-smoothing. In GPM, the analogous hyperparameter is the random walk length, which controls the receptive field of each pattern. To investigate this, we conducted experiments on WikiCS (node classification) and COLLAB (graph classification), varying the random walk length in [4, 8, 16, 32, 64]. As shown in the table below, while standard models like GraphSAGE and GIN suffer significant performance degradation as depth increases, GPM maintains strong performance, with only a slight drop at extreme walk lengths. We attribute this to GPM's architecture, where a Transformer processes each sampled walk independently, effectively decomposing hop-level interactions, rather than stacking layers that prioritize low-order information. \| Model Layer / Walk Length \| 4 \| 8 \| 16 \| 32 \| 64 \| \| --- \| --- \| --- \| --- \| --- \| --- \| \| WikiCS (Node classification) \| \| \| \| \| \| \| SAGE \| 78.50 \| 73.38 \| 68.35 \| 64.32 \| 30.58 \| \| GPM (ours) \| 79.64 \| 80.19 \| 80.52 \| 78.98 \| 77.31 \| \| COLLAB (Graph Classification) \| \| \| \| \| \| \| GIN \| 80.31 \| 79.30 \| 75.44 \| 72.68 \| 65.38 \| \| GPM (ours) \| 80.45 \| 80.70 \| 80.66 \| 79.53 \| 77.39 \| > Experiments on heterogeneous graphs > We appreciate the suggestion and have conducted additional experiments on heterogeneous graphs. Specifically, we evaluated GPM on two widely used datasets: ACM and DBLP. To handle heterogeneity, we adopt a simple yet effective strategy: for each node type, we use a type-specific Mapping to project the features into a shared latent space, following the approach in [1]. We compare GPM with strong baselines including Metapath2vec, RGCN, HAN, HeCo, and HGT. Using the standard 20/40/40 split and Micro-F1 as the metric, GPM outperforms all baselines: \| Dataset \| Metapath2vec \| HAN \| HeCo \| HGT \| GPM (ours) \| \| --- \| --- \| --- \| --- \| --- \| --- \| \| ACM \| 82.96 \| 90.45 \| 91.23 \| 91.12 \| 93.27 \| \| DBLP \| 89.02 \| 92.60 \| 93.24 \| 92.55 \| 94.29 \| [1] Are we really making much progress? Revisiting, benchmarking, and refining heterogeneous graph neural networks, KDD 21. > Experiment on large graphs, like OGB. > Thank you for pointing this out. In fact, we already include experiments on large-scale OGB benchmarks in the main paper: ogbn-arxiv (Arxiv), ogbn-products (Products), and ogbl-collab. The ogbn-products dataset, for instance, includes 2,449,029 nodes and 123,718,024 edges. Despite the scale, GPM maintains high scalability and consistently outperforms baselines across these large benchmarks. For example, GPM achieves 82.62 in ogbn-products yet the best baseline just achieves 82.00. > Strongly recommend the author publicly disclose the code to facilitate reproducibility. > We completely agree, and we are fully committed to open research. We have provided the code in the supplement. We will release the full source code and instructions upon publication. --- Rebuttal Comment 1.1: Comment: Thanks for the authors' reply, I'd like to maintain my score. --- Reply to Comment 1.1.1: Comment: Thank you for your response. Your feedback is genuinely appreciated and helps us continue to improve our work.	Summary: This paper proposes GPM, a graph transformer based on randomly sampling walks in the graph. GPM achieves strong empirical results across a variety of datasets and types of tasks. Furthermore, by sampling a large number of paths (or very long paths) GPM achieves high expressivity. ## update after rebuttal The authors did provide substantial explanations and additional experiments during the rebuttal. This has caused me to increase my score (see latest rebuttal comment). Claims And Evidence: The experimental claims are solid, the evidence supporting theoretical claims could be improved (see below). Methods And Evaluation Criteria: See below. Theoretical Claims: I have skimmed all proofs in the appendix. While they seem to hold, mathematical statements are often imprecise (see below). Experimental Designs Or Analyses: This paper very thoroughly evaluates their methods for different tasks and datasets. Overall, I think that the experiments are solid (see Strengths) except the question I raise in (Questions For Authors). Supplementary Material: I did not. Relation To Broader Scientific Literature: I think the related work is mostly fine, but is missing a few references (see below). Essential References Not Discussed: The expressivity of of GPM is based on randomly sampling graph patterns. It seems that (1) is essential related work, as (1) propose expressive GNNs based on randomly sampled patterns (homomorphisms). Furtherme, since the architecture is based on walks I believe that recent literature on path-based GNNs should also be discussed such as (2,3). (1) Welke at al., _Expectation-Complete Graph Representations with Homomorphisms_, ICML 2023 (2) Gaspard et al., _Path Neural Networks: Expressive and Accurate Graph Neural Networks_, ICML 2023 (3) Drucks et al., _The Expressive Power of Path based Graph Neural Networks_, ICML 2024 Other Strengths And Weaknesses: Strengths: - (S1). The (non mathematical) sections are well written and easy to follow. - (S2). The proposed method is conceptually elegant and the paper has many small, clever ideas. In particular, the test time augmentation (only sampling few paths during training to speed it up but sampling a lot of paths to achieve strong inference results) seems really interesting. - (S3). The experiments are more than solid. The authors select a wide range of different tasks (node predictions, link predictions, graph predictions, synthetic graph distinction) and achieve good results. All in all, I believe that the experimental part of this paper is excellent. Weaknesses: - (W1). Theoretical runtime. The proof of Proposition 3.2 requires sampling as many paths as the size of the $k$-hop neighborhood (for each node). Sampling this many paths for every node is computationally expensive (at least quadratic in the worst case). - (W2). Mathematical precision. Definitions are incomplete (see below), Propositions and Theorems are formulated descriptively but are not precise mathematical statements. Some examples of this: - Proposition 3.2 and 3.3 are informal. - Theorem 3.4: "GPM can distinguish non-isomorphic graphs given a sufficient number of graph patterns." This formulation is wrong: MPNNs are also able to distinguish non-isormophic graphs (just not all of them). I think what was meant is: "GPM can distinguish all pairs of non-isomorphic graphs given a sufficient number of patterns". - If my interpretation of Theorem 3.4 is correct, then Theorem 3.5 should be a simply corrollary of Theorem 3.4 instead of a theorem. - Theorem 3.4 and 3.5 rely on the reconstruction conjecture to be true which I believe is not mentioned in the main text. - Proof of Theorem 3.4: _"The simplified case assumes $n = 1$ with a sufficiently large walk length $l$, whereas GPM operates with $n > 1$. Since random walks can start from any node in the graph, an $l$-length random walk can be split into $k$ segments ($k$ is large enough), each of length $l/k$. Each sub-walk can be encoded individually and later combined to form the final embedding"_. I do not think long walks can simply be reconstructed from shorter walks as anonymous walks do not allow to match nodes between different walks. Overall, this is a difficult decision for me. The experimental side of this paper is strong and I wish all GNN papers would so thoroughly evaluate their architecture on different tasks. However, the mathematical / theoretical side needs extensive improvements. Thus, I am in favor of rejecting as I believe that the required changes are too large to be done in the process of the rebuttal. I hope the authors will re-write the problematic sections and look forward to seeing this paper at a future conference. Other Comments Or Suggestions: - A graph is defined as $G = (V, E)$, this should also include the node features. Since the paper also mentions edge feature, they should also be defined here. - Definition 3.1 seems incomplete as the $pos$ function is not defined Questions For Authors: - For the "Empirical expressiveness analysis" (Tab 8 Appendix), did you ensure that the same patterns get sampled for pairs of graphs that you try to distinguish? If not, then your model would be trivially be able to distinguish 100% of all pairs. Code Of Conduct: Affirmed. Overall Recommendation: 2	Rebuttal 1: Rebuttal: We sincerely appreciate your recognition of the strengths of our method and experimental evaluation. While we take your concerns about the theoretical aspects seriously, we would like to emphasize that the primary contribution of our work lies in the model design and empirical success; the theoretical components are included to provide insight into our design choices, rather than to serve as the core contribution. We address each point in detail below and are committed to improving clarity and rigor in future revisions. > Related works on graph expressiveness > Thank you for pointing out these relevant works. While GPM shares high-level similarities with [1], it differs significantly in approach: GPM is a data-driven framework that learns task-relevant patterns through sampling and optimization, whereas [1] takes a theoretical route, leveraging homomorphism counts to prove expectation-completeness using random subgraph probes. Compared to PathNN [2] and PAIN [3], which also rely on random walks, GPM distinguishes itself by using a Transformer to aggregate pattern-level embeddings, rather than encoding enumerated paths [2] or sampled paths [3]. This enables pattern-centric reasoning and contributes to improved generalization across tasks and graph scales. Empirically, GPM outperforms all three baselines on the ZINC regression benchmark, evaluated via MAE: \| Dataset \| GIN + hom + F [1] \| PathNN-AP [2] \| PAIN [3] \| GPM (ours) \| \| --- \| --- \| --- \| --- \| --- \| \| ZINC \| 0.174 \| 0.090 \| 0.148 \| 0.064 \| [1] Expectation-Complete Graph Representations with Homomorphisms [2] Path Neural Networks: Expressive and Accurate Graph Neural Networks [3] The Expressive Power of Path based Graph Neural Networks > Theoretical runtime > We appreciate the reviewer raising this point. Indeed, in the worst-case scenario (e.g., dense graphs), the number of paths within a k-hop neighborhood can grow exponentially with k, making full enumeration intractable. However, GPM does not require exhaustive enumeration. Instead, we perform efficient random walk sampling to approximate the distribution over substructures: - In practice, we sample a fixed number of paths per node (e.g., 128) of fixed length (e.g., 8), independent of the total k-hop neighborhood size. This provides predictable runtime and memory cost, even on large-scale graphs. Notably, sampling random walks on graphs with over 2.5 million nodes in under two minutes. - Theoretical analysis in Proposition 3.2 assumes access to the full pattern space, but empirically we find that a small number of walks (i.e., 128) is sufficient for strong performance. > Mathematical precision > We thank the reviewer for the detailed feedback. We agree that the current formulation of Propositions 3.2, 3.3, and Theorems 3.4 and 3.5 is informal and lacks full mathematical rigor. These results were intended to provide conceptual insights into the representational power of GPM, not to constitute formal theoretical contributions. That said, we will: (1) Revise Theorem 3.4 to state clearly that GPM can distinguish all pairs of non-isomorphic graphs given a sufficiently rich set of patterns. (2) Demote Theorem 3.5 to a corollary or informal observation, as it logically follows from Theorem 3.4. (3) Explicitly mention the reconstruction conjecture and its role in the assumptions underlying these results. Regarding the proof of Theorem 3.4: we agree that our phrasing was misleading. We did not mean to suggest that long walks can be fully reconstructed from shorter ones, especially since anonymous walks cannot preserve node identity across segments. Rather, we intended to describe an approximate strategy, where long walks are segmented into shorter sub-walks, each encoded independently. This design allows the transformer to aggregate distributed long-range information across these sub-patterns. We will revise the wording in the appendix to reflect this more accurately and avoid overstating the implications. To reiterate, our theoretical analysis is included to motivate and clarify design choices. We will clearly label these components as heuristic or informal in future revisions to avoid confusion. > Other modifications and clarifications > Modifications: We thank the reviewer for pointing this out. We will update the definition of a graph and the definition 3.1 in our future version. Clarifications: We appreciate the question about sampling consistency in the expressiveness analysis (Table 8). To clarify: GPM samples patterns locally from each graph, with the goal of capturing the structural fingerprint of each instance via its own distribution of substructures. different patterns are not a source of trivial separability, but rather a core mechanism for capturing graph-specific structure. Using a shared pattern set would reduce discriminative power. --- Rebuttal Comment 1.1: Comment: I thank the authors for the reply. I believe these changes will improve the paper and thus will slightly improve my score (reject -> weak reject). --- Reply to Comment 1.1.1: Comment: Thank you for your response and for raising the score. Your feedback is genuinely appreciated and helps us continue to improve our work.	Summary: This paper introduces a framework for graph learning named Neural Graph Pattern Machine (GPM). It aims to directly capture substructure patterns instead of relying on message-passing mechanisms. The model leverages random walks to extract graph patterns, and then convert them into semantic paths and anonymous paths. These paths are encoded separately through a Transformer-based architecture to learn deep representations. Empirical evaluations are conducted across multiple tasks, including node classification, link prediction, and graph regression. The experimental results can demonstrate GPM’s superiority over baseline models including message-passing and other Transformer-based models. The paper also highlights its robustness to distribution shifts, scalability, and interoperability. ## update after rebuttal Thank you for the authors' rebuttal. I will keep my score. Claims And Evidence: Strengths: 1. The advantages of the proposed GPM are empirically supported by experimental results on node/edge/graph learning tasks. The method is computationally efficient compared to the naive GCN. 2. The paper is well-structured and clearly written. The authors effectively explain their motivation, methodology, and results. Methods And Evaluation Criteria: Strengths: 1. The method is both conceptually sound and practically feasible 2. The evaluation criteria follow common practices and make sense. Theoretical Claims: Strengths: 1. The paper provides a comprehensive theoretical study. These theoretical insights help establish the foundations of the proposed method and its advantages over traditional message-passing GNNs. Weaknesses: 1. The statement of proposition 3.3 “provide a comprehensive representation…” lacks rigor. The term “comprehensive” is a subjective description. Also, I didn’t understand how the proof in Appendix C.2 proves this claim. Experimental Designs Or Analyses: Strengths: 1. The experimental evaluation is thorough, covering multiple tasks including node classification, link prediction, and graph regression. A wide range of baseline models are compared. 2. The proposed GPM demonstrates strong empirical results across various datasets, outperforming or matching state-of-the-art models in benchmark tasks. These results suggest that the method is competitive and effective in real-world applications. Weaknesses: 1. The missing numbers in Table 1 are not explicitly explained in the text. Supplementary Material: I briefly reviewed the theoretical part in supplementary material. Relation To Broader Scientific Literature: Strengths: 1. A wide range of existing methods are discussed including both message-passing based and tokenization based models. Weaknesses: 1. Extracting subgraph patterns with random walk and anonymous walk have been studied in previous papers [1, 2]. [1] was published on the recent ICLR’25 but was posted on arxiv on Jun, 2024. [2] studied anonymous walks for temporal networks which are based on GNNs. These papers should be discussed and compared as well since the main idea of GPM seems very relevant to them. 2. The proposed Important Pattern Identifier is a straightforward application of Transformer interpretability. This part doesn’t show a significant technical contribution. [1] Learning Long Range Dependencies on Graphs via Random Walks. (ICLR’25) [2] Inductive Representation Learning in Temporal Networks via Causal Anonymous Walks. (ICLR’21) Essential References Not Discussed: See above [1,2]. Other Strengths And Weaknesses: NA Other Comments Or Suggestions: NA Questions For Authors: Please address the Weaknesses listed above. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We sincerely thank the reviewer for their detailed and insightful feedback, as well as for recognizing our contributions in methodology, theoretical insights, and empirical performance. We particularly appreciate the constructive suggestions regarding theoretical clarity, experimental completeness, and related work comparisons, which have helped us significantly improve the manuscript. > Discussion and comparison to related works. > We highlight several key differences between GPM and NeuralWalker: (1) Task-adaptive tokenization: NeuralWalker tokenizes graphs into random walks uniformly across all tasks. In contrast, GPM performs task-specific pattern sampling—for example, node-level tasks focus on patterns centered around each node, while graph-level tasks use global structures. This adaptivity is a central design of GPM. (2) Representation granularity: NeuralWalker encodes each node within a walk and updates node-level embeddings, resulting in multiple embeddings per walk. GPM, on the other hand, produces a single representation per walk, capturing the semantics of the entire pattern rather than individual nodes. (3) Architecture paradigm: GPM is a fully message passing-free architecture, whereas NeuralWalker still relies on message passing components to explicitly model local information. Regarding CAW, both CAW and GPM use anonymous paths as substructure patterns. However, their purposes and applications differ: (1) Domain: CAW is designed for temporal graphs, while GPM is intended for attributed static graphs. (2) Tokenization: Like NeuralWalker, CAW performs uniform walk sampling, regardless of the task. GPM introduces an adaptive tokenizer tailored to different downstream objectives. (2) Task scope: CAW primarily focuses on link prediction, while GPM supports node, link, and graph-level tasks. We summarize the empirical comparison between GPM and NeuralWalker in the following table. Since CAW is designed for temporal graphs, it does not naturally apply to the datasets used in this paper: \| Task \| Dataset \| NeuralWalker [1] \| CAW [2] \| GPM (ours) \| \| --- \| --- \| --- \| --- \| --- \| \| Node Classification \| WikiCS \| 78.55 \| - \| 80.19 \| \| Link Prediction \| Cora \| 87.50 \| - \| 92.85 \| \| Graph Regression \| ZINC \| 0.053 \| - \| 0.064 \| [1] Learning Long Range Dependencies on Graphs via Random Walks. (ICLR’25) [2] Inductive Representation Learning in Temporal Networks via Causal Anonymous Walks. (ICLR’21) > Elaborate on Proposition 3.3. > We apologize for the confusion and appreciate the opportunity to clarify. In Proposition 3.3, the term "comprehensive" refers to the ability to capture both semantic (feature-level) and structural (topological) information of a graph pattern by jointly modeling its semantic path and anonymous path. Specifically, a graph pattern can be decomposed into a semantic path (preserving node/edge attributes) and an anonymous path (preserving topology only). These paths, being sequential, can be bijectively projected into fixed-size embeddings without loss of information. Therefore, embedding a graph pattern can be obtained by combining the embeddings of its semantic and anonymous paths. This proposition is intended to provide the intuition behind GPM’s dual encoding design and emphasizes the necessity of modeling both views to capture rich structural and semantic signals. > The Important Pattern Identifier is a straightforward application of Transformer interpretability. > We appreciate this feedback and would like to clarify the intent of this module. This component serves primarily as an aggregation mechanism over encoded graph patterns. We chose to use the Transformer for this role due to its proven effectiveness across domains, e.g., CV and NLP. While we acknowledge that Transformer attention is not novel per se, its emergent interpretability—i.e., its ability to highlight important substructures—was a valuable and interpretable byproduct. This insight supports GPM’s modular design, where effective aggregation and interpretability naturally align. > The missing numbers are not explicitly explained in the text. > Thank you for pointing this out. We will update the text to clarify that missing values (denoted as “-”) correspond to baselines for which: (1) Computational constraints (e.g., tuning models such as VCR-Graphormer, GEANet) made training impractical, or (2) Reproducibility issues (e.g., unavailable official code for RAW-GNN, GraphMamba, GCFormer) prevented fair comparison. We prioritized reporting results for the most informative and representative baselines under a consistent evaluation protocol.	null	null	null	null	null	null
Ladder-Residual: Parallelism-Aware Architecture for Accelerating Large Model Inference with Communication Overlapping	Accept (poster)	Summary: This paper proposes a communication-friendly Transformer layout, Ladder Residual, to accelerate tensor-parallel training. Ladder Residual enables straightforward computation-communication overlapping compared with vanilla sequential or parallel layout. It achieves 29% end-to-end speedup in TP8 training. Ladder Residual outperforms Parallel Transformer and shows a narrow gap than standard sequential Transformers. As a candidate of hardware-friendly layout, Ladder Residual has potential on replacing standard Transformer in LLM pre-training. ## Update after rebuttal My score keeps as weakly accept. I think a TP-friendly architecture is an interesting idea and the proposed method actually makes accelerations. However, the biggest disagreement between my and authors is the actual usefulness of Ladder Residual. Since the architecture's performance is not on par with baseline, and the large-TP training is not often used in actual LLM training, Ladder Residual is not a general-promoted architecture. Claims And Evidence: There are two main claims in this paper: end-to-end latency and overall performance. These two experiments are conducted under the same environment and hyper-parameters. The evidence is solid. Methods And Evaluation Criteria: The proposed method is simple and direct, focusing on the macro layout of Transformer models. The evaluation criteria is widely-accepted in the community. Theoretical Claims: No Theoretical claims. Experimental Designs Or Analyses: The experimental designs are sound to me. However, I have concerns on the experiment settings. Since large TP brings heavy communication latency, the proposed method will show a stronger advantages. In the paper, some experiments are conducted under TP16, where inter-node communication cost is stronger on 8-gpu per node clusters. Large TP size is not commonly used due to the heavy communication latency. For example, in Deepseek V3, EP and PP is activated instead of large TP to avoid heavy communication. (Of course Deepseek V3 is published within 3 months and should not be considered.) But the other option of LLM pre-training always exists. Admittedly, Ladder Residual should also work under EP setting. I think it's better to conduct more experiment on these more practical settings. Supplementary Material: No supplementary material. Relation To Broader Scientific Literature: The proposed method is an extension for hardware-friendly layout, after standard sequential layout, and parallel layout. Since there are not many closely related works, this work will be a strong candidate among these macro layouts. This work is orthogonal to other efficient architectures, such as Linear Attention, Group Query Attention. Essential References Not Discussed: Since there are not many references on the connection efficiency, the most essential references are all discussed. However, if the authors think it is essential to discuss other strands of efficient architectures, there will be more references. For example, if this paper discusses [1], a broader discussion of different linear-time models may be essential. [1] The mamba in the llama: Distilling and accelerating hybrid models, 2024. Other Strengths And Weaknesses: Strength: 1. It is a very simple and elegant design. I think it will be broadly discussed in the future and a strong candidate for communication-friendly architecture. Weakness: 1. It's possible that the advantage of this paper only happens in large TP settings, which may be not often used. Other Comments Or Suggestions: No other comments. Questions For Authors: 1. Following my comments on Experimental Designs Or Analyses, is Ladder-Residual useful under different settings? 2. Since the performance is not comparable with sequential layouts, could you evaluate performance with a efficiency-aware metric? For example, the performance under same training time instead of same training tokens. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Thanks for your feedback on our paper! Below we provide a few clarifications on how our experiments demonstrate practical gain from ladder-residual and its compatibility with other parallelism. > In the paper, some experiments are conducted under TP16, where inter-node communication cost is stronger on 8-gpu per node clusters. We agree with the reviewer that tensor parallelism is not commonly conducted across nodes due to the heavy communication. Our TP16 experiment is intended to demonstrate the potential of Ladder-Residual in scenarios where cross-node model parallelism becomes necessary. Generally, larger models are served with TP+PP (for example DeepSeek 671B model). However, it should be noted that with newer generation GPUs (B200 NVL72) and the recently announced (Rubin NVL576), it will become very feasible to run these models with purely TP since these systems expand the NVLink (high bandwidth) domain from 8 GPUs to 72 and 576 GPUs respectively. We also want to note that Ladder-residual is compatible with multi-dimensional parallelism, please see our response to Reviewer 9rvM for further details. Therefore, even if we want to combine TP with other parallelism, ladder-residual can still be applied to accelerate the TP part. Furthermore, despite we didn't explore it in this work, we believe ladder-residual can accelerate other heavy-communication parallelism like EP as well. > It's possible that the advantage of this paper only happens in large TP settings, which may be not often used. Table 1 and Figure 2 investigates the benefit of ladder-residual when intra-node TP (2, 4 and 8 GPUs) is used, which is the most common and flexible inference-time parallelism approach. In this regime, ladder-residual consistently show a large speedup against the standard Transformer and beats the parallel attn-mlp alternative until the batch size is very large. Figure 4 also shows that under the intra-node TP setting, Ladder-residual can reliably push the Pareto-frontier between latency and throughput. --- Rebuttal Comment 1.1: Comment: Thanks for the reply. Ladder-Residual is a trade-off algorithm, where the pareto curve is not always better than traditional baselines, depending on the parallelism and hardware circumstances. Besides, even though pure TP training is possible in the future GPU designs, the communication bandwidth also changes. I believe it is an interesting idea, but I will keep my score. --- Reply to Comment 1.1.1: Comment: Thanks for the further reply! Regarding the point that communication bandwidth also changes, we want to provide a little more context on why we think optimizing for communication will have an even higher impact in the future. First, as models continue to scale, multi-GPU inference, our main focus, will become more central, and communication overhead will grow accordingly. Second, as shown in Figure 2 of [1], while newer generations of hardware bring higher communication bandwidth, it has a slower scaling trend than the scaling of peak FLOPS and memory bandwidth, making communication a growing bottleneck. Third, communication can often be latency-bounded when the message size is small, therefore doesn't benefit much from increased bandwidth. We appreciate the reviewer’s recognition of our architecture as "a very simple and elegant design." and " will be broadly discussed in the future and a strong candidate for communication-friendly architecture". While our method already shows substantial speedups on current models and hardware, we are confident that it will make an even greater impact in the future due to its simplicity and flexibility, and the growing concern about communication bottlenecks. [1] Fire-Flyer AI-HPC: A Cost-Effective Software-Hardware Co-Design for Deep Learning	Summary: This paper proposes Ladder-Residual, which modifies the residual connection in Transformers such that the i-th block reads from the (i−2)-th block's result instead of the (i−1)-th. This interleaved schedule allows direct overlap between the Transformer block's computation and the subsequent all-reduce communication step, thus significantly speeding up tensor parallelism across multiple devices. Claims And Evidence: I think the Ladder-Residual approach is conceptually straightforward and effective, enabling communication-computation overlap without altering underlying systems or kernels. However, a few points need additional clarification: - "Liu et al. (2023b) found that activation changes slowly in Transformer, as the norm of each update $h_{i+1}(x_i)$ is small compared to the residual." It conducts the experiments under an inference setting. Is this still true in the training? Do you have any theoretical guarantees that this property still holds during training, i.e., whether activation differences remain bounded across consecutive blocks. - Deja Vu's Appendix C.3 already discusses the possibility of parallelizing MHA and MLP blocks. Can you explain the novelty of Ladder-Residual over it? - Can Ladder Residual be combined with existing communication optimization methods, such as [A] and [B] that decompose the computation into small chunks to enable better compute-communication overlapping? You mentioned that your work does not rely on decomposition, but can such chunking approaches be combined with Ladder-Residual to further boost performance? Methods And Evaluation Criteria: - It would be valuable to demonstrate Ladder-Residual using widely adopted frameworks such as Megatron-LM or DeepSpeed. For instance, instead of purely self-comparison in Table 2, showing improvements relative to standard baselines in these frameworks would help the community judge the method's portability and real-world impact. Theoretical Claims: - Is there a formal proof or theoretical justification indicating that altering the residual connection in this way preserves the Transformer’s representational power or performance? Experimental Designs Or Analyses: - While Ladder-Residual aids tensor parallelism, cross-layer dependencies can complicate pipeline parallelism. Section 3.3.2 focuses on multi-node experiments with TP=16, yet it remains unclear how Ladder-Residual would perform compared to standard 3D parallelism (e.g., Megatron-LM) or ZeRO-3 (DeepSpeed). Clarification of its interplay with pipeline parallelism is necessary. - Results on 3B models appear worse than those on 1B models, raising questions about scalability. Can you provide additional experiments or explanations for how Ladder-Residual scales with model size? Supplementary Material: - It would be good to have a diagram in the main text to illustrate the pipeline that Ladder Transformer achieves (similar to Figure 5). Relation To Broader Scientific Literature: The proposed approach is simple but potentially impactful, requiring no special modifications to kernels or communication libraries. This simplicity may facilitate broad adoption across diverse hardware environments. Essential References Not Discussed: * [A] Wang, Shibo, et al. "Overlap communication with dependent computation via decomposition in large deep learning models." Proceedings of the 28th ACM International Conference on Architectural Support for Programming Languages and Operating Systems, Volume 1. 2022. (Already in the reference) * [B] Chen, Chang, et al. "Centauri: Enabling efficient scheduling for communication-computation overlap in large model training via communication partitioning." Proceedings of the 29th ACM International Conference on Architectural Support for Programming Languages and Operating Systems, Volume 3. 2024. Other Strengths And Weaknesses: See the above sections. Other Comments Or Suggestions: See the above sections. Questions For Authors: See the above sections. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Thanks for the valuable feedback and the questions. Below we discuss how our paper is novel, why it’s compatible with other parallelism, address the concern on scaling, and provide analysis on the change of activations. We also thank the reviewer for the suggestions on the presentation. We will incorporate them in the next draft. _________________ Novelty over parallelizing MHA and MLP blocks First, Ladder-residual is a fundamentally different architecture from parallelizing MHA and MLP blocks, with distinct motivations. Ladder-residual is designed to decouple computation and communication to enable their overlap. In contrast, the goal of parallelizing MHA and MLP blocks is to combine computation for speedup. Due to the reduced depth, parallelizing MHA and MLP blocks also saves communication but is not its original focus. The speedup of Ladder-Residual comes from overlapping all (except last) communication where parallelizing MHA and MLP focuses on accelerated matmul and as a byproduct, it cuts 50% of the communication. _________________ Combining with other communication optimization methods Yes. A key advantage of Ladder-Residual is that it is hardware-agnostic and does not rely on custom kernels, making it fully compatible with other low-level optimization methods. However, since Ladder-residual hides latency of all communication except the last one, further applying these techniques can only accelerate the final communication which won’t achieve much gains. _________________ Comparison with other frameworks We focus on inference speedups in this paper and gpt-fast and vLLM are highly optimized for inference. We choose gpt-fast to demonstrate the inference speedups but it should be noted that we still achieve training speedups (around 5-8%) when combining TP+FSDP. _________________ Compatibility with other parallelism It is possible to use Pipeline Parallel (PP) with the Ladder architecture: just before the pipeline boundary, we wait for the async AllReduces to complete, and send 3 tensors to the next pipeline stage: residual, current_mlp_output tensor and current_attention_output. It should be noted that this is still pretty cheap since generally the P2P communication during inference is latency bound and can be implemented easily using the batch_isend_irecv API (https://pytorch.org/docs/stable/distributed.html#torch.distributed.batch_isend_irecv). ``` def forward( self, previous_attention_out: Tensor, previous_mlp_out: Tensor, residual: Tensor, attention_handle, mlp_handle, ) -> Tensor: attention_handle.wait() residual = residual + previous_attention_out current_attention_out = self.attention(self.attention_norm(residual)) current_attention_out = all_reduce(current_attention_out, async_op=True) mlp_handle.wait() residual = residual + previous_mlp_out current_mlp_out = self.feed_forward(self.ffn_norm(residual)) current_mlp_out, mlp_handle = all_reduce(current_mlp_out, async_op=True) if is_last_layer_on_pp_stage: attention_handle.wait() mlp_handle.wait() return current_attention_out, current_mlp_out, residual, attention_handle, mlp_handle ``` For Data Parallelism or FSDP, the cross-layer dependency doesn’t pose any complications. Therefore Ladder-residual can be seamlessly incorporated in a multi-dimensional parallelism training paradigm. Our training framework already supports TP+FSDP for ladder residual model training and can be easily extended to support PP as illustrated by the above code snippet. _________________ Performance and scaling In our response to Reviewer Mhub, we provide experiments where we increase the number of parameters of the Ladder-Transformer by 30%. We show that at both 1B and 3B scale, the 30% larger ladder-Transformer has both higher accuracy and higher TPS than the standard-Transformer. This confirms our architecture truly pushes the Pareto frontier. It’s difficult to conclude the scaling trend from just two sizes and in the future we hope to run models of more sizes to study this more carefully. _________________ Activation difference analysis Our motivation is that, given in a trained standard Transformer, the activation differences between modules are small, replacing with the Ladder architecture won’t lead to large degradation. We don’t care too much if this property is still held during training, and it’s difficult to have a theoretical guarantee due to unpredictable training dynamics. To further verify this intuition, we analyze block similarity (between consecutive attention and MLP modules) in both original Llama-3.1-8B-Instruct and Hybrid-Ladder-8B-16L-retrained. The visualization can be found at [This Anonymous GitHub link](https://anonymous.4open.science/r/ICML25_rebuttal-F932/README.md). Overall there is a slight decrease in activation similarity after adapting to Ladder-residual but the similarity remains high overall (above 0.9 at most of the layers).	Summary: This paper proposes Ladder Residual, an alternative to the transformer architecture that breaks the communication-computation dependency in conventional parallelism patterns, in order to accelerate the inference, at the cost of accuracy degradation. Claims And Evidence: I have some doubts about the claim "We also show that it is possible to convert parts of the Llama-3.1 8B model to our Ladder Residual architecture with minimal accuracy degradation by only retraining for 3B tokens" According to the experiment results in Table 3 and 4, it seems that the proposed architecture has significant degradation in accuracy compared to the baseline. For Table 3, Ladder-Transformer has a gap of 1 to the Standard-Transformer. For Table 4, although the average score of Hybrid-Ladder-8B-16L-retrained is comparable to Llama-3.1-8B-Instruct, in most of the evaluation categories (6 out of 9) the hybrid ladder is worse than the baseline. Thus, it is difficult to justify that such degradation of accuracy is acceptable. Methods And Evaluation Criteria: The method makes sense. The evaluation could be more comprehensive, such as adding more models (there are a lot of open-sourced pretrained models could be used for post-training adaptation) Theoretical Claims: N/A Experimental Designs Or Analyses: For the experiments, I hardly find it convincing that the evaluation could justify the degradation of accuracy of the proposed architecture. May be adding more experiments (on different models, etc.) could make the results more convincing. Supplementary Material: I've checked the pytorch profiler trace. Relation To Broader Scientific Literature: There is nothing related to the broader scientific literature. Essential References Not Discussed: The references look good to me. Other Strengths And Weaknesses: Minor issue: 1. The abbreviation "AAR" in Algorithm 1 is not defined or explained. I guess AAR means AsyncAllReduce, but the paper shouldn't let the readers to guess what an abbreviation means. Please use "... Note that the AsyncAllReduce (AAR) returns a handle ..." in the algorithm caption, so that it could be more friendly to the readers. 2. For some unknown reason, there is a "‘" in page 1 on the left-hand side of "Abstract" (check the 1st column, between line 010-011). Please double check the latex source file. Other Comments Or Suggestions: N/A Questions For Authors: Is it possible to replace the transformer block with ladder transformer in ViT? If so, is there any corresponding experiments? Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Thanks for your time and the feedback! We want to clarify that in a lossy efficient method (where a more efficient architecture is proposed to approximate the original one), trading accuracy for efficiency is common and we provide a good trade-off. It’s difficult to have one-size-fits-all as some users might prefer higher efficiency while others prefer higher accuracy. However, to make things more clear, we provide additional results that achieve both higher accuracy and higher throughput (token-per-seconds) below. This was accomplished by training a slightly larger ladder model for the train-from-scratch experiment and employing an improved post-training pipeline for the post-training-adaptation experiment. > For Table 3, Ladder-Transformer has a gap of 1 to the Standard-Transformer. In our train-from-scratch experiments, we previously reported that the Ladder-Transformer slightly underperformed compared to the Standard-Transformer of the same size. As shown in Table 1 from the paper, Ladder-residual can offer at least 30% speedup for any model size. To further explore the accuracy-throughput trade-off, we increased the parameter count of the Ladder-Transformer by 30%. This allows us to answer the question: _For two models with similar throughput, how does accuracy compare?_ Importantly, increasing the Ladder-Transformer’s size by 30% leads to less than a 30% decrease in throughput. As a result, the scaled-up Ladder models still achieve higher tokens-per-second (TPS) than their smaller Standard counterparts. We report both accuracy and TPS below following the format of Table 3 in the paper. (Note: the “1B” and “3B” models in the paper correspond to 1.2B and 3.5B parameters respectively; here, we write out the exact values for clarity.) \| Model \| ARC-C \| ARC-E \| HellaSwag\| PIQA \| SciQ \| WinoGram \| Average \| Wikitext PPL \| TPS \| \| ----------- \| ----------- \| ----------- \| ----------- \| ----------- \| ----------- \| ----------- \| ----------- \| ----------- \| ----------- \| \| Standard-Transformer-1.2B \| 34.22 \| 70.33 \| 41.10 \| 71.49 \| 87.30 \| 55.41 \| 59.98 \| 18.54 \| 1008.29 \| \| Ladder-Transformer-1.55B \| 33.96 \| 70.16 \| 42.58 \| 71.98 \| 87.90 \| 55.41 \| 60.33 \| 17.47 \| 1277.66 \| \| Standard-Transformer-3.5B \| 38.99 \| 74.12 \| 46.48 \| 74.59 \| 92.00 \| 58.48 \| 64.11 \| 14.48 \| 949.6 \| \| Ladder-Transformer-4.5B \| 40.96 \| 75.00 \| 46.81 \| 73.99 \| 90.80 \| 57.70 \| 64.21 \| 14.05 \| 1217.71 \| As shown above, the Ladder-Transformer achieves higher average accuracy, lower perplexity, and significantly higher TPS at both the 1.2B and 3.5B sizes. > For Table 4, although the average score of Hybrid-Ladder-8B-16L-retrained is comparable to Llama-3.1-8B-Instruct, in most of the evaluation categories (6 out of 9) the hybrid ladder is worse than the baseline. We retrain the hybrid-ladder-8B-16L model with the same data (3B tokens, all open-source datasets), but this time with logit distillation (KL divergence loss with the logits from the original Llama-3.1-8B-Instruct). Following the format of Table 3 in our paper: \| Model \| MMLU \| ARC-C \| OBQA \| HS \| TQ \| GSM \| HE+ \| IE \| AE \| Average \| \| ----------- \| ----------- \| ----------- \| ----------- \| ----------- \| ----------- \| ----------- \| ----------- \| ----------- \| ----------- \| ----------- \| \| Llama-3.1-8B-Instruct \| 68.14 \| 60.32 \| 43.00 \| 80.04 \| 36.84 \| 84.99 \| 60.40 \| 52.57 \| 18.69 \| 56.11 \| \| Hybrid-Ladder-8B-16L-retrained \| 67.33 \| 59.98 \| 79.05 \| 45.00 \| 37.58 \| 86.81 \| 60.51 \| 59.76 \| 22.43 \| 57.61 \| Now we are better on 5 out of 9 tasks while being 1.5 points higher for the average score, and all tasks we are worse at are within a very small margin (< 1 point). This confidently demonstrates Hybrid-Ladder-8B-16L-retrained can be a drop-in replacement to Llama-3.1-8B-Instruct, achieving 23% speedup with no accuracy lost. We also thank the reviewer for the feedback on clarity and the formatting issue, we will incorporate these in the next version. --- Rebuttal Comment 1.1: Comment: Thanks for the clarification and additional results. Before I give some further comments, could the authors double-check the columns of OBQA and HS of the last table? The numbers do not look right to me. I guess the results of these 2 columns are somehow mixed up. --- Reply to Comment 1.1.1: Comment: Yes I mixed them up when I copied the number from my spreadsheet to here. In the second column of the last table, Hellaswag (HS) should be 79.05 and OpenBookQA (OBQA) should be 45.00 (the average stays the same). I double-checked other numbers and they are correct. Thanks for pointing that out! We also address one remaining question from the initial review phase that we didn't get to during the initial rebuttal: > Is it possible to replace the transformer block with ladder transformer in ViT? If so, is there any corresponding experiments? We believe so, and in fact, ladder-residual can be applied to almost any popular architecture (eg: ViT, mamba, mixture-of-experts) to overlap communication and computation due to the inherent sequential computation nature in all these architectures. In this paper, we only focus on the language domain and experiment with the transformer-based language model, we are looking forward to extending ladder-residual to more architectures and domains in the future.	null	null	null	null	null	null	null	null
The Price of Linear Time: Error Analysis of Structured Kernel Interpolation	Accept (poster)	Summary: The authors provide a theoretical treatment of structured kernel interpolation in Gaussian processes, particularly focusing on cubic convolutional interpolation methods. They provide a comprehensive characterization of error and complexity. Their main results focus on the interplay between the number of inducing points and the error bound (both on the “elementwise” kernel values themselves and on the corresponding Gram matrix spectral norm), finding that there is a distinct difference in this relationship as the dimension increases. Namely, they show that any error tolerance can be achieved in linear time (given enough samples) for dimension less than or equal 3. Moreover, they bound the error of kernel hyper-parameter inference in SKI and posterior parameter approximation error. ## update after rebuttal: I believe my initial score holds after the rebuttal, as the paper remains a strong contribution, in my opinion. Claims And Evidence: The main claim is related to the choice of the number of inducing points to achieve (sub-)linear time complexity with respect to a fixed error tolerance. This is shown rigorously in Section 4, where it is noted that this is possible for any error tolerance for dimension at most 3, and that the error tolerance must grow in higher-dimensional settings to satisfy linear time complexity. Other key claims are related to the hyper-parameter estimation via inexact gradient ascent on the approximate log-likelihood and approximation error of the posterior parameters. In all cases, the authors leverage common techniques in the literature to prove their findings. Methods And Evaluation Criteria: As this is a theoretical work, there are no technical evaluation criteria. The authors employ common and new methods from the literature to show their results, such as recent work related to inexact gradient descent and common techniques related to error characterization in kernel regression. Theoretical Claims: I have checked through the proofs in Appendix B, and they seem relatively straightforward. Experimental Designs Or Analyses: Not relevant, as there are no experiments included in this theoretical work. Supplementary Material: I mostly reviewed the supplementary material Appendix B. Relation To Broader Scientific Literature: The authors position their work in the context of three scientific domains. (1) Within the domain of theoretical analysis of Gaussian process regression/kernel regression with approximated kernels, they have contributed an analysis of a method which has previously been rarely treated: SKI. It is noted that prior works analyzing SKI focused only on one-dimensional features and did not analyze the posterior approximation. (2) In the context of the SKI literature, this works provides a theoretical basis for the widely-used method. (3) The authors also relate to theoretical works from which they utilize results, such as the inexact gradient descent literature. Essential References Not Discussed: There are no missing references, to my knowledge. Other Strengths And Weaknesses: This is a strong paper and provides valuable theoretical insight into a widely-used method. I believe this will be a useful contribution to the community. The only weaknesses would be a bit of lack of clarity in Section 3, as the exact implementation of the SKI method (particularly, the cubic convolutional interpolation) is not clear to me. Other Comments Or Suggestions: Left Column Line 125: I assume SPD kernel means positive semidefinite here and throughout the paper. I believe PSD is the more common nomenclature, and this acronym should be fully spelled out when first introduced. Left Column Line 160-161: “compute the action of the inverse of the regularized…” I don’t think the word “action” needs to be included here. Is it not correct to just say “compute the inverse of the regularized…” Right Column Line 116-119: The inducing points matrix U definition should not be part of the paragraph, but should be separated into its own line. Left Column Line 216: SKI should be capitalized Right Column Line 234: “linearly for d=2” should be “linearly for d=3” Right Column Line 242: healthcar -> healthcare Questions For Authors: Right Column Line 125-128: It is not clear to me how the weight vectors w(x) can be obtained from the convolutional interpolation kernel u(s) of definition 3.1-3.2. Can this be made more clear, or at least can a more direct connection between Section 3.2 and 3.3 be made? Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: Thank you for your support and positive assessment of our work as a valuable contribution! We are glad that you found the proofs straightforward and the work well-positioned. Regarding your points: * Clarifying the SKI Implementation (Sec 3.2 / 3.3 Connection): We will make the connection between the general SKI formulation and cubic interpolation clearer. We will explicitly state that the weight vectors $w(x)$ in $\tilde{k}(x,x^{\prime})=w(x)^{\top}K_{U}w(x^{\prime})$ are constructed using the tensor-product cubic interpolation function $g(x)$ from Definition 3.2. In this context, $g(x)$ uses the cubic kernel $u(s)$ from Definition 3.1, and the function values being interpolated, $f(c_x+hk)$, corresponding to kernel evaluations between inducing points, $k(u_i, u_j)$, which form the matrix $K_U$. We will add cross-references to make this link explicit. * Writing Suggestions: * We will define the SPD (symmetric positive definite) acronym on first use (line 125) but instead replace it with the suggested PSD (positive semi-definite) nomenclature for consistency. * We will rephrase "compute the action of the inverse" to simply "compute the inverse times a vector" or similar. * We will format the definition of the inducing points matrix U on its own line for clarity. * We will ensure consistent capitalization of SKI. * Regarding the comment on Line 234 ("linearly for $d=2$" should be "linearly for $d=3$"): Thank you for prompting us to double-check. You are correct and we will fix this. We appreciate the careful reading. * We will fix the typo "healthcar". Thank you again for your encouraging review and constructive suggestions. --- Rebuttal Comment 1.1: Comment: Thank you for addressing my concerns. I believe my original score holds, and this is a good contribution. --- Reply to Comment 1.1.1: Comment: Thank you for your support!	Summary: For a fixed kernel, non-zero noise-variance parameter, and spatial dimension, the authors give an asymptotic bound on the number of inducing points needed to reach some accuracy threshold with the SKI approximation as a function of the number of data points. Upper bounds on error in the kernel matrix, the log-likelihood, and the posterior mean and variance are all considered. Based on their arguments, the authors recommend a scaling of inducing points like n^(d/3), at least when cubic interpolation is used for mapping onto the structured grid in SKI. ## Update after rebuttal I do not believe that these bounds are tight; from discussion with the authors during the rebuttal period, it seems as though they are in agreement. Nonetheless, after thinking about it, I think this is an interesting enough step in the right direction that I would be fine with seeing it in print. I have thus updated my recommendation to a weak accept. Claims And Evidence: The authors analyze error as a function of the number of inducing points. This is not the same as the time to do almost any calculation involved. Even a matrix-vector product with SKI involves some FFTs, adding a log term into the mix. Moreover, the SKI construction just gives a matrix-vector product; computing likelihoods and linear system solves involves some additional iterative method. The rates of convergence can indeed be bounded by the condition number, and this is controlled via the bound on the kernel (times the number of data points) divided by the noise variance. But these are all potentially rather pessimistic bounds with very large constants. Methods And Evaluation Criteria: This paper is purely theoretical. No empirical evaluation is given, though I would have appreciated it in some places (it would be nice to have a sense of how tight the bounds are). Theoretical Claims: I checked the first proofs in the supplement, though I started skimming toward the end. There are some erroneous statements, though I am not sure how significant they are. For hyper-parameter estimation, the authors claim that dk/dtheta is itself a kernel; but this clearly cannot be true for any family k(x,y) = phi(norm(x-y), theta) s.t. phi(0,theta) is constant, since in that case the diagonal of the kernel is zero. Hence, for example, this statement is invalid for most length-scale parameters for standard kernels -- the derivative matrices will be symmetric, but indefinite. Experimental Designs Or Analyses: There were no experiments. I would have appreciated some, as the bounds given here are mostly upper bounds for which it is hard to judge tightness. Supplementary Material: The supplementary material is where all the proofs are. I did review it, though I was not reading as carefully by the end. Relation To Broader Scientific Literature: The authors claim there is not much other error analysis in the literature of this type. Essential References Not Discussed: I did not see any essential references not discussed. Other Strengths And Weaknesses: Some of the proofs in the supplementary material were a bit of a slog. The first proof, in particular, is essentially an application of distributivity; writing down an induction is fine, but seems like more than really needed. As indicated above, I am not convinced of the tightness of most of these bounds. Some computational experiments (or matching lower bounds, but that seems harder) would have assuaged my skepticism. The fact that SKI suffers a curse of dimensionality is fairly well-known. I also observe that the SKI kernel is a kernel, even if it is only an approximation to the original kernel. However, the original kernel is usually chosen by a modeler based on a rough assessment of the regularity of the function at hand. So altogether, it's not so straightforward to go from statements about error in the kernel matrix (for example) to statements about generalization error. The comment about the use of LLMs in writing the model was interesting, though perhaps left me a little less trusting of the results than I otherwise would have been. Other Comments Or Suggestions: My comments all fit into the boxes above. Questions For Authors: No important questions. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Thank you for your thorough and critical reading of our manuscript. We appreciate the detailed feedback, particularly regarding the assumption about kernel derivatives. Regarding the critique of Assumption 5.3: You are absolutely correct. Our claim that the partial derivative of the kernel $k_\theta$ with respect to lengthscale $\ell$ for RBF is a valid SPD kernel (Assumption 5.3 and a short description about RBF kernel’s before the formal statement) is false. For stationary kernels $k(x,y) = \phi(\|\|x-y\|\|^2/\ell^2)$, the derivative with respect to $\ell$ is symmetric but indefinite. Thanks for noticing this. Crucially, we do not actually need positive definiteness. We only rely on the spectral norm error we derived: this starts with tensor-product convolutional cubic interpolation error (not for kernels specifically). It then moves to elementwise kernel error, which relies on neither positive definiteness nor symmetry. After that the spectral norm bound relies on symmetry (so that the $l_1$ and $l_\infty$ norms are equal), but not positive definiteness. We will thus adjust the assumption to not claim positive definiteness. Regarding Bound Tightness/Experiments: We appreciate the request for empirical validation. We performed experiments measuring $\|\|K - \tilde{K}\|\|_2$ on synthetic data using an RBF kernel. Specifically, we set the number of inducing points according to our theoretical scaling, $m = \lceil n^{d/3} \rceil$, for dimensions $d=2, 3, 4$. We then plotted the log of the approximation error against the log of the sample size $n$. Our theoretical bounds predict that the error should asymptotically approach a constant $O(1)$ for this scaling ($m \propto n^{d/3}$). However, the experiments revealed a more favorable trend: for all tested dimensions ($d=2, 3, 4$), the approximation error actually decreased as $n$ increased. This suggests our theoretical upper bounds are likely pessimistic as you suggested and that the method's practical scaling performance is better than the worst-case guarantee. Furthermore, a careful re-reading of our theory (Theorem 4.5 proof) confirmed the correct threshold condition is $d<3$ vs $d \ge 3$; we had made a typo and written $d \le 3$ vs $d > 3$ and will correct this throughout the paper. We will include plots and details of these experiments in the next revision of the paper. Regarding Novelty (Curse of Dimensionality): While the curse of dimensionality impacting SKI is known, our contribution lies in its theoretical characterization that we can control error by growing inducing points at an $n^{d/3}$ rate and that for $d<3$ this guarantees linear time controlled error, further supported by our empirical findings showing performance exceeding the pessimistic bounds. Regarding Proof Style/LLMs: Lemma A.1 was included for completeness. Regarding LLMs, they assisted in outlining and literature search, but all final proofs were a combination of human and AI derived and human verified. Regarding Generalization Error: We agree kernel matrix error isn't the full story. Our bounds on the posterior mean and covariance approximation errors (Lemmas 5.9, 5.10) provide a more direct theoretical link between the SKI approximation and the resulting predictive distribution's accuracy. Thank you again for your detailed critique. Clarifying the assumption issue and incorporating the empirical results will significantly strengthen the paper. --- Rebuttal Comment 1.1: Comment: Thank you for your responses. I am still on the fence about this, but warmer than I was. The general sentiment of the reviews seems warm enough that I expect this will likely be accepted -- anticipating that this might be the case, I note a few smaller issues below that I suggest correcting in a final version. Regarding tightness of the bounds, I think it is worth noting that interpolation will generally work better in the "tails" of the kernel where there is increased smoothness. So while I think the bound on the spectral norm error is basically correct, I think that it has some built-in looseness for many practical situations. Regarding generalization and time: I think it is worth emphasizing the assumption here that the kernel hyperparameters (including the noise variance term) will not vary as a function of n. Particularly, the results here depend strongly on the assumption that the noise variance term is a nonzero constant. This is not often the case one sees where scaling up the number of measurements -- often the length scale decreases, and sometimes the noise variance term decreases. On more minor notes: - The statement that big-O is only being used for the cubic case should be moved up to the start of 4.1 (before Lemma 4.2, which uses the convention but does not state it). - In the header to 4.1, change "Ski" to "SKI" - Just before Lemma 5.9, change "Similarly to for the score function error" to "Similarly for the score function error" - Change "healthcar" to "healthcare" in the broader impact. --- Reply to Comment 1.1.1: Comment: Thank you for the additional feedback. Regarding the fixed hyperparameters assumption (especially noise variance), you raise a valid point about the scope of our analysis. We will add a brief discussion acknowledging this assumption in the final version and noting that analyzing the setting where hyperparameters vary with $n$ is an important direction for future investigation. Your comment on bound tightness/tails also aligns well with our experimental findings showing potentially pessimistic bounds, as discussed in our rebuttal. We confirm all suggested minor edits (Big-O statement, casing, grammar, typos) will be corrected in the camera-ready version. Thanks again for the constructive feedback.	Summary: In this paper, the authors prove several bounds for quantities of interest when using the structured kernel interpolation approximation of Gaussian processes. These bounds include element-wise errors in the kernel matrix, the spectral norm of the difference between the approximated and true Gram matrices, the log marginal likelihood (referred to as the score function in the paper), and the $L^2$/spectral norm error between the posterior mean and covariance for the same set of hyperparameters. These bounds are derived using results from optimization theory and kernel ridge regression. Claims And Evidence: The authors' claims are substantiated with formal proofs provided in the appendix. Methods And Evaluation Criteria: There are no evaluation criteria. Theoretical Claims: I have checked some of the initial proofs and the ideas behind them, and they sound reasonable. However, I am not familiar with the literature on approximate gradient descent/ascent. Overall, I found the paper overly dense. Although earlier results are used in the later theorems, the paper focuses on theoretical analysis, yet all proofs are relegated to the appendix. I have set my score to weak accept due to this. I believe the paper would be more valuable if the authors included at least a high-level description of their proofs in the main paper, as these are the paper’s main contributions. Experimental Designs Or Analyses: There are no experiments. Supplementary Material: I have reviewed part of the proofs but not results that are not directly linked to the main text. Relation To Broader Scientific Literature: The contributions of the paper provide an important theoretical lens on the properties of SKI, whose experimental validations show that its strength lies in lower-dimensional data; this property could be related to the authors' bounds, which change asymptotic behavior when $d \\geq 3$. As far as I know, such an analysis has not been done before and represents a good initial step toward analyzing methods based on local kernel interpolation. Essential References Not Discussed: I believe no essential references are missing. Other Strengths And Weaknesses: A strength of this paper is that the authors explore all facets of Gaussian process approximation, from the kernel to the final predictive distribution. Other Comments Or Suggestions: - On line 254, the theorem in question was not referenced. - Please revise the referencing of equations and sections, as the same paragraph (lines 294–300) contains inconsistent capitalization. - "Gram matrix" should always be capitalized, as it is derived from the surname of Jørgen Pedersen Gram. Similarly, "SKI" should always be capitalized. - Some citations would be better suited as textual citations rather than parenthetical citations. For example: “In the second group, the foundational work by (Wilson & Nickisch, 2015) that [..]” would be better displayed as “In the second group, the foundational work by Wilson & Nickisch (2015) that [..]”. You can achieve this by replacing `\cite` with `\citet` (if using natbib) or `\textcite` (if using biblatex). - On line 125, left column, the acronym SPD (semi-positive definite?) is not introduced. In GP literature, the acronym PSD (positive semi-definite) is more commonly used. - Please avoid citing very old or inaccessible papers. For example, Lagrange interpolation is referenced as “Lagrange, J.-L. Leçons élémentaires sur les mathématiques. Imprimerie de la République, 1795.” However, it is unclear whether this citation format is correct, as I could not locate this version under this specific publisher. Additionally, it is not specified where in the text the interpolation is defined. The same issue applies to Kolmogorov’s 1940 paper, which is cited in relation to Gaussian processes. Questions For Authors: No additional concerns. Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: Thanks for your helpful review and for recognizing the paper's comprehensive scope. We acknowledge the concern regarding the density of the paper due to proofs being in the appendix. In the next version, we will incorporate additional proof intuitions or summaries of the key steps for our main theorems and lemmas into the main body of the paper to improve readability, as requested. Specifically, while the main text already outlines the core strategy for some results (like Theorem 4.5 relating error bounds to grid spacing and $m$, and Lemma 5.6 using quadratic form bounding techniques for the score function), we will add or enhance the intuitions for several key steps: * For Lemma 4.1 (Interpolation Error), we will note the proof uses induction on dimension $d$, showing how the error bound accumulates multiplicatively based on the 1D case from Keys (1981). * For Prop 4.3 (Gram Matrix Error) and Lemma 4.4 (Cross-Kernel Error), we will clarify that the proofs rely on standard matrix norm inequalities ($\Vert A\Vert_2 \leq \Vert A\Vert_\infty$ for Prop 4.3 using symmetry, and $\Vert A\Vert_2 \le \sqrt{\Vert A\Vert_1 \Vert A\Vert_\infty}$ for Lemma 4.4) combined with the elementwise error bounds derived in Lemma 4.2. * For Lemma 5.9 (Posterior Mean Error), which currently mentions the standard strategy, we will elaborate on the specific steps: using algebraic manipulation (add and subtract terms) and the triangle inequality to decompose the error $\Vert \mu - \tilde{\mu}\Vert_2$ into terms involving the error in the cross-kernel matrix ($K_{\cdot,X} - \tilde{K}_{\cdot,X}$) and the error in the inverse Gram matrix ($(K+\sigma^2I)^{-1} - (\tilde{K}+\sigma^2I)^{-1}$), then applying our previously derived bounds for these components (Lemma 4.4 and Lemma B.4). * For Lemma 5.10 (Posterior Covariance Error), which currently highlights the quadratic form bounding, we will add detail on bounding the prior covariance term ($K_{\cdot,\cdot} - \tilde{K}_{\cdot,\cdot}$) using Prop 4.3, and explicitly mention how the update term's error decomposition utilizes the bounds derived in previous lemmas. We will address the formatting and writing suggestions: * We will carefully revise referencing for consistency (including theorems in Sec 4) and ensure consistent capitalization (e.g., Gram matrix, SKI). * We will use textual citations (\citet/\textcite) where appropriate for better flow. * We will define the SPD (symmetric positive definite) acronym upon first use (line 125), but change it as you suggested to PSD for consistency with common GP literature. * We will review the older citations (Lagrange, 1795; Kolmogorov, 1940). These were included to credit the original foundational works. We will check for standard modern references. Thank you for your constructive feedback, which will help us enhance the clarity and presentation of our work. --- Rebuttal Comment 1.1: Comment: Thank you for the changes, I believe these will enhance the paper and better prime the readers when reading the the full proofs. --- Reply to Comment 1.1.1: Comment: We are glad that we were able to clarify the intuition: thank you for raising your score!	Summary: This paper presents a theoretical analysis for the structured kernel interpolation (SKI, Wilson and Nickisch, 2015), a popular method for scaling Gaussian processes (GPs). The paper proves the error bounds for the SKI gram matrix and examine its effect on GP hyperparameter estimation and posterior inference. Crucially, they identify the number of inducing points needed for error control is $O(n^d/3)$. When $d\leq 3$, SKI can achieve linear complexity for any error tolerance, but for $d>3$ the error must increase with sample size to maintain linear time. This analysis provides key insights into SKI's accuracy-scalability trade-offs. ## Updated after rebuttal: The paper provides a novel theoretical contribution to SKI analysis. The biggest limitation of the current submission is the lack of practical implication. Furthermore, according to authors rebuttal, the experiment results suggest that the bound can be pessimistic and the practical performance of SKI seems to be better than what the worst-case theory indicates. Based on these points, I would suggest authors to incorporate a more comprehensive empirical validation in the next draft to bridge the theory and practice. I will adjust my score from 4 to 3. Claims And Evidence: This paper remains theoretical. The theoretical claims are rigorous. However, I'd appreciate some empirical simulation to validate the theoretical rates, in particular for the regime of $d>3$. Methods And Evaluation Criteria: The paper does not involve proposing a new method. Theoretical Claims: I have checked the proofs of main lemmas and theorems up to section 4 and they seem to be correct. Experimental Designs Or Analyses: NA Supplementary Material: I have checked the proofs of main lemmas and theorems up to section 4 and they seem to be correct. Relation To Broader Scientific Literature: This paper fills in the gap of theoretical analysis of SKI. SKI has been a popular scalable GP method, however, there has not been analysis in its approximation error and how that impacts the downstream GP learning and inference. The error analysis builds on many existing theoretical tools, such as convolutional cubic interpolation error analysis and gradient ascent analysis. But the application of these analysis to GP is still novel. Essential References Not Discussed: NA Other Strengths And Weaknesses: Strength: the paper is well-organized and for most part the intuition behind the theorems and proofs are clear. Weakness: - Writing clarity. I'd appreciate the authors make explicit references of the definitions for various symbols. For example, the K in section 5.1 (line 307 on page 6) is used without reference. It only became clear to me in Theorem 5.7 that $K$ stands for the number of iterations. - Technical clarity. A lot of technical terms are used without clarification/definition. For example, in lemma 4.1 how is the error of tensor-product cubic convolution interpolation defined? And in lemma 4.2, what is $delta_{m,L}$ exactly? I only got a sense of these terms after going over the proofs. Also please clarify what norm you used when mentioning "error". - Missing empirical validation. While I understand the paper's main contribution is the theory, I'd still appreciate some (toy) empirical study that confirms the theory, in particular in the two regimes $d\leq 3$ and $d>3$ and see how their behaviors diverge. And I think highlighting the empirical behavior when $d>$ can really help practitioners understand the practical limitation of SKI. Other Comments Or Suggestions: - Sec 4.1 title, Ski -> SKI - Section 7: typo, healthcar -> healthcare Questions For Authors: - In Lemma 4.2, should we have inequality $\leq$ instead of $=$ in the main equation? - App. A: is lemma A.1 essentially the distributive property of multiplication over addition? - The authors stated that the paper has largely used LLM. Can the authors clarify if any part of the proof is LLM-written? If so, which part, and if the authors have carefully examined through these parts? Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Thank you for your positive feedback and insightful suggestions! We are encouraged that you found the theoretical claims rigorous and the proofs correct. We will address the clarity issues raised: * We will explicitly define $k=1,\ldots,K$ as the iterations when we first use it in Section 5.1. * We will clarify the definition of interpolation error in Lemma 4.1 (as the uniform error bound over the domain using functions) and $\delta_{m,L}$ in Lemma 4.2 (as the tensor-product convolutional cubic interpolation error). We will also ensure the specific norm (spectral, elementwise, L2) is clear whenever "error" is discussed. * We will correct the noted typos (e.g., "healthcar"). * We confirm Lemma 4.2 should use an inequality ($\le$), and will correct this. * Regarding Lemma A.1, you’re right that it essentially shows the distributive property; we included the inductive proof for formal completeness but will add a few sentences that summarize it before the full proof. * Regarding LLM usage: LLMs assisted with brainstorming, literature search, and initial proof drafting. However, all final mathematical arguments, proofs, and derivations presented were significantly refined, validated, and verified by the authors. Regarding the request for empirical validation: We appreciate the suggestion and performed experiments simulating the spectral norm error $\|\|K - \tilde{K}\|\|_2$ for varying $n$ and $d$ using an RBF kernel on synthetic data. Specifically, we set the number of inducing points according to our theoretical scaling, $m = \lceil n^{d/3} \rceil$, for dimensions $d=2, 3, 4$. We then plotted the log of the approximation error against the log of the sample size $n$. Our theoretical bound (Prop 4.3 combined with $m \propto n^{d/3}$) predicts that the error should asymptotically approach a constant $O(1)$ independent of $n$. However, our experiments showed a more favorable outcome for all tested dimensions ($d=2, 3, 4$), the approximation error actually decreased as the sample size $n$ increased with $m$ scaled precisely as $n^{d/3}$. This suggests our theoretical upper bound, particularly the $O(n)$ factor in the numerator derived from the infinity norm bound, is likely pessimistic, and the practical performance of SKI with this scaling is better than the worst-case guarantee. We will add these figures along with experimental details to the next revision. Furthermore, upon reviewing our theoretical derivation (specifically Corollary 4.7 and its proof), there is a typo: the correct regimes are $d<3$ and $d \ge 3$, but this was incorrectly stated as $d \le 3$ vs $d > 3$. We will correct this inconsistency throughout the text. Thank you again for your valuable feedback which has helped improve our paper.	null	null	null	null	null	null
Generalizing Causal Effects from Randomized Controlled Trials to Target Populations across Diverse Environments	Accept (poster)	Summary: This paper studies the identification and estimation problem in generalizing treatment effects from an RCT to an observational dataset. Instead of assuming all relevant separate set is observed, it is assumed that part of them are only observed in one dataset. The identification is made possible by introducing the notion of shadow variables, which is a subset of commonly observed covariates and is conditionally independent of observability given other covariates. The authors then develop the identification theory for the target treatment effect. In addition, they propose a two-stage doubly robust estimator that involves both the selection of shadow variables and doubly robust estimation of the target treatment effect. The efficacy of the proposed methods is demonstrated by extensive numerical experiments. Claims And Evidence: The experiments are solid, but I have several confusion regarding identification theory and estimation procedures. It is not fully clear to me why the theory goes through under the given assumptions -- please see my questions below. Methods And Evaluation Criteria: Yes. Theoretical Claims: I checked the correctness but cannot arrive at a clear conclusion, and clarification is needed. Experimental Designs Or Analyses: Yes, the experiments seem solid. Supplementary Material: Yes, I reviewed the proof in the SM. Relation To Broader Scientific Literature: Generalizing treatment effects to target populations is an important topic, and this paper proposes methods that relax existing conditions, which contributes to this literature and may inspire future developments. Essential References Not Discussed: No to my knowledge. Other Strengths And Weaknesses: If all results are correct, this paper would be interesting. Strengths include: rich results, new identification conditions for generalization, new procedures. But given the confusions I list in the "questions" section, I would urge the authors to clarify them for me to give a fair judgement. Other Comments Or Suggestions: Please see the Questions section below. Given the confusions my current rating is towards reject, but would love to adjust if the authors can address the confusions in the rebuttal. Questions For Authors: 1. Why is Assumption 3.2 testable using observational data, given that $X^m$ is only observed in one dataset? 2. On page 13 (the proof of Lemma 3.4), why Assumptions 2.5 and 3.2 can lead to the first equation (line 664-665)? It seems to use the equivalence between the conditional distributions of $X^m \mid X^c, S=1$ and $X^m \mid X^c$, but I'm not sure this can be implied by the two assumptions, and some clarifications are needed. 3. In Lemma 3.5, what do you mean by "identified"? Do you mean these quantities allow you to compute OR($X^m=x^m, X^c=x^c)$ for every value of $x^m, x^c$? If so, only knowing the conditional expectation $\mathbb{E}[\tilde{OR}(X^m,X^c) \mid X^c,S=1]$ wouldn't allow you to get back to a function of $x^m$ and $x^c$. Please clarify so that I can make a more clear judgement. 4. In step 2 in the identification, why "Under Assumption 2.3, we have $T\indep X^m\mid S=1$"? If I understand correctly, $S=1$ represents the observational dataset in setting 2, so this cannot be true? I think this should be conditional on $S=0$. 5. Can you provide a proof for Theorem 4? 6. Why do you use mean value imputation for $X^m$? Why is this enough for estimating $\tau$ given that Theorem 3.3 uses the density of $X$ given $R=0$? 7. Could you develop consistency and inference guarantees for the resulting estimator? Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We sincerely appreciate the reviewer’s great efforts and insightful comments to improve our manuscript. In below, we address these concerns point by point. > [Q1] Regarding the testability of Assumption 3.2, we would like to clarify the following: 1. Assumption 3.2(1), i.e., $Z\notindep X^m \|\widetilde{X^c}, S=1$, is testable because all three variables are observable in the dataset with $S=1$, where $S=1$ indicates that $X^m$ is observable in this dataset. 2. Assumption 3.2(2), i.e., $Z\indep S \|X^m, \widetilde{X^c}$, is testable for the following reason. Although $X^m$ is unobservable in the dataset with $S=0$, we can still conduct the test based on Theorem 4.1, which does not require the values of $X^m$ in the dataset with $S=0$ since the only expression involving $X^m$ in the equation to be solved, i.e., $\frac{S}{Q(X^m, \widetilde{X^c})}$, is always zero when $S=0$. > [Q2] Thank you for pointing out the issue caused by our accidental omission of the factor $\frac{P(S=1\|X^m,X^c)}{P(S=1\|X^c)}$ in the corresponding lines. However, we would like to clarify that this does not affect our final conclusion (the result on lines 674-675). The corrected proof is as follows: $ E\left[\frac{P(S=0\|X^m,X^c)}{P(S=1 \|X^m,X^c)}\cdot\frac{P(S=1\|X^m=0,X^c)}{P(S=0\|X^m=0,X^c)}\middle\|X^c,S=1\right]$ $=\sum_{x^m}\frac{P(S=0\|X^m=x^m,X^c)}{P(S=1\|X^m=x^m,X^c)} \cdot\frac{P(S=1\|X^m=0,X^c)}{P(S=0\|X^m=0,X^c)}\cdot P(X^m=x^m\|X^c,S=1)$ $=\sum_{x^m}\frac{P(S=1\|X^m=0,X^c)}{P(S=0\|X^m=0,X^c)}\cdot\frac{P(S=0\|X^m=x^m,X^c)}{P(S=1\|X^m=x^m,X^c)}\cdot\frac{P(S=1\|X^m=x^m,X^c)}{P(S=1\|X^c)}\cdot P(X^m=x^m\|X^c)$ $=\frac{P(S=1\|X^m=0,X^c)}{P(S=0\|X^m=0,X^c)\cdot P(S=1\|X^c)}\cdot\sum_{x^m}P(S=0\|X^m=x^m,X^c)\cdot P(X^m=x^m\|X^c)\\ =\frac{P(S=1\|X^m=0,X^c)}{P(S=0\|X^m=0,X^c)\cdot P(S=1\|X^c)}\cdot\sum_{x^m}P(S=0,X^m=x^m\|X^c)$ $=\frac{P(S=1\|X^m=0,X^c)\cdot P(S=0\|X^c)}{P(S=0\|X^m=0,X^c)\cdot P(S=1\|X^c)} $ Thank you again for your insightful feedback. We will address this issue in the revised version of the manuscript. > [Q3] The identification of $OR(X^m,X^c)$ is guaranteed by Theorem 1 in [1], as referenced in Appendix D. The core idea relies on the completeness condition being satisfied. The detailed proof can be found in the Appendix (Proof of Theorem 1 on Pages 14-15) of [1]. Due to the character limit in the rebuttal stage, we regret that we are unable to provide the full proof here. We kindly ask that the reviewer refer to the original paper for further details. We will include this proof in Appendix D of the revised manuscript. Thank you for the suggestion. > [Q4] Thank you for pointing out a typo in our manuscript. Indeed, it should be $T\indep X^m\|R=1$, where $R=1$ is equivalent to $S=0$ in Setting 2. We will correct this typo in the revised version of the manuscript. > [Q5] As cited in the manuscript, Theorem 4.1 is derived from Theorem 2.3 in [2], and the detailed proof can be found in Appendix A.3 (Page 12) of [2]. Due to the character limit in the rebuttal stage, we regret that we are unable to provide the full proof here. We kindly ask that the reviewer refer to the original paper for further details. We will include this proof in the appendix of the revised manuscript. Thank you for your valuable suggestion. > [Q6] We employed mean value imputation to reduce the complexity of imputation and improve its practicality and efficiency. Performing distributional-estimation-based imputation would be perfect, but it requires additional estimation of quantities such as variance, higher-order moments, etc., or the use of generative methods, all of which would increase complexity. Mean value imputation is a commonly used technique to reduce complexity [3], and our experimental results demonstrate that it performs well. Of course, Theorem 3.3 supports distributional-estimation-based imputation, and we will explore it in future work. Thank you for your insightful suggestion. > [Q7] Due to the character limit in the rebuttal stage, we are unable to include the full proof here. We promise to provide the consistency proofs for both doubly robust imputation and doubly robust ATE estimation in the appendix of the revised version. Thank you for your insightful suggestion. * We hope the above discussion will fully address your concerns about our work, and we would really appreciate it if you could be generous in raising your score. Thank you! > References** [1] Miao, W., Liu, L., Li, Y., Tchetgen Tchetgen, E. J., & Geng, Z. (2024). Identification and semiparametric efficiency theory of nonignorable missing data with a shadow variable. ACM/JMS Journal of Data Science, 1(2), 1-23. [2] d’Haultfoeuille, X. (2010). A new instrumental method for dealing with endogenous selection. Journal of Econometrics, 154(1), 1-15. [3] Lin, W. C., & Tsai, C. F. (2020). Missing value imputation: a review and analysis of the literature (2006–2017). Artificial Intelligence Review, 53, 1487-1509. --- Rebuttal Comment 1.1: Comment: Thank you for the response! I have updated the score. --- Reply to Comment 1.1.1: Comment: We are glad to have addressed your concerns and sincerely appreciate your support for our work, as well as your valuable suggestions for improving it. Thank you!	Summary: This paper deals with generalizing treatment effects estimated from RCTs to different environments where there exists environmental shifts. Existing methods assume that covariates common to both source and target datasets contain the separating set, which is often violated in real-world. The authors propose a Two-Stage Doubly Robust (2SDR) method to address this. The key idea is to relax the standard assumption. Instead of requiring the separating set to be present in the common covariates, they only require it to be present in at least one of the datasets. They then use shadow variables (covariates correlated with the missing ones but not directly influencing the environmental shift) to impute the missing covariates. The authors also provide theoretical justification and evaluate the method on synthetic and real-world datasets. Claims And Evidence: 1. The theory assumes that the chosen shadow variables are sufficient to fully determine the distribution of the missing covariates. There's no guarantee that such a set of shadow variables exists or that the proposed selection procedure will find them. If the shadow variables are only weakly predictive of the missing covariates, the imputation will be poor, leading to bias. 2. The claim of unbiasedness also depends on the correct specification of the imputation models or the odds ratio function. The paper acknowledges the doubly robust property, but this only protects against misspecification of one model in each pair. It does not guarantee unbiasedness if both models in a pair are misspecified, or if the shadow variable assumption is violated. The empirical evaluation doesn't systematically investigate the impact of model misspecification. 3. The selection procedure depends on the reliability of the conditional independence tests (RCIT). I would recommend authors discuss these tests' own assumption and limitations because these tests are not perfect, especially in high-dimensional settings with limited data. Methods And Evaluation Criteria: While I know it may be beyond the scope of this rebuttal, simulating scenarios where the shadow variable assumption is partially violated (e.g., by introducing a weak dependence between Z and S) and quantify the resulting bias in the TATE estimates would significantly strengthen the work. Theoretical Claims: I quickly went over the proof of Theorem 3.3, I did not notice significant flaw in the proof. Experimental Designs Or Analyses: The experiments in general demonstrate the effectiveness of the proposed method. Supplementary Material: I quickly review the Appendix. Relation To Broader Scientific Literature: Estimating causal effects from multiple environments is quite important in a lot of the applications, in particular, experiments with multiple sites. Essential References Not Discussed: N/A Other Strengths And Weaknesses: N/A Other Comments Or Suggestions: Figure 1(a) and the related definitions in its caption need improvement. I am confused what type of variables are "covariates affecting treatment effect heterogeneity". Are these variables confounders? Why author state $X_2$ is a covariate affecting neither treatment effect heterogeneity nor environmental shifts in line 68-69? Furthermore, the wording "variables affect environmental shifts" was misleading. Seems like the covariates exhibit distributional differences, but they don't cause the underlying environmental shift. Questions For Authors: Refer to all the weaknesses in the "Claims and Evidence" and "Methods and Evaluation Criteria" sections above. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We sincerely appreciate the reviewer’s great efforts and insightful comments to improve our manuscript. In below, we address these concerns point by point. > [Claims And Evidence 1] First, we would like to clarify that the method we propose for automatically selecting shadow variables is theoretically guaranteed, based on the testability of Assumption 3.2: 1. Assumption 3.2(1), i.e., $Z\notindep X^m \|\widetilde{X^c}, S=1$, is testable because all three variables are observable in the dataset with $S=1$, where $S=1$ indicates that $X^m$ is observable in this dataset. 2. Assumption 3.2(2), i.e., $Z\indep S \|X^m, \widetilde{X^c}$, is testable for the following reason. Although $X^m$ is unobservable in the dataset with $S=0$, we can still conduct the test based on Theorem 4.1, which does not require the values of $X^m$ in the dataset with $S=0$ since the only expression involving $X^m$ in the equation to be solved, i.e., $\frac{S}{Q(X^m, \widetilde{X^c})}$, is always zero when $S=0$. The shadow variables selected by the proposed method should pass the above hypothesis tests, ensuring that they satisfy Assumption 3.2. Second, the existence of shadow variables can also be assessed through hypothesis testing. Moreover, as discussed in the manuscript, Assumption 3.2 is reasonable because not all variables in $X^c$ with predictive ability for $X^m$ are direct causes of $S$ in many real-world scenarios, such as the example of the AIDS study mentioned in the manuscript. Of course, in certain cases, shadow variables may indeed be weak or even absent. We have followed the reviewer's suggestion and conducted experiments in such cases. > [Claims And Evidence 2] Our method, as most DR methods do, requires that at least one of the two models in both stages, either the regression model or the selection score model, be correctly specified to ensure the consistency of the imputation and ATE estimation. However, such requirement for correct model specification is very common in related work [1, 2], and we can leverage techniques such as neural networks to learn the correct model specification as accurately as possible. Of course, we value the reviewer's suggestion and have also conducted experiments to assess the impact of incorrect model specification due to violations of Assumption 3.2. > [Claims And Evidence 3] Thank you for your insightful suggestion. Our method does not rely on specific CIT methods; any CIT method can be used for our hypothesis testing of Assumption 3.2(1). The choice of the method should be determined based on the specific application context. Due to the character limit in the rebuttal phase, we regret that we cannot provide a detailed discussion of the various CIT methods here. We promise to include the relevant discussion in the appendix of the revised manuscript. > [Methods And Evaluation Criteria] Thank you for the suggestion. We have conducted experiments in cases where Assumption 3.2 is violated. Specifically, we conducted experiments on the synthetic dataset by 1. changing the coefficient of Z on S from 0 to \{0.1, 0.3\} to introduce weak dependence; 2. reducing the correlation coefficient between Z and $X^m$ from 0.8 to \{0.3, 0.1\}, so that Z only has a weak predictive ability for $X^m$. \|Extent\|Case 1\|Case 2\| \|:-:\|:-:\|:-:\| \|High\|0.355$\pm$0.319\|0.383$\pm$0.280\| \|Low\|0.311$\pm$0.293\|0.341$\pm$0.281\| \|None\|0.268$\pm$0.212\|0.268$\pm$0.212\| The results demonstrates that while the performance of 2SDR does decline when Assumption 3.2 is violated, the decline is steady as the extent to which Assumption 3.2 is violated increases. > [Other Comments Or Suggestions] Thank you for your valuable suggestions. 1. "Covariates affecting treatment effect heterogeneity" are not equivalent to confounders: Suppose there are three covariates, A, B, and C, and the generation process of Y is $Y=A\cdot T+B+C$. In this case, A is the only variable affecting treatment effect heterogeneity, as the value of $Y(1)-Y(0)$ changes with variations in A. We will improve the related definitions in the figure and its caption. 2. "Variables affect environmental shifts" refers to the variables in the causal graph that point to R (the causes of R). We will revise this statement to make it clearer. * We hope the above discussion will fully address your concerns about our work, and we would really appreciate it if you could be generous in raising your score. Thank you! > References [1] Miao, W., Liu, L., Li, Y., Tchetgen Tchetgen, E. J., & Geng, Z. (2024). Identification and semiparametric efficiency theory of nonignorable missing data with a shadow variable. ACM/JMS Journal of Data Science, 1(2), 1-23. [2] Colnet, B., Mayer, I., Chen, G., Dieng, A., Li, R., Varoquaux, G., ... & Yang, S. (2024). Causal inference methods for combining randomized trials and observational studies: a review. Statistical science, 39(1), 165-191. --- Rebuttal Comment 1.1: Comment: Thank you for your rebuttal. My main concerns are addressed. Thus I will raise my score to 3. But as I go through the comments from other reviews to ensure I give a fair judgment on the work, exploring distributional-estimation-based imputation in the paper could enhance robustness. If possible, could you provide the consistency proofs for both doubly robust imputation and doubly robust ATE estimation during the rebuttal period? I understand there exists 5000 character limit, but at least providing sketch proofs here would be really helpful to evaluate the work. --- Reply to Comment 1.1.1: Comment: We are glad that our previous response has addressed your concerns. We greatly appreciate your support of our work, as well as the constructive suggestions you have provided for improving our paper. Below are our responses to your new suggestions: > [S1] Exploring distributional-estimation-based imputation Thank you for the valuable suggestion. We use mean value imputation because it is more efficient while remaining effective. We agree that performing distributional-estimation-based imputation could enhance robustness, and our Theorem 3.3 also supports this approach. We will take your suggestion and explore it in future work. > [S2] Sketch consistency proofs 1. The DR imputation model $\hat{\psi}$ is consistent if either the $X^m$ regression model or the selection score model of S is correctly specified, and the $\widetilde{OR}$ model is correctly specified. Proof: We only need to prove the unbiasedness of $\hat{\psi}$, and then the consistency of $\hat{\psi}$ in large samples holds under the conditions specified in [2,3]. Step 1: Unbiasedness of the OR model. Given the conditions specified in [1], $\hat{f}(Z\|\widetilde{X^c},S)$ is a consistent estimate of $P(Z\|\widetilde{X^c},S)$. Therefore, based on Eq.(6), if the $\widetilde{OR}$ model is correctly specified, its unbiasedness holds, and thus the unbiasedness of the OR model also holds based on Eq.(4). Step 2: Unbiasedness of $\hat{\psi}$. We need to prove that $E[\hat{\psi}-\psi]=E[(S\cdot(\omega\cdot X^m-\omega\cdot \hat{\delta}(X^c))-\hat{\delta}(X^c))-X^m]=E[(\omega\cdot S-1)\cdot(\hat{\delta}(X^c)-X^m)]=0$ holds, where $\omega=1/P(S=1\|\widetilde{X^c},X^m)$. It is equivalent to proving that $E[(\omega\cdot S-1)\cdot(\hat{\delta}(X^c)-X^m)\|\widetilde{X^c},X^m]=0$ holds. Under Assumption 3.2(2), this further reduces to proving that $E[\omega\cdot P(S=1\|\widetilde{X^c},X^m)-1]\cdot E[\hat{\delta}(X^c)-X^m\|\widetilde{X^c},X^m]=0$ holds. We provide proofs for the following two cases. (1) The $X^m$ regression model is correctly specified while the selection score model is not. In this case, as the $X^m$ regression model is correctly specified, $\hat{\theta}$ is an unbiased estimate of $E[X^m\|\widetilde{X^c},S=1]$. Therefore, given the unbiasedness of the OR model, based on Eq.(2), the unbiasedness of $\hat{\delta}$ holds. Consequently, $E[\hat{\delta}(X^c)-X^m\|\widetilde{X^c},X^m]=0$ holds, and thus the unbiasedness of $\hat{\psi}$ holds. (2) The selection score model is correctly specified while the $X^m$ regression is not. In this case, as the selection score model is correctly specified, $\hat{\gamma}$ is an unbiased estimate of $P(S\|\widetilde{X^c})$. Therefore, given the unbiasedness of the OR model, based on Corollary 3.7, the unbiasedness of $\hat{\pi}_s$ holds. Consequently, $E[\omega\cdot P(S=1\|\widetilde{X^c},X^m)-1]=0$ holds, and thus the unbiasedness of $\hat{\psi}$ holds. 2. If the imputation model is consistent, the DR TATE estimator $\hat{\tau}$ is consistent if either the $Y$ regression model or the selection score model of R is correctly specified, and the $\widetilde{OR}$ model is correctly specified. Proof: When either $\hat{\pi}_r$ or $\hat{\mu}_t$ is consistent, the consistency theory of the DR TATE estimator in large samples has already been established in [5]. Therefore, we focus on proving the consistency of $\hat{\pi}_r$ and $\hat{\mu}_t$ here. (1) If the selection score model and the $\widetilde{OR}$ model are correctly specified, $\hat{\pi}_s$ is consistent, as proved earlier. Since $\hat{\pi}_r$ equals $\hat{\pi}_s$ or $1-\hat{\pi}_s$ based on Corollary 3.7, $\hat{\pi}_r$ is also consistent. (2) Given that the imputation model is consistent, if the outcome regression model is correctly specified, $\hat{\mu}_t$ estimated using the imputed data still maintains consistency under the conditions specified in [2,5]. Therefore, at least one of $\hat{\pi}_r$ or $\hat{\mu}_t$ is consistent, and thus $\hat{\tau}$ is consistent. We will provide full proofs in the revised manuscript. * We hope the new discussion will fully address your remaining concerns, and we would really appreciate it if you could be generous in raising your score further. Thank you again for your valuable suggestions. > References [1] Silverman, B. W. (2018). Density estimation for statistics and data analysis. Routledge. [2] Newey, W. K., & McFadden, D. (1994). Large sample estimation and hypothesis testing. Handbook of econometrics, 4, 2111-2245. [3] Miao, W., & Tchetgen Tchetgen, E. J. (2016). On varieties of doubly robust estimators under missingness not at random with a shadow variable. Biometrika, 103(2), 475-482. [4] Colnet, B., Josse, J., Varoquaux, G., & Scornet, E. (2022). Causal effect on a target population: a sensitivity analysis to handle missing covariates. Journal of Causal Inference, 10(1), 372-414. [5] Little, R. J., & Rubin, D. B. (2019). Statistical analysis with missing data. John Wiley & Sons.	Summary: This paper studies the problem of generalizing RCTs under environment shifts, particularly shifts in the distribution and quantity of covariates. It relaxes the assumption in the prior literature where the separating set (variables that simultaneously affect treatment effect heterogeneity and environmental shifts) is present in both the RCT dataset and target observational dataset. Instead it assumes that the separating set belongs to at least one of the two datasets. Leveraging a shadow variable, the authors introduce a novel Two-Stage Doubly Robust (2SDR) estimator for the Target Average Treatment Effect (TATE). They support their solution through identification theory and demonstrate its effectiveness on both synthetic and real datasets. Claims And Evidence: (1) The paper extends the TATE identifiability conditions, which traditionally require the separating set to be fully observable in both the RCT and the target observational datasets. Instead, it allows for partial observability, requiring the separating set to be present in at least one of the datasets. This generalization is theoretically supported by a novel identifiability framework. (2) The authors propose a Two-Stage Doubly Robust (2SDR) TATE estimator that leverages a shadow variable Z. Empirically, the estimator outperforms existing baselines. Methods And Evaluation Criteria: Yes, the proposed method appears to be novel, and the evaluation seems to be well-suited and thorough. Theoretical Claims: I have reviewed the proofs of Lemma 3.4 and Lemma 3.5, and they seem to be correct to me. Experimental Designs Or Analyses: I haven’t reviewed the dataset generation procedures in detail, but the overall experimental design and analysis seem appropriate and suggest that 2SDR outperforms the alternatives. Supplementary Material: I have reviewed the proofs of Lemma 3.4 and Lemma 3.5. Relation To Broader Scientific Literature: The paper generalizes the TATE identifiability conditions, which traditionally require the separating set to be fully observable in both the RCT and target observational datasets, to allow for partial observability. In this case, the separating set needs to be a subset of one of the datasets. In general, generalizing RCT results beyond the sites where they are conducted is an important problem. This paper addresses environmental shifts, particularly changes in the distribution and quantity of covariates, to enhance the generalizability of RCT results. Essential References Not Discussed: The relevant literature appears to be sufficiently discussed. Other Strengths And Weaknesses: Strengths (1) The extended TATE framework appears to be novel and well-motivated. The relaxation of the separating set to belong to just one of the datasets offers practical value, as it accounts for potential covariate shifts or missing data when generalizing to other sites. (2) Experimental results suggest that 2SDR outperforms other baselines on real datasets, particularly in the JTPA dataset experiment, where it improves estimates for sites different from the RCT data. Weaknesses (1) Assumption 3.2 seems to be a strong condition that may be difficult to satisfy in practice (see questions below). (2) A more detailed discussion is needed to convey the intuition behind why the 2SDR estimator performs better. Other Comments Or Suggestions: (1) A more detailed practical example for Settings 1 and 2 would be helpful. (2) Figure 1 is not very clear or readable unless the entire Section 2 is read. There is room for improving the figure by making some of the definitions more explicit. (3) Readability of Section 4.1.2 needs some improvement (maybe by explaining what is happening in each step or having a diagram). Questions For Authors: (1) How realistic is it to assume the existence of a shadow variable Z that satisfies Assumption 3.2? Under what conditions can we expect this to hold? (2) Will results deteriorate smoothly w.r.t. the extent to which this Assumption 3.2 is satisfied? (3) Typically, under environmental shifts, there may also be shifts in Y\|X shifts. It would be beneficial if the authors discussed situations where we expect only X-shifts and where both X- and Y-shifts might occur, thereby clarifying where 2SDR can be effectively applied? Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: We sincerely appreciate the reviewer’s great efforts and insightful comments to improve our manuscript. In below, we address these concerns point by point. > [Other Comments Or Suggestions] Thank you for your valuable suggestions. We will carefully revise our manuscript based on your recommendations. 1. We will provide more detailed descriptions of the practical examples for Settings 1 and 2. 2. We will improve the related definitions in the figure and its caption to make them clearer. 3. We will add a brief summary at the beginning of each proof step to explain what is happening in that step, and we will also provide a diagram to further illustrate it. > [Q1] How realistic is it to assume the existence of a shadow variable Z that satisfies Assumption 3.2? Assumption 3.2 requires that among the common covariates shared by the two datasets, there exist variables that are correlated with the covariates missing in one of the datasets but do not directly influence environmental shifts (not a direct cause of R). Assumption 3.2 is reasonable in many real-world scenarios, as, typically, most covariates only indirectly affect R, with relatively few variables being direct causes of R. Moreover, Assumption 3.2 is testable: 1. Assumption 3.2(1), i.e., $Z\notindep X^m \|\widetilde{X^c}, S=1$, is testable because all three variables are observable in the dataset with $S=1$, where $S=1$ indicates that $X^m$ is observable in this dataset. 2. Assumption 3.2(2), i.e., $Z\indep S \|X^m, \widetilde{X^c}$, is testable for the following reason. Although $X^m$ is unobservable in the dataset with $S=0$, we can still conduct the test based on Theorem 4.1, which does not require the values of $X^m$ in the dataset with $S=0$ since the only expression involving $X^m$ in the equation to be solved, i.e., $\frac{S}{Q(X^m, \widetilde{X^c})}$, is always zero when $S=0$. Therefore, we can assess whether Assumption 3.2 holds in real-world applications by conducting hypothesis tests on the covariates. > [Q2] Will results deteriorate smoothly w.r.t. the extent to which this Assumption 3.2 is satisfied? Thank you for your insightful suggestion. We have conducted experiments in cases where Assumption 3.2 is violated. Specifically, we conducted experiments on the synthetic dataset under the following cases: 1. Case 1: Assumption 3.2(2) is violated. We changed the coefficient of Z on S from 0 to \{0.1(Low), 0.3(High)\} to introduce weak dependence between Z and S; 2. Case 2: Assumption 3.2(1) is violated. We reduced the correlation coefficient between Z and $X^m$ from 0.8 to \{0.3(Low), 0.1(High)\}, so that Z only has a weak predictive ability for $X^m$. \|Extent\|Case 1\|Case 2\| \|:-:\|:-:\|:-:\| \|High\|0.355$\pm$0.319\|0.383$\pm$0.280\| \|Low\|0.311$\pm$0.293\|0.341$\pm$0.281\| \|None\|0.268$\pm$0.212\|0.268$\pm$0.212\| The results demonstrates that while the performance of 2SDR does deteriorate when Assumption 3.2 is violated, it deteriorates smoothly as the extent to which Assumption 3.2 is violated increases. We will include the results and analysis of this experiment in the revised manuscript. > [Q3] Typically, under environmental shifts, there may also be shifts in Y\|X shifts. It would be beneficial if the authors discussed situations where we expect only X-shifts and where both X- and Y-shifts might occur, thereby clarifying where 2SDR can be effectively applied? Thank you for your valuable suggestion. 2SDR relies on Assumption 3.1, which requires that $Y(t)\indep R\|X^m,X^c$ holds. Therefore, the applicable situations for 2SDR can be summarized as follows: 1. X-shifts. As stated in Definition 2.1, the original definition of environmental shift in our work is X-shifts, i.e., $P(X\|R=1)\neq P(X\|R=0)$. 2. Both X- and Y-shifts caused by X. Although we did not explicitly state this in Definition 2.1, due to the fact that variables in X may be causes of Y, the distribution of Y will also shift along with the distribution of X, i.e., $P(Y\|R=1)\neq P(Y\|R=0)$, or alternatively, $P(X,Y\|R=1)\neq P(X,Y\|R=0)$. 3. $Y\|X^c$ shifts. Given that $Y(t)\indep R\|X$ holds, we have $P(Y\|X,R=1)=P(Y\|X,R=0)$. Therefore, our problem setting essentially assumes the absence of Y\|X shifts. However, for the common covariates $X^c$ shared by the two datasets, there still exist $Y\|X^c$ shifts, i.e., $P(Y\|X^c,R=1)\neq P(Y\|X^c,R=0)$. Assumption 3.2 required by 2SDR is still satisfied under $Y\|X^c$ shifts, and therefore, 2SDR can address $Y\|X^c$ shifts. However, existing methods rely on Assumption 2.8, which requires that $Y(t)\indep R\|X^c$ holds. Under $Y\|X^c$ shifts, Assumption 2.8 does not hold, and thus, in contrast to 2SDR, previous methods cannot address $Y\|X^c$ shifts. We will include the above discussion in the revised manuscript. * We hope the above discussion will fully address your concerns about our work, and we would really appreciate it if you could be generous in raising your score. Thank you!** --- Rebuttal Comment 1.1: Comment: Thanks for your detailed response. My concerns have been appropriately addressed, I have raised my score to 4. --- Reply to Comment 1.1.1: Comment: We are glad to have addressed your concerns and sincerely appreciate your support for our work, as well as your valuable suggestions for improving it. Thank you!	null	null	null	null	null	null	null	null
Multi-Session Budget Optimization for Forward Auction-based Federated Learning	Accept (poster)	Summary: This paper explores the design of bidding strategies for data consumers in auction-based federated learning (AFL), involving three key stakeholders: (1) data owners, who are willing to share their potentially sensitive data in exchange for appropriate compensation; (2) data consumers, who require data to train their federated learning models; and (3) a trusted third-party “auctioneer,” responsible for orchestrating auctions between data owners and consumers to optimize the latter’s key performance metrics. typically assume a single-session setting. However, in practice, data consumers often recruit data owners across multiple training sessions. This limitation in existing works leads to suboptimal performance, as they fail to account for budget allocation across sessions and the complex interplay between inter-session and intra-session dynamics. This paper presents a novel budget allocation strategy under multi-session FL sessions for data consumers in AFL. By tackling a critical issue for AFL sustainability through a theoretically grounded and empirically validated approach, this work makes a valuable contribution to the field Claims And Evidence: Extensive experiments across diverse scenarios (IID/Non-IID data, noisy settings, varying budgets) strongly support the claims. The results hold consistently across key metrics (utility, data volume, accuracy), and comparisons with baselines (e.g., RLB, Fed-Bidder) confirm the advantage of hierarchical RL. Reproducibility is ensured with detailed implementation guidelines in the appendix. Methods And Evaluation Criteria: The hierarchical RL framework well suit the inter-session budget allocation and intra-session budget allocation case, addressing both pacing and bidding dynamics. The datasets used in this paper are widely adopted in the filed of AFL and considering of realistic scenarios (e.g., noisy, Non-IID data) ensures thorough evaluation. Metrics (utility, accuracy) align with the DC’s goal of maximizing model performance under budget constraints Theoretical Claims: No issue found with regard to theoretical claims Experimental Designs Or Analyses: The experiments conducted are rigorous: five runs with averaged results, varied budgets, and multiple noise levels. In addition, the inclusion of both IID and Non-IID settings strengthens validity. Supplementary Material: I have reviewed all the parts of the supplementary material. Relation To Broader Scientific Literature: The work extends DC-oriented AFL by addressing multi-session budget pacing, a gap in prior single-session methods (e.g., Fed-Bidder, RLB). It connects hierarchical RL [Ref 1] to AFL, offering a novel integration. [Ref 1] Pateria, S., Subagdja, B., hwee Tan, A., and Quek, C. Hier archical reinforcement learning: A comprehensive survey. ACM Computing Surveys, 54(5):109:1–109:35, 2021 Essential References Not Discussed: No critical omissions found. Other Strengths And Weaknesses: S1. The paper is mostly clearly written. S2. The paper offers analysis and hence justification for the proposed bidding method, which is technically sound. S3. The empirical results are promising against other baseline bidding strategies, although existing methods are limited because the literature is scarce. W1. More motivation of why multi-session auction scenario is realistic seems to be helpful. W2. The paper would benefit from a clearer exposition of its assumptions regarding data owner behaviors. While the authors describe the decision decision-making process of data consumers, it's unclear whether these are based on empirical observations, theoretical models, or simplifying assumptions. A more explicit statement of the behavioral assumptions underpinning the model would strengthen the paper's foundation and help readers better understand the scope and limitations of the proposed approach. W3. It is suggested to discuss the technical challenges of designing proposed mechanisms. Other Comments Or Suggestions: Typo: Figure 3, MultiBOS-AFL -> MBOS-AFL? Questions For Authors: What bidding strategies did the other bidders use in the experiments? Were their approaches similar or distinct? Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: Thank you for your insightful and encouraging feedback. Below, we provide detailed, point-by-point responses to the key questions raised in the comments. >W1. More motivation of why multi-session auction scenario is realistic seems to be helpful. Practical federated learning environments typically require sequential collaboration phases where the collective model evolves gradually through repeated information consolidation and parameter adjustments. Consider healthcare applications: medical facilities (serving as information contributors) supply clinical data incrementally across various timeframes, leading to progressive enhancement of the shared analytical framework. The operational reality demonstrates that participating entities join the collaboration asynchronously, while available funding resources may vary throughout the project lifecycle. This dynamic creates an ideal application for multi-round bidding structures. Such an approach accurately reflects the continuous nature of knowledge development in these collaborative ecosystems, where both informational assets and processing capabilities are distributed through successive competitive allocation events. >W2. The paper would benefit from a clearer exposition of its assumptions regarding data owner behaviors. While the authors describe the decision decision-making process of data consumers, it's unclear whether these are based on empirical observations, theoretical models, or simplifying assumptions. A more explicit statement of the behavioral assumptions underpinning the model would strengthen the paper's foundation and help readers better understand the scope and limitations of the proposed approach. The method we've developed operates without assumptions regarding the other types of stakeholders' behaviors. Rather, it features inherent adaptability to accommodate diverse stakeholder actions across multiple contexts. Our outlined decision protocols maintain flexibility and remain independent of underlying models, enabling effective functioning regardless of participant motivations or strategic choices. This versatility represents a fundamental advantage of our approach, as it facilitates widespread implementation across various aggregated federated learning environments without limitations imposed by strict behavioral assumptions or predefined conduct expectations. >W3. It is suggested to discuss the technical challenges of designing proposed mechanisms. The first technical challenge lies in optimizing the computational efficiency of utility estimation. Our methodology implements a framework combining Shapley-derived valuations with beta-based reputation tracking to quantify the utility a DC can gain from each DO. However, while Shapley-based methods are conceptually straightforward, they are computationally intensive. Additionally, another challenge is ensuring robust winning price modeling across diverse data owner distributions, as well as balancing the bidding strategy’s performance with budget constraints. Addressing these complexities is crucial for adapting our approach to practical AFL market environments, and we will add further details on these points in the revised paper. >Typo Thank you for pointing that out. We have corrected the typo in the revised manuscript. > What bidding strategies did the other bidders use in the experiments? Were their approaches similar or distinct? As detailed in the experiment section, we compared diverse advanced bidding strategies such as FBs, FBc, among others, by various bidders. This setting is designed to address concerns regarding the potential impact of competitors with advanced bidding strategies. However, if all bidders adopt the same bidding strategy, the differences in their individual historical data could lead to variations in their utility estimation and winning price models. This variance might result in differences in their bidding behaviors. Moreover, in practice, different bidders target diverse data owners due to their distinct training tasks. These factors influence their bids through specific parameters and model approaches in their bidding strategies. Nevertheless, it remains an intriguing area for future research to analyze the dynamics and potential equilibria that arise when all data consumers adopt the same strategy. --- Rebuttal Comment 1.1: Comment: I have read the rebuttals from the authors, which have addressed most of my previous concerns. Thus I decide to remain my score unchanged.	Summary: This paper introduces MBOS-AFL, a hierarchical reinforcement learning-based strategy for multi-session budget optimization in forward auction-based federated learning (AFL). The key idea is to enable data consumers (DCs) to dynamically allocate budgets across multiple FL training sessions (via an inter-session pacing agent) and optimize per-session bidding (via an intra-session agent). The method aims to maximize utility, defined as the aggregated reputation of recruited data owners (DOs). Experiments on six FL benchmarks (MNIST, CIFAR-10, etc.) demonstrate that MBOS-AFL outperforms seven baselines. The author addressed my concerns and I kept my score for technical contribution perspectives ## update after rebuttal Claims And Evidence: The claims are convincingly supported by experiments across diverse settings, including IID/Non-IID data and noisy conditions. The consistent outperformance of MBOS-AFL over RLB and Fed-Bidder variants highlights its novelty in multi-session pacing. Methods And Evaluation Criteria: The hierarchical RL design effectively decouples pacing and bidding decisions. Benchmark datasets and realistic noise/heterogeneity settings ensure relevance to real-world FL challenges. Theoretical Claims: No theoretical claims are made; the work is empirically driven. Experimental Designs Or Analyses: The experimental design is extensive with five budget settings and multiple experimental scenarios. Supplementary Material: Have reviewed all the parts. Relation To Broader Scientific Literature: This paper studies bidding strategy for data consumers in AFL, advancing bidding strategies beyond data privacy concerns. Essential References Not Discussed: All relevant AFL and RL works appear to be cited. Other Strengths And Weaknesses: Strength: 1) The paper’s contents are well-organized. 2) The proposed method is technique soundness. 3) The paper provides insight analysis through its analysis and comparison experiments. 4) The paper proposes a new benchmark dataset processing for auction-based federated learning. Weakness: 1) The system uses the SPSB auction mechanism, why is not bidding the value truthfully optimal? That is the main promise of this type of auction. 2）How to make sure the utility estimation is accurate? 3) The experiments could be enhanced by including some auction-based datasets or data from AFL market. 4) How practical is the proposed framework for real-world use? Other Comments Or Suggestions: 1) In page 7 (Figure 3) "MultiBOS-AFL" seems shall be "MBOS-AFL"; the accuracy plots could benefit from clearer legends 2) In page 8 (Table 2), missing the percentage sign Questions For Authors: refer to the Weakness Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Thank you for your encouraging and insightful feedback. Below, we provide point-by-point explanations to key questions raised in the comments. >W1): The system uses the SPSB auction mechanism, why is not bidding the value truthfully optimal? That is the main promise of this type of auction. In the generalised second price auctions, auction theory [1] proved that bidding the true value of the data resources is optimal towards maximizing the accumulated utility. However, the authors in [2] demonstrated that truthful bidding might not be optimal under budget constraints and limited availability of data resources. In this sense, it is necessary to design bidding strategies for data consumers to automatically calculate bid prices for the available data resources in view of the budget limit, instead of bidding with the prices in the simplified linear form. >W2）How to make sure the utility estimation is accurate? Accurate utility estimation is crucial for the proposed. In practice, it is recommended to continuously monitor and update the utility estimation model as new bidding data becomes available, ensuring its adaptation to potential changes in the AFL environment. >W3) The experiments could be enhanced by including some auction-based datasets or data from AFL market. Thanks a lot for your suggestion. Since publicly available data from the AFL market is not accessible, and existing auction-based datasets, such as those from online advertising, are not directly applicable to a federated learning setting, we have followed established methods [3,4] to collect and generate the datasets used in our experiments. We will also explore additional auction-based datasets that could potentially be adapted for a federated learning setting. >W4) How practical is the proposed framework for real-world use? Indeed, the proposed method can be adapted for use in most FL settings that include an incentive mechanism with data consumers competing to bid for data owners [5,6,7], particularly in auction-based FL scenarios. A practical real-world application is in gas usage estimation within the power generation and delivery industry [8]. >1) In page 7 (Figure 3) "MultiBOS-AFL" -> "MBOS-AFL"; the accuracy plots could benefit from clearer legends >2) In page 8 (Table 2), missing the percentage sign Thanks for your correction and suggestions. We have revised the typos in the manuscript and revised the legend of the accuracy plots to make it clear following your suggestions. ----- [1] Vijay Krishna. Auction theory. Academic press, 2009. [2] Weinan Zhang et al. Optimal real-time bidding for display advertising. In KDD, 2014. [3] Yutao Jiao et al. Toward an automated auction framework for wireless federated learning services market. TMC, 2020. [4] Rongfei Zeng et al. Fmore: An incentive scheme of multi-dimensional auction for federated learning in MEC. In ICDCS, pages 278288, 2020. [5] Yutao Jiao et al. Toward an automated auction framework for wireless federated learning services market. TMC, 2020. [6] Rongfei Zeng et al. Fmore: An incentive scheme of multi-dimensional auction for federated learning in MEC. In ICDCS, pages 278288, 2020. [7] Palash Roy et al. Distributed task allocation in mobile device cloud exploiting federated learning and subjective logic. Journal of Systems Architecture, 113(2):doi:10.1016/j.sysarc.2020.101972, 2021 [8] Hao Sun et al, "HiFi-Gas: Hierarchical Federated Learning Incentive Mechanism Enhanced Gas Usage Estimation," in IAAI-24, 2024.	Summary: The authors deal with the multi-session budget allocation problem for data consumers in auction-based federated learning and propose the MBOS-AFL by introducing a a hierarchical RL framework. Claims And Evidence: claims are well-supported. Methods And Evaluation Criteria: The method is novel and appropriate for multi-session AFL. Theoretical Claims: This paper focuses on problem and algorithmic innovation, and empirical validation Experimental Designs Or Analyses: The experimental setup is sound, with detailed descriptions of datasets, baselines, and training protocols. Supplementary Material: The appendix covers FL training (A.1), RL basics (A.2), and extended experiments (A.6), helpful for reproducibility. Relation To Broader Scientific Literature: This work advances AFL by addressing the multi-session budget pacing gap while integrating reputation systems and hierarchical RL. Essential References Not Discussed: No major omissions. Other Strengths And Weaknesses: The research problem is important and the proposed approach is clear and technique soundness. However, 1. The selected baselines are outdated to some extent. It is suggested to incorporate more recent ones like [1, 2] with the same setting to help position the proposed method. In addition, Can you compare your bidding strategy in auctions with that of [3], though it is not designed for FL settings, it seems quite relevant. Also, can you comment on peer-based mechanisms (e.g., [4],[5],[6] or the references cited therein) vs auction-based mechanisms? 2. Limited exploration of communication costs in FL training rounds. [1] Tang X, Yu H, Li Z, et al. A bias-free revenue-Maximizing bidding strategy for data consumers in auction-based federated learning[C]//Proc. IJCAI. 2024. [2] Tang X, Yu H. Competitive-Cooperative Multi-Agent Reinforcement Learning for Auction-based Federated Learning[C]//IJCAI. 2023: 4262-4270. [3] Chandlekar, Sanjay, et al. "Multi-unit Double Auctions: Equilibrium Analysis and Bidding Strategy using DDPG in Smart-grids." Proceedings of the 21st International Conference on Autonomous Agents and Multiagent Systems. 2022. [4] Richardson, Adam, Aris Filos-Ratsikas, and Boi Faltings. "Budget-bounded incentives for federated learning." Federated Learning: Privacy and Incentive (2020): 176-188. [5] Witkowski, Jens, and David C. Parkes. "A robust bayesian truth serum for small populations." Twenty-Sixth AAAI Conference on Artificial Intelligence. 2012. [6] Radanovic, Goran, Boi Faltings, and Radu Jurca. "Incentives for effort in crowdsourcing using the peer truth serum." ACM Transactions on Intelligent Systems and Technology (TIST) 7.4 (2016): 1-28.】 Other Comments Or Suggestions: 1. Several citations are missing publication years or have unclosed brackets, like "Tang and Yu ()"（Page 2, Section 3). 2. Table 1’s formatting could be improved for readability Questions For Authors: 1: How does MBOS-AFL perform in scenarios with competing DCs using similar strategies? 2: Could the method be extended to handle non-static budget constraints (e.g., dynamically changing total budgets)? 3: How does MBOS-AFL handle abrupt changes in DO availability across sessions? Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: We sincerely appreciate your thoughtful suggestions and valuable feedback. >1. The selected baselines are outdated to some extent. It is suggested to incorporate more recent ones like [1, 2] with the same setting to help position the proposed method. In addition, Can you compare your bidding strategy in auctions with that of [3], though it is not designed for FL settings, it seems quite relevant. Also, can you comment on peer-based mechanisms (e.g., [4],[5],[6] or the references cited therein) vs auction-based mechanisms? Both [1] and [2] propose bidding strategies for DCs in the AFL marketplace, but with different objectives. While [1] focuses on revenue maximization, differing from the utility maximization in this paper, the formulations are distinct. [2], however, aims to maximize utility and maintain the AFL marketplace's health, using a reinforcement learning approach similar to the RLB baseline method in this paper. Both [3] and this paper focus on designing bidding strategies. However, different from [3] which aims to reach an equilibrium between buyers and sellers by designing bidding strategies for both buyers and sellers, we focus on guiding DCs (buyers) to bid for DOs (sellers) by budget management strategies to maximize their KPIs within a given budget. This difference in overall design goals makes it unsuitable to compare [3] (similarly [4][5][6]) with the proposed approach. >2. Limited exploration of communication costs in FL training rounds. The proposed MSBO-FL framework consists of two main parts: the multi-session budget optimization mechanism (i.e., DO recruitment process) and the FL model training (described in “Preliminaries”). In the DO recruitment part, computational complexity primarily arises from the utility estimation function and hierachical reinforcement learning (HRL)-based budget allocation phase. The HRL-based budget allocation is with a time complexity of $O(\|S\|·d + \|C_s\|·d + m)$, where $\|S\|$ represents the state space size, $\|C_s\|$ denotes the number of available qualified DOs in session $s$, $d$ is the neural network dimension, and $m$ is the minibatch size used in the training procedure. For the utility estimation, the computational demand largely stems from the Shapley value-based contribution evaluation. We employ the Beta Reputation System combined with Shapley Value technique, which has a computational complexity of $O(T·N·log N)$, where $T$ and $N$ are the number of training rounds and data owners, respectively. Efficient contribution evaluation remains a challenging issue in federated learning, where high time complexity is common in related problems. In the FL model training part, we adopt the FedAvg method, which is widely used in FL research. To compare the computational complexity of different bidding methods for data consumers in AFL, we can focus on the DO recruitment part, as the FL model training generally relies on FedAvg across methods. This recruitment part typically involves utility estimation and other functions, with the distinguishing feature of our proposed MBOS-AFL method being the two-level HRL-based budget allocation that optimizes both inter-session budget pacing and intra-session bidding strategies. >Other Comments Or Suggestions Thanks a lot for your correction. We have revised the manuscript following your suggestions. >Q1: How does MBOS-AFL perform in scenarios with competing DCs using similar strategies? If all DCs adopt the same bidding strategy, the differences in their individual historical data could lead to variations in their utility estimation and their states. This variance might result in differences in their bidding behaviors (i.e., actions). Moreover, in practice, different DCs target diverse data owners due to their distinct training tasks. These factors influence their bids through specific parameters and model approaches in their bidding strategies. Nevertheless, it remains an intriguing area for future research to analyze the dynamics and potential equilibria that arise when all data consumers adopt the same strategy. >Q2: Could the method be extended to handle non-static budget constraints (e.g., dynamically changing total budgets)? MBOS-AFL framework be naturally extended to accommodate dynamically changing total budgets with minimal modifications. The current design already incorporates state representations that track remaining budgets and historical allocations, making it well-positioned to handle budget fluctuations. >Q3: How does MBOS-AFL handle abrupt changes in DO availability across sessions? The changes in DO availability have limited impact on the operation of MBOS-AFL. This is because such changes directly influence the state observed by the bidding agents, which then adjust their actions based on the learned policy. As a result, MBOS-AFL can dynamically generate appropriate bids in response to variations in DO availability, maintaining robust and adaptive performance under changing conditions. --- Rebuttal Comment 1.1: Comment: Thank you for the author's response. After reading the author's rebuttal, the main concerns I had have been addressed, and I will maintain my score.	null	null	null	null	null	null	null	null
Language Models as Implicit Tree Search	Accept (poster)	Summary: This submission proposes a novel preference optimization method for LLMs, grounded in the theoretical insight that LLMs can be viewed as implicit tree search, combining direct performance optimization with Monte Carlo Tree Search (MCTS). Claims And Evidence: No Methods And Evaluation Criteria: Yes Theoretical Claims: Yes, the proofs are correct Experimental Designs Or Analyses: Experimental Designs Or Analyses are solid and extensive Supplementary Material: I check the proof of theorem and this part is solid. Relation To Broader Scientific Literature: This submission is quiet related to reinforcement learning and MCTS, like AlphaGo. Essential References Not Discussed: No Other Strengths And Weaknesses: Pros: This paper provides solid theoretical demonstration, connecting direct performance optimization and MCTS, showing a novel idea for LLMs preferences alignment without additional reward or value model. Cons: The concept of Implict Tree search is not clearly stated in the main part. The figure 2 in the appendix should be put in the main part, so that readers can have a clear high-level intuitive understanding at the begining. And authors should explain what the difference between explicit and implicit tree search and what the advantages of implicit tree search in the introduction seaction. Other Comments Or Suggestions: Line 137, a typo Convnetional Questions For Authors: What the difference between explicit and implicit tree search and what the advantages of implicit tree search? How to implement an implicit tree search process? Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Thanks for your comments and suggestions. Q1. The concept of Implict Tree search (ITS) is not clearly stated in the main part, and authors should explain what the difference between explicit and implicit tree search and what the advantages of implicit tree search in the introduction section R1: The concept ITS is derived from the theoretical result in (Grill et al. 2020), which verfiies that given each intermediate node in MCTS, if the intermediate node is treated as a state $s$ in RL, then the search process can be approximated by a state-specific stochastic policy $\overline{\pi}(\cdot\|s)$ (Theorem.3.3). With such regards, for each AlphaZero-like MCTS, it always holds a stochastic variant defined by $\overline{\pi}(\cdot\|s)$ across all possible intermediate nodes in the MCTS. However, $\overline{\pi}$ can not be universally optimized by gradient descent. Instead, given each state $s$, $\overline{\pi}(\cdot\|s)$ can only be obtaind by solving a state-specific problem via dichotomic search. To this end, $\overline{\pi}(\cdot\|s)$ can not be used as explicit search like MCTS and instead, only applicable for policy distillation to update the Q value function in AlphaZero-like MCTS (see Eq.7). The difference between MCTS (i.e., explicit tree search) and ITS mainly refers to three parts. First, MCTS is defined and executed by UCB in Eq.7, while ITS is defined through the set of policy optimization objectives (Eq.8) across all possible intermediate nodes in MCTS. Second, the execution of MCTS relies on the empirical visit distribution $\frac{1 + n(s,a)}{\|\mathcal{A}{\sf MCTS}\| + \sum_{a'\in \mathcal{A}_{\sf MCTS}}n(\boldsymbol{s},\boldsymbol{a}')}$. The empirical visit distribution suffers from the cold-start search problems and its expressivness is always lower than the continuous distrbituion. It implies that ITS is more powerful than MCTS. Third, ITS can not be explicitly used to search like MCTS due to its complexity to obtain the universal form of $\overline{\pi}$. Instead, ITS was mostly used in policy distillation to enhance Q-learning. The introduction would be updated to present more details of ITS. Q2. The figure 2 in the appendix should be put in the main part, so that readers can have a clear high-level intuitive understanding at the begining; Line 137, a typo Convnetional R2: Will rearrange the figures, and fix all typos in the next version. Q3. How to implement an implicit tree search (ITS) process? R3: In the original ITS defined in (Grill et al. 2020), it can not be implemented as the search strategy. However, in this paper, we establish a connection between ITS and DPO. So the universal ITS policy $\overline{\pi}$ can be approximated using a second LLM $\varphi$ by solving either Step-Synchronous IT-PO (Eq.16) or Step-Asynchronous IT-PO (Eq.18), alongside the LLM $\theta$ obtained through DPO-like algorithms. Once LLM $\varphi$ is properly trained, the ITS process can be implemented either by directly using $\varphi$ for next-token prediction or by employing our newly proposed decoding strategies: ITS-$\alpha$ and ITS-rollout. --- Rebuttal Comment 1.1: Comment: Thanks for your responsible response that clarifies more details. I maintain my positive score.	Summary: This paper introduces a novel preference optimization framework called Implicit Tree Search Preference Optimization (IT-PO) that addresses the reasoning limitations of existing LM alignment methods like Direct Preference Optimization (DPO). The key innovation is incorporating a second language model policy that approximates AlphaZero-like tree search behavior without requiring explicit tree construction or value modeling. By leveraging the asymptotic equivalence between stochastic policy optimization and MCTS, the authors formulate a preference optimization approach that maintains DPO's advantages while enabling more effective exploration and reasoning. The authors develop both step-synchronous and step-asynchronous variants of IT-PO, along with self-improved policy distillation and decoding strategies. Empirical evaluations demonstrate that IT-PO outperforms both DPO variants in human preference alignment tasks and surpasses MCTS-based language models in mathematical reasoning and planning benchmarks like GSM8K and Game24, while maintaining computational efficiency. Claims And Evidence: The paper's claims are generally well-supported by theoretical analysis and empirical evidence, though with some limitations. The mathematical formulation establishing asymptotic equivalence between implicit tree search and MCTS (Theorem 3.3) provides a sound theoretical foundation for the approach. Methods And Evaluation Criteria: The proposed methods and evaluation criteria are appropriate and well-aligned with the paper's objectives. The authors use established datasets (Anthropic HH for preference alignment, GSM8K and Game24 for reasoning tasks) that are standard in the field, enabling fair comparison with baseline methods. Theoretical Claims: I reviewed the theoretical claims and proofs presented in the paper, with particular focus on the foundational results in Sections 3 and 4. The proof of Theorem 3.3, which establishes the asymptotic equivalence between implicit tree search policy and AlphaZero-like MCTS, appears to be mathematically sound. The authors clearly derive the upper bound on the approximation error between the empirical visit distribution and the stochastic policy solution. The theorem appropriately builds on prior work by Grill et al. (2020), and the adaptation to the language modeling context is logical. Lemma 3.4, which provides the solution form for the implicit tree search policy, is correctly derived. The constraints and conditions for the parameter α(st) are well-specified, though the process of dichotomic search to find this parameter is somewhat glossed over in terms of practical implementation. Experimental Designs Or Analyses: I reviewed the experimental designs and analyses presented in the paper, focusing on the main empirical evaluations in Section 5. The human preference alignment experiments (Section 5.1) use a standard methodology with the Anthropic HH dataset. The authors appropriately use Pythia 2.8B as the base model and employ consistent evaluation metrics (accuracy, diversity, win rate) across all methods. The win rate evaluation using GPT-4 follows established protocols in the field. The visualization of win rates across temperature scaling (Figure 1a) and across iteration rounds of policy distillation (Figure 1b) provides valuable insights into the model's behavior. The mathematical reasoning experiments (Section 5.2) on GSM8K and Game24 datasets are well-designed. The authors properly implement both Path@1 and Equal-Token evaluation settings, allowing for fair comparison across computational budgets. Tables 2 and 3 effectively demonstrate performance across different search widths and node sizes, which helps validate the method's robustness. Supplementary Material: I thoroughly reviewed the supplementary material. The supplementary material effectively supports the main paper's claims with detailed mathematical formulations and implementation specifications. Relation To Broader Scientific Literature: The paper's key contributions intersect several important research directions in language model alignment, reinforcement learning, and reasoning capabilities. Essential References Not Discussed: None Other Strengths And Weaknesses: Strengths 1. The authors establish a solid theoretical connection between Monte Carlo Tree Search (MCTS) and policy optimization through stochastic search, building on previous work by Grill et al. (2020). This provides a principled basis for their implicit tree search approach. 2. IT-PO elegantly combines the benefits of DPO (avoiding reward modeling) with the exploration capabilities of tree search algorithms, addressing a significant gap in current LM alignment methods. 3. Using two separate language models - one for token selection (πθ) and another for implicit tree search exploration (πφ) - is an innovative solution to the reasoning limitations of traditional preference optimization. Weaknesses 1. While avoiding reward modeling, IT-PO introduces additional complexity by requiring two language models instead of one, which increases computational and memory requirements compared to standard DPO. 2. The experiments are conducted using relatively small models (Pythia 2.8B and Llama-7B). It remains unclear how IT-PO would scale to much larger language models, e.g. meta-llama/Llama-3.3-70B-Instruct. 3. While the GSM8K and Game24 benchmarks are standard, they represent relatively constrained reasoning tasks. Evaluation on more diverse and complex reasoning scenarios would strengthen the claims, e.g. MATH and AIME. Other Comments Or Suggestions: - The abbreviation "T-DPO" is used in Figure 1 but "TDPO" in the text, which creates confusion. Questions For Authors: 1. Your method employs two language models (πθ and πφ) during inference, which potentially increases computational requirements compared to standard DPO. Could you provide quantitative metrics on the inference-time overhead of IT-PO compared to alternatives like standard DPO and MCTS-based approaches? 2. For the mathematical reasoning tasks, you mention generating hard negative preference pairs using responses from other questions. How sensitive is your method to the quality of these synthetic preference pairs? Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: Thanks for your comments and suggestions. Q1. The limitation due to the demand of two language models. R1: It is a good question since the requirement of LLM $\theta$ and $\varphi$ is inevitable in IT-PO. Despite so, the implementation can partially mitigate the limitation. First, despite the alternative training between $\theta$ and $\varphi$, we may only use one of them for inference, in particular, we may decode with either $\theta$ or $\varphi$ while the LLMs are derived from the IT-PO for token-level alignment. Second, since LLM $\varphi$ is the key to achieve reasoning, we may resort to the small-size LLM to reduce the training burden. The experiment of MATH in R2 verified this claim. Q2. Larger language models as the base of IT-PO; Q3. Evaluation on more diverse and complex reasoning scenarios. R2-R3: We provide the experiment to simultaneously address the concerns 2 and 3. It is because larger LLMs demand a more difficult task setup for the evaluation, and sufficiently complex reasoning task also requires a base model strong enough to support IT-PO. Specifically, we consider the reasoning-based evaluation on MATH and construct the training set integrated with the training splits of GSM8K and MATH. Due to our computation resource limited in the rebuttal period, comphrensive results based on 70B-size LLM are hardly achieved. Instead, we resort to other larger base LLMs in the Qwen family, i.e., Qwen1.5-32B. Besides, we introduced LLAMA3.1-8B as a small LLM, aiming to verify our claim in R1. Then our evaluated LLMs ($\theta$, $\varphi$) in IT-PO are defined Qwen1.5-32BX2, (Qwen1.5-32B,LLAMA3-8B), then employed the decoding strategies ITS-$\alpha$ and ITS-rollout, respectively. For a comparison, we further train Qwen1.5-32B with MCTS to provide the baselines MCTS-$\alpha$ and MCTS-rollout, where the search depth = 4 and search width = 3. In our implementation, all IT-PO models are trained with the hyper-parameters consistent with GSM8K in SFT, cDPO, and IT-PO, while the search depth and breadth for training are not limited in MATH (i.e., LLM $\varphi$ trained as a stochastic policy without restriction). For decoding, all tree-search baselines use the search depth and width setup in GSM8K. The results are presented as \| \| Baselines/Decoding \| greedy CoT \| -$\alpha$ \| -rollout \| \|--------\|--------\|--------\|--------\|--------\| \| \| Qwen1.5-32B \| 36.1 \| - \| - \| \| \|MCTS- (Qwen1.5-32B) \| - \| 36.0 \| 36.7 \| \| \|ITS- ($\theta$=Qwen1.5-32B, $\varphi$=Qwen1.5-32B) \| - \| 39.8 \| 40.2 \| \| \|ITS- ($\theta$=Qwen1.5-32B, $\varphi$=LLAMA3-8B) \| - \| 37.9 \| 38.2 \| In terms of the greedy CoT results in LLAMA3-8B (20.5), some observations can be found in the table. First, we note that the MCTS strategy derived from is unreliable in MATH, probably due to the conflict between the problem complexity and limited search width and depth during training, while ITS does not suffer from this problem. Second, with a weaker model (LLAMA3-8B) for LLM $\varphi$, IT-PO still enable the improvement of LLM-based reasoning. Q4. Confusion between T-DPO and TDPO. R4: Will fix it in the next version. Q5. Quantify the inference-time overhead of IT-PO compared to alternatives like standard DPO and MCTS-based approaches. R5: The inference-time overhead of IT-PO can be significantly different w.r.t. decoding methods. For token-level alignment, IT-PO used a single model for decoding so that the overhead is consistent of standard DPOs. For reasoning tasks, it refers to ITS-$\alpha$ and ITS-$rollout$ strategies. ITS-$\alpha$ decodes the token like beam-search and for generated sentences, it evaluates their advantages via Eq.22. The process is similar with value inference, and ITS-$\alpha$ holds the similar inference time with MCTS-$\alpha$ (In GSM8K, each token is generated in $\sim$16ms by MCTS-$\alpha$ and in $\sim$18ms by ITS-$\alpha$ using a single A100 80G). ITS-$rollout$ can be treated as test-time-training version of ITS-$\alpha$, which updates $\varphi$ by Eq.21 to execute ITS-$\alpha$ afterwards. It generates 8 (K=8 in Reviewer MF7d's R1) responses for each test prompt to achieve self-training. In our experiment, it results in the extra 30min~1h for each evaluation. Q6. The sensitivity of the preference pairs to the hard negative response. R6: We evaluate ITS-$\alpha$ in GSM8K with hard negative ratio ranged from 100%, 75%, 50%, 25%, 0%, along with the results ranged from 53.2, 52.9, 53.4, 51.8, 50.1, accordingly. The performance drastically drops when the ratio less than 50%. --- Rebuttal Comment 1.1: Comment: Thank you for your thorough response. As my score reflects, I believe this is a commendable piece of work.	Summary: The paper introduces a novel approach to preference optimization for LLM by incorporating Implicit Tree Search, drawing inspiration from Monte Carlo Tree Search and AlphaZero-like algorithms. The key contribution is an alternative preference optimization framework that allows LMs to implicitly execute a tree search strategy without relying on explicit value modeling, which is typically required in traditional MCTS-based methods. Claims And Evidence: The claims presented in the submission are partially supported by empirical evidence, specifically in the experimental comparisons provided in Tables 1-3, which demonstrate performance improvements in preference alignment and mathematical reasoning tasks. However, several claims remain problematic due to unclear presentations. Additionally, the assertion that the proposed method "inherits all advantages of DPO" without introducing drawbacks is unprecise. It's also concerning to use the language model policy as a "universal approximator". Methods And Evaluation Criteria: The proposed methods in the submission are conceptually relevant to the intended application—integrating implicit tree search (ITS) into language model preference optimization. The authors employ empirical comparisons using datasets (Anthropic HH, GSM8K, and Game24) suitable for evaluating preference alignment and reasoning capabilities. However, the performance improvements reported in these experiments are marginal in many cases, raising questions about the practical advantage and meaningfulness of the proposed methodological complexity. Theoretical Claims: The paper introduces a dense and highly formalized mathematical framework, but its presentation could be significantly improved. Currently, it lacks sufficient intuitive justification before diving into complex formulations, making it extremely difficult to follow. I think it's a pity that the theoretical contribution is buried in dense formalism, making it hard to assess whether ITS is a fundamentally new insight or just a reformulation of existing search techniques. Experimental Designs Or Analyses: While empirical results mostly demonstrate some performance gains over existing methods, such improvements are often marginal rather than substantial. By the way, why are some numbers in table 2 missing? Supplementary Material: N/A Relation To Broader Scientific Literature: The key contributions of this paper build on prior literature by integrating ideas from Direct Preference Optimization (DPO), Reinforcement Learning from Human Feedback (RLHF), and Monte Carlo Tree Search (MCTS), particularly AlphaZero-like variants, into a unified implicit policy optimization framework. Specifically, the authors leverage theoretical results from Grill et al. (2020) that interpret AlphaZero-like MCTS as regularized policy optimization and propose using language models as implicit policies to replace explicit tree search. Essential References Not Discussed: N/A Other Strengths And Weaknesses: The manuscript currently lacks a clear motivation, intuition, and sufficient background prior to introducing complex mathematical content. Both the abstract and introduction do not effectively fulfill their intended roles of providing context and engaging readers. Moreover, the manuscript includes many informal and imprecise statements, negatively impacting clarity and professionalism. Some specific examples from the abstract and introduction are: - The phrase "... remains enabling LLM-based reasoning as AlphaZero" - The sentence "While MCTS demands the value function to execute its procedure, contradicting the critical advantage of DPO that skips value learning to achieve faster and more stable preference optimization than RLHF," contains grammatical errors and requires restructuring for readability. Additionally, the current title, "Language Models as Implicit Tree Search," is confusing. Based on the content presented in the main text, a more accurate title would be "Language Models as Implicit Tree Search Policies." Addressing these points will enhance readability, precision, and overall scholarly quality. Other Comments Or Suggestions: N/A Questions For Authors: N/A Code Of Conduct: Affirmed. Overall Recommendation: 2	Rebuttal 1: Rebuttal: Thanks for your comments and concerns. We attempt to address the concerns by discussing the writing quality and the causes of marginal performance gain. Q1: Writing quality. R1: We response from three aspects. First, we appreciate the critique to phrases and grammar, and commit that our writing can be largely improved to encourage the readability. In contrast to complicated terms, particularlly, our abstract and introduction, opt for more accessible and illustrative expressions to enhance comprehension. Here are the argues to some cases found by Reviewer U4U8: Case 1.1 "... remains enabling LLM-based reasoning as AlphaZero": AlphaZero (Silver et, al. 2017b) is the famous Chess game Go system combining MCTS and value-based RL. Our IT-PO exactly uses the stochastic tree-search strategy derived from the consistent AlphaZero-like MCTS pipeline in (Feng, et al. 2023). Case 1.2 "It's also concerning... as a universal approximator": Policies separatly learned by state-specific objectives (Eq.8) can be uniformly approximated by the same LLM. Such writing style aims to provide a straightfoward sight of our work before diving into our formulations. It may also cause the unexpected confusion, which is promised to fix. Second, though the clarity can be improved, we do not agree with the judge "unclear motivation and lack of sufficient background" to our work. Our motivation is intuitivly explained in the first paragraph: LLM trained for preference alignment hardly achieves reasoning without value modeling or RL, in particular, LLM-based reasoning with MCTS. To this, through analyzing the connection between MCTS and its stochastic variant (i.e. implicit tree search in our paper) , we propose IT-PO, the first alignment framework that simultaneously achieve LLM-based reasoning without RL and value modeling. Then we provide the prelimary and warm-up sections (2.5 pages) to elaborate our technical motivation and background. The comments in Reviewers MF7d, REkf, zco2, and also your summary, captured the motivation of this paper. Beyond this, we found that some unjustified comment misinterpret our claim, e.g.""inherits all advantages of DPO" without introducing drawbacks is unprecise" (we did not claim its escape from the DPO drawbacks.) Third, we did provide some intuitions to our theoretical parts. In Figure.2, we have illustrated the theoretical connection across MCTS, ITS derived from (Grill et, al. 2020b), and ITS learned by IT-PO. And each formula was always followed by its source and interpretation, e.g., 131-136 (right) for Theorem 3.3; 175-181 (left) for Lemma 3.4; 207-214(right), 234-237(left) for Lemma 4.1; 263-269 (left) for Theorem 4.2, etc. We commit that more illustrative examples can be introduced to improve the understanding of Theorem 4.3 (and will be refined), while the line of proofs in the paper still can be followed by the majority of reviewers. In general, we acknowledge the manuscript's writing deficiencies and promise for revision, yet we believe the aforementioned evidences insufficient to rate it below the ICML bar. Q2: The causes of marginal performance gain. R2: Our following experiments further explain, even refine the marginal gain: Insufficient iterations of policy distillation. In Sec.4.3, we know IT-PO trains LLM $\varphi$ along with cDPO with respect to fine-tuning LLM $\theta$, which constructs the alternative optimization between $\varphi$ and $\theta$. While in our implementation, we only set the iter=5 in AnthropicHH, and iter=1 in mathematical reasoning tasks (consistent with MCTS-based baselines). With regards to the analysis to Eq.19, increasing the iter number supposes to benefit the IT-PO performance. To this, we reset the IT-PO's evaluation with iter=7 in AnthropicHH, and iter=2 in GSM8K (we also reset iter=2 for MCTS for a fair comparison in Path@1). The results below support our claim. \| AnthropicHH \| Metric \| TDPO$_2$ \| IT-PO (ours, iter=5) \| IT-PO (ours, iter=7) \| \|--------\|--------\|--------\|--------\|--------\| \| \| Alignment (Acc) \| 67.33 \| 69.12 \| 70.83 \| \| \|Diversity (Ent)\| 4.915 \| 5.315 \| 5.421 \| \| GSM8K \| Baselines \| \| iter=1 \| iter=2 \| \|--------\|--------\|--------\|--------\|--------\| \| \| CoT-greedy \| \| 41.4 \| 41.4 \| \| \|BFS-V\| \| 52.5 \| 52.5 \| \| \|MCTS-$\alpha$ \| \| 51.9 \| 51.8 (-0.1) \| \| \|MCTS-rollout \| \| 47.8 \| 48.4 (+0.6) \| \| \|ITS-$\alpha$ (ours) \| \| 53.2 \| 54.3 (+1.1) \| \| \|ITS-rollout (ours) \| \| 51.6 \| 54.8 (+3.2) \| More appropriate experimental setup. Based on the analysis in Sec.2, ITS could be promising in the cold-start search senarios, or more complex reasoning problems. This claim is supported by the results in ProofWriter (R2 in Reviewer MF7d, gain 6%$\sim$17%) and MATH (R2 in Reviewer REkf). Q3. Missing numbers in table 2 R3: In GSM8K, the numbers in Equal-Token are consistent with those in Path@1 using tree-search baselines (see (Feng, et al. 2023)).	Summary: The paper proposes "Implicit Tree Search" (ITS), a stochastic approach that reformulates Monte Carlo Tree Search (MCTS) as a policy optimization problem. Unlike traditional MCTS methods that rely on discrete visit counts for exploration, ITS uses a continuous policy with reversed KL-divergence constraints. Claims And Evidence: The math checks out for their theoretical connection between ITS and MCTS - they've got formal proofs showing how their stochastic policy approach converges to AlphaZero-style search. And when they show their method beating DPO variants on that Anthropic human preference dataset, the numbers in their tables and graphs seem convincing. They're also showing competitive results on those math reasoning benchmarks compared to MCTS approaches. Methods And Evaluation Criteria: Their Implicit Tree Search approach tackles a real problem with traditional MCTS - those discrete visit counts can be limiting, especially early in the search process. Moving to a stochastic policy feels like a natural solution. And I like how they've connected this to preference optimization without needing explicit rewards - that's clever and practical given recent trends. The datasets they picked seem reasonable. Anthropic HH is pretty standard for testing human preference stuff. And those math datasets (GSM8K and Game24) make sense since they need multi-step reasoning where tree search should help. Theoretical Claims: I took a look at several of the theoretical claims and proofs in the paper. The main ones I examined were Theorem 3.3 about the asymptotic equivalence between ITS and MCTS policies, Lemma 3.4 on the solution of ITS policy, and the proofs surrounding Lemma 4.1 and Theorem 4.2 that establish the connection between preference optimization and their implicit tree search approach. Overall the proofs seem technically correct for the most part, but they sometimes gloss over implementation details that would matter in practice. The theoretical foundation is sound enough to justify their approach, even if some of the finer points might benefit from more detailed explanation or justification. Experimental Designs Or Analyses: I examined several aspects of the experimental designs and analyses in the paper. The key experiments involve comparing IT-PO against baseline methods on preference alignment tasks (Anthropic HH dataset) and mathematical reasoning tasks (GSM8K and Game24). For the preference alignment experiments (Section 5.1), I looked at their design for evaluating accuracy, diversity, and win rates. The way they measure these metrics is relatively standard in the field. They use accuracy on chosen vs. rejected completions, predictive entropy for diversity, and GPT-4 judgments for win rates - all common approaches. Their win rate evaluation method involves a temperature scaling study (Figure 1a) which shows how performance varies with different sampling temperatures. This is a solid approach to examine robustness across different decoding strategies. The preference policy distillation experiments (Figure 1b) also make sense methodologically - they're measuring improvement over iterations of their approach. For the mathematical reasoning experiments (Section 5.2), I examined their Path@1 and Equal-Token evaluation setups. The Path@1 metric (success rate for first-path generation) makes sense for evaluating reasoning quality. The Equal-Token comparison is a good attempt to control for computational budget differences between methods. Supplementary Material: The supplementary material provides important details that clarify the theoretical foundations and implementation aspects of their approach. The proofs section in particular adds substantial technical depth to support the claims made in the main paper, especially regarding the equivalence between their stochastic policy and traditional MCTS exploration. Relation To Broader Scientific Literature: The paper effectively creates a bridge between two previously distinct approaches: direct preference optimization methods that are computationally efficient but struggle with complex reasoning, and tree search methods that excel at reasoning but require explicit reward modeling and significant computational resources. By reformulating tree search as implicit policy optimization, it offers a novel way to get "reasoning with free lunch" - complex reasoning capabilities without the overhead of explicit tree search or reward modeling. Essential References Not Discussed: I think most of the citations are discussed in the paper. Other Strengths And Weaknesses: Weakness: While the mathematical reasoning tasks do demonstrate reasoning capabilities, testing on a wider range of reasoning domains (logical puzzles, programming tasks, etc.) would strengthen generalizability claims. Other Comments Or Suggestions: I don't have any major comment left. Questions For Authors: Your evaluation focuses primarily on mathematical reasoning tasks and preference alignment. Have you tested IT-PO on other reasoning-heavy domains such as logical puzzles, programming tasks, or complex planning scenarios? Evidence of broader applicability would strengthen your claim that this approach provides general reasoning improvements Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Thanks for your comments and suggestions. Q1. More implementation details behind theory ("they sometimes gloss...more detailed explanation"). R1: Despite Theorems 4.2, 4.3 containing numerous variables, most are derived from the data rather than serving as hyperparameters. Thus, IT-PO holds implementation consistency with its theoretical foundation except for only two details: 1.1 $\lambda_N(s^{(w)}_t),\lambda_N(s^{(l)}_t)$ indicate how many reasoning paths generated from the state $s_t$, which consists of a prompt $x$ and its responses $y^{(w)}$,$y^{(l)}$ with their contents in the previous $t-1$ steps. For each preference pair, we set $\forall t\in${$1,\cdots,T_w$}, $\lambda_N(s^{(w)}_t)=K_w$ and $\forall t\in${$1,\cdots,T_l$}, $\lambda_N(s^{(l)}_t)=K_l$, where $K_w$, $K_l$ denote how many search start from the $t$-th leaf nodes $s^{(w)}_t, s^{(l)}_t$, respectively. Note that $T_w, T_l$ change with respect to the preference pair. So IT-PO adaptively configure $K_w=\frac{K}{T_w}$, $K_l=\frac{K}{T_l}$ to balance the optimization with different response lengths in $y^{(w)}$,$y^{(l)}$ for each pair. We set $K=8$, inspired from the number of sampled responses for each prompt in many RLHF implementations. 1.2 In gradient analysis in Eq.19, the gradient of $\varphi$ consists of terms in the form $\frac{\pi{\theta}(a_t\|s_t)}{\overline{\pi}{\varphi}(a_t\|s_t)}$ $\nabla \log [{\overline{\pi}}(a_t\|s_t)]$. Due to $\frac{\pi{\theta}(a_t\|s_t)}{\pi{\varphi}(a_t\|s_t)}\in(0,+\infty)$, updating the models with $\frac{\pi{\theta}(a_t\|s_t)}{\overline{\pi}{\varphi}(a_t\|s_t)}$ $\nabla \log [{\overline{\pi}}(a_t\|s_t)]$ may suffer from exploding/vanishing gradients. To this, we used their logarithmic scaling $\frac{\pi{\theta}(a_t\|s_t)}{\overline{\pi}{\varphi}(a_t\|s_t)}$$\rightarrow$ $\exp(\log(\pi{\theta}(a_t\|s_t))-\log(\overline{\pi}{\varphi}(a_t\|s_t)))$ to ensure the less sensitive update ratio. We also took the logarithmic scaling for the gradients in the Step-Asynchronous case (Eq.17), which will be elaborated in our next version due to our rebuttal limit. Q2. More experiments for other reasoning tasks (Weakness and Questions For Authors). R2: We offer evaluation based on ProofWriter [1] for deductive logical reasoning, and Chess Endgame [2] for long-term decision making. For ProofWriter, we follow [3] to generate the test set, then the rest are merged to 41,433 training instances. All training and test instances employed the prompt template in [3] that initiated the start of CoT, then we employ LLAMA2-7B as the base model and all fine-tuning methods only run for a single epoch. For Chess Endgame, we follow the experimental setup in (Feng, et al. 2023). With regards to each prompt-response pair $(x,y^{(w)})$ in ProofWriter and Chess Endgame, we find the dispreferred response $y^{(l)}$ using the same strategy in our mathematical reasoning tasks. We ensure the evaluation in the fair comparison with the CoT and LLM-based tree-search baselines : CoT-greedy, BFS-V, MCTS-$\alpha$tr, MCTS-rollout, CoT-SC-MAJ, CoT-SC-ORM, BFS-V-ORM, MCTS-ORM, whose implementations are consistent in the paper. \| Setting \| Baselines \| \| ProofWriter (Acc %) \| Chess Endgame (Win rate %) \| \|--------\|--------\|--------\|--------\|--------\| \| Path@1 \| CoT-greedy \| \| 37.72 \| 58.14 \| \| \|BFS-V\| \| 48.94 \| 67.75 \| \| \|MCTS-$\alpha$ \| \| 66.71 \| 96.90 \| \| \|MCTS-rollout \| \| 69.23 \| 98.76 \| \| \|ITS-$\alpha$ (ours) \| \| 71.77 \| 99.21 \| \| \|ITS-rollout (ours) \| \| 75.31 \| 99.83 \| \|--------\|--------\|--------\|--------\|--------\| \|Equal-Token \|CoT-SC-MAJ\| \| 36.50 \| 9.84 \| \| \|CoT-SC-MAJ\| \| 36.58 \| 73.80 \| \| \|BFS-V-ORM\| \| 63.42 \| 93.18 \| \| \|MCTS-ORM\| \| 60.86 \| 94.26 \| \| \|ITS-$\alpha$ (ours)\| \| 74.26 \| 96.48 \| \| \|ITS-rollout (ours)\| \| 78.15 \| 98.57 \| For simplicity, we skip the average token number metric to highlight Acc in ProofWriter and Win rate in Chess Endgame. While their results remain based on Path@1 to promise the computation efficiency, and Equal-Token to encourage the comparison in the similar scale of computation consumption cross baselines. In the table, we found that CoT variants almost fail in ProofWriter due to their performances close to random guess (33.33%). MCTS variants obtain significantly better results yet basically under-perform ITS variants with substantial gap in ACC, probably due to the cold-start effect in MCTS learned with one epoch. As for Chess Endgame, ITS variants almost solve the problems with Win rates 99.83% in Path@1 and 98.57% in Equal-Token. It proves ITS also competitive in long-horizon reasoning. Ref: 1. Tafjord, O., et al. ProofWriter: Generating Implications, Proofs, and Abductive Statements over Natural Language (ACL-IJCNLP 2021). 2. Abdulhai, M., et al. Lmrl gym: Benchmarks for multi-turn reinforcement learning with language models. arXiv preprint 3. Pan L, et al. Logic-LM: Empowering Large Language Models with Symbolic Solvers for Faithful Logical Reasoning[C] EMNLP-2023	null	null	null	null	null	null
Automated Red Teaming with GOAT: the Generative Offensive Agent Tester	Accept (poster)	Summary: The authors introduce a new method for an important scenario of multiturn red teaming. The authors propose to use a helpful LLM agent system to dynamically use and combine existing jailbreaking methods to adaptively attack target models. Experiments show its superior performance and efficiency over baseline methods. Claims And Evidence: The claims made are sound Methods And Evaluation Criteria: The proposed method makes sense for the application at hand Theoretical Claims: N/A Experimental Designs Or Analyses: The experiment design are valid Supplementary Material: N/A Relation To Broader Scientific Literature: The key method is a good way to automate the laborous red teaming process Essential References Not Discussed: N/A Other Strengths And Weaknesses: # Strengths - relevant and important topic in LLM safefy - method is using agentic solution, which is novel in this new application - writing is easy to understand # Weaknesses - it is unlikely for the agent to invent new jailbreak techniques, since it is incentivized to reuse or combine existing techniques - a handcrafted workflow CoT pattern is used to better guide the attack LLM at every turn, the current way might not be the most optimal strategy - overall, the paper lacks novelty; it presents a manually designed agent workflow that, while demonstrating strong engineering effort, lacks the conceptual innovation necessary for acceptance at ICML Other Comments Or Suggestions: N/A Questions For Authors: - what model is used for attack agent? Give the exact name of the model, or if it is self trained, provide details on data / training method. Provide them in revised manuscript Code Of Conduct: Affirmed. Overall Recommendation: 2	Rebuttal 1: Rebuttal: Thank you for your comments! We would like to point out that the novelty of our work lies in automating manually discovered red teaming strategies. We achieve very high attack success rates with a lower computational budget than the most comparable work. We do this by following an established evaluation protocol on a curated dataset of adversarial prompts published in peer review work. Our attack method is easily extendible with newly discovered techniques simply by describing them in plain English. Our method is also easily extensible to new models. We have conducted additional experiments showing that the deepseek-r1 model can be “plugged in” to GOAT without any modifications. Under the same evaluation protocols, When we use DeepSeek-r1 as the attacker model and: * GPT-4o as the target, we achieve 63% ASR@1 (compare to 54% from Fig. 2 with the original attacker and 70% from Fig. B.1 with GPT-4o as the attacker) * DeepSeek-r1 as the target: 54% * o1 as the victim: 30% These are the strongest ASR@1 results for any attacker and victim and we believe this shows the method is applicable as-is to newer models with more advanced capabilities. Additionally, our method is directly applicable to new datasets. To show this, we conducted additional experiments without modifying GOAT on a new benchmark. We picked AILluminate – a safety benchmark released by the MLCommons alliance and endorsed by 72 universities and research labs, including 4 major foundational model labs (OpenAI, Anthropic, Meta, and Google) and prestigious universities such as Stanford, MIT, and Cambridge. When rerunning on the widely endorsed Ailluminate benchmark with the original the attacker and Llama 3.1 70B as the target, GOAT maintains its advantage over Crescendo: \| Attack \| Ailluminate \| JailbreakBench (from Fig. 2) \| \|-------------\|--------------\|-------------------------\| \| GOAT \| 43% \| 55% \| \| Crescendo \| 25% \| 28% \| We used the sample publicly available at https://github.com/mlcommons/ailuminate and first described in arXiv:2404.12241. We excluded the prompts on the topic of CSE (due to legal restrictions) but otherwise used all prompts labeled as “unskilled” - since GOAT and Crescendo both transform basic questions into successful jailbreaks. This left us with 550 prompts. We hope these additional results prove the versatility and usefulness of the GOAT method! We look forward to engaging with the reviewer at length about the work and welcome any thoughtful and detailed comments!	Summary: The paper introduces GOAT (Generative Offensive Agent Tester), an automated multi-turn red teaming framework to assess how large language models (LLMs) respond to adversarial prompts. Unlike single-prompt attacks, GOAT uses a separate “attacker model” that dynamically applies various prompt-level “jailbreaking” strategies (such as role-play, hypotheticals, and refusal suppression) during extended back-and-forth conversations with the target LLM. By adapting its approach in each dialogue turn, GOAT more effectively uncovers hidden vulnerabilities and elicits policy-violating outputs. Experiments show that GOAT achieves high attack success rates on both open-source (e.g., Llama) and commercial (e.g., GPT-4) models, outperforming other multi-turn methods within a small number of conversation turns. Claims And Evidence: 1. Automated vs. Human-Like Behavior: GOAT is presented as simulating realistic adversarial behavior (“like a human red teamer”), yet the paper does not provide direct empirical comparisons to actual human-generated multi-turn attacks. Demonstrating that GOAT’s conversation strategies align closely with real user behaviors—or are at least comparably effective—would help bolster this claim. 2. The author states that they conduct experiments on "the latest iteration of this curation and its corresponding scoring method," which refers to JailbreakBench. However, the JBB-Behaviors dataset from JailbreakBench includes only 100 harmful questions, partially derived from existing works. While I acknowledge that JailbreakBench represents the latest benchmark, the limited number of harmful questions may be insufficient for a comprehensive evaluation. I suggest conducting additional experiments on AdvBench, HarmBench, and JAMBench. Methods And Evaluation Criteria: 1. 7 attacks. The rationale behind selecting these specific seven attacks is unclear. What criteria were used for their inclusion, and why were certain cipher techniques, such as [1], excluded? A justification for these choices would strengthen the paper. 2. Ablations. Although the authors highlight seven specific attacks, the paper does not present experiments where one or more techniques are removed or substituted to measure their relative contributions. Moreover, there is no clear breakdown of how crucial elements—such as the “Chain-of-Attack-Thought” reasoning or multi-turn strategy selection—individually impact overall success rates. Without an ablation analysis, it remains difficult to determine which parts of GOAT are most responsible for its observed performance gains. [1]. Yuan Y, Jiao W, Wang W, et al. Gpt-4 is too smart to be safe: Stealthy chat with llms via cipher[J]. arXiv preprint arXiv:2308.06463, 2023. Theoretical Claims: This paper focuses on empirical experimentation rather than formal theoretical frameworks or proofs. While the pseudocode effectively illustrates the general loop of the GOAT approach, it lacks explicit definitions, thorough commentary, and deeper integration with the main text. Experimental Designs Or Analyses: 1. More Benchmarks: I suggest evaluating on JAMBench [1], which includes more challenging and severe harmful questions. 2. More Target LLMs: The proposed method relies on reasoning and conversation chains. Would it be effective against highly reasoning models such as OpenAI's o1, o3, and DeepSeek-R1? 3. Baselines: Although the paper shows GOAT outperforming Crescendo (another multi-turn attack), it does not compare to a broader range of multi-turn or single-turn jailbreak methods beyond Crescendo, such as PAIR, COLD-Attack, and etc. This narrower scope of baselines makes it harder to assess whether GOAT’s improvements generalize across a wider variety of adversarial strategies[2-4]. 4. The attacker LLM. The authors evaluated their approach using GPT-4o as the attacker LLM and concluded that the proposed method enables a plug-and-play adversary with off-the-shelf models, without being dependent on a specific attacker model. However, I am still curious—would using reasoning models such as OpenAI’s o1, o3, or DeepSeek-R1 improve the effectiveness of jailbreak attacks on the target LLM? 5. Human Evaluation To validate GOAT’s “human-like” behavior claims, a direct human evaluation or user study could be conducted. By recruiting experienced red teamers and comparing their multi-turn attack conversations against GOAT’s logs, the authors could quantitatively assess similarities in strategies, escalation patterns, and overall effectiveness. Such a study would not only highlight how closely GOAT mirrors real human adversaries, but also provide insights into potential blind spots or additional techniques real users might employ that the automated system currently lacks. [1]. Jin H, Zhou A, Menke J, et al. Jailbreaking large language models against moderation guardrails via cipher characters[J]. Advances in Neural Information Processing Systems, 2024, 37: 59408-59435. [2]. Ren Q, Li H, Liu D, et al. Derail Yourself: Multi-turn LLM Jailbreak Attack through Self-discovered Clues[J]. arXiv preprint arXiv:2410.10700, 2024. [3]. Jin H, Chen R, Zhou A, et al. Guard: Role-playing to generate natural-language jailbreakings to test guideline adherence of large language models[J]. arXiv preprint arXiv:2402.03299, 2024. [4]. Sun X, Zhang D, Yang D, et al. Multi-Turn Context Jailbreak Attack on Large Language Models From First Principles[J]. arXiv preprint arXiv:2408.04686, 2024. Supplementary Material: The authors did not upload supplementary material. However, I encourage the authors to provide additional resources, such as code or extended experimental details, to enhance the reproducibility and transparency of their work. Relation To Broader Scientific Literature: In the broader context of adversarial prompting and red teaming, GOAT extends prior single-turn jailbreak techniques (e.g., gradient-based or chain-of-thought “single prompt” attacks) by explicitly modeling multi-turn adversarial conversations. While earlier works like Crescendo also explored multi-turn escalation, GOAT differs by employing a separate “attacker model” that dynamically selects from multiple prompting techniques, building on findings that human red-teamers often switch strategies over a conversation. The authors draw upon recent public datasets (e.g., JailbreakBench) and automated evaluators to benchmark, which likewise examine LLM policy refusal rates in adversarial settings. By treating each attack style as an in-context “tool,” GOAT synthesizes ideas from chain-of-thought reasoning and multi-step adversarial probing, contributing a more generalized, agentic red teaming approach to the literature. Essential References Not Discussed: Please see my aforementioned related papers. Other Strengths And Weaknesses: Several multi-turn jailbreaking attacks have been proposed in the past, including Crescendo, as mentioned by the authors. This diminishes the novelty and impact of the proposed work. Other Comments Or Suggestions: Including an illustrative figure of the proposed method would greatly enhance reader comprehension by providing a visual representation of its key components and workflow. Questions For Authors: Please see my aforementioned comments. Code Of Conduct: Affirmed. Overall Recommendation: 1	Rebuttal 1: Rebuttal: We thank the reviewer for their thorough and constructive feedback! # Response to Concerns and Questions We agree with the reviewer that some additional experiments are warranted and we have expanded to cover additional attacker models (deepseek-r1), target models (deepseek-r1 and o1), additional scoring functions (the OpenAI Moderation API), and additional benchmarks (AIlluminate – a safety benchmark endorsed by 72 major AI institutions). In all cases, GOAT maintains its advantage over Crescendo, even if the numbers vary slightly. We agree with the reviewer that comparability to other works is important and that is why we have chosen JailbreakBench with its clear and reproducible evaluation protocols and leaderboard with results for multiple attacks. We have included these comparisons in the last section. Next, we will cite all related works brought up by the reviewer in case of acceptance. We selected the manual attacks we included for automation in GOAT based on our own experience manually red teaming LLMs. There are certainly many more jailbreaking techniques available but we do not claim or aim for comprehensiveness. Instead, GOAT offers a starting point and is designed to be easily extensible. In fact, we believe that narrowly scoped attacks like the ones suggested can easily be automated with the GOAT method. We also thank the reviewer for suggesting that an overview figure be provided. We agree and we refer the reviewer to Figure 1. We welcome all further constructive feedback on the figure! The reviewer also raises an interesting point about ablations – that it is not clear how the multiturn nature of the attacks contributed to the ASR. In Appendices B.2 and B.3, we conducted experiments extending to 50 conversational turns. Based on Figure B.2, we can conclude that the multi-turn nature of the attack is crucial: ASR is low on the first turn and it climbs over the course of a conversation. However, in Figure B.3, we also observe that there is a diminishing return to conversation turns as the ASR plateaus around 10. We look forward to further discussion and appreciate the constructive feedback! # Additional Experimental Results ## New Attacker Model When we use DeepSeek-r1 as the attacker model and: * GPT-4o as the target, we achieve 63% ASR@1 (compare to 54% from Fig. 2 with the original attacker and 70% from Fig. B.1 with GPT-4o as the attacker) * DeepSeek-r1 as the target: 54% * o1 as the victim: 30% ## Additional Scoring Functions When using the the OpenAI moderation API as the scoring function and using the logged conversations of the original attacker model with Llama 3.1 70B as the target, GOAT maintains its advantage over Crescendo. \| Judge \| OpenAI Moderation API \| JailbreakBench (as reported in Fig. 2) \| \|-----------\|----------------------\|----------------\| \| GOAT \| 36% \| 55% \| \| Crescendo \| 18% \| 28% \| ## Additional Datasets Unfortunately, we found that the JAMBench dataset is not readily available. The cited paper contains no download link and the paper itself does not contain the exact set of 160 prompts curated by the authors. Additionally, we note that JailbreakBench represents a curated peer-reviewed selection of HarmBench and AdvBench selected for behaviors that are diverse and achievable. Instead, we picked AILluminate – a safety benchmark released by the MLCommons alliance and endorsed by 72 universities and research labs, including 4 major foundational model labs (OpenAI, Anthropic, Meta, and Google) and prestigious universities such as Stanford, MIT, and Cambridge. When rerunning on the widely endorsed Ailluminate benchmark with the original the attacker and Llama 3.1 70B as the target, GOAT maintains its advantage over Crescendo: \| Attack \| Ailluminate \| JailbreakBench (from Fig. 2) \| \|-------------\|--------------\|-------------------------\| \| GOAT \| 43% \| 55% \| \| Crescendo \| 25% \| 28% \| We used the sample publicly available at https://github.com/mlcommons/ailuminate and first described in arXiv:2404.12241. We excluded the prompts on the topic of CSE (due to legal restrictions) but otherwise used all prompts labeled as “unskilled” - since GOAT and Crescendo both transform basic questions into successful jailbreaks. This left us with 550 prompts. ## Other Comparisons Since we followed the standard evaluation protocol of JailbreakBench, we can directly compare to other methods on the leaderboard at https://jailbreakbench.github.io. In order to allow for an apples-to-apples comparison, we focus on attacks reporting results on the same models as us (Llama 2 7B and GPT-4) and filter out attacks with greater access than ours (e.g. attacks requiring logprobs or white-box access). \| Attack \| Llama 2 7B (ASR@1) \| GPT-4 (ASR@1) \| \| --- \| --- \| --- \| \| PAIR \| 0% \| 34% \| \| AIM \| 0% \| 0% \| \| GOAT \| 30% \| 46% \|	Summary: This paper introduces a novel automated red teaming approach (GOAT) for conversational AI systems. GOAT uses recent reasoning capabilities of advanced LLMs equipped with a set of tools, ie. attack models (here, multiple adversarial prompt strategies). In a multi-turn conversation with the target model, GOAT selects these tools and reasons on the LLM's responses (e.g., refusal) to develop attack strategies with the goal of eliciting harmful behavior from the target LLM. The presented red team system is evaluated on the JailbreakBsnch dataset and compared to the related Crescendo approach. Claims And Evidence: The paper is motivated by (Li et al., 2024), demonstrating that human red teamers can circumvent LLM defenses more easily with multi-turn jailbreaks. The paper claims that it improves existing automated red teaming approaches. To this end, it is compared to the recent Crescendo approach, which outperforms previous approaches by a large margin. For the evaluation, the authors used a LLM-judge assessing the safety of the target LLM after being attacked by the red team approaches, which is one of the common practices. The presentation of evidence is clear. Methods And Evaluation Criteria: The choice of evaluation datasets makes sense for the type of assessment. However, as the authors already mentioned, the selected evaluation (LLM-as-a-judge) approach has its limitations. As in the original Crescendo paper, such the evaluation could be extended by considering external APIs. Theoretical Claims: The paper does not introduce new theoretical foundations, therefore N/A. Experimental Designs Or Analyses: - The selection of the evaluation benchmark JailbreakBench (including the exclusion of specific topics that violated the terms of use of target models) seems to be reasonable and sufficient. Various target models are considered, and a fixed budget for attack model queries and the use of the same attack model are used throughout the experimental setup, so the comparison with Crescendo seems fair. - Experimental evaluation could be extended beyond the usage of an LLM-judge, see above. - Next to quantitative results, the authors present two sample conversation turns leading to successful attacks. These could be extended by failure cases and a discussion of those to provide more details on limitations. Supplementary Material: I briefly check the Appendix, especially section B.1. to find more details on the attack model used. Unfortunately, no information is provided on the attack model used in the main text. Relation To Broader Scientific Literature: The paper is well grounded related works. Li et al. (2024) demonstrate that human red teamers can circumvent LLM defenses more easily with multi-turn jailbreaks. The paper draws inspiration and extends the related approach Crescendo (Russinovich et al., 2024) which also relies on this observation to gradually escalate a conversation into violating outputs. Essential References Not Discussed: The paper adequately covers key literature on LLM adversarial robustness, jailbreaking and (automated) red teaming. Other Strengths And Weaknesses: Strengths: - well-described limitations and future work Weaknesses: - missing details on attack model implementation (see questions). Other Comments Or Suggestions: As mentioned above, I would suggest considering additional evaluation approaches, such as external API, to evaluate the safety of the responses of the target model. Minor suggestions to improve clarity and readability. - line 51 left column: (Zou et al., 2023) seems to be misplaced - readability of figure 3 could be increased - place Fig 4 and 5 on the top of the page. Questions For Authors: - In line 180, you describe that you encourage the attack model to stay on topic and reason adversarially, progressing each turn of the conversation towards the desired unsafe objective. Were you able to observe cases where the attack model is deviating from the desired 4-step reasoning process? If so, how do you handle such cases? - I was not able to find detailed information on the used attack model / helpful-only within the experiments. Could you provide more details? In B.1, you describe re-conducted experiments with Gpt-4o, but what was the original model used in the experiments outlined in the main text? - Could you provide more details on your statement, "Thus, this attack success rate is achieved with very limited access and a very low computational budget relative to other published work,“ While you touch upon it, based on your experimental settings, what is the difference between the required computational budget of GOAT and Crescendo? - Similar to the examples presented in Fig 4 and 5 could you elaborate on failure cases? For example, are there failure cases where the attacker model assesses that the attack goal is reached, but the judge evaluates the response as safe? If yes, is the judge wrong or the attack model? Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: We appreciate the reviewer’s thorough review and suggestions that help us make the paper stronger! We agree with the reviewer about the suggestions for better clarity and readability and will fix these in a potential camera-ready submission! # The attacker model First of all, we apologize as we dropped the discussion of the attacker model used during editing! We used a generic helpful-only language model. Due to the conference’s anonymization policies, we can only share the following information at this point: this model was trained on data that bordered between harmless and harmful content, where the desired response was always to be helpful regardless of safety compliance. No explicit specific attack training data was introduced. All red teaming information is later introduced to the model through in-context learning via the system prompt. Additionally, we have now conducted further experiments with the unmodified deepseek-r1 model and unmodified GOAT system under the same evaluation protocols (see last section), indicating that the exact choice of the attacker model is not critical to the method. # The computational budget Crescendo requires 2 more queries for any given attack turn as it makes use of two supplementary judges external to the attacker model, making it more expensive than GOAT at any given time step. We also note that GOAT achieves any given ASR in fewer turns. (See Appendix B.3, where we extend the number of conversational turns to 50.) Therefore, GOAT requires both less computation per turn and fewer turns overall, making it more efficient than Crescendo. # Handling deviations from reasoning This is a very important question! While we did not observe deviation from the chain of thought format, we experienced a similar issue in early experimentation. In some cases, the attacker model would restate the goal in the prompt it suggested for the target, which would trigger safety due to the overtly unsafe statement of the goals. That is why we introduced reminders in the followup prompt about the expected format. If this issue does appear with other language models, we would suggest automated retries with a higher temperature when deviations are encountered based on string matching. The followup prompt can also be tweaked further to encourage adherence to the reasoning format. # Expanding on failure cases The reviewer brings up a very interesting observation about failure cases! In practice, the failure cases we observe are more often in the opposite direction – the attacker model can be slow to reach a violation. This is because it tends to refrain from directly asking for more violating responses and sometimes runs out of turns before it has reached true violating territory. This can be seen in Figures 3, B.2, and B.3 where the judge’s assessment that a conversation is violating increases with the number of turns. We also agree that early stopping based on an external judge is a fruitful direction for future work to improve on the efficiency of the method. # Additional Experimental Results ## New Attacker Model When we use DeepSeek-r1 as the attacker model and: * GPT-4o as the target, we achieve 63% ASR@1 (compare to 54% from Fig. 2 with the original attacker and 70% from Fig. B.1 with GPT-4o as the attacker) * DeepSeek-r1 as the target: 54% ASR@1 * o1 as the victim: 30% ASR@1 ## Additional Scoring Functions When using the the OpenAI moderation API as the scoring function and using the logged conversations of the original attacker model with Llama 3.1 70B as the target, GOAT maintains its advantage over Crescendo. \| Judge \| OpenAI Moderation API \| JailbreakBench (as reported in Fig. 2) \| \|-----------\|----------------------\|----------------\| \| GOAT \| 36% \| 55% \| \| Crescendo \| 18% \| 28% \| ## Additional Datasets When rerunning on the widely endorsed Ailluminate benchmark with the original the attacker and Llama 3.1 70B as the target, GOAT maintains its advantage over Crescendo: \| Attack \| Ailluminate \| JailbreakBench (from Fig. 2) \| \|-------------\|--------------\|-------------------------\| \| GOAT \| 43% \| 55% \| \| Crescendo \| 25% \| 28% \| ### Context on AILluminate Note: AILluminate is a safety benchmark released by the MLCommons alliance and endorsed by 72 universities and research labs, including 4 major foundational model labs (OpenAI, Anthropic, Meta, and Google) and prestigious universities such as Stanford, MIT, and Cambridge. We used the sample publicly available at https://github.com/mlcommons/ailuminate and first described in arXiv:2404.12241. We excluded the prompts on the topic of Child Sexual Exploitation (due to legal restrictions) but otherwise used all prompts labeled as “unskilled” - since GOAT and Crescendo both transform basic questions into successful jailbreaks. This left us with 550 prompts.	Summary: The paper introduces GOAT (Generative Offensive Agent Tester), an automated red teaming system designed to identify vulnerabilities in LLMs. GOAT simulates adversarial conversations by leveraging various known prompting techniques to jailbreak LLMs. The key innovation is its multi-turn conversational approach that uses a general-purpose LLM to reason through attack strategies dynamically. This mimics how real users might attempt to circumvent safety guardrails. The authors implement GOAT with 7 different red teaming techniques and demonstrate its effectiveness against various models. They report high attack success rates (ASR@10 of 96% against Llama 3.1 8B, 91% against Llama 3.1 70B, and 94% against GPT-4o) while requiring fewer conversation turns than comparable methods. --- ## update after rebuttal: I would like to thank the authors for a clear and comprehensive rebuttal. The authors have addressed the limitations I raised, and with these changes I believe this is a good paper. I will raise my recommendation from weak accept to accept. Claims And Evidence: The paper's primary claims are generally well-supported. However, the claim that GOAT outperforms existing approaches is limited as they only compare to a re-implemented version of Crescendo. No other methods are used for comparisons. Methods And Evaluation Criteria: The authors evaluate GOAT on a diverse set of LLMs. The benchmark used (JailbreakBench) is appropriate. Theoretical Claims: The paper does not make theoretical claims. Experimental Designs Or Analyses: The authors do not disclose what model they use for their main experiments and only say it is a generic helpful-only language model. They do show similar performance if they use GPT-4o as the adversary model (appendix B1) but I find the omission of the details of the main model puzzling. The authors re-implement Crescendo to use the same model as their GOAT method used. But it would be interesting to also compare the original Crescendo with GPT-4. Supplementary Material: I reviewed the appendix. Relation To Broader Scientific Literature: The paper does a good job situating GOAT within the broader red teaming and jailbreaking literature. The authors appropriately differentiate their approach from both single-turn methods and other multi-turn approaches like Crescendo. They acknowledge prior work on adversarial prompting techniques and explain how GOAT builds upon and extends these approaches. Essential References Not Discussed: N/A Other Strengths And Weaknesses: Strengths: - The GOAT framework is simple and sufficiently novel - The paper is well written Weaknesses: - Some key details regarding the model used are not disclosed - The paper could be stronger with discussion on possible defensive measures that could mitigate GOAT attacks. - The context window limitation (capping at 5 turns) may not fully demonstrate the system's capabilities - Only comparison is to Crescendo Other Comments Or Suggestions: Some of the figure labels are too small. L93 (right column): space missing Questions For Authors: 1. Could you clarify which model was used as the "generic helpful-only language model" in your main experiments? This information is critical for reproducibility and for understanding the full capabilities of your system. 2. The paper shows impressive attack success rates, but how might systems defend against GOAT attacks? 3. How might the results change if the context window limitation (5 turns) was removed? The paper mentions this as a limitation, but some additional analysis on how performance might scale with more turns would help readers understand if GOAT's advantages would persist in longer conversations. Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: We thank the reviewer for their thoughtful engagement with the work! We believe the questions and concerns raised will help strengthen the paper. # Q1 Clarifying the attacker model used We apologize for the omission and we will certainly explain this in a potential final revision! For the experiments in the main body, we used a generic helpful-only language model. Due to the conference’s anonymization policies, we can only share the following information at this point: this model was trained on data that bordered between harmless and harmful content, where the desired response was always to be helpful regardless of safety compliance. No explicit specific attack training data was introduced. All red teaming information is later introduced to the model through in-context learning via the system prompt. However, we believe that GOAT is directly applicable to other off-the-shelf attacker models (see appendix B.1 for GPT-4o and the additional results below for deepseek-r1). # Q2 Discussing defenses We believe that models become more robust through an attack/defense iteration cycle. By proposing GOAT, we are encouraging the community to offer stronger defenses to multi-turn attacks. Dedicated moderation classifiers may filter out some of the worst responses, LLMs can be post-trained to better handle multi-turn attacks and GOAT itself can be used to generate such mitigation data. We would be happy to add these suggestions in our Limitations and Future Work section. # Q3 Longer conversations Thank you for bringing up this important point! In Appendix B.3, we have extended conversations up to 50 turns with the Llama 3.1 70B model as the target. GOAT maintains its higher ASR for any given turn over Crescendo. It achieves this with 2 times less queries per turn. This is due to the Crescendo method’s need for two external judge model calls at each turn. We also note that the ASR plateaus at 10 turns, revealing a diminishing return on computational budget. # Other comparisons Since we followed the standard evaluation protocol of JailbreakBench, we can directly compare to other methods on the leaderboard at https://jailbreakbench.github.io. For an apples-to-apples comparison, we focus on attacks reporting results on the same models as us (Llama 2 7B and GPT-4) and filter out attacks with greater access than ours (e.g. logprobs or white-box access). \| Attack \| Llama 2 7B (ASR@1) \| GPT-4 (ASR@1) \| \| --- \| --- \| --- \| \| PAIR \| 0% \| 34% \| \| AIM \| 0% \| 0% \| \| GOAT \| 30% \| 46% \| # External API as Judge To address this concern, we have now used the OpenAI Moderation API and rescored the conversations where Llama 3.1 70B was the victim model. We notice a slight drop in ASR but note that GOAT maintains its relative advantage over Crescendo. (See last section.) We hope this lends further credence to the claim that GOAT outperforms the most comparable method available and we thank the reviewer for the suggestion! # Misc We will certainly adjust our figure sizes for readability and fix the spacing. Thank you for pointing these out! # Additional Experimental Results ## New Attacker Model When we use DeepSeek-r1 as the attacker model and: * GPT-4o as the target, we achieve 63% ASR@1 (compare to 54% from Fig. 2 with the original attacker and 70% from Fig. B.1 with GPT-4o as the attacker) * DeepSeek-r1 as the target: 54% ASR@1 * o1 as the victim: 30% ASR@1 ## New Scoring Functions When using the the OpenAI moderation API as the scoring function and using the logged conversations of the original attacker model with Llama 3.1 70B as the target, GOAT maintains its advantage over Crescendo. \| Judge \| OpenAI Moderation API \| JailbreakBench (as reported in Fig. 2) \| \|-----------\|----------------------\|----------------\| \| GOAT \| 36% \| 55% \| \| Crescendo \| 18% \| 28% \| ## Additional Datasets When rerunning on the widely endorsed benchmark Ailluminate with the original the attacker and Llama 3.1 70B as the target, GOAT maintains its advantage over Crescendo: \| Attack \| Ailluminate \| JailbreakBench (from Fig. 2) \| \|-------------\|--------------\|-------------------------\| \| GOAT \| 43% \| 55% \| \| Crescendo \| 25% \| 28% \| ### Context on AILluminate AILluminate is a safety benchmark released by the MLCommons alliance and endorsed by 72 universities and research labs, including 4 major foundational model labs (OpenAI, Anthropic, Meta, and Google) and prestigious universities such as Stanford, MIT, and Cambridge. We used the sample publicly available at https://github.com/mlcommons/ailuminate and first described in arXiv:2404.12241. We excluded the prompts on the topic of CSE (due to legal restrictions) but otherwise used all prompts labeled as “unskilled” - since GOAT and Crescendo both transform basic questions into successful jailbreaks. This left us with 550 prompts. --- Rebuttal Comment 1.1: Comment: I would like to thank the authors for a clear and comprehensive rebuttal. The authors have addressed the limitations I raised, and with these changes I believe this is a good paper. I will raise my recommendation from weak accept to accept. In addition, I have read the other reviews and their associated rebuttals. The other reviewers raised some valid concerns, but I believe the authors have responded well. I don't completely agree with Reviewer vgNe on two points: - "The paper does not provide direct empirical comparisons to actual human-generated multi-turn attacks". I agree this would strengthen the paper. However, I don't think this comparison is necessary to validate the claim that "[GOAT] responds dynamically based on how the conversation is trending and picks and chooses from multiple techniques available at its disposal, just like a human red teamer would". I think the authors' own domain knowledge is sufficient to make this claim. The authors might consider clarifying this statement in the paper. - The lack of an illustrative figure of the proposed method. I find Figure 1 to be a good high-level overview of the method.	null	null	null	null	null	null
L3A: Label-Augmented Analytic Adaptation for Multi-Label Class Incremental Learning	Accept (poster)	Summary: This work studies the task of Multi-Label Class Incremental Learning (MLCIL), where a model is tasked to incrementally learn to assign multiple labels for each image during each incremental session. The goal is to not forget previously leanred classes while learning novel classes. This task is an extension of class incremental learning. To tackle MLCIL, the authors proposed Label-Augmented Analytic Adaptation (L3A), an exemplar-free approach without storing past sample. Exemplar-free based approach has advantage of protecting privacy, since no past data will be stored. L3A has two modules: i) the Pseudo-Label (PL) module, which generates pseudo-labels for previously learned classes to address label absence, and the ii) Weighted Analytic Classifier (WAC), which uses a closed-form solution with sample-specific weights to mitigate class imbalance. Experiments on MS-COCO and PASCAL VOC (multi-label, or say tags, benchmarks) shows that L3A achieved SOTA performance. The main contribution of this paper is an exemplar-free MLCIL solution L3A that avoids storing past samples, making it suitable for privacy-sensitive applications, and provides a theoretical framework for recursive updates of the classifier using an autocorrelation matrix. Claims And Evidence: Yes. Methods And Evaluation Criteria: Yes. Theoretical Claims: Yes. Experimental Designs Or Analyses: Yes, the experimental design is fair and well-established. Supplementary Material: Yes, I reviewed full supp. material. Relation To Broader Scientific Literature: The main contribution of this paper is an exemplar-free MLCIL solution L3A that avoids storing past samples, making it suitable for privacy-sensitive applications, and provides a theoretical framework for recursive updates of the classifier using an autocorrelation matrix. Essential References Not Discussed: To the best of my knowledge, this paper sufficiently discussed related literature. Other Strengths And Weaknesses: Strengths: 1) The proposed appraoch is, as a whole, novel to a certain degree, with a solid theoretical framework. 2) The Pseudo-Label (PL) module generates pseudo-labels for previously learned classes, effectively addressing the challenge of label absence in multi-label incremental learning. However, this has been widely used in examplar-free pipelines. 3) The paper is well-written 4) The performance of the proposed method L3A looks good, consistenly outperforming the compared methods across two benchmarks. Other Comments Or Suggestions: See below. Questions For Authors: Q1: How does the Pseudo-Label (PL) module handle cases where the confidence scores for pseudo-labels are ambiguous (e.g., close to the threshold)? Does the method incorporate any mechanisms to refine or correct pseudo-labels over time? Q2: The WAC uses a weighting mechanism based on class frequency ((v^{(k)} = 1/\sqrt{f^{(k)}})). Why was this specific weighting function chosen, and how does it compare to other possible weighting schemes (e.g., inverse frequency or log-based weighting)? Q3 (main): Do the authors think the two studied benchmarks are sufficient? MS-COCO and PSACAL VOC indeed have multiple labels. However, the labels are mainly object tags, since these images have multiple objects in every single image. In reality, "Multiple-label" should come from different pespectives about the visual content, such as: time of the day, mood, action, color scheme, even noises type (ImageNet-C). Will the proposed method also work in the settings where the multiple-lables from different aspects? In addition, when the labels are from different granularity, such as: {person, dog, cat} is a common granularity, however, the label can also be: {green T-shirt with a dog, black dots, yellow ear} where the labels are from more fine-grained visual details. How can we prove the proposed method also effective in such scenarios? Q4: It would be interesting to compare the proposed method with open-vocabulary detectors and taggers. My main concern is about the insufficient evaluation of the propsoed method. Code Of Conduct: Affirmed. Overall Recommendation: 2	Rebuttal 1: Rebuttal: Thank you for your insightful feedback and constructive suggestions. Below, we provide a point-by-point response to your questions and concerns. --- Q1: Ambiguous confidence scores and refinement mechanisms in the PL module. --- 1. Ambiguous confidence scores, To clarify this issue, we validate our L3A with different thresholds. The results are shown below and we find that the change of results from 0.65 to 0.80 is not significant. This demonstrates that PL could be robust to ambiguous confidence scores since varying thresholds do not have large effect. Table1: The threshold studies on confidence threshold ($\eta$) in COCO dataset. \| $\eta$ \| COCO B0-C10 Avg. mAP \| COCO B0-C10 Last mAP \| COCO B40-C10 Avg. mAP \| COCO B40-C10 Last mAP \| \|-\|-\|-\|-\|-\| \|0.55\|71.25\|67.21\|78.30\|76.12\| \|0.60\|78.63\|74.21\|79.52\|78.09\| \|0.65\|80.97\|77.08\|79.85\|78.68\| \|0.70\|81.45\|77.57\|79.91\|78.77\| \|0.75\|81.36\|77.58\|79.80\|78.62\| \|0.80\|81.34\|77.57\|79.69\|78.47\| 2. Self-Correction, During the learning, pseudo-labels are not treated as static annotations. Instead, they are continuously re-evaluated as new data is introduced. This iterative correction mechanism helps mitigate the impact of early-stage pseudo-labeling errors. --- Q2: The choice of different weighting mechanism in WAC module. --- In this paper, we use the 1/sqrt(f^(k)) to compute the weight. To validate its superiority, we compare different weighting mechanisms and weighting strategy using 1/sqrt(f^(k)) achieved the best performance. Due to smoothing effect of 1/sqrt(f^(k)), WAC can maintain a good balance against extreme class imbalances. We will include this study in the manuscript. Table2: Different weighting mechanism in WAC module. \|Weighting mechanism\|COCO B0-C10 Avg. mAP\|COCO B0-C10 Last mAP\|COCO B40-C10 Avg. mAP\|COCO B40-C10 Last mAP\| \|-\|-\|-\|-\|-\| \|1/sqrt(f^(k))\|81.45\|77.57\|79.91\|78.77\| \|1/f^(k)\|81.13\|77.30\|79.60\|78.27\| \|1/(log(f^(k))+1)\|81.36\|77.41\|79.87\|78.27\| --- Q3: Analyze the generalization of the L3A method in more diverse multi-label settings. --- Regarding dataset selection, we followed previous multi-label class incremental learning studies [1,2] by using COCO and VOC datasets as benchmarks. The data for multi-label classification needs to contain multi-classes within a single sample, and "multiple objects in every single image" is easy to meet this requirements. We acknowledge that real-world multi-label data can extend beyond object tags to include attributes like time, mood, action, or fine-grained details, but we do not find a dataset having such features while meeting the requirement of multi-classes in a sample (ImageNet-C performs different noises on an image to generate several samples). For the scenario that multi-labels from different aspects, our L3A can also work in theory. When denoting the fine-grained tags as distinct labels, there is less difference between the labels coming from different objects in the training of WAC. Moreover, the buffer layer could enhance separability of features [3] then help distinguish originally similar features during fine-grained classification. We are willing to include the validation of L3A on such a dataset, but unfortunately, we did not find a suitable dataset which has different aspects and meets the requirement of multi-classes in a single sample with limited time. Since we may overlook any relevant datasets, could you please designate a suitable dataset? We are open to include the validation accordingly. --- Q4: Comparison with open-vocabulary detectors and taggers methods. --- In this paper, we focus on the class-incremental continual learning, where the goal is for the model to learn new classes while retaining previously learned knowledge. We need to achieve good performances on both old and new datasets. In contrast, open-vocabulary detectors and taggers typically evaluate on data outside their training distribution (unseen data) to test generalization ability. The motivation is quite different from the continual learning and it may be not appropriate to directly transfer L3A to this task. [1] S. Dong, et al, "Knowledge restore and transfer for multi-label class-incremental learning," in CVPR 2023. [2] K. Du, et al, "Confidence self-calibration for multi-label class-incremental learning," in ECCV 2024. [3] K.-A. Toh, et al, "Between classification-error approximation and weighted least-squares learning," TPAMI, 2008.	Summary: This paper focuses on the multi-label class-incremental continual learning (ML-CICL) task. To address the challenges of missing historical labels and class imbalance in this task, the authors propose an exemplar-free L3A method. Specifically, L3A utilizes a pretrained language model (PLM) to supplement historical labels for samples, mitigating the issue of missing classes. Additionally, it employs weight adaptive calibration (WAC) to obtain sample-adaptive weights, thereby alleviating the class imbalance problem. Experimental results validate the effectiveness of the proposed model. ### update after rebuttal Based on the author's response, I don't have any other questions, and I will keep my rating. Claims And Evidence: The paper presents a approach to addressing the challenges in multi-label class-incremental continual learning. The proposed L3A method is supported by logical reasoning, proof reasoning, and the experimental results are provided to validate its effectiveness. Methods And Evaluation Criteria: The evaluation criteria, including benchmark datasets and performance metrics, appear appropriate for assessing the effectiveness of the method. The experimental setup provides comparisons, supporting the validity of the proposed approach. Theoretical Claims: The paper provides a theoretical proof for WAC, which is intended to mitigate class imbalance by assigning sample-adaptive weights. The provided proof appears to be logically sound and aligns with established principles in adaptive weighting strategies. Experimental Designs Or Analyses: The experimental design is sound, as the proposed method is evaluated on two public benchmark datasets, COCO and PASCAL VOC, making the results reliable. However, the paper includes limited ablation studies, and a more detailed analysis of different backbone setting would further strengthen the evaluation. Supplementary Material: I read the appendix, specifically the proof of Equation (12). Relation To Broader Scientific Literature: This method contributes to the broader scientific literature by proposing an exemplar-free approach for multi-label class-incremental continual learning, which reduces memory consumption compared to traditional exemplar-based methods. Essential References Not Discussed: No. Other Strengths And Weaknesses: WAC is a dynamic weighting-based method. Can it be compared with learnable parameter-based methods? What are the key differences between WAC and such methods? In other tasks, such as long-tailed classification, there are existing methods to address class imbalance. Would it be possible to compare WAC with these approaches? Regarding pretrained parameters, L3A uses pretrained weights from ImageNet-21k, but the paper does not specify what pretrained parameters are used for the comparison methods. Does this affect fairness? In Table 4, why is there a difference of more than 50 between the baseline and the last row? Additionally, the last row should correspond to the L3A method, but it is incorrectly labeled as WAC. Other Comments Or Suggestions: The motivation behind each module is not sufficiently explained. It would be helpful to provide more detailed justifications. The paper lacks experiments with different backbones. It would be beneficial to include such experiments. Questions For Authors: None Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Thank you for your constructive feedback and insightful suggestions. Below are our point-to-point responses: --- W1: Comparison between WAC and learnable parameter-based methods. --- To clarify, the Weighted Analytic Classifier (WAC) is a recursive analytical learning method, where we address class imbalance using a weighting mechanism. Since analytical learning relies on least-squares solutions, it operates without loss functions or gradient computations. This differs from many parameter-based weighted methods using gradient-based optimization, for example: KRT, which adds an Asymmetric Loss [1] in the loss function to handle class imbalance. CSC, which incorporates maximum entropy regularization [2] in the loss function. In contrast, L3A directly computes the closed-form solution for network parameters (without backpropagation), requiring less computational time and lower memory than most parameter-based methods. L3A outperforms the existing learnable parameter-based methods in terms of performance as shown in the manuscript and we further validate the efficiency here. L3A can also improve over existing methods in terms of efficiency. Table1: Comparison of methods in terms of runtime and memory usage in COCO B40C10 benchmark. \|Method\|Time (s)\|GPU Memory (MB)\| \|-\|-\|-\| \|L3A\|1108\|5750\| \|KRT (BP-based)\|16971\|8170\| --- W2: Lack of comparison with class imbalance methods. --- We have selected several class imbalance methods for comparison in the manuscript, including BiC and PRS, which are originally designed for single-label long-tailed continual learning. However, these methods perform poorly in multi-label scenarios. Another compared method KRT is designed for the class imbalance issue in MLCIL which L3A also outperforms. Detailed experimental results can be found in Table 1 of our paper. If you believe we need to include more relevant techniques, could you please provide some methods we need to include? We are open to include the experiments accordingly. --- W3: Unclear pretrained parameters for comparison methods. --- In this paper, all the backbones including TResNetM and ViT-B/16 are pretrained on ImageNet-21k. We will clarify this in the manuscript. --- W4: Large performance gap between baseline and mislabeling in Table-4. --- 1. Performance Gap, the baseline method in Table-4 of paper is a continuous learning method that does not employ any anti-forgetting method. Only the classifier is trained with a frozen backbone in the baseline and the baseline could suffer from catastrophic forgetting, resulting in a very low Last mAP. With the WAC and PL, L3A can achieve high performance with less forgetting. 2. Label Correction, thank you for pointing the mislabeling problem. We will correct "WAC" to "L3A" in the manuscript. --- S1: The motivation behind each module. --- Our paper proposes two main modules, and their motivations are mentioned in the Introduction part. We provide additional clarification: 1. To address the challenges of class imbalance and privacy protection, we introduce a replay-free recursive analytic continual learning method. However, since this approach struggles with class imbalance, we further propose the Weighted Analytic Classifier (WAC), which employs a sample-specific weighting mechanism that adaptively adjusts the importance of samples weights based on class frequency. This correction ensures balanced least-squares optimization 2. To tackle the label absence problem, we adopt a pseudo-labeling strategy (PL module) to generate labels for past tasks. This allows WAC to utilize complete label information during training. --- S2: Lack of experiments with different backbones. --- We add experiments with L3A on pre-trained ViT-B/16. The performance of L3A on ViT-B/16 is slightly worse. The reason could be that vanilla ViTs achieve the less local attention than CNN networks when dealing with complex multi-label images (e.g., scenes with many small objects) [3]. Table2: Performance results on different backbones \|Method\|backbone\|COCO B0-C10 Avg. mAP\|COCO B0-C10 Last mAP\|COCO B40-C10 Avg. mAP\|COCO B40-C10 Last mAP\| \|-\|-\|-\|-\|-\|-\| \|L3A\|TResNetM\|81.45\|77.57\|79.91\|78.77\| \|L3A\|ViT-B/16\|78.32\|73.89\|73.35\|71.66\| [1] T. Ridnik, et al, "Asymmetric loss for multi-label classification," in ICCV 2021. [2] K. Du, et al, "Confidence self-calibration for multi-label class-incremental learning," in ECCV 2024. [3] Z. Liu, et al, "Swin Transformer: Hierarchical Vision Transformer using Shifted Windows," in ICCV 2021.	Summary: This paper proposes Label-Augmented Analytic Adaptation (L3A), an exemplar-free approach without storing past samples, for Multi-Label Class Incremental Learning (MLCIL). It integrates two key modules: the pseudo-label (PL) module implements label augmentation by generating pseudo-labels for current phase samples, and the weighted analytic classifier (WAC) derives a closed-form solution for neural networks. It also introduces sample-specific weights to adaptively balance the class contribution and mitigate class imbalance. Experiments demonstrate the effectiveness of the proposed method. The main contributions of this paper are: - It proposes L3A, an exemplar-free approach that provides a closed-form solution to address catastrophic forgetting in MLCIL. - It introduces the PL module to implement label-augmented by generating labels for previously learned classes. - It introduces the WAC that iteratively updates the classifier by analytic learning and adaptively assigns sample-specific weights. ## update after rebuttal Thank you for your response. However, in my opinion, the motivation is still somehow confusing. Although the authors indicate some of MLCIL's challenges, the approach they take, especially in tackling class imbalance, is not specially designed for MLCIL's unique challenges. Therefore, I keep my rating. Claims And Evidence: The claims are supported by evidence. The proposed method's superiority is evident in its consistent outperformance of existing methods. Methods And Evaluation Criteria: The proposed methods and evaluation criteria make sense for the problem of MLCIL. The proposed L3A is designed to handle the specific challenges of MLCIL, and the evaluation metrics are appropriate for assessing the performance of the proposed method. Theoretical Claims: The theoretical claims in the paper are correct. However, Theorem 3.1 is not exactly called a "Theorem", but a computational method. Experimental Designs Or Analyses: The experimental designs and analyses are overall reasonable. However, the parameter sensitivity analyses are missing. It is not clear how the regularization term $\gamma$ and the buffer layer size affect the final performance. Supplementary Material: I have reviewed the appendix. Relation To Broader Scientific Literature: The key contributions of the paper are related to the broader scientific literature. The authors discuss the related works in single-label CIL, multi-label CIL, and analytic continual learning (ACL). They clearly position their work within the context of existing research and highlight the novelty of their approach. Essential References Not Discussed: There are no essential references that are missing from the paper. Other Strengths And Weaknesses: ### Strengths - The problem studied in this paper is interesting. - This paper is well written and in good sharp, which is easy to follow. - The experimental results are somehow promising. ### Weaknesses - This paper mainly tackles the label absence, class imbalance, and privacy protection challenges in MLCIL. However, the uniqueness of these challenges in the MLCIL problem is not clear. For example, the class imbalance problem, which can be solved using common weighting means, does not seem to be special in the MLCIL problem. The authors should further explain the uniqueness of these challenges in the MLCIL problem to highlight the significance of the proposed approach. - The parameter sensitivity analyses are missing. It is not clear how the regularization term $\gamma$ and the buffer layer size affect the final performance. - From Table 4, one can observe that the effectiveness of PL in the proposed method is not obvious. The authors should analyze the reason for this phenomenon. Other Comments Or Suggestions: The chosen strategy of the threshold values used for generating pseudo-labels needs to be further refined. Moreover, discussing the limitations of the proposed method and potential future research directions can better facilitate the reader's understanding. Questions For Authors: 1. What are the uniqueness of the label absence, class imbalance, and privacy protection challenges in the MLCIL problem? 2. How do the regularization term $\gamma$ and the buffer layer size affect the final performance? 3. The effectiveness of PL in the proposed method is not obvious. The authors should analyze the reason for this phenomenon. Code Of Conduct: Affirmed. Overall Recommendation: 2	Rebuttal 1: Rebuttal: Thank you for your insightful feedback and constructive suggestions. Below we provide point-by-point responses to your comments: --- W1 & Q1: Uniqueness of challenges in MLCIL problem. --- Following prior research [1,2], we consider label absence as a unique challenge in MLCIL. Unlike single-label class-incremental learning (SLCIL), MLCIL inherently suffers from missing labels of previous and future labels during training. This increases the difficulty of learning new classes while preserving knowledge of previous ones since learning with only current labels could erase the previous knowledge, making MLCIL fundamentally different from SLCIL in handling label distribution shifts. For class imbalance, while it is a common issue across machine learning tasks, it has a more severe impact in MLCIL due to catastrophic forgetting. In MLCIL, class distributions are imbalanced not only within each learning phase but also across different incremental stages, where multiple labels coexist per sample, making the imbalance problem even more complex. This leads to the severe under-representation of certain classes as training progresses. As a result, simple class weighting methods often fail to mitigate forgetting effectively in MLCIL, necessitating additional analysis of the class distribution shifts across different incremental learning phases. For privacy protection, it is a challenge across CIL and existing MLCIL approaches rely on data replaying [1,2], which are incompatible with real-world scenarios when data storage is restricted. This makes exploring exemplar-free methods particularly crucial in MLCIL. We will further clarify these challenges in the manuscript. --- W2 & Q2: Parameter sensitivity analyses of $\gamma$ and buffer layer size. --- We include the parameter analysis as below. For $\gamma$, as it increases, the performance of L3A first improves and then declines in Table 1. A value of $\gamma$ (1000) achieves consistently good results. Table1: The ablation study on regularization term $\gamma$. \|$\gamma$\|COCO B0-C10 Avg. mAP\|COCO B0-C10 Last mAP\|COCO B40-C10 Avg. mAP\|COCO B40-C10 Last mAP\| \|-\|-\|-\|-\|-\| \|0.1\|80.41\|76.83\|79.36\|78.22\| \|1\|80.39\|76.90\|79.37\|78.27\| \|10\|80.49\|76.90\|79.38\|78.28\| \|100\|80.86\|77.09\|79.51\|78.29\| \|1000\|81.38\|77.56\|79.89\|78.75\| \|10000\|81.22\|77.61\|79.67\|78.69\| For the buffer size, in Table 2, the accuracy of L3A improves with an increase in buffer layer size, but the improvement becomes negligible once the size reaches 4096. The size of 4096 is sufficient and a larger size entails more computation on matrix inversion. Table2: The ablation study on buffer layer size. \|Buffer layer size\|COCO B0-C10 Avg. mAP\|COCO B0-C10 Last mAP\|COCO B40-C10 Avg. mAP\|COCO B40-C10 Last mAP\| \|-\|-\|-\|-\|-\| \|512\|79.33\|75.24\|77.78\|76.43\| \|1024\|80.47\|76.52\|78.89\|77.67\| \|2048\|81.08\|77.20\|79.58\|78.44\| \|4096\|81.38\|77.55\|79.91\|78.77\| \|6144\|81.43\|77.60\|79.94\|78.75\| \|8192\|81.43\|77.56\|79.96\|78.79\| \|12288\|81.40\|77.56\|79.93\|78.82\| --- W3 & Q3: PL module effectiveness analysis. --- We include the analysis as follow. "The PL module to address the label absence problem. However, notably, we found that the improvement of using PL upon WAC is less significant in our experiments, while directly using PL upon baseline introduces large improvement. The reason could be that, during the training of WAC, it retains information of previous classes via $R_t$. Then adding the PL is less effective. Nonetheless, the use of the PL module could be still beneficial when using upon both baseline and WAC." --- S1: Refine the threshold strategy and analyze limitations. 1. Threshold strategy. To refine this threshold strategy, we explore and validate a dynamic threshold approach, where the threshold is adjusted based on the number of pseudo-labels to be generated in each phase. The result of this approach is denoted as "Dynamic" and is not better than current results. It can add additional hyperparameters of target number of pseudo-labels, which may be unavailable in practice. We will further explore to improve the threshold strategy in future. Table3: Studies on $\eta$ \|$\eta$\|COCO B0-C10 Avg. mAP\|COCO B0-C10 Last mAP\|COCO B40-C10 Avg. mAP\|COCO B40-C10 Last mAP\| \|-\|-\|-\|-\|-\| \|0.55\|71.25\|67.21\|78.30\|76.12\| \|0.6\|78.63\|74.21\|79.52\|78.09\| \|0.65\|80.97\|77.08\|79.85\|78.68\| \|0.7\|81.45\|77.57\|79.91\|78.77\| \|0.75\|81.36\|77.58\|79.80\|78.62\| \|0.8\|81.34\|77.57\|79.69\|78.47\| \|Dynamic\|81.12\|76.56\|79.86\|78.45\| 2. Limitations analysis. L3A utilizes a frozen backbone and updates only the WAC. This could limit the improvement of feature extraction. We will explore to strengthen the backbone's representation to further improve L3A. [1] Dong, S., et al. Knowledge restore and transfer for multi-label classincremental learning. in ICCV, 2023. [2] K. Du, et al, "Confidence self-calibration for multi-label class-incremental learning," in ECCV 2024.	Summary: This paper addresses the challenges of multi-label class-incremental learning (MLCIL), specifically label absence, class imbalance, and privacy constraints. The proposed method, L3A, introduces two key modules: 1) Pseudo-Label (PL) Module: Generates pseudo-labels for historical classes using the previous classifier, addressing label absence, 2) Weighted Analytic Classifier (WAC): Uses a closed-form solution with sample-specific weights to balance class contributions, mitigating imbalance. L3A achieves state-of-the-art (SOTA) performance on MS-COCO and PASCAL VOC datasets, outperforming existing exemplar-free and replay-based methods. Claims And Evidence: The claims (addressing label absence and class imbalance) made in the submission are well-supported as follows, * Section 4.4 supports the label absence. * Section 4.5 supports the class imbalance. Methods And Evaluation Criteria: Yes, the manuscript employs reasonable methods and evaluation criteria, including common datasets scenarios (MS-COCO and PASCAL VOC), well-recognized metrics (Avg. mAP and Last mAP). Theoretical Claims: Yes, I have reviewed them. The manuscript includes good theoretical claims, such as the process of optimal solution in Theorem 3.1. Experimental Designs Or Analyses: Yes, I have checked them. The overall design of experiments and analysis are quite good (e.g., sec. 4.4 and 4.5) Supplementary Material: Yes, I have reviewed the supplementary material. It gives the entire proof of Theorem 3.1 Relation To Broader Scientific Literature: The submission provides a very good discussion of literature. The branches of CL are well partitioned, and can provide reasonable guidance to broader group of readers. Essential References Not Discussed: It seems the references cover all the important ones (just a feeling). Other Strengths And Weaknesses: Strengths * Exemplar-Free Privacy: L3A’s analytic updates avoid storing historical data, addressing privacy concerns. * Comprehensive Evaluation: Rigorous experiments across datasets and protocols validate L3A’s robustness. * Modular Design: The PL and WAC modules are independently justified and validated. Weaknesses * The recursive updates of the autocorrelation matrix (Equation 13) may be computationally intensive for large-scale datasets? * The PL module’s confidence threshold (η) is fixed; Other Comments Or Suggestions: * Test L3A on datasets with extreme class imbalance (e.g., long-tailed distributions) to further validate its robustness. * Clarify the buffer layer’s role in feature extraction (e.g., why random linear projections are used). Questions For Authors: * How to choose the weighting strategy? * How does the claim in Theorem 3.1 helps the multi-label incremnetal learning scenario? Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: Thanks for your review and valuable comments. Here we address your concerns individually as follows: --- W1: Recursive updates in Eq. 13 may be computationally intensive. --- The computational cost of our method primarily comes from the matrix inversion in Eq. 13 with the complexity of $\mathcal{O}(d^2N_t + N_t^2d + N_td\|C^{1:t}\|)$ where `N_t` is the number of samples at stage t and `\|C^{1:t}\|` is the total number of classes up to stage t. The complexity scales up linearly with the dataset size and L3A provides training with one-epoch closed-form solution. This makes L3A more efficient than existing iterative BP optimization. As shown below, L3A is 10x faster than KRT. Table1: Comparison of methods in terms of runtime and memory usage in COCO B40C10 benchmark. \|Method\|Time(s)\|GPU Memory(MB)\| \|-\|-\|-\| \|L3A\|1108\|5750\| \|KRT(BP-based)\|16971\|8170\| --- W2: Fixed confidence threshold in PL. --- To address this weakness, we explore and validate a dynamic threshold approach, where the threshold is adjusted based on the number of pseudo-labels to be generated in each phase. The results of this approach is denoted as "Dynamic" and is not better. It can add additional hyperparameters of target number of pseudo-labels, which may be unavailable in practice. We will further explore to address the fixed threshold in future. Table2: The threshold studies on confidence threshold ($\eta$) in COCO dataset. \|$\eta$\|B0-C10 Avg. mAP\|B0-C10 Last mAP\|B40-C10 Avg. mAP\|B40-C10 Last mAP\| \|-\|-\|-\|-\|-\| \|0.55\|71.25\|67.21\|78.30\|76.12\| \|0.6\|78.63\|74.21\|79.52\|78.09\| \|0.65\|80.97\|77.08\|79.85\|78.68\| \|0.7\|81.45\|77.57\|79.91\|78.77\| \|0.75\|81.36\|77.58\|79.80\|78.62\| \|0.8\|81.34\|77.57\|79.69\|78.47\| \|Dynamic\|81.12\|76.56\|79.86\|78.45\| --- S1: Test on long-tailed datasets. --- We follow [1] to construct a long-tailed dataset (LT-COCO) by applying a power-law decay sampling method on the COCO dataset then validate on it. Although L3A's performance slightly declined under the long-tailed distribution, it still outperformed other methods, demonstrating its robustness in multi-label continual learning scenarios. Table 3: Comparative results on the LT-COCO dataset (classes are randomly shuffled). \|Method\|LT-COCO B0-C10 Avg. mAP\|LT-COCO B0-C10 Last mAP\|LT-COCO B40-C10 Avg. mAP\|LT-COCO B40-C10 Last mAP\| \|-\|-\|-\|-\|-\| \|KRT\|74.41\|66.89\|73.77\|70.54\| \|L3A\|76.92\|72.61\|74.58\|73.40\| --- S2: Clarify the buffer layer. --- The buffer layer is used to project the model's output to a higher-dimensional space. According to Cover's theorem [2], projecting features into a higher-dimensional space via nonlinear projection functions can improve linear separability. Following ACIL [3], we use a randomly initialized linear projection in this paper and it is simple and effective. We will further clarify this in the text and explore other type of buffer in future. --- Q1: Choosing weighting strategy. --- In this paper, we use the 1/sqrt(f^(k)) to compute the weight. To validate its superiority, we compare different weighting mechanisms and weighting strategy using 1/sqrt(f^(k)) achieved the best performance. Due to smoothing effct of 1/sqrt(f^(k)), WAC can maintain a good balance against extreme class imbalances. We will include this study in the manuscript. Table4: Different weighting mechanism in WAC module. \|Weighting mechanism\|COCO B0-C10 Avg. mAP\|COCO B0-C10 Last mAP\|COCO B40-C10 Avg. mAP\|COCO B40-C10 Last mAP\| \|-\|-\|-\|-\|-\| \|1/sqrt(f^(k))\|81.45\|77.57\|79.91\|78.77\| \|1/f^(k)\|81.13\|77.30\|79.60\|78.27\| \|1/(log(f^(k))+1)\|81.36\|77.41\|79.87\|78.27\| --- Q2: How Theorem 3.1 helps MLCIL. --- Our work focuses on the MLCIL where we cannot directly apply standard ridge regression (Eq. 10) to optimize all data at once. Here, we extend standard ridge regression into the recursive analytical learning method presented in Theorem 3.1. This allows us to update the classifier through analytical solutions at each incremental learning phase, effectively addressing the MLICL problem. Also, Theorem 3.1 incorporates two key components of our approach to address issues in MLCIL: 1. PL (Eq. 3) generates pseudo-labels for past phases, solving the label absence issue. 2. WAC uses weighted iterative least squares to update classifier, addressing both class imbalance and privacy protection concerns. Theorem 3.1 provides theoretical support for L3A by proving optimal closed-form solution sample-specific weighting for MLCIL. [1] W. Tong, et al, "Distribution-Balanced Loss for Multi-Label Classification in Long-Tailed Datasets," in EECV 2020. [2] K.-A. Toh, et al, "Between classification-error approximation and weighted least-squares learning," TPAMI, 2008. [3] H. Zhuang, et al, "ACIL: Analytic class-incremental learning with absolute memorization and privacy protection," in NeurIPS 2022. --- Rebuttal Comment 1.1: Comment: Thank you for the detailed rebuttal. The authors responded to all concerns, as follows, (i) the efficiency of their work is well justified, with its closed-form solution making it significantly faster than BP-based methods. (ii) the validation on long-tailed setting shows the robustness. (iii) The buffer layer clarification strengthens its theoretical grounding. (iv) The weighting strategy is empirically validated, confirming its effectiveness. (v) Theorem 3.1 is well explained. Thus, I am inclined to accept this work and have raised my score. --- Reply to Comment 1.1.1: Comment: Thank you for taking the time to read our response and increasing your score! We are glad to hear that the response addressed your concern.	null	null	null	null	null	null
Dynamic Sparse Training of Diagonally Sparse Networks	Accept (poster)	Summary: This paper introduces DynaDiag, a structured Dynamic Sparse Training (DST) method that enforces a diagonal sparsity pattern in neural networks. The method aims to overcome the inefficiencies of unstructured sparsity, which struggles to translate into hardware acceleration. The authors propose a custom CUDA kernel to optimize computations, making DynaDiag more hardware-friendly. Claims And Evidence: The paper is generally clear, and the claims are supported by empirical evaluations on vision and language models. The reported inference acceleration (3.13×) and training speedup (1.59×) on GPUs at 90% sparsity is backed by experimental results. However, I question the necessity of LoRA-FA fine-tuning in the context of the paper's efficiency claims, as it introduces unstructured sparsity, which may counteract the structured sparsity benefits. Methods And Evaluation Criteria: The proposed methods and evaluation criteria are generally appropriate, as they include evaluations on vision and language tasks across different architectures. However, analyzing the applicability of DynaDiag to CNN-based models could strengthen its claims, as CNNs are still widely used in real-world applications. Theoretical Claims: The paper presents a relatively good theoretical foundation, particularly in its proof of transposability for diagonal sparse matrices and Top-K selection mechanism. However, the justification for diagonal sparsity is weak. While inspired by small-world networks, the paper lacks an intuitive explanation for why diagonal sparsity performs better than other structured sparsity methods (e.g., block sparsity, N:M sparsity). A comparative theoretical analysis would be beneficial. Experimental Designs Or Analyses: No standard deviation for accuracy results. At extreme sparsity levels, instead of focusing solely on high sparsity, it might be more insightful to scale up the model first and then test at high sparsities while keeping the total parameter count comparable. Supplementary Material: Yes, I reviewed the supplementary material. It primarily includes additional experimental results and implementation. Relation To Broader Scientific Literature: The paper is well-situated within the broader field of Dynamic Sparse Training (DST) and relates well to prior work. However, some claims could be further refined with more details in the suggestions section. Essential References Not Discussed: I did not find any critical missing references that significantly impact the understanding of the paper’s contributions. Other Strengths And Weaknesses: ### Strengths - This paper introduces a hardware-friendly approach that leverages the Block Compressed Sparse Row (BCSR) format to optimize GPU execution. While it successfully accelerates both inference and training, the full potential of sparsity speedup for training has yet to be fully realized. - The introduction of diagonal sparsity, inspired by small-world networks, enables the method to scale effectively for large ViT models and GPT-2, demonstrating its robustness across different architectures and modalities. ### Weaknesses - It would be useful to include a theoretical comparison explaining why the diagonal sparsity pattern works better under certain conditions. The paper lacks a clear, intuitive explanation for why it performs better than other structured sparsity patterns and why it achieves performance comparable to unstructured sparsity. - Given that CNNs are still widely used in real-world applications, discussing the potential impact of DynaDiag on CNNs would strengthen the paper. - The necessity of LoRA-FA for improving DST efficiency in this paper is unclear. Since it introduces unstructured sparsity after fine-tuning (as mentioned in Section 4.3.1, Paragraph 3), how does it affect inference speedup? - How is the BCSR transformation performed, and how time-consuming is it? The effectiveness of this operation should be further analyzed, ideally with an ablation study comparing accuracy and computation time with and without the BCSR transformation. The lack of impact analysis weakens the discussion. - The paper lacks an in-depth analysis of speedup at lower sparsity levels. In this case, what causes slower training but faster inference? - Is it valuable to explore extreme sparsity levels if it only slightly outperforms RigL? How about scaling up the model first and then exploring extreme sparsity levels? Would it be more informative to maintain the same number of parameters under 90% sparsity for the original models and test both accuracy and computation time? Other Comments Or Suggestions: ### Some sections are confusing: - In the beginning of the second paragraph, the description of randomly pruning weights is unclear and confusing. - In Section 2.2, Paragraph 3, RigL removes weights based on magnitude, while regrowth is based on gradient-this should be clarified. - In Section 2.2, Paragraph 4, Mocanu (2018) is an earlier work on DST, which should be acknowledged appropriately. - Bold text in all tables should be double-checked, as it may be misleading or confusing. Questions For Authors: This paper introduces a new structured sparsity approach that improves both accuracy and hardware speedup, paving the way for advancements in the sparse training community. Please consider the provided comments, and these questions are open for discussion. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We thank the reviewer for their comments and feedback, especially about grounding our work in theoretical foundations. We address the questions and comments below: ## LoRA-FA Finetuning We used LoRA-FA (Sec 4.3.1) primarily to interpret the performance gap between RigL and DynaDiag by introducing limited unstructured sparsity. While we acknowledge that LoRA-FA introduces additional computational overhead at inference, this was purely an exploratory experiment rather than a core component of our method. To avoid confusion, we will rename the section to “Interpreting the gap between unstructured sparsity and DynaDiag” in the final version. ## DynaDiag on CNNs We agree with the reviewer, and we are working towards extending DynaDiag for CNNs. The current implementation of DynaDiag uses one $alpha$ vector for each linear layer. This approach is not scalable to a CNN directly as there are many weight matrices (filters) for each layer, and each matrix can have diagonals in different positions, resulting in an $alpha$ vector per filter and increasing the memory overhead. ## Exploring Extreme Sparsity We agree with the reviewer that it will be beneficial to compare DynaDiag’s performance with unstructured sparsity by scaling the models up. For such a study, we ideally need models that posses more than one diagonal when sparsity reaches levels such as 99.999\%, where RigL has been shown to collapse [[1]](https://openreview.net/pdf?id=szRHR9XGrY). Our currently chosen models do not possess such properties, and hence, we welcom any suggestions from the reviewer on which models would be suitable for such a study. ## Reporting Standard Deviations We do not report std dev values at this stage as we find that our training is relatively stable for vision tasks and language tasks, which has previously been the case [[2]](https://openreview.net/pdf?id=MWZWUyfFHC). However, we plan to add more elaborate results to the final version of our manuscript. We do, however, report the p-values from our statistical significance tests for all the experiments in Table 8, Table 9, and Table 10 in Appendix A.4. ## Theoretical Explanation of DynaDiag’s Performance We submit a theoretical justification of why diagonal sparsity works better than other structured sparsity patterns. Theoretical Explanation: We request the reviewer to check out our [theoretical explanation for DynaDiag’s performance](https://figshare.com/s/06ea8e6cf2c4b86f38f0). Conclusion: Briefly, we show that diagonal sparsity offers a full input-output coverage i.e. each row and column contains at least one non-zero entry in each weight matrix, even with a single diagonal). This: 1) Preserves the rank of the matrix, maintaining the same expressivity as that of the dense matrix. 2) Ensures global input-output connectivity and coverage, avoiding dimension collapse. 3) Preserves theoretical guarantees of universal approximation capability. ## Diagonal-to-BCSR Transformation We request the reviewer to kindly check our [response to the Reviewer vAzp](https://openreview.net/forum?id=bAUVnNc0Ky&noteId=HoMgMLdsaV) under the section “BCSR Transformation and Contribution” and “Performance Impact of Diags to BCSR conversion (Q4)”, where we discuss how the conversion takes place and its impact on the performance. ## Speedup at Lower Sparsities At lower sparsity levels, we have a larger (but still less than dense) number of diagonals in all weight matrices. We see an increase in training time as compared to high sparsity due to the following overhead: Diag to BCSR conversion: We find that the time taken to convert a diagonal matrix to BCSR using our method is proportional to the number of diagonals in the matrix. For example, for a projection matrix (ViT-B/16) of size 768x768 in an attention block, the total conversion time varies as 4.35 us, 5.23 us, 7.78 us, and 10.53 us at sparsities 90%, 80%, 60%, and 50% respectively. DynaDiag can still accelerate inference at lower sparsities as the conversion of diagonal matrices to BCSR takes place offline and is done just once at the start of inference. ## Writing Edits We appreciate the reviewer’s feedback regarding clarity. We commit to improving: 1) The description of random pruning in the introduction. 2) Clarifying RigL’s growth strategy in Sec 2.2, Para 3. Proper acknowledgment of SET approach in Sec 2.2, Para 4. Verifying and updating bolded values in tables to clearly reflect best-performing methods. These edits will be included in the camera-ready version of our manuscript. We thank the reviewer again for their valuable input. --- Rebuttal Comment 1.1: Comment: I greatly appreciate that the authors have completed numerous experiments within a limited time, and most of my initial concerns have been addressed. I would raise my score to 3. Nonetheless, there remain some concerns and suggestions: 1. Regarding lower sparsity levels, the authors note that a larger (albeit still less than dense) number of diagonals in weight matrices results in only marginal speed improvements. I recommend including visualizations or other analytical approaches to clearly demonstrate how the number of diagonals correlates with speedup across varying sparsity levels. 2. Model scaling, Figure 6 indicates a substantial performance decline at extremely high sparsity levels, potentially restricting practical applicability. Therefore, I suggest exploring the scaling of models under these high sparsity conditions, as in [1], as this could reveal more compelling insights. [1] Sparse-IFT: Sparse iso-FLOP transformations for maximizing training efficiency[J]. ICML, 2024. --- Reply to Comment 1.1.1: Comment: We thank the reviewer for raising their score and address their concerns below: ## Performance at Extreme Sparsity Thank you for this insightful suggestion. As shown in Figure 6 of the paper, all methods—including unstructured approaches (Jie et al., 2024)—exhibit a noticeable performance drop at extreme sparsity levels. While DynaDiag rivals RigL at these extremes and outperforms other structured patterns, such a decline is unsurprising at 99.9% sparsity, where some layers are reduced to just three diagonals. We are actively exploring how scaling models width-wise, in line with references like Sparse-IFT (Thangarasa et al., 2023), might mitigate this effect under ultra-high sparsity. However, these new results will not be ready before the rebuttal deadline. We appreciate your feedback and look forward to incorporating these insights in future work. ## Speedup at varying sparsity level Thank you for this constructive suggestion. We already included performance measurements for DynaDiag at 60–90% sparsity in Figure 4 of our paper. To address your request for even lower sparsity insights, we performed an additional experiment on an NVIDIA A100 GPU with a 768×768 matrix-matrix multiplication (matching the size of the blocks.I.attn.proj.linear.weight layer in ViT where I is the block count) to isolate the impact of number of diagonals on potential speedup. Each configuration was run 100 times, and we averaged the total time of converting diagonals to BCSR plus the subsequent BCSR computation. Result: The [plot with speedups can be accessed here](https://figshare.com/s/7f2de1bed877c35917a5). Conclusion: As expected, below ~50% sparsity, speed gains taper off, and below ~20% sparsity, we see some slowdown—yet this remains more favorable than comparable block-sparse approaches (Takuma et al., 2021). We hope these results clarify how the number of diagonals (i.e., sparsity levels) affects speedup, and we appreciate your consideration of our updated analyses. ## References Thangarasa, Vithursan, et al. "Sparse-IFT: Sparse iso-FLOP transformations for maximizing training efficiency." arXiv preprint arXiv:2303.11525 (2023). Ji, Jie, et al. "Advancing dynamic sparse training by exploring optimization opportunities." Forty-First International Conference on Machine Learning. 2024. Yamaguchi, Takuma, and Federico Busato. "Accelerating matrix multiplication with block sparse format and nvidia tensor cores." NVIDIA Developer Technical Blog, https://developer. nvidia. com/blog/accelerating-matrixmultiplication-with-block-sparse-format-and-nvidia-tensor-cores (2021).	Summary: This paper introduces DynaDiag, a novel structured Dynamic Sparse Training (DST) method based on the composition of diagonal matrices. This parametrization is then transformed into the BCSR format to enable actual GPU acceleration. The proposed model is evaluated by training from scratch vision VIT and MLP-Mixer models, as well as the GPT-2 model, closing the gap between the unstructured and structured DST algorithms. Claims And Evidence: The claims in the paper are mostly clear, supported either by empirical analysis or previous research. I do have, however, one issue with the contributions. In particular, with the last point. The paper presents the conversion of matrices to BCSR format as a contribution, but it remains unclear how novel this conversion method is. Does it simply apply existing techniques from Section 3.3, or does it introduce new fundamental ideas? Methods And Evaluation Criteria: The paper evaluates DynaDiag primarily on ViT and MLP-Mixer architectures using vision datasets, with a single experiment on GPT-2 for text. The selected baselines include other common structured sparse-to-sparse methods and RigL as the sole representative of unstructured Dynamic Sparse Training (DST). While RigL is a strong baseline—often matching dense model performance in sparse training for vision tasks—expanding the evaluation to additional LLM architectures would strengthen the analysis. I recognize that pretraining larger LLMs may be computationally prohibitive, but exploring sparse-to-sparse finetuning (e.g., using LLaMA) could offer valuable insights. This would not only increase model diversity but also allow for comparisons with widely used pruning-based methods like Wanda and SparseGPT. Additionally, investigating the impact of dataset size could make the paper more relevant to the broader research community and enhance its impact. Theoretical Claims: The paper does not include theorems or proofs, the claims are evaluated via empirical experimentation. Experimental Designs Or Analyses: The experimental designs and analyses seem sound (Table 1, Table 2, Figure 4, Figure 1, Table 8). However, in terms of replicating the experiments, the Appendix lists the used hyperparameters in tables, but the section responsible for their summary (A.2.2) lacks reference to those tables. Furthermore, it would be beneficial to explain why such configurations were used (are they an effect of grid search, or maybe they were adapted from literature etc.) Supplementary Material: I did review the appendix, I did not review the supplementary materials (i.e. code). Relation To Broader Scientific Literature: Dynamic Sparse Training (DST) is a well-established field focused on developing algorithms for training models that are sparse from initialization. The term “dynamic” refers to methods that adaptively modify the connectivity or sparse structure throughout training. The core contribution of this paper is the introduction of a new structured DST algorithm. While prior structured DST approaches, such as SparseRigL, have been proposed and are discussed by the authors, I am not aware of any previous attempts that leverage the composition of diagonal matrices as presented here. More broadly, in the context of sparsity in transformer-based models, this work is also relevant to pruning-at-initialization methods. Consequently, I believe the paper would benefit from a comparison with pruning approaches such as Wanda or SparseGPT to provide additional context and insights. Essential References Not Discussed: I do not indicate any missing essential references at this point Other Strengths And Weaknesses: Strengths: - The proposed method is built on an elegant idea of parametrizing linear projection matrices as a composition of diagonal matrices. - It helps bridge the gap between unstructured Dynamic Sparse Training (e.g., RigL) and structured approaches while also reducing computational time, as measured in terms of wall-clock time. - The paper is well-structured and easy to follow. The core idea is simple yet elegant and shows great promise both in empirical evaluations and in its potential for real-world speedups. Weaknesses: - I have discussed the weaknesses in the corresponding paragraphs above. Other Comments Or Suggestions: - Questions For Authors: 1. What is the precise contribution regarding the transformation to the BCSR format? The authors present this as a key contribution, but Section 3.3 leaves some ambiguity. Are they merely applying existing methods, or does their approach introduce novel aspects? Clarifying this is essential for assessing whether the paper fully delivers on its claims. 2. Could the evaluation be extended to sparse-to-sparse finetuning? (See Methods and Evaluation Criteria.) Including this aspect could enhance my assessment of the experimental results. Clarification Questions (to ensure a proper understanding of the paper): 3. The paper states, "We derive the per-layer sparsity budget from the global sparsity budget." How exactly is per-layer sparsity distributed, and how do different distribution strategies impact DynaDiag’s performance? 4. Additionally, could the BCSR conversion influence overall performance? How would DynaDiag perform if implemented naïvely using simple masking instead? Minor (curiosity-driven) Questions (unlikely to impact my overall score but still of interest): 5. What effect do temperature and alpha initialization have on DynaDiag’s final results? Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: We thank the reviewer for their feedback and positive comments. We are glad to hear that the reviewer appreciates the novelty of our work. We address the questions and comments below: ## BCSR Transformation and Contribution (Q1) For acceleration on GPUs, a diagonal matrix is converted to blocks (represented in BCSR) by calculating a row transformation $P$. Contribution: We propose a heuristic-based method to convert diagonal matrices to block matrices which is built on top of SMAT[[1]](https://arxiv.org/pdf/2408.11551), which proposes a method to calculate $P$ for the general case of unstructured matrices. Where SMAT uses Jaccard similarity between the rows to block them efficiently (see Section IV C of SMAT), we modify Jaccard’s similarity (as mentioned in detail in Appendix A.3) with a diagonal proximity term to prioritize diagonals close to the main diagonals, which maximizes the total number of dense blocks. Our heuristics take advantage of the fact that each row in the matrix has the same number of nonzeros which help with load balancing when running on the GPU. ## Performance Impact of Diags to BCSR conversion (Q4) Converting a diagonal matrix $W_{diag}$ to a blocked matrix (in BCSR) $W_{BCSR}$ is done by applying row permutation to $W_{diag}$ given as: $W_{BCSR} = P_{perm}W_{diag}$ Matrix-Vector equivalence in diag and BCSR Format: To ensure that matrix-vector multiplication remains equivalent between the two formats, an inverse of $P_{perm}$ (which is its transpose) is applied to the incoming input $x$. We show the equivalence below: We can write: $Output_{diag} = W_{diag}X$ $Output_{diag} = W_{BCSR}P_{perm}^{-1}X$ $Output_{diag} = W_{BCSR}(P_{perm}^{-1}X)$ Therefore, the two methods result in the same output. Experiment: With empirical experiments on ViT-B/16 at 90% sparsity with ImageNet-1K, we verify that there is no significant accuracy difference between direct diagonal computation and the BCSR-based approach. Results: Please refer to [Table 16 here](https://figshare.com/s/b6386a7f35eca3ebcfeb). Conclusion: We see no significant difference in the accuracies of the two methods, proving their equivalence. However, the training time is significantly improved using our custom BCSR kernel. ## Comparison with Sparse-to-Sparse finetuning methods (Q2) We agree with the reviewers' suggestion to apply our training method to LLaMA models for comparison with SOTA pruning methods such as Wanda and SparseGPT. Doing so will require us to train a LLaMA model from scratch, and hence, we propose to share those results in our final manuscript. However, we ran Wanda (SparseGPT did not work out of the box with GPT-2) with the GPT-2 model and reported the results. Results: Please refer to [Table 15 here](https://figshare.com/s/b6386a7f35eca3ebcfeb). Conclusion: As expected, Wanda, a pruning method, produces models with better perplexity than DST-based methods. However, the performance difference is not significant compared to DST methods (as evident from McNemar’s test results). However, Wanda's results are produced at a significantly higher computational cost (dense training + fine-tuning), whereas our method remains computationally efficient. ## Per Layer Sparsity (Q3) Please refer to our [response to Reviewer XE14](https://openreview.net/forum?id=bAUVnNc0Ky&noteId=K2Jst84n3i), under the section titled: “Per Layer Sparsity”. ## Justification For The Choice Of Training Configurations We thank the reviewer for pointing out the missing justification for the choice of training configurations in Tables 3, 4, 5, 6, and 7. All the configurations are obtained from the literature, and here are the references: 1) Tbl 3 [[2]](https://shorturl.at/QFzJw) 2) Tbl 4 [[3]](https://shorturl.at/bc3hz) 3) Tbl 5 and Tbl 7 [[4]](https://shorturl.at/4Hzxp) 4) Tbl 6 [[5]](https://shorturl.at/4qmmR) ## Temperature and Alpha Initialization (Q5) ### Temperature: We employ a temperature-based softmax for differentiable TopK approximation. Initially set high (T=1.0), the temperature gradually anneals to T=0.01, focusing the search from broad exploration to a sharp selection of diagonals. This approach balances exploration and computational overhead effectively, guided by prior methods such as Sander et al [[6]](https://dl.acm.org/doi/10.5555/3618408.3619649). ### Alpha Initialization: Currently, all $\alpha$s are initialized equally, assuming initial equal importance across diagonals. For future exploration, we are working with two alternative initialization methods: Distance-Based Initialization: Higher initial values for diagonals near the main diagonal. Data-Driven Initialization: Input data-driven initial importance reflecting intrinsic data structure or correlations. These strategies may enhance convergence speed and overall performance. We appreciate the reviewer’s valuable suggestions, which can considerably improve the clarity and strength of our paper. --- Rebuttal Comment 1.1: Comment: Thank you for the clarifications. I appreciate both the quality and the number of additional comparison experiments conducted for the rebuttal. One observation I have, however, is that the performance of DynaDiag appears to degrade more significantly with increasing sparsity compared to DST or Wanda methods (as seen in Tables 11 and 15). Do the authors attribute this to the structured vs unstructured sparsity setups? Overall, assuming the additional results on DST and Wanda are incorporated into the main text, I am willing to raise my score. --- Reply to Comment 1.1.1: Comment: We thank the reviewer for their support of our work. We address their query below. ## DynaDiag at Higher Sparsity DynaDiag consistently outperforms other structured sparsity methods, reflecting both the expressiveness of its pattern and the strength of our training strategy. However, at extreme sparsities (>95%), it does experience a slightly higher degradation (e.g., ~2.14% at 95% sparsity vs. CHT in Table 11) compared to unstructured methods. We do attribute this to the inherently higher flexibility of unstructured sparsity. Nonetheless, we believe insights from scaling sparse networks (as mentioned by the reviewer NGkq) akin to Sparse-IFT (Thangarasa et al., 2023) could help close the gap between DynaDiag and unstructured approaches such as DST and Wanda at these extreme sparsity levels. ## Reference Thangarasa, Vithursan, et al. "Sparse-IFT: Sparse iso-FLOP transformations for maximizing training efficiency." arXiv preprint arXiv:2303.11525 (2023).	Summary: The paper introduces DynaDiag, a novel structured Dynamic Sparse Training (DST) method that enforces diagonal sparsity to improve both computational efficiency and model accuracy. Unlike unstructured DST methods, which often fail to achieve hardware acceleration despite high sparsity ratios, DynaDiag maintains structured sparsity throughout training, enabling significant speedup in both training and inference. The key idea is to enforce a diagonal sparsity pattern that remains structured under transposition, making it well-suited for efficient GPU execution. To optimize learning, DynaDiag employs a dynamic TopK-based selection mechanism to adaptively update the most critical diagonals, allowing the model to learn the optimal sparse connectivity during training. Additionally, the authors introduce a custom CUDA kernel that utilizes Block Compressed Sparse Row (BCSR) format, ensuring fast execution for both forward and backward passes. Empirically, DynaDiag achieves a 3.13× inference speedup and a 1.59× training speedup compared to dense models, while matching or outperforming existing structured sparse training methods. The method is evaluated on Vision Transformers (ViTs), CNNs, and GPT-2 models across ImageNet, CIFAR-10, CIFAR-100, and WikiText-103, demonstrating strong generalization even at extreme sparsities (up to 99.99%). The results indicate that DynaDiag is a viable alternative to unstructured DST, offering comparable accuracy while significantly improving computational efficiency. The study highlights the limitations of existing sparse training approaches and presents DynaDiag as an effective way to achieve both hardware acceleration and model performance, making it highly promising for scaling sparse deep learning models in practical applications. By bridging the gap between sparse training and hardware efficiency, DynaDiag paves the way for more efficient deep learning architectures, especially in resource-constrained environments. Claims And Evidence: About the claim that “Empirical evaluations on diverse neural architectures demonstrate that our method maintains accuracy on par with unstructured counterparts while benefiting from tangible computational gains.” I think it should be adjusted and reduced because there are many new evidences in literature in which unstructured methods such as CHT, CHTs and CHTss can perform better than RigL, GMP and even better than fully connected architectures (see the section below on essential references not discussed). I agree of course about these second part of the claim “while benefiting from tangible computational gains.” In my opinion the current version of the paper do not report solid evidence that supports the claim because it neglects to compare with the most recent methods in unstructured and structured dynamic sparse training (see the section below on essential references not discussed). In addition, also the related work and the Figure 1 and 2 and the other section of the article should be adjusted reporting appropriate claims on the most recent methods in the literature. Methods And Evaluation Criteria: Yes, they make sense but the number of tested methods are few. I recommend discussing and add SET, MEST, CHTs, CHTss (see the section below on essential references not discussed). Theoretical Claims: I have checked the proof of this article and it is correct Experimental Designs Or Analyses: Yes, I checked, and I believe the manuscript should be improved. I recommend to test and discuss result including MEST, CHTs, CHTss (see the section below on essential references not discussed). Supplementary Material: Yes I have checked all the supplementary material Relation To Broader Scientific Literature: The idea and method of this article is nice and solid, and I believe that if the authors address my concerns this article would be interesting for all the community. However, considering the current version of the paper, I think that the relation to Broader scientific literature should be significantly improved. The authors are not aware of relevant new finding in unstructured/structured dynamic sparse training and that there are today also methods such as CHT, CHTs and CHTss that can perform better than fully connected networks. In addition, the authors do not discuss that the network topology initialization with network science modelling such as bipartite small-world and bipartite scale-free modelling or with method such as CSTI that are input data based in Figure. 2. The study overclaims the relevance of their results with respect unstructured methods not comparing with current SOTA. I invite the authors to largely revise the study to put in the appropriate and balanced context, because I believe this study can be of value for the community. Essential References Not Discussed: Mocanu, D. C.,et al. Scalable training of artificial neural networks with adaptive sparse connectivity inspired by network science. Nature Communications (2018), 9, Article number: 2383. Yuan, G., et al. "MEST: Accurate and fast memory-economic sparse training framework on the edge." Advances in Neural Information Processing Systems 34 (2021): 14476-14489. Zhang, Y. et al. Epitopological learning and Cannistraci-Hebb network shape intelligence brain-inspired theory for ultra-sparse advantage in deep learning. Proceedings of the Twelfth International Conference on Learning Representations (ICLR) 2024. Wu, B., et al. Dynamic Sparse Training versus Dense Training: The Unexpected Winner in Image Corruption Robustness. Proceedings of the Twelfth International Conference on Learning Representations (ICLR) 2025. Zhang, Y., et al. "Brain-inspired sparse training enables Transformers and LLMs to perform as fully connected." arXiv preprint arXiv:2501.19107 (2025) Other Strengths And Weaknesses: Strengths This article introduces the diagonal sparse training which is novel in this field. Very nice idea. The proposed methods outperform the other structured sparsity sparse training methods in Comprehensive Benchmarking on Vision and Language Tasks Weakness: The study section on related work is incomplete and far from reporting the most recent advancements in the field. The study needs to compare with SOTA unstructured methods to support their claims and offers an updated comparison of their method. A lot of the training details of this article are unclear and the work necessity a robust revision to match the standard of reproducibility Other Comments Or Suggestions: Please see the question section Questions For Authors: I kindly ask to the authors whether they can revise the study: 1. balancing their claims under the light of my comments above and the new literature I provided. 2. rewrite all the articles sections, and in particular the related work section, taking in consideration my comments and the new literature I provided. In particular: Fig1 should modified including if possible other methods such as SET, MEST, CHTs, CHTss. Fig. 2 should be modified including other sparsity patterns such as bipartite small-world (BSW, which for beta=1 includes the random pattern) and bipartite scale-free (BSF) modelling or with methods such as CSTI which create a regular diagonal pattern that is input data based. 3. The authors should offer a quantitative proof that their topologies are really small-world using the small word measures. The claim is not really theoretically well posed from the network science standpoint, it necessity evidences by small-worldness measures to offer evidence that their sparsity patter is characterized by the small-world phenomenon. To me it seems that their sparsity pattern is more inspired by a regular highly clustered pattern which is indeed very similar to CSTI (see Zhang et al ICLR2014 in the section Essential References Not Discussed) or BSW with beta=0 (which in reality is not small-world because the Watts-Strogatz small-world model for beta=0 is a regular clustered structure for which the small-world effect vanishes). But I might be wrong and for this I kindly ask a quantification of small-worldness. 4. insert in the computational experiments, when it is possible , the comparison with new methods such as SET, MEST, CHTs, CHTss. 5. How the alpha initialized? If alpha is initialized equally, then it will start from a fully connected network. Then how is the learned density decay curve? 6. I'm not sure how the unstructured sparse training method RigL is tested. As the article said, "We use CUSPARSE, as RigL lacks exploitable structure." Which kind of sparse format is the author using? Can you provide the single module running time of the proposed diagonal sparse training/inference and the other structures? As the density changes, the running time of RigL doesn't change. However, as my experience, if using the torch.sparse module, the running time will change significantly based on sparsity. However as shown in the article, the running time doesn't change from 60-90% sparsity. 7. Could the authors compare their method with CHTs [1], which has been shown to outperform RigL in most cases, as a baseline for unstructured sparse training? 8. In Figure 3a, what are the arguments of TopK(α, t, s)? Specifically, what do t and s represent? 9. The per-layer sparsity budget ρj is derived from the global sparsity budget ρglobal, and the number of diagonals Kj for each layer is determined based on ρj. Does the paper adopt a non-uniform sparsity distribution across layers? And what does the final sparsity distribution look like. 10. In Formula (5), the authors use min(max(oi, 0), 1). However, shouldn't oi always be ≥ 0? Also, what does k represent in the formula, and how is it tuned? 11. The authors mention that to encourage sparsity in α, they employ an ℓ1 regularization term. Could they elaborate on how this is implemented and its impact on training? 12. The authors apply a cosine-annealing schedule to adjust T during training, starting from a high value for a smoother TopK selection. Have they tested alternative scheduling methods? 13. Many training details is missing which makes the article hard to reproduce. If the article is accepted, do the authors plan to release the code? Code Of Conduct: Affirmed. Overall Recommendation: 5	Rebuttal 1: Rebuttal: We thank the reviewer for their insightful and constructive feedback, which has significantly helped enhance our work. Below, we concisely address each comment: ## Comparison with SET, MEST, CHT, CHTs Methods (Response to Q1, Q4, Q7) Due to time constraints, we chose the above four of the five methods suggested by the reviewer and carried out experiments on ViT-B/16 with ImageNet-1K. Results: Please refer to [Table 11 here](https://figshare.com/s/b6386a7f35eca3ebcfeb) for performance numbers. We also [updated Figure 1](https://figshare.com/s/3c8b904acdce99263d30) to incorporate the methods suggested by the reviewer. Conclusion: CHT and CHTs outperform RigL at most sparsities. We calculate the statistical significance (using McNemar’s test) of the performance at various sparsities, and find that all the models in bold can be considered equivalent for that sparsity level. DynaDiag’s performance is also equivalent to that of the best model at that sparsit.; Thus, our structured sparsity performs comparable to current SOTA unstructured methods. ## Small-Worldness (Response to Q3) We agree with the reviewer, and we take a ViT-B/16 trained with DynaDiag and calculate the small-world factor, $\sigma$ using NetworkX[[1]](https://shorturl.at/7qS5A) library in Python. Results: Please refer to the results for various layers in [Table 12 here](https://figshare.com/s/b6386a7f35eca3ebcfeb) Conclusion: All tested layers exhibit $\sigma \geq 1$, confirming that DynaDiag's structured sparsity indeed reflects small-world characteristics. ## Alpha Initialization and Other Scheduling Strategies (Response to Q5 & Q12) All $\alpha$s are initialized equally to start with, which are then passed as input to our $TopK$ function. The output of the TopK function is a sparse vector $\tilde{\alpha_i}$, which is used to obtain a diagonally sparse weight matrix for a layer, given as: $W_{K} = \sum_{j=1}^K \tilde{\alpha}_j \,P_j \,\mathrm{diag}(V_j)$ Results: We obtain a [density decay curve ](https://figshare.com/s/2b5d7955c1c92fb72c42). We also show how different scheduling methods affect the performance of ViT-B/16 [Table 14](https://figshare.com/s/b6386a7f35eca3ebcfeb). The duration of the exploration phase is a hyper-parameter, and we choose its value as $\frac{1}{3}\times epochs$. The initial and final temperature value is set as described by Sander et al [[2]](https://shorturl.at/eOKWy). ## Training Time of RigL (Response to Q6) For training unstructured sparse networks, we use torch.sparse for doing sparse matrix-matrix operations. We report the wall clock time for both training and inference. For Fig 1 and Fig 4a, we use the inference time with a batch size of 1 to obtain per sample inference time.Although no substantial speedup was observed from 60% to 90% sparsity, consistent with SRigL[[3]](https://shorturl.at/HX30S) and SparseRT[[4]](https://shorturl.at/baywp), noticeable improvements appear at 95% sparsity. Results: We report the inference and training time in [Tables 17 and 18 here](https://figshare.com/s/b6386a7f35eca3ebcfeb), respectively. We welcome reviewer suggestions for enhancing our unstructured timing baseline. ## Per Layer Sparsity (Response to Q9) We allocate the sparsity budget, based on a layers compute fraction (proportional to layer size) as proposed in PixelatedBFly[[1]](https://shorturl.at/Gblym) (Sec 3.3 and Appendix I.1). Experiment: We also experiment with two other distributions: Uniform and ERK. Results: We tabulate the results in [Table 13 here](https://figshare.com/s/b6386a7f35eca3ebcfeb). Conclusion: Computational fraction-based allocation yields better results, consistent with findings from PixelatedBFly. ## Arguments of $TopK(\alpha, s, t)$ (Response to Q8) The TopK function arguments are the importance vector ($\alpha$), layer sparsity ($s$), and temperature ($t$), controlling the softness/hardness of the selection. ## Clarification on Equation (5) and L1 regularization of $\alpha$ (Response to Q10 & Q11) We updated the equation considering the reviewer’s comments: $\tilde{\alpha_i} = \min \Bigl(k \cdot \frac{\exp\bigl(\tfrac{\alpha_i}{T}\bigr)}{\sum_{j=1}^n \exp\bigl(\tfrac{\alpha_i}{T}\bigr)} , 1\Bigr)$ K is the total number of diagonals per layer, determined from per-layer sparsity (footnote 1 on page 3). We apply L1 regularization on alphas to encourage sparsity and we add the L1 loss to the overall loss function as: $\text{Loss} = \text{crossEntropyLoss} + \lambda \sum_{l=1}^{L} \\|\alpha^{(l)}\\|_1$ The regularization coefficient $\lambda$ is set at 0.2 following a hyperparameter search, and we observe no noticeable impact on training speed. ## Do we plan to release the code? (Response to Q13) Yes. We also plan to provide a step-by-step guideguide for reproducibility. We sincerely hope these adjustments fully address the reviewer’s feedback and request reconsideration of our work based on these substantial enhancements. --- Rebuttal Comment 1.1: Comment: 1. The Authors made a great effort to address my questions, for this reason I increase my score to from 2 to 3. 2. The Authors forgot to address my Q2: << rewrite all the articles sections, and in particular the related work section, taking in consideration my comments and the new literature I provided. In particular: Fig1 should modified including if possible other methods such as SET, MEST, CHTs, CHTss. Fig. 2 should be modified including other sparsity patterns such as bipartite small-world (BSW, which for beta=1 includes the random pattern) and bipartite scale-free (BSF) modelling or with methods such as CSTI which create a regular diagonal pattern that is input data based.>> If the Authors address also this last question, I will increase my score to 4 or above. thanks for this excellent job. Reply to Authors rebuttal comment of 04 Apr 2025, 06:32 (modified: 05 Apr 2025, 04:15) Respected Authors your Fig. 1 legend reports: “Figure 1: Comparing the inference (left) and training speedups (right) (calculated using wall-clock time) of sparse training methods and the Top-1 classification accuracy (x-axis) for a ViT-Base model at 90% sparsity running ImageNet-1K.” To this regard I have 4 concerns: The Results reported in Table 11 at 90% sparsity are: dense accuracy = 78.5 > CHT = 77.66 > CHTs = 77.54 > RigL = 77.24, however your Fig. 1 reports: dense accuracy > RigL > CHT > CHTs. Please can you address this concern? Unfortunately at the moment the symbols indicating different methods are overlapping, generating difficulty of interpretation of the results. I would recommend reducing the size of the symbols in the revised Fig. 1 and adjusting to ensure the figure is both visually appealing and effectively communicates the intended information. Can you provide what setting did you use for the initializing the topology and the weight of CHT and CHTs? Did you consider hyper-parameter search of the initialization parameters and if yes what values did you use? As a matter of fact the goal of dynamic sparse training is to perform close or even better than dense training with a reduced number of parameters. To this regard Figure 1 reports the results at 90% sparsity which is an arbitrary value. Revising Figure 1 reporting the results at each level of sparsity mirroring the results in Table 1 would be very useful and informative. This could be achieved adding 3 small panels, reporting on the x-axis the levels of sparsity from 60% to 95% and on the y-axis in each panel a different measure such as: accuracy, inference speedup and training speedup. This could highlight already in Figure 1 that at 60% and 70% Dynamic sparse training accuracy performance is better than dense training and that DynaDiag is the only structured method to keep high its performance close to the unstructured ones that performs better than dense. I imagine DynaDiag would produce a quite stable accuracy curve that remains high in comparison to the other structured methods. It is the only structured method to present a performance stability similar to unstructured methods across different levels of sparsity. This is an impressive result that the Authors at the moment are not highlighting enough in their main article. Reply to Authors rebuttal comment of 08 Apr 2025, 07:31 Congratulations for the job done I am raising your score to 4. 1. I checked the three-panel figure and it is quite evident the great performance of DynaDiag. I am happy this figure enhance the presentations of the results regarding your algorithm, I propose to improve the figure by reporting two insets that zoon-in the results of the accuracy curves around 0.60 sparsity and around 0.95 sparsity. The same should be done for speed-up plots. 2. Why the input embedding layer of CHTs is not initialized using CSTI? This should increase performance of CHTs further. 3. In your revised text you report that: "... propose CHT and CHTs (Zhang et al., 2024b) methods where a gradient-free (and based on the network topology) approach is used during the regrow phase, which makes their method scalable and achieves state of the art performance at high sparsity." In reality looking at the results in Table 11 and in your plots the state of the art performance is obtained not only at high sparsity levels, but for each sparsity with performance at sparsity 0,6 being even larger than dense networks. Can you please address this concern adjusting your sentence accordingly? Reply to Authors rebuttal comment of 09 Apr 2025, 03:06 1. Looking at the plots of Fig.1 that you provide, I would say that the appropriate sentence is: " ... (even outperforming the dense baseline from 60% to 80% sparsity).” 2. In the insets: you could add the names of the methods close to the symbols, to facilitate interpretation. 3. My gratitude for advancing significantly the knowledge in sparse training. The score is now 5. I believe this study is exceptional and I wish you oral presentation. --- Reply to Comment 1.1.1: Comment: # Reply to reviewer’s suggestions on 08 Apr We thank the reviewer for increasing their score. We address the three queries below: 1) We have [updated the Figure 1](https://figshare.com/s/95bec1ce2911a2cc1276) with insets. 2) Our choice of using BSW initialization for CHTs is based on the text in Section 4.3 of CHTs (Zhang et al., 2024b), and from the text, we understood that CHTs can perform at par and sometimes surpass methods like CHT, which uses computationally complex methods of link prediction. 3) Thank you for pointing this out. We propose to modify the text as follows (shortened due to space limitation): “propose.... delivers state-of-the-art performance across all tested sparsities (even outperforming the dense baseline at 60% sparsity).” # Reply to the reviewer's suggestions on 04 Apr We thank the reviewer for their patience and answer their concerns below: ## Current Fig 1 Results and Three Panel Fig 1 Table 11 shows the correct set of results and we have fixed Figure 1 to reflect the same. Hence, the correct order of unstructured accuracy at 90% sparsity is: dense accuracy> CHT > CHTs > RigL> SET> MEST. We have also [updated current Figure 1](https://tinyurl.com/4h389z9b). ## Three panel fig1 We appreciate reviewers' comments. The [new figure 1 can be accessed here](https://shorturl.at/8tQ7X). We believe that the new figure clearly shows the advantages of DynaDiag for inference and training speedup and also the superior accuracy amongst other structured DST methods. ## Init Settings and Hyperparams Based on our hyperparameter search, we use the following values: ### Topology and Weight Initialization Topology: For CHT, we use CSTI for the input embedding layer and ER for the intermediate layers (MHA) in ViT. For CHTs, we use a BSW ($\beta = 0.3$, obtained after a search from 0.2 to 1) based topology for all the layers. Weight: For both CHT and CHTs, for each sparsity level, we use the SWI method mentioned in Appendix E of CHT (Zhang et al., 2024a). ### Hyperparams Parameters for training ViTs are taken from [timm models training recipe](https://shorturl.at/hrd8t). But parameters specific to CHT and CHTs are as follows (from hyperparameter search): #### CHT $zeta = 0.3$ (Fraction removed links) $StartLR = 0.01$ $EndLR = 0.0001$ $UpdateInterval = 30$ #### CHTs $zeta = 0.3$ (Fraction removed links) $startDelta = 0.5$ $endDelta = 0.8$ $K = 6$ $\alpha = 1$ $decayMethod = inoam$ $updateInterval = 40$ ########### We thank the reviewer for their support. We address the three parts of their comment below: ## Updated Figure 1 We update Figure 1 with the new results, which can be [accessed here](https://figshare.com/s/3c8b904acdce99263d30). ## Updated Figure 2 We update Figure 2 with the additional sparsity patterns (BSF with $\gamma$ = 2.76, BSW with $\beta$ = 0.5, $\beta$ = 1) highlighted by the reviewer. The revised figure can be [accessed here](https://figshare.com/s/9c2ecaebd44636cb3884). We will explain BSF and BSW networks in the appendix. ## Writing Edits ### Edit 1 We will edit the Related Work section as follows (starting from para 4 Section 2.2. Para 1, 2 & 3 remain the same): SET (Mocanu et al., 2018) is one of the earliest DST works that introduced a prune-and-regrow strategy for DST, where during the prune phase, weights are pruned based on their magnitude and are regrown randomly. MEST (Yuan et al., 2021) regrows weights randomly and uses a combination of weight magnitude and gradient magnitude of the existing weights to prune them. RigL (Evci et al., 2020), on the other hand, prunes weights based on their magnitudes and are regrown based on the gradients of missing links (zero weights), which makes the backward pass dense and unable to take advantage of the sparsity in the network. Addressing this limitation of RigL, Zhang et al. (Zhang et al., 2024a) propose CHT and CHTs (Zhang et al., 2024b) methods where a gradient-free (and based on the network topology) approach is used during the regrow phase, which makes their method scalable and achieves state of the art performance at high sparsities. ### Edit 2 We will also edit our baselines in Section 4.1 as: RigL (Evci et al., 2020), MEST (Yuan et al., 2021), SET (Mocanu et al., 2018), CHT (Zhang et al., 2024a), and CHTs (Zhang et al., 2024b) uses DST to produce unstructured sparsity, which does not yield significant speedups in training or inference. ## References [Mocanu, D. C.,et al.](https://shorturl.at/KT4G1) [Yuan, G., et al.](https://shorturl.at/wmcTB) [Evci, Utku, et al.](https://shorturl.at/O3m7g) [Zhang, Y. et al. ](https://tinyurl.com/6yswk2ru) [Zhang, Y., et al.](https://tinyurl.com/5y9mk4hp)	null	null	null	null	null	null	null	null
AssistanceZero: Scalably Solving Assistance Games	Accept (poster)	Summary: The paper proposes AssistantZero, a method to learn cooperative assistants where the reward function of the human player is unknown. The paper presents a new environment, MBAG-- a 3D grid with many possible reward functions and a variety of ways to help the human in the loop. In contrast to using a PPO, AssistantZero is similar to AlphaZero and uses MCTS equipped with a reward model and network that predicts human actions. Experiments on MBAG show that AssistantZero outperforms PPO. Claims And Evidence: - The introduction mentions that existing methods for assistance methods do not scale well and are used in toy settings. However, this paper presents results on a 3D grid world. - It is hard to articulate the second challenge around lines 104 that human model is needed to predict human's response and is a challenges for methods using assistance games. The paper presents a result with a trained human model and it is not clear how to get around this? Methods And Evaluation Criteria: This paper proposes a new environment MBAG to test if the assistant agent can help the human model to solve the task efficiently. For toy setting, the environment is fine. However, there are no environments to test if the method can scale. Theoretical Claims: There are no theoretical claims in the paper. Experimental Designs Or Analyses: The details of the baselines are not clear, see Q4 for more details. Supplementary Material: NA Relation To Broader Scientific Literature: This paper presents a method to learn assistant agents that can aid humans in solving tasks more efficiently. The proposed method uses a MCTS for planning at inference. Learning a best-response assistant player makes sense, but the paper does not discuss the setting where the human player (ideally learned with a no-regret strategy) does not have access to the reward function and is learning the task with the assistant. Essential References Not Discussed: NA Other Strengths And Weaknesses: ## Strengths - The idea of learning cooperative agents where the reward function is not known to the assistant is interesting and challenging. - The proposed method AssistantZero shows promising results and leads to lower overall steps needed to solve tasks in environment. ## Weaknesses - The introduction mentions that existing methods for assistance methods do not scale well. However, this paper presents results on a 3D grid world. - The method relies on predicting the parameters of the reward model which might not scale to larger models. - Some details are hard to follow. For example, the details of PPO training and why does the assistant need a non-Markovian policy for environments like MBAG. Other Comments Or Suggestions: NA Questions For Authors: 1. For the reward function, AssistantZero predicts the parameters of the network. How will this scale when the reward function is complex or to a setting like RLHF where the reward model is built on top of an LLM? 2. Although the paper is trying to solve assistant games, the policy of human is kept constant which is often not true in many scenarios where both human and assistant are trying to recover the reward and goal in the environment. How will this method scale to such scenarios? 3. How would exploration methods help in setting where the reward function is sparse? 4. What was the loss function used to train the PPO baseline and how does it differ with Eq 1? 5. How expensive is MCTS compared to PPO at test-time in terms of computational requirements? Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We thank the reviewer for their thorough review and helpful feedback. Below are responses to individual points and questions: * Complexity of environment: While the reviewer refers to MBAG as a toy setting, we argue it is substantially more complex than prior environments in assistance games, which used 5x5 or 9x10 grid worlds with less than a dozen possible goals like collecting lemons or gemstones [1, 2]. MBAG instead involves building houses in Minecraft, a more realistic task with over $10^{400}$ possible goals. That PPO struggles even with reward engineering and auxiliary losses underscores the environment's difficulty. Overcooked [3] and Hanabi [4], despite being simpler than MBAG, have enabled significant research on collaborative AI—further suggesting MBAG is a meaningful benchmark. * “It is hard to articulate the second challenge around lines 104 that human model is needed...” This is a challenge articulated in past work, e.g., Fisac et al. [5] write that “more realistic human models [are] therefore crucial in using the CIRL formulation to solve real-world value-alignment problems” (CIRL = assistance games). While past papers have used human models based on RL or planning [1, 2], we are the first to leverage an imitation learning-based human model for assistance games. We will update the introduction to clarify this. * “AssistantZero predicts the parameters of the [reward] network. How will this scale?” The reward function $R(s\_t, a\_t^\\textbf{H}, a\_t^\\textbf{R}; \\theta)$ is parameterized by $\\theta$, but is not generally a neural network. The parameters $\\theta$ can be any information that encodes the task/goal/preferences of the human. In our case, $\\theta$ consists of the goal structure, i.e., the configuration of blocks that the human is attempting to assemble. In the case of an LLM assistant for coding, $\\theta$ might consist of a set of test cases that the human would like to satisfy by implementing some function. We will modify Section 2 to make this more clear. * "Some details are hard to follow. For example, the details of PPO training…” We used the standard PPO loss, which consists of the clipped surrogate objective, the value function loss, and the entropy bonus. We also experimented with modifications to try to boost PPO's performance, as described in Section 4.1 and Appendix D.2. Equation (1), the AssistanceZero loss function, has the policy loss, value loss, reward loss, previous reward KL loss, and the human action prediction loss. Only the value loss is identical between PPO and AssistanceZero. We did try adding the goal prediction loss to PPO but found it did not improve performance (see Appendix D.2). * “Why does the assistant need a non-Markovian policy?” Past work on assistance games [6] has shown that finding a best response to a fixed human policy is equivalent to solving a single-agent POMDP. Solving a POMDP requires a non-Markovian policy and thus we use a recurrent policy for the assistant. * “The policy of human is kept constant which is often not true...” We agree that this is not a completely realistic assumption. If the human is also learning about their own reward/goal, then their behavior may be non-Markovian; this setting of “partially observable assistance games” is studied in a recent paper [7]. Humans could also adapt to a particular assistant policy, making their policy non-constant. However, we find that our assistant still works well with real humans, indicating that our assumption of a fixed human policy is reasonable in practice. * “How would exploration methods help in setting where the reward function is sparse?” MCTS already inherently provides exploration as part of AssistanceZero. Future work could investigate reward shaping, pretraining, and intrinsic motivation to further improve performance in sparse-reward settings. * “How expensive is MCTS compared to PPO at test-time?” We use 20 simulations of MCTS at test time, requiring 20 forward passes. Despite this, it runs in real time on a 1080 Ti GPU. Notably, AssistanceZero without test-time MCTS matches performance, using the same compute as PPO: Assistant\|Forward passes per action\|Overall goal %\|Human actions\|Assistant goal % -\|-\|-\|-\|- PPO w/o LSTM + rew. engineering and aux. loss\|1\|74.1 ± 0.9 \|191 ± 3\|7.2 ± 1.0 AssistanceZero w/ test-time MCTS\|20\|79.8 ± 0.9\|158 ± 3\|27.0 ± 1.5 AssistanceZero w/out test-time MCTS\|1\|80.2 ± 0.9\|158 ± 3\|27.3 ± 1.3 [1] Woodward et al. Learning to Interactively Learn and Assist. [2] Zhi-Xuan et al. Pragmatic Instruction Following and Goal Assistance. [3] Carroll et al. On the Utility of Learning about Humans for Human-AI Coordination. [4] Bard et al. The Hanabi challenge: A new frontier for AI research. [5] Fisac et al. Pragmatic-Pedagogic Value Alignment. [6] Shah et al. Benefits of Assistance Over Reward Learning. [7] Emmons et al. Observation Interference in Partially Observable Assistance Games.	Summary: The paper proposes using assistance games instead of RLHF to train AI assistants. The advantages of assistive games are that 1) they make AI and humans collaborate to accomplish tasks instead of AI just trying to get good ratings from humans (by potentially fooling humans); 2) AI reasons with uncertainty about human's true intention. The paper introduces a benchmark assistive game named MBAG, which is based on MineCraft and is complex enough while reasonable to work with for humans and academic labs. The authors introduce AssistanceZero, the first algorithm that can perform well in complex assistive games and outperform other assistance paradigms. This shows possibility to develop AI assistants via assistive games, which are previously seen as intractable and hard to be scaled to train AI assistants. The paper also explores approaches to model human behaviors in MBAG game to use as surrogate human models in AssistanceZero training. Overall, the paper is well-written, makes strong contributions, and provides meaningful results for several areas of audience. Therefore, I lean towards accepting the paper. ## Update after rebuttal Author's responses clearly answer my questions and the additional explanation and discussion will greatly help show the paper's value beyond controlled settings. As such, I keep my score. Claims And Evidence: Yes Methods And Evaluation Criteria: Yes. MCTS makes sense as a method to solve assistive games and the authors augmented it with a model to predict the latent objective and human-teammate actions. The performance metrics of overall task performance and human assistance provided make sense. Theoretical Claims: There is no theoretical claim in the work. Experimental Designs Or Analyses: Yes. The experiment designs for evaluating AssistanceZero, human modeling, and final human user study are sound and valid. Supplementary Material: No Relation To Broader Scientific Literature: The paper proposes to replace RLHF with assistive games due to the advantages mentioned in the paper summary. The assistive games were previously seen as intractable and the paper proposes a model-free RL with MCTS to potentially mitigate the issue. Essential References Not Discussed: Not that I am aware of Other Strengths And Weaknesses: Despite the strenths of the paper, I do have a few suggestions for further improving the paper. 1. In the intro, it seems the authors indicate the key difference between RLHF and Assistance game is whether the AI collaborates with the human on the task (in assistive games, the AI does). However, I think this teaming or collaboration may not be the most important key - for example, in a chat system the robot still only suggests ways to solve the human's problem, e.g., to fix a coding bug. There is no "action" the agent can actually take. I think the key is that the agent is also getting a ground-truth reward signal instead of just a human's thumbs-up/down. Even in chat system, the agent should aim to solve the human's problem, instead of fooling humans into thinking the problem is solved while it is actually not. In MBAG, this is also the key - the agent is getting the environment's feedback about positive or negative reward regarding the task progress (whether a block has been placed/destroyed correctly or not). 2. The training of both the human model and the assistive model seem to assume that humans are homogeneous - one model could represent human and one model could represent how to assist human. Is this a limiting assumption that future work should seek to relax? Does the authors observe heterogeneity in human data and preferences during experiment? Other Comments Or Suggestions: There is a "1" on line 129 after word "action". Questions For Authors: 1. The paper assumes access to $\hat{p}_t{\theta}$ in Line 294. How can this be available for general human tasks? Is this a restricting assumption? If so, making the limitation clear would be great. 2. More generally, is assuming the reward structure as known a restricting assumption that blocks application to general AI training? It seems unclear how human reward can be structured with a reasonable amount of parameters. What is the reward structure used in MBAG and how large is the $\theta$ space in the experiment? 3. What if the reward structure prior is incomplete or even wrong? 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: It seems unclear whether an IRB was obtained for the human study. Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: We thank the reviewer for their thorough review and helpful suggestions. Below are responses to individual questions. ## Responses to questions 1\. The paper assumes access to $\hat{p}_t(\theta)$ in Line 294\. How can this be available for general human tasks? We believe the reviewer is asking about how $\theta$ (the true reward parameter) is available during training. $\theta$ is not visible to the assistant policy when it is actually acting in the environment; the assistant infers a belief distribution over $\theta$ using the reward parameter prediction head. However, once an episode completes, the $\theta$ value that was used by the human model during that episode is available for updating the network to enable better assistance in the future, and thus we can use it as part of the loss function for AssistanceZero. 2\. More generally, is assuming the reward structure as known a restricting assumption that blocks application to general AI training? … What is the reward structure used in MBAG and how large is the $\theta$ space in the experiment? In our MBAG environment, the goal parameters $\theta$ consist of the specific arrangement of blocks in the goal house that the human is trying to build. This space contains over $10^{400}$ possible goal structures, since each block in the 3D grid that makes up the Minecraft world can be 10 different types. In a more complex setting, like a coding assistant, the goal parameters could instead consist of a set of unit tests that the user wants to satisfy by writing a function. One could collect a large dataset of function specifications along with unit tests and define the reward function based on how many unit tests pass at the end of the human-assistant interaction. In an even more general setting, an LLM judge could be used to give rewards based on detailed task descriptions that are used as the reward parameters. This would be distinct from RLAIF because a separate human model is used to interact with the assistant while a powerful LLM judge evaluates whether the latent task is actually accomplished. While these generalizations of our work still require overcoming additional challenges, we believe that our approach can scale to complex assistance settings. 3\. What if the reward structure prior is incomplete or even wrong? We note that our reward structure in MBAG is likely incomplete. It only describes the goal house and doesn’t represent other preferences the human may have for the assistant’s behavior, such as not getting in their way or obstructing their view. Despite this, our assistant performs well with real humans in the user study. Nevertheless, there are a few ways in which we can handle an incomplete/incorrect reward structure prior. One way is to detect if the human’s behavior is too unlikely under any reward function we can represent, and perform safe fallback actions. Another approach is to combine assistance games with RLHF by including an RLHF loss term that represents human preferences not described in the structured reward model. This is a good direction for future work, which we will mention in the conclusion. ## Key benefits of assistance games “the key is that the agent is also getting a ground-truth reward signal instead of just a human's thumbs-up/down.” We agree; receiving reward from the latent “true” reward function rather than (potentially biased) feedback from the human is a key ingredient in assistance games. We appreciate the reviewer’s point that the assistance game approach would encourage the AI to be more proactive in order to maximize the shared reward rather than simply react to and please the human. We'll emphasize this important distinction more clearly in the paper. ## Human heterogeneity “The training of both the human model and the assistive model seem to assume that humans are homogeneous… Is this a limiting assumption that future work should seek to relax? Does the authors observe heterogeneity in human data and preferences during experiment?” While we use a single human model, it can still represent heterogeneous behavior. Theoretically, since we use an LSTM-based human model, it can represent a mixture of human policies. In fact, we expect this to be the case since we observe significant heterogeneity in the human training data ( and the user study). Participants had very different levels of experience with playing Minecraft and computer/video games, so their building speed and play styles varied greatly. --- Rebuttal Comment 1.1: Comment: Thanks for posting author response! Q1: to clarify, I was asking about how we know the ground-truth prior distribution about $\theta$, which is $\hat{p}_t(\theta)$. It is understandable that in the MineCraft study this is designed by the experimenter and is known. However, how do we know about this for real-world applications? Q2: I understand in MBAG, the space of $\theta$ contains large number of possible goal structures due to the composition, but I was mostly asking how you represent that with $\theta$. I am guessing that it is a 400-length vector with each item being 0-9 as the 10 different types? This is reasonable to do in MBAG and make it feasible to calculate the likelihood and KL-divergence to the prior in Equation 1. However, how does this extend to less-structured real-world problems, e.g., how do you calculate the likelihood in your LLM-judge example? Human heterogeneity: very interesting extra information you mentioned! More in-depth analysis on how assistance game training helps different kinds of people would be a great add to the work. --- Reply to Comment 1.1.1: Comment: Q1: I was asking about how we know the ground-truth prior distribution about $\theta$... Thank you for clarifying your question and sorry for misinterpreting it\! We believe you are asking about $p(\theta)$, the prior distribution from which reward parameters are sampled at the beginning of an episode (defined on line 153). In our case, since each $\theta$ value represents a goal structure, we implicitly define $p(\theta)$ by a fixed dataset over goals, which consists of around 1,000 Minecraft houses. We split this into a training set and a test set; we use the training set for collecting human data and training all our assistants, and then evaluate whether they can assist with building previously unseen houses using the test set. This ensures that the assistants are not simply memorizing a fixed dataset, but can actually generalize to the large space of possible goals. In real-world applications, one could collect a similar dataset of “tasks” or “goals”. For example, for coding, one could curate a large set of coding tasks by using already-written code with unit tests in public repositories; for code without unit tests one could write tests with an LLM. This dataset would likely be representative of new coding tasks since it would cover a wide range of domains. For more general tasks, one could use a dataset of human-LLM conversations to extract task descriptions requested by humans; an LLM judge would assess whether the initial task is completed successfully. See below for more details on how this could be implemented in practice. Q2: in MBAG, the space of $\theta$ contains large number of possible goal structures... However, how does this extend to less-structured real-world problems, e.g., how do you calculate the likelihood in your LLM-judge example? In MBAG $\theta$ is represented as an 1100-length vector (11x10x10 gridword) with each item being 0-9. There is always a margin of air and ground around the house, which is why the effective goal space contains around $10^{400}$ structures and not $10^{1100}$. In less structured settings, it might not be feasible to directly predict a distribution over $\theta$, as you pointed out. However, the goal prediction head in AssistanceZero is only used to predict the intermediate rewards during MCTS. Thus, one could replace the goal prediction head with a head that directly predicts the expected reward $\mathbb{E}\[R(s, a) \mid h\]$ for an action given the history observed by the assistant, marginalizing over the reward parameters $\theta$. This head could be trained via MSE loss on observed rewards from rollouts, and would avoid the need to directly calculate a probability distribution over $\theta$. Even in more complex settings, it may still be possible to predict $\theta$ directly. In the LLM code assistant setting, $\theta$ could be a set of unit tests. One could add a $\theta$ prediction head to an LLM backbone to predict the unit tests directly since they are represented as code. The likelihood term would be the likelihood of the unit tests under the $\theta$ prediction head. In the more general LLM judge setting, $\theta$ could be a task description (e.g., “summarize this document for a lay audience”), which the $\theta$ prediction head could predict directly as well. Note that the KL divergence term isn’t strictly necessary to apply the assistance game framework. We used it for the MBAG assistant policy because it helped in practice, but it could be omitted in other domains. Nevertheless, for autoregressive LLMs, the KL divergence term can be approximated using Monte Carlo sampling. For example, this method is used in RLHF for approximating the KL divergence between the trained policy and the reference policy. Human heterogeneity: More in-depth analysis on how assistance game training helps different kinds of people... We agree that this is an interesting direction to look into\! We did some additional analysis of our human study data where we split the participants into two groups: experienced (≥100 hours playing Minecraft, 9 participants) and inexperienced (\<100 hours, 7 participants). The table below shows the average Likert ratings of helpfulness by both groups for each of the three assistants we tested, with 90% confidence intervals (since the groups are smaller the confidence intervals are quite wide). \|Assistant\|Experienced rating \| Inexperienced rating \| \|-\|-\|-\| \| SFT \| 1.6 ± 0.5 \| 1.9 ± 0.3 \| \| AssistanceZero \| 3.3 ± 0.4 \| 2.9 ± 0.7 \| \| Human \| 4.6 ± 0.3 \| 3.3 ± 0.9 \| Interestingly, inexperienced players tended to rate both the human and AssistanceZero assistants lower, and they rated them more closely together (although the confidence intervals are quite wide, indicating high variance). This could mean that inexperienced players have more difficulty judging how good an assistant is. Or, it could be that it is easier to assist more experienced players. It would be interesting to explore this more in future work.	Summary: This paper applies assistance games—where the assistant must infer the user’s hidden goal—to a challenging Minecraft building task with over $10^{400}$ possible goals. Their new AssistanceZero algorithm extends AlphaZero to partial observability by predicting both the human’s actions and the reward parameters (i.e., the hidden goal), then using MCTS to plan under that uncertainty. Compared to PPO and supervised fine‐tuning (as in RLHF), AssistanceZero yields assistants that better reduce the user’s workload and more accurately help complete tasks, validated by both simulation and a real user study. Claims And Evidence: Overall, most of the paper’s claims about their new algorithm (AssistanceZero) and its superior performance are backed by both simulation results and a user study in Minecraft. However, there are two concerns: (1) The user study is fairly small (only 16 participants), which limits the representativeness of the findings. (2) The paper assumes human behavior is purely Markovian with respect to $(s,\theta)$, whereas in reality people often rely on history (especially prior mistakes), which the model does not fully capture. Methods And Evaluation Criteria: Yes. The paper’s methods—particularly the AssistanceZero algorithm (a partial‐observability extension of AlphaZero)—and evaluation criteria are well aligned with the assistance‐game setting they propose. They also introduce a Minecraft Building Assistance Game (MBAG) benchmark, which is large‐scale (over 10^{400} possible goals) and challenging enough to meaningfully test algorithms in an interactive collaboration scenario. Theoretical Claims: There are no new theoretical results or novel proofs here. The authors rely on existing results from prior works (e.g., Hadfield-Menell et al. 2016) and cite them appropriately. Experimental Designs Or Analyses: The experiments are well-structured—comprising both simulation and a user study—but the user study's small sample size (16 participants) limits the generalizability of the findings. Additionally, while the paper critiques RLHF and proposes AssistanceZero as an alternative, it only compares against a pretraining plus SFT baseline rather than a full RLHF system. This leaves open the question of how AssistanceZero would perform compared to a complete RLHF approach. Supplementary Material: Yes. I reviewed the supplementary material. Relation To Broader Scientific Literature: The paper builds on several strands of prior work. First, it extends the concept of assistance games—also known as cooperative inverse reinforcement learning or hidden-goal MDPs—which were introduced by Fern et al. (2014) and further formalized by Hadfield-Menell et al. (2016). These works established that, under full observability of the state (and the human knowing the reward parameters), an optimal human policy can be defined as depending only on $(s,\theta)$. Second, the paper leverages ideas from model-based reinforcement learning, particularly those underlying AlphaZero (Silver et al., 2017) and MuZero (Schrittwieser et al., 2020). By extending these algorithms to a partially observable setting, the authors create AssistanceZero, which uses Monte Carlo tree search (MCTS) guided by neural network predictions—not just for policy and value, but also for predicting human actions and the hidden reward parameters. Essential References Not Discussed: The related works are properly cited. Other Strengths And Weaknesses: Strengths: The paper proposes a novel approach—AssistanceZero—which creatively adapts AlphaZero to a partially observable assistance game setting, addressing key limitations of RLHF. The introduction of the challenging Minecraft Building Assistance Game (MBAG) benchmark is also a strong contribution, as it pushes the problem to a more realistic and complex domain. Additionally, the experimental evaluation, combining simulation results with a human user study, provides compelling evidence for the method’s potential. Weakness: This will be discussed in other sections. Other Comments Or Suggestions: I don't have other comments. Questions For Authors: - Have you considered evaluating AssistanceZero against a full RLHF system? What challenges or limitations do you foresee in such a comparison? - Your model assumes that human behavior is Markovian (dependent solely on the current state and reward parameters). How might your approach perform if humans exhibit non-Markovian behavior—such as incorporating historical context or prior mistakes—and have you explored this possibility? - In future work, the authors briefly discuss LLM post-training using assistant games. However, I have several questions for discussion (not affecting my score): + In the real world, humans do not have full observation of the state, which is why they might ask an LLM assistant for help. This paper, however, assumes that the human has full observation. How can the ideas and framework be extended to training LLM assistants under such conditions? + If a human wants to complete a task and asks an LLM for help, the most efficient approach would be to communicate their intentions to the AI at the beginning (via language) so that the AI can have full observation of the goal. Given this, it is unclear how an assistant game framework would be beneficial in such cases. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We thank the reviewer for their thorough review and are glad they found the paper proposes a “novel approach” and that our MBAG environment is “also a strong contribution.” We have responded to individual points and questions below. ## Small user study “The user study is fairly small (only 16 participants), which limits the representativeness of the findings.” Our user study was in-person (1-1.5 hours per participant) because we couldn’t run it on a crowdsourcing platform due to latency constraints. Our sample size is comparable to other in-person HCI studies: the median number of participants in CHI 2019 mixed-method studies was 18 [3]. Moreover, our participants had different amounts of experience with Minecraft and computer games, making our sample diverse. Finally, our results are statistically significant based on appropriate statistical tests. Our assistant enables humans to build the goal with fewer place/break actions (one-sided t test $p \< 0.05$). ## Markovian human model “Your model assumes that human behavior is Markovian… How might your approach perform if humans exhibit non-Markovian behavior” We actually do use a non-Markovian human model by employing an LSTM to condition on past observations. Recurrence improved the model’s accuracy (Appendix D.1.2), suggesting humans exhibit non-Markovian behavior. Prior assistance game work also uses recurrent human models [1]. We kept the Markov notation for consistency with the original assistance game formalism. ## RLHF comparison “Have you considered evaluating AssistanceZero against a full RLHF system?” Comparing with RLHF would be interesting but challenging because RLHF is not easily applicable to the MBAG environment. First, RLHF is usually formulated as a single-agent problem [2, 3], so the additional human agent in our setting would make it difficult to apply standard techniques. Furthermore, in LLMs, RLHF is applied to only a single step of interaction between the assistant and the user, i.e., the comparison data used by RLHF uses conversations which only differ in the last assistant message. In MBAG, the equivalent would be to compare single assistant actions taken in response to a given history of human and assistant actions. However, it may be quite difficult to judge assistant actions in isolation; for instance, more than half of assistant actions are usually movement, and it is unclear how to judge the relative usefulness of say, moving left versus up. For these reasons, we decided to only compare to an SFT baseline, especially since SFT alone for LLMs can often achieve performance close to that of RLHF [7]. Future work could compare assistance games with RLHF in domains where it's more feasible, like LLM post-training. ## LLM post-training “In the real world, humans do not have full observation of the state…” Our approach could be applied even if the human is learning about their own reward. The assistant would still be rewarded based on the true goal, and we could train a recurrent human policy on data involving human learning. We could follow approaches like [4], which uses RL in a multi-armed bandit setting where the human learns about their reward parameters through noisy observations. Additionally, the assistant could predict the human’s internal state and learning dynamics to help them learn faster [5]. We also note that such “partially observable assistance games” are studied in [1]. We chose to study the simpler case where the human observes their own goal since it is still challenging. “the most efficient approach would be to communicate their intentions to the AI at the beginning (via language) so that the AI can have full observation of the goal.” Often, the human cannot fully communicate their goal to the AI. For example, for complex coding tasks, it would be difficult and time consuming to write long, detailed specs. Additionally, if the human wants the code to produce visual output (e.g., a diagram), natural language is insufficient to provide the AI full goal observability. Thus, an assistance game approach would remain beneficial. Even with perfect communication, an assistant trained with the assistant game framework would likely be more aligned with the human’s true intentions than RLHF, which could deceive humans since it’s trained to seek positive feedback from users [6]. [1] Emmons et al. Observation Interference in Partially Observable Assistance Games [2] Christiano et al. Deep reinforcement learning from human preferences [3] Reinhard. Participants, Incentives, and User Studies: A Survey of CHI 2019 [4] Chan et al. The assistive multi-armed bandit [5] Tian et al. Towards modeling and influencing the dynamics of human learning [6] Williams et al. On targeted manipulation and deception when optimizing LLMs for user feedback [7] Zhou et al. LIMA: Less Is More for Alignment. --- Rebuttal Comment 1.1: Comment: Thank you for the clarifications, which have addressed much of my initial concern. However, I am maintaining my current score for two reasons: 1) The size of the human study is still not convincing. 2) If the paper argues AssistanceZero as an alternative to RLHF, it should include a direct comparison. Otherwise, it should refrain from making such a claim. --- Reply to Comment 1.1.1: Comment: We thank the reviewer for their response and we are glad we were able to address some of their concerns. Just to summarize our thoughts regarding these two points: * Our in-person human study is of similar size to comparable work. It’s large enough to show a statistically significant improvement of AssistanceZero over SFT. * Current RLHF techniques are not directly applicable to our Minecraft domain because it is fundamentally interactive at a granular level in a way that LLM-based chatbots are not. This is why we chose to compare AssistanceZero to SFT. For LLMs, SFT can produce similar results to full RLHF [1], so we think this is a quite strong baseline. Thank you again for your time and valuable feedback! [1] Zhou et al. LIMA: Less Is More for Alignment.	null	null	null	null	null	null	null	null
Learning Survival Distributions with the Asymmetric Laplace Distribution	Accept (poster)	Summary: The paper introduces a novel parametric survival analysis framework based on the Asymmetric Laplace Distribution (ALD). By formulating the survival problem through ALD, the authors derive closed-form expressions for key distributional summaries (e.g., mean, median, mode, and quantiles) and propose an architecture where a shared encoder feeds into three independent heads to predict the ALD parameters. The model is trained via maximum likelihood estimation (MLE) with tailored loss functions for both observed and censored data. Comprehensive experiments on 14 synthetic and 7 real-world datasets demonstrate that the proposed approach often outperforms established methods such as LogNorm MLE, DeepSurv, DeepHit, and CQRNN in terms of predictive accuracy, discrimination (using C-index metrics), and calibration. Updates after Rebuttal I thank the authors for their rebuttal. Although I am not sure if including additional results in anonymous githubs is legitimate, the revised experiments look much more promising and well-address my concern on empirical evaluation. I will increase my score by one point. Claims And Evidence: * While the paper asserts that the ALD-based method is broadly effective, its reliance on the ALD assumption is problematic in cases with highly skewed event distributions (e.g., the SUPPORT dataset). The evidence does not fully demonstrate robustness when the underlying survival distribution deviates significantly from an ALD. This point requires more convincing ablation studies or experiments. * The paper makes claims regarding the efficiency and stability of the proposed model, bolstered by the use of a shared encoder and residual connections. Still, the experiments do not sufficiently address how the approach scales to very high-dimensional data or extremely censored datasets --- especially some heavily censored datasets. Methods And Evaluation Criteria: Yes Theoretical Claims: Yes I chwecked all theoretical proofs and claims. Experimental Designs Or Analyses: I have checked all experiment designs and analyses. Essentially I think there are several baselines missing, such as DeepCox, Deep Survival Machine, Neural Frality Machine, and Deep Cox Mixture. Supplementary Material: I have reviewed all the supplementary materials. Relation To Broader Scientific Literature: The paper’s contributions are deeply rooted in—and extend—the established literature on survival analysis and quantile regression. In particular, it builds on classical parametric models (such as exponential, Weibull, and log‐normal models) by introducing a flexible, ALD‐based approach that provides closed-form expressions for key survival summaries (mean, median, quantiles). This idea is an evolution of earlier work in quantile regression where the asymmetric Laplace distribution was used as a working likelihood (see Koenker and Bassett, 1978; Yu and Moyeed, 2001) to capture the conditional quantiles of the response. Furthermore, by integrating a neural network architecture with a shared encoder and independent heads for estimating the ALD parameters, the paper aligns with recent deep learning efforts in survival analysis (e.g., DeepSurv, DSM, Deep Cox, Neural Frality Machine, DeepHit, and CQRNN) that aim to model complex, non-linear relationships and to address limitations of traditional models like the Cox proportional hazards model. Essential References Not Discussed: * Deep Survival Machine (DSM) —which models survival times using a learned mixture of parametric distributions—shares the goal of providing a full survival distribution without relying on the proportional hazards assumption. However, while DSM flexibly combines several parametric components (such as Weibull or log-normal distributions) to capture heterogeneous survival patterns, the proposed ALD-based method offers a closed-form formulation for key event summaries (mean, median, quantiles) via maximum likelihood estimation. This paper was not discussed and compared. * Similarly the infamous DeepCox model in this field was also not compared. Other Strengths And Weaknesses: Strengths: * The paper offers detailed derivations, theoretical insights, and even proofs (presented in the appendix) that explain the loss formulation and the properties of the ALD. This depth of analysis underpins the methodological contributions. * The use of the ALD provides a neat way to capture survival distributions in closed form. This results in efficient computation of various summary statistics, which enhances interpretability compared to discretized methods. Weaknesses: * The model’s performance is contingent upon the assumption that survival times are well modeled by an ALD. In cases such as the SUPPORT dataset, where the event distribution is highly skewed, this assumption may not hold, potentially affecting calibration. * Experiments on highly censoring scenarios (e.g., refer to the experiments by DSM) are encouraged to more comprehensively evaluate the model at tails. Other Comments Or Suggestions: N.A. Questions For Authors: * How sensitive is the proposed ALD-based method when the true underlying survival distribution deviates from the ALD assumption? Can you provide results from ablation studies or additional experiments that test this robustness? * In datasets with very high censoring rates (e.g., the experiment settings of DSM), what modifications or additional regularizations might be necessary to maintain reliable calibration and discrimination? Have you considered how the method might be adapted to such scenarios? Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: We sincerely thank you for your comprehensive evaluation and insightful comments. We also appreciate the detailed review of our theory, experiments, and connections to the broader literature. Below we respond to the specific points raised: R1[Claims And Evidence, Other Strengths And Weaknesses (Weaknesses), Questions For Authors 1]: We would like to emphasize that our benchmark covers a diverse range of survival scenarios with varying censoring and skewness levels. All 21 datasets used in our experiments differ in their censoring rates, and for synthetic datasets (e.g., multivariate Normal, Log-Normal), we explicitly vary the censoring levels to create more challenging conditions. Additionally, distributions like LogNormal and Exponential inherently introduce strong skewness. Importantly, these synthetic datasets are distributionally distinct from ALD, yet our method performs well across them, demonstrating robustness beyond the assumed distribution. The latest Table 2 [https://anonymous.4open.science/r/ICML25/Fig1.png ] (4 more baselines added) highlights the superiority of our method compared to a broad spectrum of baselines, including (semi-)parametric and nonparametric models, covering both neural and non-neural architectures. Although our method shows relatively weaker results on the SUPPORT dataset, the same trend is seen in several baselines. Nevertheless, our performance remains competitive and stable across metrics. Following your suggestions, we added case studies inspired by DSM to evaluate robustness under high censoring and at key quantiles (25%, 50%, 75%). Fig 2 and 3 [https://anonymous.4open.science/r/ICML25/Fig2.png; https://anonymous.4open.science/r/ICML25/Fig3.png ] present results on METABRIC and SUPPORT datasets, which differ significantly in their censoring and distributional properties. Our method consistently achieves strong or competitive time-dependent concordance scores across censoring levels. On METABRIC, it performs especially well at higher quantiles, where skewness and censoring are more pronounced. Although our method shows relatively weaker results on SUPPORT, this is likely due to the substantial deviation of its underlying distribution from the ALD assumption. However, our method still performs comparably to DSM-based baselines without significant degradation. We also appreciate the point and agree that scaling to higher-dimensional datasets is important. While our current experiments focus on structured survival datasets with up to 14 covariates (i.e., SUPPORT), our method is lightweight, requires only 3 estimated parameters of ALD per instance, and leverages compact neural architectures. It does not rely on large time grids or mixture components, making it computationally efficient. Intuitively, we expect our method to retain its advantages even in higher-dimensional settings due to its compact parameterization and stable training behavior. We are currently exploring extensions to such settings and plan to evaluate their scalability and performance on high-dimensional survival data in future work. R2[Experimental Designs Or Analyses, Essential References Not Discussed]: In our current version, we have already reported results for DeepCox (referred to as DeepSurv in our initial submission), and have additionally incorporated new baselines such as DSM with Log-Normal and Weibull components, as well as classical non-neural models like GBM and RSF. For other models such as Neural Frailty Machine and Deep Cox Mixture, we will include a detailed discussion in the Related Work section (similar to the additional comparisons presented in our response to Reviewer rnhn) and are happy to incorporate further empirical evaluations in the revision if needed. Here, we would like to highlight that, compared to these mixture-based models, our approach offers two key advantages: 1. Computational efficiency. DSM models the survival function as a mixture of $K$ Log-Normal or Weibull components, which increases computational complexity as $K$ grows. In contrast, our model requires estimating only 3 parameters per instance, enabling faster training and inference with a much simpler architecture. 2. Performance stability. DSM is sensitive to $K$ and architecture choices. Misaligned components can lead to instability. In contrast, our model relies on straightforward neural network hyperparameters and exhibits stable performance across diverse datasets without extensive tuning. R3[Questions For Authors 2]: While we acknowledge that more sophisticated loss functions or architectural enhancements could potentially further improve performance, our current focus is on maintaining a simple and interpretable design. Despite its simplicity, our approach already achieves strong empirical results. We highly agree that integrating more advanced components is an interesting and valuable direction and plan to explore this in future work.	Summary: The paper proposes a parametric survival analysis method based on asymmetric Laplace distribution. It enables predicting continuous distribution-based predictions, unlike existing discretized nonparametric methods. Claims And Evidence: The paper mentions several limitations of the existing methods 40-54, such as strong assumptions about the underlying distribution, only predicting discretized distribution. The experiments show the proposed method is significantly better than the selected baselines. However, there seems to be not many discussion about how important each module is. Specifically, 1. the paper claims predicting continuous distribution is an advantage. I acknowledge this and it is achieved obviously through the theoretical foundation. However, how many benefits are brought by this? 2. The paper claims the strong assumptions about the underlying distribution. Why does the proposed method release the assumption and what is some evidence to show that? Methods And Evaluation Criteria: The proposed method predicts the parameters of the asymmetric Laplace distribution, and thereby predicts the survival distribution. The corollary 3.2 provides the justification of using asymmetric Laplace distribution, that tells the relationship between it and quantile regression. This method makes sense and works as expected, but the contribution is limited, mainly because of these: 1. There are many ways to model a continuous parametrized distribution other than Asymmetric Laplace Distribution. For example, predicting the coefficients of a Fourier transform, or Taylor series. They are also continuous in nature. What are the unique advantages of ALD? 2. The paper claims the proposed method offers superior flexibility in capturing diverse survival patterns. But there seems no experiments supporting this claim. Theoretical Claims: The theoretical claims make sense to me. But the detailed math is not carefully checked. Experimental Designs Or Analyses: The experiment statistics looks good, but as mentioned in previous sections, it does not sufficiently support the claims made by the paper. If possible, I would recommend adding more experiments: 1. baselines of predicting the coefficients of a Fourier transform or Taylor series. 2. compare what survival patterns can the proposed method succeeds and when it fails. Supplementary Material: Supplementary material is briefly skimmed. Relation To Broader Scientific Literature: I am unsure about this question. 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: We sincerely thank you for your careful reading and constructive feedback. We added four more baselines shown in Table 2 [https://anonymous.4open.science/r/ICML25/Fig1.png ] and more comparisons (See the reply for Reviewer rnhn) will be added. Below, we will address your concerns. R1[Claims And Evidence 1]: Unlike discretized nonparametric approaches, our method estimates only 3 parameters of the ALD per instance, providing computational efficiency and smooth, closed-form CDFs. In contrast, models such as DeepHit must balance computational cost and accuracy by discretizing time, which introduces approximation errors, especially, under coarse time grids, and limits their ability to capture fine-grained survival dynamics. Beyond theory, across 14 synthetic and 7 real-world datasets, our method outperforms DeepHit in 73% of 189 benchmark settings and underperforms in less than 4% (Table 2), underscoring the strength of continuous modeling. This advantage is most evident in the IBS metric, where our method achieves superior performance across all 21 datasets. Notably, IBS evaluates both discrimination and calibration over time, making it especially sensitive to distributional smoothness and continuity. R2[Claims And Evidence 2]: Indeed, any parametric model makes certain assumptions about the underlying distribution. We adopt the ALD assumption primarily due to its strong theoretical and practical connections to quantile regression. The widely used pinball (checkmark) loss, foundational in methods like CQRNN, is essentially derived from ALD. However, such methods lack full distributional modeling and continuity. Our work bridges this gap, retaining the empirical strengths of quantile-based approaches while introducing a fully parametric, continuous, and interpretable survival model. As noted by Reviewer 6hhK, this represents a principled evolution from loss-based to distribution-based modeling. Other parametric options (e.g., Gamma, Log-Normal) are possible but often suffer from the absence of closed-form CDFs, unstable gradients, and reduced robustness (see the reply for Reviewer rnhn and Appendix A.2). In contrast, ALD offers stable training and strong empirical results, making it a compelling choice. R3[Methods And Evaluation Criteria 1]: To the best of our knowledge, there is limited prior work exploring the use of Fourier or Taylor series expansions for continuous survival distribution modeling, making this a novel and interesting direction. We would greatly appreciate any specific references or formulations the reviewer has in mind for further consideration, and we are open to exploring this line of research in the revision. While many alternatives exist, our goal is to balance simplicity, interpretability, and performance. The ALD-based framework achieves this effectively, as demonstrated in our results. R4[Methods And Evaluation Criteria 2, Experimental Designs Or Analyses]: We now provide new analyses to support this claim. Fig 4 [https://anonymous.4open.science/r/ICML25/Fig4.png ] shows the flexibility of our method and DeepHit in capturing diverse survival patterns in the 7 real-world datasets. Specifically, we applied K-means clustering to the estimated parameters from our model, with the number of clusters set to 6. This allows us to visualize 6 representative survival patterns, where each CDF curve corresponds to the average parameters within a cluster. As shown in Fig 4, both our method and DeepHit are capable of capturing diverse survival patterns in real-world datasets. However, the patterns generated by DeepHit often appear less realistic. Its CDFs consistently converge to 1 across all identified patterns, suggesting that every individual eventually experiences the event. This outcome contradicts the existence of censoring in the data, where a non-zero censoring rate implies that a portion of individuals should remain event-free over time. Although the true underlying distribution is not observable in real-world settings, this behavior illustrates DeepHit’s limited ability to model long-term survival. To further compare what survival patterns can the proposed method succeed in and when it fails, we leverage the fact that ground-truth CDFs are available for each instance in the synthetic datasets. This allows us to perform the same clustering analysis as in the real-world setting. Specifically, Fig 5 [https://anonymous.4open.science/r/ICML25/Fig5.png ] presents the worst-estimated instance (based on Wasserstein distance) within each of the 6 clusters for the best-performing synthetic dataset, comparing our method and DeepHit. Fig 6 [https://anonymous.4open.science/r/ICML25/Fig6.png ] repeats this for the most challenging dataset. These results demonstrate that our method consistently yields lower Wasserstein distances across different survival patterns, indicating a more reliable estimation of survival distributions, even in difficult scenarios.	Summary: This paper proposes a parametric survival analysis model which uses asymmetric Laplace distributions (ALDs) to represent survival distributions, where the non-linear dependence of ALD’s parameters on static covariates is modeled by neural networks. The experiments on synthetic and real-world data confirmed the model's validity. Claims And Evidence: The primal contribution of this paper is to introduce asymmetric Laplace distributions (ALDs) to represent survival distributions. But it seems not to be clear why ALDs should be adopted or why ALDs are superior to other parametric/nonparametric approaches. For example, do ALDs have any advantages over mixture models (e.g., mixture of log-normal or gamma distributions) in terms of accuracy or computational cost? Methods And Evaluation Criteria: The proposed methods and evaluation criteria make sense. Theoretical Claims: Theoretical claims seem to be correct. Experimental Designs Or Analyses: The compared reference models seem to focus heavily on neural network-based models. More standard nonparametric approaches in survival analysis (e.g., random survival forest) should be included in the comparison. See below about essential references. Supplementary Material: I didn’t review the supplementary material. Relation To Broader Scientific Literature: This paper provides an accurate survival analysis, which could be beneficial especially in clinical fields. Essential References Not Discussed: To overcome the limitation of Cox proportional hazards model, a vast number of non-neural network survival models have been proposed that replace the log-linear parametric function with a non-linear one. Especially, generalized boosted models [a], random survival forests [b], and Gaussian process models [c,d,e], which are not cited in the paper, should be discussed in Related Work. Some of them should be included in the comparative experiments (e.g., generalized boosted models can be easily implemented via gbm(distribution = ’coxph’) in R). [a] Ridgeway G, Developers G (2025). gbm: Generalized Boosted Regression Models. R package version 2.2.2, https://github.com/gbm-developers/gbm. [b] Hemant Ishwaran, Udaya B. Kogalur, Eugene H. Blackstone, and Michael S. Lauer. Random survival forests. The Annals of Applied Statistics, 2(3):841–860, 2008. [c] Tamara Fernández, Nicolás Rivera, and Yee Whye Teh. Gaussian processes for survival analysis. In Advances in Neural Information Processing Systems 29, 2016. [d] Minyoung Kim and Vladimir Pavlovic. Variational inference for Gaussian process models for survival analysis. In Uncertainty in Artificial Intelligence, pages 435–445, 2018. [e] Hideaki Kim. Survival Permanental Processes for Survival Analysis with Time-Varying Covariates. In Advances in Neural Information Processing Systems 36, 2023. Other Strengths And Weaknesses: Strength - The validity of the proposed model was evaluated on many real-world data. Weakness - See above. Other Comments Or Suggestions: No other comments. Questions For Authors: I cannot follow the sentence on pp. 4, "However, semiparametric models face challenges in effectively handling censored data, particularly when censoring rates are very high." Could you explain why semiparametric approaches work poorly in high-rate censoring? Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Thank you for your thoughtful and constructive feedback, and for generously suggesting many references that we had not previously considered. We added 4 more baselines and the results are available in Table 2 [https://anonymous.4open.science/r/ICML25/Fig1.png ]. Below, we provide a detailed discussion comparing our proposed method with the baselines you mentioned and address your specific concerns. R1[Claims And Evidence]: Compared to parametric methods, our approach offers two key advantages: 1. For our method, both the PDF and CDF of the ALD are available in closed form and are smooth to their parameters. While it is possible to use any distribution to model survival functions, some commonly used alternatives, such as the Gamma distribution, often suffer from gradient instability during training. Specifically, the Gamma distribution lacks a closed-form expression for its CDF, which instead relies on numerically approximated special functions (i.e., the incomplete Gamma function). These operations introduce significant numerical instability when computing gradients via backpropagation, leading to unstable training dynamics or poor convergence. In contrast, the ALD offers closed-form expressions with stable gradients, making it well suited for optimization in neural network-based survival models. 2. Experimental results on 14 synthetic and 7 real-world datasets across 9 metrics show that our method consistently achieves strong performance, even under high skewness and heavy censoring. As shown in Table 2, it outperforms LogNormal in 60\% of 189 settings, with worse performance in less than 5\%, highlighting its robustness and generalizability. Compared to nonparametric methods, our approach offers two key advantages: 1. Our method provides continuous and closed-form estimates of CDFs and summary statistics, avoiding the discretization inherent in many nonparametric models. Notably, these discretization CDFs can introduce significant approximation error, especially when the interval between time steps is large, which limits their precision in capturing fine-grained temporal dynamics. 2. The parametric nature of the ALD enables faster training and inference, with fewer parameters and lower memory overhead compared to nonparametric methods. For example, our model only needs to estimate 3 parameters per instance. In contrast, nonparametric approaches, such as DeepHit, require computing and storing hundreds of discrete CDF values to achieve comparable resolution, resulting in significantly higher computational costs. Compared to the mixture models, our approach offers two key advantages: 1. DSM models the survival function as a mixture of $K$ Log-Normal or Weibull components, leading to increased computational complexity as $K$ grows. In contrast, our ALD-based model is simple and estimates only 3 parameters per instance, enabling faster training and inference. 2. In practice, DSM is highly sensitive to the choice of parameter $K$ and architectural design, partly due to its loss function, which aggregates multiple distributional components. This can make it vulnerable to instability when some mixture components fail to capture the underlying survival patterns effectively. In contrast, our model relies on simple neural network hyperparameters and delivers more stable performance across diverse settings, without the need for extensive tuning. R2[Experimental Designs Or Analyses, Essential References Not Discussed]: We will include and discuss these important works in the related work section. We have implemented both GBM and RSF, as reported in Table 2. Compared to these two standard nonparametric approaches: 1. Our method outperforms GBM in 52\% of the 189 benchmark settings while underperforming in fewer than 7\% of them. Similarly, it surpasses RSF in 55\% of the settings and performs worse in fewer than 9\%, demonstrating strong robustness and generalizability across diverse survival scenarios. 2. Ensemble-based nonparametric methods such as GBM and RSF typically require training 100 or more decision trees, which can be computationally intensive and memory demanding, especially for large datasets or when tuning hyperparameters. Moreover, once trained, our method enables fast evaluation of continuous survival functions in closed form, whereas tree-based models require traversing ensembles for each prediction. R3[Questions For Authors]: Semiparametric models like the Cox proportional hazards model incorporate censored samples only indirectly through the risk set in the partial likelihood. As a result, when censoring is high, the model relies on very limited observed events, reducing its statistical efficiency. In contrast, our parametric approach models both censored and uncensored data explicitly through a full likelihood, allowing it to make better use of all available information and remain robust under high censoring. --- Rebuttal Comment 1.1: Comment: Thank the authors for the clarification and for including additional reference methods in the experiments. While I remain somewhat unconvinced about the superiority of ALDs over other parametric distributions or mixture models, the results appear remarkably good, and I believe the proposed method offers practical value. I appreciate the authors’ efforts to better articulate the paper's contributions. I will raise my score to 3: weak accept, on the condition that the appendix includes a detailed description of how the hyper-parameters for all comparison methods were determined (e.g., the procedure for selecting the number of components in DSM, the number of trees in ensemble methods, and the number of time discretization points used for numerical integration in DeepSurv and DeepHit). --- Reply to Comment 1.1.1: Comment: We sincerely thank you for your positive feedback and for raising the score. We are glad to hear that the proposed methods are considered to have practical value, and we also appreciate your recognition of our efforts in clarifying our contribution and enriching our experimental comparison. As per your suggestion, we will detailedly describe the hyperparameter selection process of these methods and all the compared methods in our Appendix. This will cover but is not limited to: 1. the procedure for selecting the number of components in DSM. 2. the number of trees in ensemble methods. 3. the number of time discretization points used for numerical integration in DeepSurv and DeepHit. We believe that this supplement will further improve the transparency and reproducibility of our experiments. Additionally, we will update our code to include the added baselines and the case study examples. Thank you again for your thoughtful review of both our paper and rebuttal. We truly appreciate the time and effort you’ve put into evaluating our work, as well as the insightful references you’ve suggested. Your comments have consistently been constructive and valuable, and they’ve played a key role in helping us improve the clarity and quality of our paper.	Summary: - Authors introduce a parametric survival analysis model, which utilises the Asymmetric Laplace Distribution in the Quantile Regression inspired loss function. - Inspired by the mean absolute deviation loss function, which models the hyperplane with median distance from all points, the quantile regression is a modelling approach where we use weighted absolute value as a loss function to model the hyperplane which separates p and 1-p observations in the optimal way. To estimate the parameters of the Asymmetric Laplace normal, authors present their architecture based on the shared encoder, residual skip connection and 3 heads that predict the parameters of the Asymmetric Laplace Distribution. - The findings are supported by the experiments on the real data. Claims And Evidence: Claims are well supported. Evidence is provided in the form of: - the derivations, - experiments, - relevant citations. Methods And Evaluation Criteria: Yes. - Authors carry experiments on the synthetic datasets and 7 real-life dataset related to survival statistics task to support their claim. - Authors vary the number of the features, sizes of the datasets and various censored fractions of the datates. - Each experiment is repetead 10 times. Theoretical Claims: Verified Corollary 3.2 in Appendix A.1. Seems correct. Experimental Designs Or Analyses: Authors compare the performance against other 4 benchmark models: CQRNN, DeepSurv, DeepHit and LogNorn Supplementary Material: A - B.3 Relation To Broader Scientific Literature: The model design seems to be novel. Essential References Not Discussed: - All relevant text books coverring Quantile regression are cited. - The benchmark models are well described and discussedI . Other Strengths And Weaknesses: Well written paper, easy to follow, methodology is great. Other Comments Or Suggestions: Not convinced that the results itself is strong enough as a topic to publish the paper (however methodologically is the paper well composed and written). Happy to be convinced though. Questions For Authors: 1. Looking at the size of the architecture and datasets: when it comes to selection of the architecture, how can you achieve that given the sample and architecture size, the networks are generalising reasonably well rather than memorising. 2. Did you experiment with different architectures? 3. Did you consider experiments containing shifts of the test sets to verify how well the selected method generalises to domain shift? 4. How does the model behave for the edge cases, i.e. is your methodology suitable for the extreme quantiles? Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Thank you for your constructive and insightful feedback. We appreciate the time and effort spent evaluating our work and will address the concerns and questions below. R1[Other Comments Or Suggestions]: In response, we would like to emphasize that our method introduces a novel but simple loss formulation based on the ALD for survival modeling. Compared to non-parametric methods, our approach offers great flexibility and interpretability, as it enables closed-form expressions for key survival summaries (e.g., mean, median and quantiles) and continuous cumulative distribution functions. In contrast to existing (semi-)parametric methods, our approach is easy to train and offers balanced performance metrics, making it well-suited for modeling diverse survival patterns across datasets. For the experiments, we conducted extensive evaluations in 14 synthetic and 7 real-world datasets to comprehensively assess our method under diverse survival scenarios. We compare our approach against 8 competitive baselines (4 more added), covering a broad spectrum of survival models — (semi-)parametric and non-parametric —as well as both neural and non-neural architectures. Our evaluation spans 9 performance metrics, capturing the model's accuracy, discrimination, and calibration. As a result, Table 2 summarizes the superiority of our method, and the Appendix further analyzes the details of the other baselines for a better understanding of the difference between our methods from both theoretical and empirical aspects. Thanks to the insightful feedback from all reviewers, we have included additional results and case studies to highlight the following: 1. The superiority of our method compared to mixture-based models (e.g., DSM with Log-Normal and Weibull components) and non-neural survival models (e.g., Generalized Boosted Models and Random Survival Forests) [https://anonymous.4open.science/r/ICML25/Fig1.png ]; 2. The flexibility of our method in capturing diverse survival patterns in real-world datasets [https://anonymous.4open.science/r/ICML25/Fig4.png ] and synthetic datasets [https://anonymous.4open.science/r/ICML25/Fig5.png; https://anonymous.4open.science/r/ICML25/Fig6.png ], complementing our synthetic benchmarks that already span a wide range of structural variations distinct from ALD; 3. The robustness of our approach under challenging real-world conditions [https://anonymous.4open.science/r/ICML25/Fig2.png; https://anonymous.4open.science/r/ICML25/Fig3.png ], such as pronounced skewness and heavy censoring, provides further evidence of its reliability beyond the varied censoring and skewness levels considered in our initial experiments. While time constraints limited the extent of results we could include in this rebuttal, we would be more than happy to conduct and report additional experiments or case studies if the reviewers find them helpful. R2[Questions For Authors 1-2]: We did not explore alternative architectures in our work for the following reasons: 1. Dataset simplicity. Most of our datasets are low-dimensional (the highest being SUPPORT with 14 features). Given this, we focused on fully connected architectures, which offered sufficient capacity while avoiding overfitting. Empirically, we found them to generalize well across datasets with varying feature sizes and censoring levels. 2. Comparability with prior work. Most recent neural methods for survival analysis, such as CQRNN, DeepSurv, DeepHit and DeepSurv, also use fully connected architectures (see Appendix B.3). To ensure a fair comparison, we adopted the same architectural choice. While an exhaustive architecture search was beyond the scope of this work, we fully agree that this is a valuable direction. We would be happy to explore alternative configurations in future work and greatly appreciate any concrete suggestions regarding alternative architectures. R3[Questions For Authors 3]: The point about domain shift is excellent and domain shift is indeed an important and valuable direction for future research. While such an analysis falls outside the scope of our current work, we fully acknowledge its significance. In future extensions, we plan to incorporate experiments under domain shift scenarios. We will also add a discussion paragraph in the final version to explicitly reflect this limitation and outline potential directions for addressing it. R4[Questions For Authors 4]: Thank you for this valuable question. Your concern aligns closely with the feedback from Reviewer 6hhK, and we have further conducted additional case studies following the evaluation settings used in DSM. As illustrated in Fig2 and 3 [https://anonymous.4open.science/r/ICML25/Fig2.png; https://anonymous.4open.science/r/ICML25/Fig3.png ], our method consistently demonstrates superior or competitive performance across different censoring regimes and event-time quantiles. The full analysis can be found in the reply for Reviewer 6hhK.	null	null	null	null	null	null
The Surprising Agreement Between Convex Optimization Theory and Learning-Rate Scheduling for Large Model Training	Accept (poster)	Summary: This paper proposes to find optimal settings of warmup-stable-decay (wsd) learning rate (LR) scheduler for training large language models (LLMs) from a theoretical inspiration. The wsd scheduler is a piecewise function by training iterations, the first part is a constant function (named based LR) and the second part is a linear function that decays the LR with a ratio proportional to iteration. Thus, the authors aim to investigate the configuration of two controllable hyper-parameters, i.e., base LR and a fraction of the decay period to the entire training iterations, by minimizing the convergence rate of the wsd scheduler. First, the convergence rate is derived from minimizing the last loss with gradient descent and the wsd scheduler. The optimal base LR and optimal convergence rate are derived by solving a convex optimization problem of convergence rate minimization with respect to base LR. Further, an iteration-free rate is derived with respect to the fraction. The authors utilize several simulation results to demonstrate the relevance of the proposed optimal rate to base LR and the fraction. The results show that the optimal base LR decreases with training iterations but increases with the fraction's value. Then, the authors try to apply the observations of simulation results in ideal convex optimization to real-world LLM training. Two simple strategies, i.e., decrease base LR and increase fraction rate, are proposed. Simulation results demonstrate the effectiveness of the synthetic convex optimization problem. Experimental results on 0.1B and 0.2B Llama-style transformers show the improvement of the proposed method. Moreover, the authors propose to fit a convergence rate function from several running results with the wsd scheduler, where the function is defined from the inspiration of the theoretical optimal rate, to demonstrate the alignment of the proposed method to the real-world LLM training. ## update after rebuttal I keep my rating due to the following main concerns: This paper is within the scope of the study of scaling law. Thus, the only way to demonstrate its effectiveness is by experimental results on heterogeneous LLMs, especially for large LLMs. However, the selected LLMs are only 124/210M Llama-style transformers, and there are no additional experiments on large LLMs in rebuttal. Claims And Evidence: Yes. Methods And Evaluation Criteria: Not enough. First, training loss is not an important criterion for LLMs. Thus, the optimality of loss in training LLMs is not a convincing motivation for the so-called requirement of optimal learning rate. Second, the selected LLMs are too small. The selected LLMs are less than 1B, which is not sufficient to demonstrate the effectiveness of the proposed method for LLMs. Theoretical Claims: Yes. The proofs are correct. Experimental Designs Or Analyses: The experimental designs are not enough to demonstrate the so-called effectiveness of LLMs, since the selected LLMs are extremely small, less than 1B. Supplementary Material: Yes. I review all proofs and about 80% of the experiments in the supplementary material (others, like the evaluation of scaling laws, are not relevant to the main work of this paper). Relation To Broader Scientific Literature: This paper aims to improve an existing learning rate scheduling method from theoretical inspirations of ideal convex optimization. However, the gap between strict assumptions and real-world neural network training is not well-addressed. Essential References Not Discussed: No. Other Strengths And Weaknesses: Strength: 1. This paper conducts many simulations and experiments on two small LLMs. 2. This paper proposes a simulation-based learning rate (LR) scheduling method. By sampling real-world running results from different LR configurations, a function inspired by theoretical optimal LR is proposed to fit the real-world running results. Then, the optimizer to the function yields the "optimal" LR configuration. Weakness: The significance of this paper is limited. This paper tries to demonstrate that the empirical learning rate (LR) scheduling methods in training LLM align with its theoretical optimal solutions, which include three main components, i.e., theoretical proofs, LLM training, and alignment. This paper's soundness is poor in all three parts. 1. The theoretical proofs are based on a strict convex optimization scenario, which is far from the high dimensional non-convex optimization scenario in neural network (NN) training. The assumptions are too strict that the loss function is extremely smooth, in which the function's gradient can be bounded by constants (A3 in the paper). Thus, it may be the reason for the results in Fig 4, where a larger decay rate leads to under-training (large loss). 2. The selected LLMs are too small to demonstrate the effectiveness of the proposed method for LLMs. The simulation results are trivial under some specific loss functions and settings. First, most simulation results are based on extreme smooth loss ($G=1$) and a close initialization to optimum ($D=1$). Moreover, most observations (such as the specific settings of the decay fraction rate from Fig. 10, 11) are based on the 124M and 210M Llama-style transformers, which may not hold on large LLMs. 3. The alignment is problematic. The connection of the proposed theorem to neural network training is achieved by approximating a linear function of the hyper-parameters in the theorem, which is not convincing since there are no standard solutions for the function approximation for all NN models. Further, most simulations and experiments are designed to evaluate the proposed method for optimal base LR the wsd LR decay method. However, the most crucial part is whether such a theoretical upper bound of loss is close enough, which is not evaluated in the paper. For example, from Fig. 12 (b), most losses are above the approximated function, which violates the upper bound requirement of the function. Other Comments Or Suggestions: Typo: "The wsd schedule." paragraph, last sentence. Questions For Authors: 1. Does $\gamma$ in Eq. (9) represent $\gamma^{\star}$? 2. What is the $f$ in all simulation results? 3. What's the meaning of Fig. 8？ How to distinguish the training before $T_1$ and after $T_1$? The illustrated result looks like the overrides of the former training processes. 4. In Fig. 17, from the left part, the cosine scheduler converges faster than the wsd scheduler. However, the observation seems to be the opposite of the right part. Code Of Conduct: Affirmed. Overall Recommendation: 2	Rebuttal 1: Rebuttal: We thank the reviewer for the feedback and suggestions, and address each question below in detail. We hope that after clarifying all concerns we can improve the reviewer's rating of our submission. * First, training loss is not an important criterion for LLMs: For all LLM experiments in our paper, we already plot the validation set loss. We also comment on the relationship between train and test/validation loss in the last paragraph of the Limitation section. * the gap between strict assumptions and real-world neural network training is not well-addressed: The limitations of these assumptions are explicitly addressed in Section 6. As the title suggests, one of the insights of this paper is that theory and practice match very well, even though the assumptions from theory are not satisfied. * the loss function is extremely smooth: Can you explain what is meant with the term 'extremely smooth'? In fact, our theoretical results hold for non-smooth functions with bounded gradients (e.g. the absolute value function would satisfy this, but it’s not smooth). Thus we are confused by this comment. We also remark that we set $D=1$ and $G=1$ in the simulation purely for simplicity (see details further below). The bound holds for any other values. (In fact, for the LLM training setup, the gradient norms are below one except for the first ~hundred steps; we will provide a plot of the empirical gradient norms in the final version.) * is achieved by approximating a linear function of the hyper-parameters in the theorem: We did not not understand this comment. Could you explain which linearization is meant here? * Fig 4, where a larger decay rate leads to under-training (large loss): we are confused about this comment, as Fig 4 shows that larger decays lead to lower losses if the learning rate is tuned. Could the reviewer expand on this, so that we can hopefully answer the question? * The alignment is problematic: We kindly disagree: our theoretical findings are verified on multiple schedules+model sizes+time horizons, and we show that multiple aspects of the theory match the experiments (e.g. schedule adaptation for longer runs, effect of cooldown length, LR transfer across cooldown lengths etc.). * LLMs are less than 1B, which is not sufficient: Our experiments require a high number of individual runs, for example to sweep the learning rate (e.g. only Figure 12b requires around 20 runs). With our computational budget it would not be feasible to execute this amount of runs on a >10x larger scale. Besides that, scaling law research has repeatedly shown that loss improvements transfer to larger scales highly predictably in this regime (see https://arxiv.org/pdf/2203.15556). We also point out that for the central message of our paper (“convex bounds match empirical behaviour in deep learning”) any scale would be sufficient to prove the point. On Questions: 1) In Equation (9), $\gamma$ is arbitrary, and not necessarily equal to $\gamma^\star$. 2) The simulations simply evaluate the bound $\Omega_t$ for different schedules and learning rates. For this it is not necessary to specify $f$, but only constants $D$ and $G$ which we set to 1 in the simulations (purely for simplicity). The choice of $D$ and $G$ only affects the scale of the bound and learning rates, but not its shape or scaling in $T$. 3) As the caption of Fig 8 explains, T_1=400 and we test several values of T_2. Indeed the goal is to reuse the training up to iteration T_1, as it is explained in the beginning of Section 5.1 4) The right plot is only the iterate path, and one can not exactly read off the timescale of it. However, for (i) cosine at the step where its path makes a sharp left-wards turn and (ii) for WSD before cooldown are roughly similar and this matches the contours in the right plot. --- Rebuttal Comment 1.1: Comment: Clarification: 1. "extremely smooth" refers to the Lipschitz continuous setting, i.e., $D=1$ and $G=1$ is an over-simplified setting, which will be almost inconstant with NN training. 2. "linearization". As stated in the review comment, the main technique for the alignment between the ideal theorem and LLM training is approximating a linear function as a learning rate scheduler in Figure 12. Weakness: 1. "validation set". In the rebuttal, the authors still don't explain the motivation of approximation a learning rate from training loss but not validation loss. 2. "alignment". The performance of small LLMs is not enough to demonstrate the effectiveness of such approximation-based method. --- Reply to Comment 1.1.1: Comment: Dear reviewer, thank you for clarifying your questions. We respond to each point below. If any concern remains, we kindly ask the reviewer to elaborate why our responses are not satisfying. * As stated in the rebuttal, the choice of D and G in the simulations is purely for simplicity, and the bounds holds for any other values. Two further remarks: 1) For the theoretical predictions on optimal LR, we made sure that the choice of D and G has no impact on the result (see line 373 right column). We invite the reviewer to verify this by running the scripts with other values for D and G (scripts for all analyses are contained in our supplementary material). 2) In fact, the assumption that gradient norms are bounded by one is not unrealistic in LLM training: for example, see the gradient norm logs for the Olmo2-7B model, where the gradient norm is always below one except for the first few iterations: see https://wandb.ai/ai2-llm/OLMo-2-1124-7B, and then search for "optim/total_grad_norm" in the panel search box. * There is no linearization in Figure 12. You might refer to the fact that we fit a function to the loss values (as function of learning rate) on the right plot. This procedure is in detail described in the appendix (see line 792 ff.); however, the function we fit is not linear, and well-motivated from theory. * "Validation set": the theoretical bound is the expected loss, which in general describes the training loss. We argue in the last paragraph of Section 6 that in single-pass training this coincides with the test loss (see the reference Aitchison, 2024). To the best of our knowledge, there are no convergence bounds that directly estimate the test loss. Thus, we do not comprehend how we could improve our submission in this regard. * "LLMs too small" Please read our response in the rebuttal. It seems arbitrary to us to draw the line for significance at 1B, and is concerning if papers are rejected solely based on this argument. References: Aitchison, 2024: Why you don't overfit, and don't need Bayes if you only train for one epoch. https://arxiv.org/abs/2411.14478	Summary: This paper studies learning-rate schedules in large model training, by bridging a new theoretical convergence analysis to empirical observations. In particular, the first contribution (observation) is that for two popular schedules (cosine and wsd), the empirical loss curves of large model training, which is a non-convex optimization problem, has a similar shape with the theoretical bound predicted by the parameters in the convex case. The second contribution is a new theoretical convergence analysis of wsd in the convex case, which roughly shows an $\log T$ improvement over the best constant learning rate, providing an explanation to the success of wsd. The final contribution is an application of the theory, for continue training and learning rate transfer. ## update after rebuttal I have read other reviews and rebuttals. Though I agree with Reviewer rpAe that the results presented are not significant enough in either theoretical or empirical side, the new link does seem interesting and promising. I will keep my score. Claims And Evidence: Yes. Methods And Evaluation Criteria: Yes. Theoretical Claims: Yes. The only new theoretical result is Theorem 3.4. Experimental Designs Or Analyses: Yes. Supplementary Material: I mainly read part F of the appendix, which is the main proof (other proofs are standard in literature). Relation To Broader Scientific Literature: I think the results of the paper might be interesting to only only empirical ML researchers, but also optimization researchers. Essential References Not Discussed: As far as I know, no. Other Strengths And Weaknesses: The paper is well-written. The theoretical result might not be a deep one from a technical perspective. However, it's very important to provide a rigorous explanation for a popular learning rate scheduler. Other Comments Or Suggestions: NAN Questions For Authors: Is it possible to perform a rigorous convergence rate analysis for cosine? Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: We thank the reviewer for acknowledging the theoretical and empirical contributions of our paper. We are delighted that the reviewer considers the paper to be interesting to the optimization and ML community. Regarding the questions: * Convergence rate of cosine: unfortunately, due to the form of the cosine schedule it is quite difficult to explicitly derive the bound. We tried several simplifications and have not reached a nice result yet. However, from the simulations we conduct, the bound of cosine is almost the same as the one for linear-decay, for which we can explicitly derive the bound (see lines 1240 ff.).	Summary: This paper establishes a novel connection between empirical learning-rate schedules (e.g., cosine, WSD) used in LLM training and theoretical bounds on the loss at the final iterate of SGD in a non-smooth stochastic convex setting. Through empirical studies on Llama-style transformers, the paper demonstrates that the theoretical bound effectively predicts the actual loss curve based on the learning rate schedule. Building on this observation, the authors show how insights from these theoretical bounds can guide learning-rate tuning for continued training and enable learning-rate transfer across different schedules in practice. ## update after rebuttal After carefully considering the authors’ responses in their rebuttal, my assessment remains unchanged, and I continue to recommend acceptance. The authors have adequately addressed my initial concerns, and the clarification provided further strengthens the contributions of the paper. Claims And Evidence: The main claim of the paper is that the theoretical performance bound on the final iterate of SGD in non-smooth stochastic convex optimization aligns well with the loss curve in LLM training. This claim is strongly supported by a series of experiments on language model training, as well as theoretical simulations. Methods And Evaluation Criteria: The proposed application of the theoretical bound—schedule construction for continued training and learning-rate transfer across schedules—seems convincing and could be a valuable tool in practice. Theoretical Claims: The main theoretical framework is adopted from the existing work by Defazio et al. (2023). Building on these theoretical results, this paper derives the theoretical bound for different learning rate scheduling scenarios. These theoretical results appear to be correct. Experimental Designs Or Analyses: Overall, the experiments are well-designed, and the results look convincing. Supplementary Material: I read the appendix as well as the supplementary material that includes the code that can reproduce the experiments. Relation To Broader Scientific Literature: N/A Essential References Not Discussed: The paper discusses all the essential references related to the main contribution. Other Strengths And Weaknesses: Overall, this paper is well-written and makes a solid contribution by connecting non-smooth convex theory with language model training. This bridges a critical gap between optimization theory and deep learning practice, which I find to be very interesting. The main strength lies in demonstrating that the theoretical performance bound has strong predictive power in practice. There are a few minor weaknesses. First, while the non-smooth convex theory is derived from SGD, all the experiments in this paper use AdamW. This limitation is well acknowledged in the paper. The paper would be even stronger if it included experiments using SGD and compared the loss curves with the theoretical bound. Other Comments Or Suggestions: Here are some additional experiments I would suggest: 1. Experiments using SGD on vision tasks could provide insights into the broader applicability of the theoretical bound. 2. Testing a more diverse range of learning rate schedules beyond the popular cosine and WSD, and comparing them with the theoretical bound, would be interesting. For example, in Tissue et al. (2024), the authors tested various learning rate schemes—see Figures 3 and 4. However, the current paper remains valuable even without these additional experiments. Tissue et al. (2024) - Scaling Law with Learning Rate https://arxiv.org/abs/2408.11029 Questions For Authors: 1. Does the alignment between non-smooth convex optimization theory and learning rate scheduling apply only to “large” model training? 2. Does the alignment hold only for AdamW, or can similar observations be made for other modern optimizers (e.g., Shampoo, Schedule-Free, Muon, MARS, etc.)? Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: We thank the reviewer for their positive feedback, especially for the assessment that our experimental results are strongly supporting the claims/contributions. * We ran additional experiments with SGD on Imagenet as suggested by the reviewer (see details here: https://anonymous.4open.science/r/icml25-additional-experiments-lr-schedules/). The results confirm the close match between the bound and actual loss curves. * Regarding additional schedules, we would like to point to Fig 18 and 23 where we compare many different schedules beyond cosine and WSD, including constant and 1/sqrt schedule as well as the 1-sqrt schedule proposed in Hägele et al 2024. We also test a piecewise constant schedule with cooldown for the continual learning experiment. * Regarding other optimizers, we have not done a systematic comparison. However, from results reported in the literature, it is known that the sudden drop of the loss also appears for other optimizers, for example Muon, Shampoo and SOAP (see https://github.com/KellerJordan/modded-nanogpt/tree/master/records/102924_Optimizers) or Ademamix (see Fig 3b in https://arxiv.org/pdf/2409.03137). This makes us confident that the characteristic schedule behaviours that we describe also generalize to other optimizers; investigating this in detail would be an interesting direction for followup work. --- Rebuttal Comment 1.1: Comment: Thank you for the detailed response and for conducting the additional experiments. I have a follow-up question regarding the SGD results on ImageNet. In Figure 25, the theoretical bound does not appear to align closely with the validation loss curve, which is understandable given the multi-pass setting. However, in Figure 26, the training loss curve also seems to deviate from the theoretical bound. For example, the predicted loss at the final iterate based on the theoretical bound does not match the actual training loss in terms of the relative ordering across different schedulers. Could the authors clarify this discrepancy? --- Reply to Comment 1.1.1: Comment: Dear reviewer, thank you for your comments. For the theoretical plot (Fig 25a), we had used the same three base LRs for cosine and wsd, whereas the empirical plots shows a range of base LRs which are doubled for cosine (in line with our findings that cosine needs roughly a twice as large LR). The updated theoretical plot (same link as before) now matches the empirical plot also in terms of relative ordering - thanks for catching this! Another minor factor is the range of LRs, which we slightly reduced (the sensitivity to base LR depends on problem constants, which are unknown and can be different for datasets, models etc). Two additional remarks on the theory-practice alignment for Imagenet: 1) in our experience the randomness on Imagenet is slightly larger (might be due to data augmentation), and we had only ran one seed due to the limited rebuttal time. Some differences might be only due to this noise. 2) We noticed that for Imagenet the gradient norms are slowly increasing over training, in contrast to the LLM training, where the gradient norm is almost constant (see e.g. also Fig 3 in https://arxiv.org/pdf/2310.07831). We think that the impact of gradient norms on the performance of schedules is an interesting direction for follow-up work.	Summary: This work demonstrates that several empirical observations align with the last-iterate sub-optimality gap in convex optimization. Furthermore, the authors show that adjusting the learning rate in continual learning—an approach that theoretically improves this sub-optimality gap—also enhances real-world training performance. Lastly, the study establishes a convergence guarantee for the WSD schedule. ## update after rebuttal Thank you for your detailed response. In light of the additional experiments, I will raise my score. Claims And Evidence: The claims linking the theoretical bounds to practical performance are supported by the experiments in the paper. However, the experiments are limited to a single synthetic problem and one real dataset. Consequently, the assertion that the theoretical bounds accurately reflect real-world behavior—allowing for extrapolation from the sub-optimality gap—is not strongly justified. Methods And Evaluation Criteria: The methods and evaluation criteria are well-founded. However, experiments on additional datasets would further strengthen the analysis. Theoretical Claims: Given the last-iterate guarantee from previous work, which accommodates general step-size sequences, the convergence result is reasonable and unsurprising. It is well established that a linearly decaying step-size sequence leads to last-iterate convergence guarantees. Therefore, when the cooldown period is of the same order as the training duration, the observed behavior aligns with the theoretical expectations. Experimental Designs Or Analyses: In general, the experimental design and analysis appear valid. The behavior of WSD across the experiments aligns with findings from previous work. Supplementary Material: The reviewer briefly examined the supplementary material to understand the proof technique and the datasets used in the experiments. For the mirror descent result, please refer to the "Essential References Not Discussed" section. Relation To Broader Scientific Literature: Understanding the relationship between theory and practice is an important topic for the machine learning community. Essential References Not Discussed: The work of Liu and Zhou establishes a last-iterate convergence guarantee that applies to both convex Lipschitz and convex smooth problems, including mirror descent. These results can also be leveraged to obtain guarantees in the convex smooth case. Notably, (A) these guarantees rely on Lipschitz/variance bounds rather than the $G_t$ assumption used in this paper, and (B) the constants in this work may be slightly worse. Z. Liu and Z. Zhou. Revisiting the last-iterate convergence of stochastic gradient methods. In The Twelfth International Conference on Learning Representations, 2024. Other Strengths And Weaknesses: Strengths - The work presents multiple observations that align well between theory and experiments. Weaknesses - The theoretical results are relatively straightforward. While the reviewer is not aware of prior results specifically for the WSD schedule, deriving such guarantees using existing general last-iterate convergence results does not require significant innovation. - Additional experiments would substantially strengthen this work. Other Comments Or Suggestions: No additional comments. Questions For Authors: - Given the last-iterate guarantee for convex smooth objectives established by Liu and Zhou (referenced above), should there be any notable differences in the predictions and alignment of this work, which assumes convex Lipschitz objectives? This question assumes that the number of steps is sufficiently large for the $1/T$ smooth term to be negligible. - Can the authors provide justifications for Assumption A3 beyond a general Lipschitz assumption? While the reviewer is familiar with optimization theory, they are not aware of other instances where this assumption has been used, especially since it depends on the algorithm, as the authors mentioned. Overall, while this work presents interesting observations, its limited empirical evaluation and lack of significant theoretical novelty make it a borderline case for acceptance. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We thank the reviewer for their thoughtful review and detailed feedback. We address all questions in detail below. We hope that this will clarify all concerns, and allows for a higher scoring of our submission. * limited empirical evaluation, one real dataset: We agree that it is beneficial to validate our findings on additional datasets, and for the rebuttal we performed additional experiments on Imagenet and OpenWebText; the results confirm our previous findings (see detail here https://anonymous.4open.science/r/icml25-additional-experiments-lr-schedules/). However, even though we had only considered one dataset, our empirical evaluation is not limited: we verify our findings on multiple schedules+model sizes+time horizons, and find that multiple aspects of the theory match the experiments (e.g. schedule adaptation for longer runs, effect of cooldown length, LR transfer across cooldown lengths etc.). Besides the dataset choice (which we address in the rebuttal), are there any other reasons why the reviewer considers our empirical evaluation to be limited? * Related to the above, the characteristic behaviour of WSD during cooldown has been reported in multiple papers (which all train in slightly different settings and on different datasets). For example (see also references in our paper): https://arxiv.org/pdf/2410.05192, https://arxiv.org/abs/2502.15938. These independent experiments further justify that the bound indeed reflects real-world behaviour, and our paper is the first one to highlight and exploit this connection between theory and practice. * lack of significant theoretical novelty: One interesting theoretical insight is that the cooldown of WSD achieves to remove a log-factor in the convergence bound (compared to the constant schedule). Moreover, this improvement is obtained exactly by the drop during cooldown, as Figure 20 (left) shows. More broadly, the main goal of our paper is not to develop new proof techniques, but to show how existing theory can be used in order to (i) design/tune the learning rate (schedule) and (ii) explain the benefit of cooldown observed in practice (and the behaviour of LR-schedules in general). * Correct, Assumption A3 is implied when assuming Lipschitzness of the objective. However, as the bound only depends on the expected gradient norms on the SGD trajectory (and the proof does not explicitly use the Lipschitz condition), we wanted to formulate the assumption as tight as possible - bounded gradient norms over a finite number of steps could be satisfied with much weaker assumptions than Lipschitz continuity. * We thank the reviewer for pointing out the work by Liu and Zhou; we were not aware of this paper and will discuss it in the related work section. From our understanding the main differences are: - the results by Liu and Zhou do not hold for arbitrary schedules - In the Lipschitz-smooth case (M=0 in Liu and Zhou), instead of the Lipschitz constant, we have the noise constant in the bound, and additionally the step size needs to be smaller than $\mathcal{O}(1/2L)$. However, as we can decompose the bound $G_t$ in our notation in a noise part plus the Lipschitz constant of the objective $f$, this appears to result in a very similar structure. Extending our analysis to the smooth case is definitely interesting and we are actually working actively in this direction. --- Rebuttal Comment 1.1: Comment: Thank you for your detailed response. In light of the additional experiments, I will raise my score. For the benefits of the authors, I will also mention that Liu and Zhou in fact do prove convergence guarantees for arbitrary schedules, see in Lemma 4.2, in case the authors would like to extend their results to the smooth case. (I do not ask for this addition, only mentioning it for the benefits of the authors.) --- Reply to Comment 1.1.1: Comment: We thank the reviewer again for their efforts to review at ICML, and are delighted that our response and new experiments lead to a higher score.	null	null	null	null	null	null
DragLoRA: Online Optimization of LoRA Adapters for Drag-based Image Editing in Diffusion Model	Accept (poster)	Summary: The paper proposes a new method, named DragLoRA, for drag-based image editing using a pre-trained Stable Diffusion model. Specifically, the paper proposes two novel steps: DragLoRA online optimization (DOO) and Input Latent Feature Adaptation (ILFA). In DOO, instead of optimizing the latent representation like the classic DragDiffusion, it optimizes the LoRA with feature drag loss and the DDS loss. In IFLA, the latent representation passes through DragLoRA and is renoised to adapt the latent representation to dragging. Meanwhile, the paper also discovered that IFLA itself could occasionally achieve point moving, even without DOO steps. Therefore, the paper proposes an adaptive switching scheme (ASS) based on point tracking: if IFLA itself can achieve reliable point moving, DOO can be skipped for this step until the result of point tracking reveals that IFLA cannot provide a good move, DOO is resumed to supervise point moving using optimization. DragLoRA is evaluated on the DragBench benchmark against previous methods and shows superior performance in the MD metric with comparable computational time. ## Update after rebuttal I appreciate the author's response, and it solved most of my concerns. Therefore, I keep my original rating. Claims And Evidence: Based on the results of experiments, DragLoRA improves the baseline on MD and m-MD metrics in the DragBench benchmark (Table 1). The effectiveness of each proposed components: DOO, ILFA, ASS and EPT are demonstrated by the ablation study in Table 3 and Figure 10 in the supplementary material. Therefore, the effectiveness of DragLoRA could not be denied. However, some points require further clarification to understand how they work, and I lay out my questions regarding this part in Methods And Evaluation Criteria section. Experiments are thorough in general, and they do substantiate the claims. However, I have some concerns and questions regarding the experiments, and I elaborate on these in Experimental Designs Or Analysis section. Methods And Evaluation Criteria: Although the effectiveness of the proposed method is empirically demonstrated, further clarification is required on some points: 1. The paper employs the DDS loss to reduce the performance degradation caused by LoRA optimization. The original DSS loss aims to have a cleaner gradient than the SDS loss in editing direction by deducting bias from the editing SDS loss. Mathematically, it is $\nabla_{\theta} L_{DSS} = \nabla_{\theta} L_{SDS}(\hat{z}, c_{edit}) - \nabla_{\theta} L_{SDS}(z, c_{ori})$. The bias is $\nabla_{\theta} L_{SDS}(z, c_{ori})$ and the intuition is that if the latent of the original image $z$ already aligns with the text $c_{ori}$, the derivative should be zero and any remaining value is bias. If we apply the analogy to this case, shouldn't the DSS loss be $(\epsilon^{drag} - \epsilon^{ori})\frac{\partial \hat{z_{0}}}{\partial \Delta \theta}$ rather than $(\epsilon^{ori} - \epsilon^{drag})\frac{\partial \hat{z_{0}}}{\partial \Delta \theta} $ as shown in equation 8? 2. The adaptive optimization scheme noticed that after DOO, LoTA can move the handle point toward the targets without DOO. There lacks a intuition behind this phenomenon. Finetuning LoRA for one moving step is very likely to cause LoRA to overfit to that specific step, so it is quite counter-intuitive in this point. Theoretical Claims: This paper is an application paper with no significant theoretical contribution. Experimental Designs Or Analyses: 1. In Table 1, it is shown that DragLoRA achieves better results than its baseline DragDiffusion with a comparable inference time. Given the fact that DragLoRA has a more complicated pipeline and a larger number of parameters to optimize, I guess that the reason for DragLoRA to catch up DragDiffusion in inference time is ASS, which allows DragLoRA to skip several optimization steps. Therefore, it would be best to show how much time and how many optimization steps can be saved by adopting ASS. 2. The curves that compare DragLoRA and DragDiffusion in Figure 1 and Figure 8 are good. It shows the variation of the quality of the handle point during the optimization process. However, the plot is misleading in terms of drag steps. The plot shows that the DragLoRA finishes editing with fewer drag steps than DragDiffusion, implying DragLoRA is faster and more efficient than DragDiffusion. This is not true according to the results in Table 1, which shows that DragLoRA and DragDiffusion have similar inference times. According to Algorithm 1, DragLoRA only increment drag step count $i$ when DOO is triggered. All steps in the while loop are ignored, which makes DragLoRA appear to be much more efficient. A more appropriate curve would be that the drag step still counts ILFA in the while loop but uses a different color for this section, indicating that these steps are faster than the optimization step. This can also reflect how many optimization steps are skipped. 3. Figure 7 in the supplementary material plots MinD vs drag steps for all methods. It would be better if $d(h_{i}^{k}, t_{i})$ vs drag steps can also be plotted in a similar way as it will reflect how fast each method completes the dragging. 4. Although mean distance is widely used to evaluate the dragging result, it cannot always reflect the true quality of the editing. A more appropriate metric is the human evaluation, which is widely adopted in text-to-image and text-to-video generation methods. However, it is inappropriate to ask for a human evaluation during the author-reviewer discussion period, and I simply want to share my opinion on it. Supplementary Material: I have read all the supplementary material. Relation To Broader Scientific Literature: The paper addresses the drag-based image editing problem using diffusion models. It is built on top of DragDiffusion, which is one of the pioneering works in this direction. The general pipeline of this work is similar to that of DragDiffusion, and it proposes its own innovation to improve the baseline. Essential References Not Discussed: All relevant works have been included in the literature review. Other Strengths And Weaknesses: All strengths and weaknesses are laid out in the previous sections. Other Comments Or Suggestions: There are several minor issues: 1. In the right column of Ln200, "we adopt the initla latent input $z_{35}^{0}$" should be "we adopt the initla latent input $z_{35}^{0} = z_{35}$" 2. In Section 4.1 Implementation Details, $\lambda_{Mask}$ and $\lambda_{DSS}$ are not defined in the previous section. Questions For Authors: I would appreciate it if the authors could address my concerns regarding the Method and Experiment sections. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Thank you very much for your insightful and constructive feedback. We appreciate the depth of your analysis and the valuable suggestions you provided. Below, we address your concerns point by point: ### 1. Difference from the Original DDS Loss. In the original DDS paper, $\nabla_{\theta} L_{\text{DDS}}=(\epsilon^{edit}-\epsilon^{ori})\frac{\partial{z_0}}{\partial {\theta}}$ is applied to guide the image towards the semantic editing direction, which points from the original text to the target text. In our work, however, we employ $L_\text{drag}$ for the editing operation and use $\nabla_{\Delta\theta} L_{\text{DDS}}=(\epsilon^{ori}-\epsilon^{drag})\frac{\partial{\hat{z_0}}}{\partial {\Delta\theta}}$ as a regularization term. This regularization constrains the edited model to remain close to the original model’s generative capability, thereby preventing excessive updates. In essence, our application of the DDS loss is intentionally reversed relative to the original purpose. That's why we apply grad $\epsilon^\text{ori} - \epsilon^\text{edit}$ to $\hat{z}_0$. ### 2. Intuition Behind ILFA Without DOO. We observe that after sufficient DOO (Dual-objective LoRA optimization), ILFA (Input Latent Feature Adaptation) can solely move the handle point. In this setting, accumulated DOO gradients from previous optimizations, can be utilized for moving handle points at the new positions without extra driving force. In each gradient step, although the specific tasks are not exactly the same, they share a low-variance handle feature and a common direction. DragLoRA can learn these commonalities and generalize, which is comparable with meta-learning. Note that ILFA-only is not stable enough, so we introduce adaptive switching scheme (ASS). Here we explain this process and intuition behind this: * Initialization and Thresholding: We initialize DragLoRA from a reconstruction LoRA and activate the no-training mode only after LoRA has been optimized for a certain number of steps. This ensures that the LoRA module learns a robust directional signal over multiple iterations, rather than merely shifting from one fixed point to another. * Optimization Confidence Assessment: We employ minD and coordinate distance of points to evaluate the confidence of previous-step LoRA optimization. When LoRA's guidance is deemed reliable with an effective movement and a smaller value of minD, ILFA can incrementally adjust the nearby handle points in a small, controlled manner, thereby effectively advancing in the intended direction. * Fallback Mechanism: In cases where LoRA is compromised due to overfitting, ILFA can hardly advance the handle points that LoRA is unfamiliar with or produce large minD. Our ASS strategy can detect these unreliable cases and switch back to DOO with a new supervisory signal. In summary, IFLA-only can be potentially used with detection metric as the safty guard. ### 3. Time Efficiency via Adaptive Switching. You correctly noted that our ASS allows us to bypass several DOO steps by relying on the training-free ILFA mechanism. This substantially reduces the number of optimization steps and, as a result, saves significant time. Specifically, the time consumed by one DOO step is around 0.26s while one ILFA step costs around 0.05s, and we apply 54 DOO steps and 87 ILFA steps per image on DragBench. ### 4. Visualization of the Optimization Process. We appreciate your suggestion to enhance the visualization of our optimization process. In response, we have supplemented our manuscript with two additional figures that more clearly illustrate the progression of the drag editing process. The first image, which separates the ILFA-only steps (displayed in a different color) from the DOO+ILFA steps, clearly indicates how many optimization steps are skipped. And the second image, which calculates the average normalized Euclidean distance $d(h_i^k,t_i)$ on DragBench, indicates how fast the handle points move. You can view these visualizations at the following link: https://imgur.com/a/PVuceIo. ### 5. Incorporating Human Evaluation. We agree that human evaluation is crucial for fully assessing the quality of editing results. While our current work primarily relies on quantitative metrics, a comprehensive user study would provide further insights. We plan to conduct such evaluations and release the results in our Github. ### 6. Symbol Corrections and Minor Issues. We have noted the suggested corrections and will address them in the revised version of our manuscript. Thank you once again for your detailed and thoughtful comments. We eagerly await your feedback on our rebuttal. --- Rebuttal Comment 1.1: Comment: Thank you for your detailed response. It addresses all my concerns. I am particularly grateful that the author illustrates the trend of DOO and ILFA along the editing. I have no more questions. --- Reply to Comment 1.1.1: Comment: Thank you once again for your insightful questions and valuable suggestions. We deeply appreciate your expertise, which has been instrumental in helping us improve our submission.	Summary: The authors presented the DragLoRA method for efficient and more accurate drag-editing, which is specified by a mask of the area to be edited and pairs of points specifying the direction of shift editing. The method is based on the use of LoRA adaptors for simultaneous gradual shifting towards target points, but at the same time keeping the model prediction with adaptors close to the original model ones. For this purpose, the authors use dual-objective LoRA optimization (DOO), combining feature shift loss and DDS loss. In addition, the authors propose an adaptive switching scheme (ASS), the idea of which is to choose a strategy with or without updating the adapter weights depending on how far the handle point is from the target point. The authors also propose Input Latent Feature Adaptation (ILFA) mechanism, which is to renoise the latent once by 1 step and then noise with Gaussian noise. The authors do this adaptation at each step of the algorithm regardless of whether there is an optimization step, and the goal is to ensure coherent updates on LoRA parameters across iterations. Finally, the authors use Efficient Point Tracking (EPT) to efficiently select the next handle points, reducing the complete enumeration. The proposed method requires fewer optimization steps compared to existing methods and preserves the details of the original image better. Claims And Evidence: The authors provide an extensive comparison with existing methods, both quantitative and qualitative. However, there are questions about the visual quality of the method. In Figure 4, the first and third rows show results that are better than the baselines, but the proposed method outputs a rather unrealistic image. The girl in the first row has unrealistic facial features and the camera has lost its shape. Given that these images are highlighted as the best, there are questions about the real quality of the method and how applicable it is in practice. Methods And Evaluation Criteria: The proposed method solves the drag-editing problem, which has been widely spread recently, as it could simplify the image editing process for real users. The problem has been studied many times and methods that solve it have been proposed, and there are also benchmarks such as DragBench in order to compare the methods proposed in the community. The authors use just this benchmark for comparison. The metrics that the authors use are common and standard for this task. Theoretical Claims: For the most part, there is no theoretical evidence in the article. However, the supplementary contains the derivation of formula 9 for latent updating using the Input Latent Feature Adaptation (ILFA) mechanism. I see no inaccuracies in this conclusion. Experimental Designs Or Analyses: For the experimental part of the work, the authors chose to compare the proposed method with baselines on the DragBench dataset. The metrics chosen for quantitative comparison are 1-LPIPS, Mean Distance (MD) and masked Mean Distance. Also, a comparison in terms of the running time and the number of parameters is added in Table 1. From the comparison, it is observed that in terms of MD and m-MD metrics, the proposed method is indeed on top. However, I think it is not very fair to compare by runtime. The authors write in Section 4.3 that for DragLoRA, only the time required for finetuning for editing was included in the comparison table, and the time for initializing this finetuning (actually finetuning on reconstruction) was not included. In this regard, there is a question, for the DragDiffision method the corresponding time was also excluded in the comparison? What is the order of the time required for this step in general? Is it possible to neglect it in the comparison on the basis of the fact that it can be done offline, although the user still has to wait for this time to upload his image? The authors also offer an interesting analysis on the Drag-Back Pipeline. The image is first edited with a set of point pairs and then edited again in the reverse direction of point shifts. This should ideally result in a reconstruction of the original image. The authors compare a subset of methods on this task and show in Table 2 that in terms of LPIPS and CLIP metrics, which are responsible for image preservation, the proposed method performs almost the best, which is supported by the visual comparison in Figure 5. Finally, the authors conducted an ablation study (Table 3) in which the authors show the need for each of the four components of the method, which was supported by the visual comparison in Figure. 10. Supplementary Material: I have familiarized myself with all parts of the Supplementary Material. It includes an additional comparison of the method and baselines based on the minD metric. This metric was used by the authors to select the next intermediate handle point in the editing process, so it is not surprising that the proposed method beats the baselines on this metric. The ILFA component of the method was also further analyzed. The impact of adding this part is clearly shown, which is a more consistent image. A comparison of different Efficient Point Tracking tactics on metrics and runtime is also presented. Finally a visual comparison for the ablation study component of the method. Relation To Broader Scientific Literature: The idea of optimizing weights by gradually shifting points in a given direction is not new and has been proposed as early as DragGan and DragDiffusion. However, the authors proposed a number of modifications that improved the quality of the Pipeline. As mentioned earlier, the proposed method consists of 4 main components. 1. Dual-objective LoRA optimization (DOO) 2. Input Latent Feature Adaptation (ILFA) 3. Adaptive switching scheme (ASS) 4. Efficient Point Tracking (EPT) DOO uses delta denoising score, which has been proposed earlier but not used as a component of loRA for optimization in drag-editing. The combination of the two losses is rather a new approach for this task. ILFA has also not been presented in the literature before, but there was an attempt to use a close idea in GoodDrag. ASS is an entirely new idea, although it stands out for its simplicity. Finally, EPT has already been proposed in papers such as CLIPDrag and FreeDrag and is not novel. Overall the combination of these ideas has shown to be quite good, there are both completely new ideas as well as utilizing existing ones as separate components. The main novelty is in the combination of these parts with each other, which gave a fairly high quality output. Essential References Not Discussed: GDrag [1] is one of the latest published methods that shows high metrics on a drag-editing task. The SDE-Drag [2] article showed that using SDE instead of ODE improves the quality of various types of editing, including drag-editing. [1] GDrag:Towards General-Purpose Interactive Editing with Anti-ambiguity Point Diffusion, Xiaojian Lin, Hanhui Li, Yuhao Cheng, Yiqiang Yan, Xiaodan Liang [2] The Blessing of Randomness: SDE Beats ODE in General Diffusion-based Image Editing, Shen Nie, Hanzhong Allan Guo, Cheng Lu, Yuhao Zhou, Chenyu Zheng, Chongxuan Li Other Strengths And Weaknesses: Strengths: A clear and reasonable idea of the method. Weaknesses: The method is based on the outdated sd-1.5 model, the quality of which is initially inferior to such models as SD3, Flux. Other Comments Or Suggestions: Typos: 127: InstanceDrag → InstantDrag 305: DragDiffuaion → DragDiffusion 660: Aadption → Adaption Questions For Authors: 1. My main question is, as I wrote earlier about measuring the runtime of the method. For the DragDiffision method the corresponding time was also excluded in the comparison? What is the order of the time required for this step in general? Is it possible to neglect it in the comparison on the basis of the fact that it can be done offline, although the user still has to wait for this time to upload his image? 2. How were the constants used in the pseudocode selected? What is their intuition? How did they get out? Is there an analysis of them? 3. How do you assess the applicability of the proposed method, taking into account such significant distortions in the visual comparison in Figure 4, as I wrote earlier? Will the user be satisfied with such unrealistic output images? Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Thank you for your thorough review and constructive feedback. Below are our point-by-point responses: ### 1. Runtime Comparison Fairness. Our reported time excludes the offline LoRA finetuning time for reconstruction (~48s per image over 80 steps on NVIDIA 4090 GPU), which applies to all methods with reconstruction steps $>0$. We agree that this is long and it can't be ignored. However, the trained LoRA can be stored and reused for multiple drag editings by various annotations of points. They can also be applied in other customized editing. Here, the exclusion of offline training emphasizes the comparison of time cost on dragging. We will describe this cost in the revised paper. ### 2. Clarification on minD. We propose minD, which measures the distance between feature of the tracked new handle points and initial handle point, to serve as a training-time indicator of the stability of the LoRA optimization. However, lower minD does not definitly result in good drag quality. Metrics such as MD and m-MD are more reliable for evaluating the final results. Therefore, minD curves are used only for reference. Specifically, minD is applied in Adaptive Switching Scheme (ASS) and Efficient Point Tracking (EPT). In ASS, minD and coordinate distance assess whether LoRA or input latent feature updates are confident. If updates are confident, the system enters IFLA-only mode; otherwise, $L_{drag}$ continues driving in next step. In EPT, minD checks if tracked handle points accurately reflect the previous updates. If minD is low, the system moves to the next step; otherwise, it stays with additional motion supervision. MinD does not decrease in ASS, and is only lowered down in EPT. When the ASS and EPT strategies are ablated (DragLoRA-wo/minD, dark purple), as shown in https://imgur.com/a/UYhzqfD, the observed minD is even lower than DragLoRA. So we mainly use minD to gauge the online optimization, but do not reduce its value in purpose. The lower minD in DragLoRA mainly comes from the LoRA structure and DOO. ### 3. Incorporation of GDrag and SDE-Drag. Thank you for the advices on adding essential references. SDE-Drag presents a unified probabilistic formulation for diffusion-based image editing, including drag, while GDrag categorizes point-based manipulations into three atomic tasks with their dense trajectory, and jointly optimizes point-wise adaptation scales and latent feature biases at a sampled timestep, achieving less ambiguous outputs. We adopt the metric values reported by GDrag and evaluate SDE-Drag on DragBench introduced by DragDiffusion. As shown below, DragLoRA achieves better editing accuracy than the others while GDrag achieves better image consistency. \| Methods \| 1-LPIPS↑ \| MD↓ \| m-MD↓ \| Time(s)↓ \| Params(M) \| RecSteps \| DragSteps \| Category \| \|----------------\|----------\|--------\|--------\|----------\|-----------\|----------\|-----------\|----------\| \| SDE-Drag \| 0.91 \| 44.48 \| 41.53 \| 62.74\| 0 \| 100 \| 0 \| TrFree \| \| GDrag \| 0.91 \| 26.49 \| / \| / \| 0.08 \| 80 \| 250 \| Optim \| \| DragLoRA \| 0.87 \| 23.77\| 22.70 \| 29.84 \| 3.19 \| 80 \| 80 \| Optim \| ### 4. Generative model Limitation. Since all methods are based on Stable Diffusion 1.5, we also implement our method on this model for fairness. While Flux/SD3 have higher generative capacity, indicating the potential to boost editing performance, they require more cost on both time and computation sources. We will explore this potential in the future and release code for easy model swapping among SDXL and Stable Diffusion 2.1. ### 5. Parameter Selection in Pseudocode. Since focusing on practical strategy, we do have some threshold params in Alg. 1 determined via empirical analysis: $k_{ini}=10,th_{low}=1,th_{high}=1.3,d_m=1.4$. As shown in Fig.7, after $k_{ini}$ steps, minD plateaus, indicating that LoRA optimization tends to be stable. According to the observation on DragLoRA wo/ ASS, minD $>th_{high}$, usually correlates with unrealistic edits. Besides, we set $minD<th_{low}$ and $\|\|h-n\|\|_2<d_m$ to indicate high confidence to balance the efficiency and stability. However, these two values are still not fully tuned. ### 6. Current Limitations of Drag-Editing Methods. We acknowledge that a limitation common to current drag-editing methods, including our own, is that in some challenging cases the output may still appear unnatural or low edit-accuracy. In the case of "moving the camera away to supplement the girl's facial details," the editing results can be suboptimal. We believe that incorporating reference face ID additionally could help meet user expectations better. ### 7. Symbol Corrections and Minor Issues. We have noted the suggested corrections and will address them in the revised version. Thank you again for your valuable comments. We eagerly await your feedback on our rebuttal. --- Rebuttal Comment 1.1: Comment: Thanks for the comments provided. There is more clarity, especially on the runtime evaluation. --- Reply to Comment 1.1.1: Comment: Thank you once again for your valuable feedback and the time you dedicated to reviewing our work. We greatly appreciate your constructive comments.	Summary: This paper introduces the DragLoRA framework to enhance point tracking in drag-based image editing, thereby improving editing precision. It proposes a DDS loss combined with drag loss, along with a cyclic denoise-renoise process to maintain semantic fidelity with the source image. Additionally, an adaptive optimization scheme is employed to minimize further LoRA adjustments, improving overall efficiency. Claims And Evidence: All claims are supported by clear evidence. Methods And Evaluation Criteria: The method and evaluation criteria make sense for the problem. Theoretical Claims: No theoretical claims. Experimental Designs Or Analyses: In the experiments section, the paper selects DragDiffusion, DragNoise, and GoodDrag as the main comparison methods. For DragDiffusion and DragNoise, the same dataset and metrics are used, whereas GoodDrag includes an additional dataset and new metrics. However, these are missing from the quantitative comparison. Supplementary Material: I've read the supplementary material. Relation To Broader Scientific Literature: N/A Essential References Not Discussed: Essential references are all discussed. Other Strengths And Weaknesses: Strength: 1. The DragLoRA framework enhances the point tracking stage, which is crucial for achieving high image quality and precise drag-editing results. 2. Various point tracking schemes for drag editing are discussed, and the proposed search strategy is more advanced compared to the vanilla method 3. In quantitative comparisons, the proposed method is evaluated against many approaches, demonstrating both high image fidelity and time efficiency. Weakness: 1. The paper mentions other selected images, more details are needed for this new dataset. 2. For m-MD, further clarification is required on how it is computed and why it is an improvement over MD. 3. Based on Table 2, which presents the quantitative comparison on DragBench, the paper claims to achieve state-of-the-art editing quality. However, for 1-LPIPS, STABLEDRAG and EASYDRAG outperform the proposed method, while for m-MD, GoodDrag performs better. In Lines 366–367 of the Evaluation Metrics section, the paper states that m-MD reduces uncertainty errors compared to MD. If m-MD is indeed superior to MD, then the proposed method does not achieve state-of-the-art performance in any metric presented in Table 2. Other Comments Or Suggestions: 1. In Figures 2 and 3, some characters appear as "?". 2. The paper lacks discussion about its limitations. Questions For Authors: No additional questions. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Thank you for your thoughtful feedback. We address your concerns below: ### 1. Test data details. We mainly conduct our experiments on DragBench and Drag100, which are proposed by DragDiffusion and GoodDrag. The qualitative comparisons in Fig.4. and Fig.6 are mainly based on these two test sets. The qualitative comparisons on DragBench has been presented in Tab.1 while results on Drag100 are given below: \| Methods \| MD↓ \| m-MD↓ \| 1-LPIPS↑ \| Time(s)↓ \| \|---------------\|----------\|----------\|----------\|----------\| \| GoodDrag \| 26.72 \| 25.26 \| 0.86 \| 72.06 \| \| DragLoRA \| 26.31 \| 25.20 \| 0.87\|37.93 \| \| DragLoRA-Fast \| 29.18 \| 27.78 \| 0.87 \| 24.32\| Compared to GoodDrag, DragLoRA achieves better MD and m-MD on Drag100, and also reduces editing time by 47.4%, while DragLoRA-Fast reduces editing time by 66.2%. To enrich the test scenarios, we select a few images from VITON-HD$^{[1]}$ dataset and our private collections, and manually annotate them with handle-target points and masks. Qualitative comparisons on these constructed pairs are presented in row 5 of Fig.4 and rows 3–4 of Fig.6. These original images and results will be released on our Github. ### 2. MD v.s. m-MD. We observe that applying DIFT to search final handle points $h_f$ around the entire edited image may mislead the found points to excessively deviate from editing region, especially when there are semantically similar points with the source handle in the image, resulting in high MD. E.g., points on the left and right hands are often confused by DIFT. To eliminate these cases, given the user input mask $M$ to indicate the editing region, we treat points within $M$ as candidate set $\Omega_\text{mask}$. Formally, the searching process is: \begin{equation} h_f = \arg\min_{p \in \Omega_\text{mask}} d(F_{ori}(h), F_{edit}(p)) \end{equation} where $F_{ori}, F_{edit}$ are feature maps extracted by Stable Diffusion 2.1 from original and edited images, $d$ is a cosine distance metric, and $h$ is the given handle points in original image. Following MD, we calculate the mean Euclidean distance between target points and their corresponding final handle point to derive m-MD. While m-MD is numerically lower than MD, it may yield optimistic scores in cases of image distortion, where the mask constraint forces final handle points closer to the target. Thus, the two metrics complement each other. Notably, the inherent limitations of both MD and m-MD affect all methods uniformly, making them fair for comparison. ### 3. Quantitative comparison. In terms of both MD/m-MD and visual editing quality, our DragLoRA performs comparably to GoodDrag and shows significant advantages over other methods. Meanwhile, our approach achieves the highest efficiency among optimization-based methods, substantially reducing time compared to GoodDrag, which is presented in Tab.1. Besides, as mentioned in Sec. 4.3, 1-LPIPS inherently favors under-edited results. StableDrag and EasyDrag achieve high 1-LPIPS by insufficiently moving points (see their larger MD/m-MD in Tab.1). As a supplement, we introduce the DragBack pipeline (Sec. 4.5) to measure the similarity between the edited image and original image. After two symmetric edits, there is no doubt that the higher the similarity, the better. As shown in Tab.2, DragLoRA achieves the best LPIPS while GoodDrag achieves the best CLIP, both showing high consistency with original image, which can not be verified in Tab.1. ### 4. Figure Rendering Issues. Perhaps the "?" symbols in Figs. 2–3 are related to rendering engine version of Edge browser. We reconfirm that: symbols render correctly in Chrome, macOS Preview and other PDF viewers. ### 5. Limitations. We acknowledge that a more detailed discussion of our limitations would improve the manuscript. In the revised version, we will add a section that presents the following points: (1) considering the quantitative metrics are not direct and accurate, we plan to conduct a user study in the future. (2) There are challenging cases where DragLoRA does not perform optimally, producing edited image with low fidelity, such as moving the camera down to show up the face behind it, which also challenges other methods. (3) Due to computational constraints, we have not integrated the latest generative models with our method. Thank you once again for your valuable comments and suggestions. We eagerly await your feedback on our rebuttal. [1] Choi S, Park S, Lee M, et al. Viton-hd: High-resolution virtual try-on via misalignment-aware normalization[C]//Proceedings of the IEEE/CVF conference on computer vision and pattern recognition. 2021: 14131-14140.	Summary: This paper introduces DragLoRA, a framework that integrates LoRA into drag-based editing. Instead of optimizing the input feature obtained from DDIM inversion, the paper claims to improve accuracy and efficiency by utilizing lora adaptation. A denoising score distillation loss is proposed to align the outputs with the original model , ensuring stable and accurate features for motion supervision. An adaptive optimization scheme enhances both precision and computational efficiency. The experiments show that DragLoRA boosts efficiency in drag-based editing benchmarks. Claims And Evidence: yes Methods And Evaluation Criteria: The paper proposes three modules: A dynamically lora adapter integrated into UNet for optimizing the editing task, a DDS Loss that claimed by the paper to establish "semantic fidelity" by comparing noise predictions of the original and LoRA-enhanced UNet, and "Adaptive Optimization", which is a strategy that dynamically switches between efficient input updates and motion supervision based on tracking quality. 1. The dynamically lora adapter is simply using lora on Unet for fine-tuning the diffusion model, which seems incremental and naive. 2. The paper proposes three modules with complex design, while I do not see strong motivations to do so. I personally do not like papers that introduce intricate methods without clear justification. Furthermore, the experiments do not show that the method significantly overperforms other methods by a notable margin. I think this field still lacks high-quality data at scale, and fancy tricks or heuristic design can only bring incremental improvements. Theoretical Claims: No theoretical claims given. Experimental Designs Or Analyses: The experimental result is based on a well-established benchmark: DragBench and Drag100. The paper also conducts a sufficient comparison with other methods. The ablation study also verifies the effectiveness. Supplementary Material: Not given Relation To Broader Scientific Literature: N/A Essential References Not Discussed: The paper has discussed essential references Other Strengths And Weaknesses: I also highly recommend to make the Preliminaries section easy-to-understand to help readers who are unfamiliar with Motion Supervision and Point Tracking. Other Comments Or Suggestions: target points "t" and timestep "t" should used different denotation. Questions For Authors: N/a Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Thank you for your feedback regarding the clarity of our Preliminaries section and symbolic expressions. We appreciate the opportunity to clarify our approach. ### More details about drag-based image editing, particularly its motion supervision and point tracking. Drag aims to make the semantic positions of the handle points $\mathbf{h}\in \mathbb{R}^2$ reach targets $\mathbf{g}\in \mathbb{R}^2$ through online optimization, breaking down the journey of $\mathbf{h}$ into small steps. Each step consists of motion supervision and point tracking: * Motion supervision relies on $L_\text{drag}$ in eq.(4) to optimize input latent feature $z_{35}$, obtained by DDIM inversion, transforming the region around temporal target points $\mathbf{h} + \mathbf{d}$ into handle points region, where $\mathbf{d}$ means a small displacement, and implicitly filling the handle point region by utilizing the generation capability of model. * Point tracking locates the new handle points $\mathbf{h}$ on updated deep features in Unet, as defined in eq.(6), which gives a new guidance for next-step motion supervision. This optimization is performed per image, eliminating the need for a training set. ### Difference between DragLoRA and LoRA finetuning. For our work, the DragLoRA is online optimized to control the dynamic motion, gradually editing local image features towards the final goal, which is quite different from simply fine-tuning the Unet with LoRA based on a set of images or a single image. Instead, we intend to control the optimization and use LoRA to steer the handle points. ### Motivation behind each module. Besides, as shown in Fig.10 and Tab.3, only changing the trainable parameters from $z_{35}$ to LoRA $\Delta \theta$, which serves as our baseline, proves to be unstable. To address this, we devise a series of strategies based on problem analysis: 1. The primary challenge of optimizing LoRA is that excessive deviation in LoRA parameters can compromise the generative capability of model. Regarding this, we introduce $L_\text{DDS}$ as Eq.(8) to build dual-objective optimization (DOO), which aligns the generative capability of the optimized model with the pre-trained model. 2. Meanwhile, the fixed input feature $z_{35}$ retains its initial spatial layout, which requires the LoRA to generate the growing displacements for handles as they move towards the targets, and it conflicts with the small step during drag, contributing to instability of optimization. This phenomenon can be observed in cross-attention map visualizations (see Fig. 1 at: https://imgur.com/a/Cb01npK), where the conflicts lead to unclear mask of duck's beak and suboptimal results. To mitigate this, we design input latent feature adaptation (ILFA) to align the input $z_{35}$, updating it with the motion learned by LoRA in a denoise-renoise way. 3. Through experiments, we observe that once LoRA is well optimized, applying multiple ILFA steps alone can facilitate the movement of handle points. Since ILFA is training-free, it is faster than DOO. This suggests the potential benefits of a balanced integration of ILFA and DOO. To achieve this balance dynamically, we propose an adaptive switching strategy (ASS) that: (1) Solely applies ILFA when LoRA has learned the accurate motion. (2) Reactivates LoRA optimization when ILFA alone becomes unreliable. 4. While ASS enhances motion supervision efficiency, we further propose an efficient point tracking (EPT) with limited search region and minD-based retreat, achieving an balance between computational cost and editing effectiveness. Each module in our design is introduced progressively based on problem analysis and experimental observations. Rather than being arbitrary design choices, they address specific limitations of directly applying LoRA. We hope this clarification provides a stronger motivation for our method and demonstrates the necessity of our contributions. ### Comparisons with other works. The combination of modules above achieves an much higher editing accuracy than most of the methods, and our results are comparable with GoodDrag. While GoodDrag optimizes input $z$ over multiple timesteps, sacrificing efficiency, our method costs the least time among optimization-based methods. Thank you again for your insightful feedback. We eagerly await your feedback on our rebuttal.	null	null	null	null	null	null
Piloting Structure-Based Drug Design via Modality-Specific Optimal Schedule	Accept (poster)	Summary: This paper focuses on modeling twisted probability path of multimodalities in structure-based drug design. It analyzes the theoretical link between noise schedules and VLB in multimodality probabilistic modeling and further proposes a VLB-optimal scheduling strategy to address this bottleneck. By integrating the VLB-optimal scheduling with the BFN framework, the proposed MolPilot achieves state-of-the-art performance in de novo design and competitive performance in local docking, demonstrating the effect of the proposed VLB-optimal scheduling. Claims And Evidence: The claims made in the submission are supported by clear and convincing evidence. Methods And Evaluation Criteria: This paper proposes a VLB-optimal scheduling strategy to model twisted probability path of multimodalities, which makes sense for structure-based drug design. Furthermore, it introduces an OOD subset of PoseBusters to serve as a more reliable held-out test, which also makes sense for this problem. Theoretical Claims: I checked the correctness of the theoretical analysis between noise schedules and VLB in multi-modality probabilistic modeling. Experimental Designs Or Analyses: I checked the soundness/validity of the experimental designs and analyses. I think it's necessary to demonstrate the effect of the proposed VOS by integrating it with more frameworks. Supplementary Material: I reviewed the supplementary material. Relation To Broader Scientific Literature: This paper aims to overcome the twisted probability path bottleneck of multimodalities, thus related to various tasks involving multimodal generative modeling. Essential References Not Discussed: Many essential references are not discussed in this paper, such as IPDiff [1], DecompOpt [2], IRDiff [3], DecompDPO [4], and BINDDM[5]. [1] Huang Z, Yang L, Zhou X, et al. Protein-ligand interaction prior for binding-aware 3d molecule diffusion models[C]//The Twelfth International Conference on Learning Representations. 2024. [2] Zhou X, Cheng X, Yang Y, et al. DecompOpt: Controllable and Decomposed Diffusion Models for Structure-based Molecular Optimization[C]//The Twelfth International Conference on Learning Representations. 2024. [3] Huang Z, Yang L, Zhou X, et al. Interaction-based retrieval-augmented diffusion models for protein-specific 3d molecule generation[C]//Forty-first International Conference on Machine Learning. 2024. [4] Cheng X, Zhou X, Yang Y, et al. Decomposed direct preference optimization for structure-based drug design[J]. arXiv preprint arXiv:2407.13981, 2024. [5] Huang Z, Yang L, Zhang Z, et al. Binding-adaptive diffusion models for structure-based drug design[C]//Proceedings of the AAAI Conference on Artificial Intelligence. 2024, 38(11): 12671-12679. Other Strengths And Weaknesses: Strengths: 1. This paper provides the theoretical analysis between noise schedules and VLB in multimodality probabilistic modeling, showing the importance of designing optimal noise schedules for this twisted probability path. 2. This paper introduces an OOD subset of PoseBusters to serve as a more reliable held-out test, addressing these potential problems with CrossDock evaluation. Weakness: 1. The description of the proposed MolPilot is not clear, lacking many implementation details. 2. This paper ignores many essential references, limiting its impact and connection to existing research. Other Comments Or Suggestions: It's optional for authors to decide whether to provide their code. However, providing an anonymous repository link but with an empty codebase is not respectful. Questions For Authors: 1. Why not integrate the proposed VOS with more frameworks? It's necessary to demonstrate its practical applicability within various frameworks. 2. Is the ID CrossDock test set identical to those used in previous studies? Ethical Review Flag: Flag this paper for an ethics review. Ethics Expertise Needed: ['Other expertise'] Ethical Review Concerns: This paper has modified the template to delete the template content in the bottom left corner of the first page. Considering the deleted content, this paper should exceed the 8-page limit by over two lines. According to ICML 2025 Peer Review FAQ (https://icml.cc/Conferences/2025/PeerReviewFAQ), it's not allowed to modify the template to gain an unfair "space" advantage relative to other authors. Therefore, please check if such an operation is a violation of the ICML formatting requirements. Code Of Conduct: Affirmed. Overall Recommendation: 2	Rebuttal 1: Rebuttal: We sincerely thank the reviewer for the careful reading and insightful feedback. Below, we address each question and concern to improve the clarity and completeness of our work, as well as demonstrate its generality. ## Questions Q1: Integration with More Frameworks > Why not integrate the proposed VOS with more frameworks? It's necessary to demonstrate its practical applicability within various frameworks. Thank you for this valuable suggestion. To demonstrate VOS's broader applicability, we integrated it with the diffusion-based framework TargetDiff. Specifically, we reimplement TargetDiff with our generalized training objective and train 140k steps following the default training configuration (TargetDiff, with code provided), and then derive the test-time optimal schedule that resembles the shape in Figure 4B. The results on CrossDock show that VOS successfully enhances conformation quality for diffusion models too, with generated poses achieving Vina Scores closer to Vina Min values, indicating near-optimal realistic poses. \| Metric \| PB-Valid \| Vina Score Avg \| Vina Score Med \| Vina Min Avg \| Vina Min Med \| Vina Dock Avg \| Vina Dock Med \| scRMSD<2 \| Energy Passed \| Connected \| QED \| SA \| \|---\|---\|---\|---\|---\|---\|---\|---\|---\|---\|---\|---\|---\| \| TargetDiff \| 50.5% \| -5.47 \| -6.30 \| -6.64 \| -6.83 \| -7.80 \| -7.91 \| 37.1% \| 69.8% \| 90.4% \| 0.48 \| 0.58 \| \| TargetDiff \| 53.7% \| -6.27 \| -6.31 \| -6.82 \| -6.78 \| -7.87 \| -7.90 \| 36.8% \| 70.3% \| 89.2% \| 0.50 \| 0.62 \| \| TargetDiff* + VOS \| 58.1% \| -6.46 \| -6.53 \| -7.04 \| -7.09 \| -8.04 \| -8.12 \| 40.2% \| 73.2% \| 93.4% \| 0.49 \| 0.59 \| Q2: CrossDock Test Set Consistency > Is the ID CrossDock test set identical to those used in previous studies? Yes, we confirm that we used the identical CrossDock test set as proposed in previous studies, ensuring fair and consistent comparison with existing methods. ## Weaknesses W1: Clarity of Implementation Details > The description of the proposed MolPilot is not clear, lacking many implementation details. We appreciate this feedback and will enhance the clarity of our description by adding more detailed description to Section 4, Algorithm 1, and Appendix A. We will move key implementation details from the Appendix to the main text where appropriate. Thanks again for the advice, and we will revise our manuscript accordingly. W2: Essential References > This paper ignores many essential references, limiting its impact and connection to existing research. For example, many essential references are not discussed in this paper, such as IPDiff [1], DecompOpt [2], IRDiff [3], DecompDPO [4], and BINDDM[5]. Thank you for highlighting these important references. We agree that IPDiff, DecompOpt, IRDiff, DecompDPO, and BINDDM represent meaningful advancements in controllability and practicality by incorporating guidance signals (e.g. binding affinity, interactions) to enhance molecular properties of generated ligands. We will expand our related work section to include thorough discussion of these approaches and their contributions. Additionally, we report the results of IPDiff and BindDM on CrossDock, where we calculated PB-Valid and other metrics based on the samples obtained by using the official code, showing that they indeed enhance affinities through binding signals from pretrained predictors, yet also with the issue of conformation plausibility. \| \| PB-Valid \| Vina Score Avg \| Vina Score Med \| Vina Min Avg \| Vina Min Med \| Vina Dock Avg \| Vina Dock Med \| scRMSD<2 \| Energy Passed \| Connected \| QED \| SA \| \|---\|---\|---\|---\|---\|---\|---\|---\|---\|---\|---\|---\|---\| \| IPDiff \| 37.1% \| -6.41 \| -7.01 \| -7.45 \| -7.48 \| -8.57 \| -8.51 \| 33.7% \| 51.1% \| 90.4% \| 0.52 \| 0.59 \| \| BindDM \| 31.3% \| -5.92 \| -6.81 \| -7.29 \| -7.34 \| -8.41 \| -8.37 \| 38.6% \| 42.3% \| 91.5% \| 0.51 \| 0.58 \| W3: Code Repository We sincerely apologize for the oversight regarding our code repository. We had uploaded our code to GitHub before the reviewing process began, but failed to verify the auto-update mechanism for the anonymous repository. This unintentional mistake has been rectified now, and we have force-updated the repository with all necessary code to ensure full reproducibility, including the newly added experiment with TargetDiff. W4: Ethical Review Concerns We appreciate the attention to formatting requirements. The missing content was due to that we have commented out `printAffiliationsAndNotice{}`, yet it was not intended to create extra space. As noted in the ICML 2025 Peer Review FAQ (March 18, 2025 update), the Program Chairs have acknowledged that papers with this specific issue will not be desk-rejected "due to confusion in the LaTeX template." We will restore this element in our revision to ensure full compliance with formatting requirements. We thank the reviewer again for the constructive feedback that helps us improve our manuscript, and we welcome further discussion.	Summary: The present paper is concerned about structure-based drug design (SBDD) using a Bayesian Flow Network (BFN). One of the issues when applying BFN to SBDD is that the model has to generate a molecular graph, which is a discrete object, as well as its 3D structure, which is a continuous object. A numerical example in Section 2 demonstrates that many of the related models favor 3D structure than 2D structure, and it leads to an unrealistic 3D structure that is incompatible with the 2D structure. Theoretically, when the data has both continuous and discrete parts, the variational lower bound depends on the entire noise schedule, which motivates the authors to find the best noise scheduling. The authors have successfully derived a dynamic programming based algorithm to obtain the best noise schedule, which is the main theoretical contribution of the paper. The authors investigate the effectiveness of the proposed method by numerical experiments. One of the highlights is that the proposed method achieves the best PB-Valid score, which suggests that the generated 2D and 3D structures are consistent. Claims And Evidence: Most of the claims in this paper are clear and well supported by both empirical and theoretical statements. Methods And Evaluation Criteria: This paper uses a standard benchmark for deep learning-based SBDD, which makes sense to me. Theoretical Claims: I have followed the theoretical statements, but not followed their proofs. Experimental Designs Or Analyses: The experiments are well designed and are very informative for readers. I have no addition to the experimental protocol. Supplementary Material: No. Relation To Broader Scientific Literature: This paper is related to drug discovery, and in this sense, is connected to the broader scientific literature. Essential References Not Discussed: No Other Strengths And Weaknesses: N/A 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 thorough reading of our manuscript and the positive evaluation. We are pleased that the reviewer recognized the key challenges and contributions of our work on deriving optimal schedules for structure-based drug design, and we certainly welcome further discussion. Regarding Theoretical Contributions We appreciate the reviewer's acknowledgment of one of our main contributions - the dynamic programming algorithm for VLB-optimal noise scheduling when dealing with the twisted discrete-continuous probability path. We believe the theoretical foundation is sound and provides an important advancement for handling the challenging joint generation of molecular graphs (discrete) and their 3D structures (continuous). Regarding Experimental Results We are particularly encouraged by the reviewer's recognition of our experimental design and results, especially highlighting our improvement in PB-Valid. As the reviewer correctly noted, this metric demonstrates our method's ability to generate consistent 2D and 3D molecular structures - addressing a key limitation in previous approaches that often favored 3D structure at the expense of 2D topology. We thank the reviewer again for the supportive evaluation. We remain committed to further developing and refining our method to contribute to the field of structure-based drug design.	Summary: This paper presents a novel method for finding optimal noise scheduling in structure-based generative models. Typically, deep generative networks used for structure-based drug design generate molecules directly within the binding pocket of a protein, allowing the problem to be defined as 3D molecular graph generation conditioned on the protein binding pocket. Diffusion models that have been applied to this problem generally diffuse continuous atom positions and discrete graph topology separately. The authors of this paper contend that designing a joint noise scheduler may enhance generation results for multi-modal data, where the variational lower bound is not solely dependent on the endpoints, as is the case in unimodal scenarios. A dynamic programming algorithm is proposed to find the optimal scheduler on the discretized grid. The experiments demonstrate the advantages of the proposed model in conditional molecule generation and docking scenarios. ## update after rebuttal The Authors addressed all my comments. I decided to maintain my positive score. Claims And Evidence: The claims in the paper are supported by the experimental results. Methods And Evaluation Criteria: The methods make sense for the problem at hand, but I noticed two problems with the method description and reproducibility: 1. The linked repository is empty, making this work irreproducible. 2. Some potential abuses of notation can complicate the understanding of the methods section. For example, $\alpha$ in Equation 2 is constant, and later it is a function of time. $K$ is not introduced near that equation, only earlier $K_h$ and $K_A$ are introduced. $\mathbf{e}_\mathbf{x}$ is not defined. The benchmarks are carefully selected to showcase the effectiveness of the methods. Theoretical Claims: I read the proofs but did not check them thoroughly for correctness. Experimental Designs Or Analyses: The experimental design and analyses are sound. However, the molecular docking study should include more baselines because MolPilot was trained on more data (CrossDocked), and models such as DiffDock were trained on PDBbind. Additionally, examining the novelty of the generated compounds would be valuable, such as through measuring their distance from the training set. Supplementary Material: I read the entire supplementary material. There’s a possibility I might have missed something during my initial reading. Relation To Broader Scientific Literature: The results presented in this paper demonstrate that careful optimization of the noise schedule enhances the outcomes of structure-based molecule generation. The proposed theory could have a wider impact on other multi-modal generation scenarios in chemistry and beyond. Essential References Not Discussed: The key references have been described. Other Strengths And Weaknesses: The strengths and weaknesses have been described in the other sections. Other Comments Or Suggestions: N/A Questions For Authors: 1. Are there any architectural changes that have improved the performance of MolPilot compared to other models like MolCRAFT and DecompDiff? The difference is quite significant, especially regarding the docking experiment. If there are any modifications in the architecture mentioned in Section A.3 compared to previous models, it would be advisable to include this model, trained similarly to the other models, as a baseline. 2. Have you tested how sensitive the results are to the choice of the optimal path, e.g. by interpolating between linear and optimal time-rescaling functions? Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We sincerely thank the reviewer for the thorough evaluation and valuable feedback. Below, we address each point raised to improve the clarity, reproducibility, and depth of our work. ## Questions Q1: Architectural Changes The backbone of MolPilot aligns with DecompDiff, where we only replaced the MLP in the q, k, v calculation with LinearNoBias to reduce GPU memory consumption. This decreases memory usage from 42177MB to 34699MB for batch size 8 in the first 500 steps, enabling more efficient training without compromising performance. We report this baseline trained by default loss in Figure 6. Q2: Sensitivity to Optimal Path Choice Thank you for this insightful question. We conducted additional experiments interpolating between linear $t_l$ (coef $c=0$) and our optimal time-rescaling functions $t_o$ ($c=1$), by setting time functions $t=c\cdot t_l + (1-c)t_o$. Our findings show a clear trend of improving performance as we move toward the optimal schedule on both datasets. For CrossDock: \| c \| Vina Score Avg \| Vina Score Med \| Vina Min Avg \| Vina Min Med \| QED \| SA \| Connected \| PB-Valid \| \|---\|---\|---\|---\|---\|---\|---\|---\|---\| \| 0 (Linear) \| -6.63 \| -6.94 \| -7.06 \| -7.06 \| 0.55 \| 0.76 \| 0.95 \| 0.95 \| \| 0.25 \| -6.66 \| -6.88 \| -7.02 \| -7.01 \| 0.55 \| 0.76 \| 0.94 \| 0.96 \| \| 0.5 \| -6.70 \| -6.82 \| -7.04 \| -6.94 \| 0.55 \| 0.76 \| 0.95 \| 0.97 \| \| 0.75 \| -6.87 \| -6.97 \| -7.21 \| -7.11 \| 0.55 \| 0.76 \| 0.96 \| 0.96 \| \| 1 (Optimal) \| -6.92 \| -7.02 \| -7.23 \| -7.18 \| 0.55 \| 0.75 \| 0.96 \| 0.95 \| For PoseBusters: \| c \| Vina Score Avg \| Vina Score Med \| Vina Min Avg \| Vina Min Med \| QED \| SA \| Connected \| PB-Valid \| \|---\|---\|---\|---\|---\|---\|---\|---\|---\| \| 0 (Linear) \| -7.35 \| -7.38 \| -7.64 \| -7.48 \| 0.48 \| 0.73 \| 0.94 \| 0.79 \| \| 0.25 \| -7.42 \| -7.37 \| -7.66 \| -7.50 \| 0.48 \| 0.73 \| 0.94 \| 0.79 \| \| 0.50 \| -7.20 \| -7.36 \| -7.56 \| -7.51 \| 0.48 \| 0.73 \| 0.95 \| 0.78 \| \| 0.75 \| -7.44 \| -7.43 \| -7.75 \| -7.54 \| 0.48 \| 0.73 \| 0.95 \| 0.79 \| \| 1 (Optimal) \| -7.52 \| -7.52 \| -7.79 \| -7.65 \| 0.49 \| 0.73 \| 0.95 \| 0.80 \| ## Additional Clarifications Q3: Repository and Reproducibility We sincerely apologize for the oversight regarding the code repository. We had uploaded our code to GitHub before the reviewing process, but failed to verify the auto-update mechanism for the anonymous repository. This unintentional mistake has been rectified, and we have now force-updated the repository with necessary code to ensure reproducibility. Q4: Notation Clarifications We appreciate your careful reading that identified these notation inconsistencies. $\alpha$ in Equation 2 is actually the discretized $\alpha_i$ for time step $i$ in the sequence, derived from time-dependent function $\alpha(t)$, not a constant. $K$ is defined as the number of classes for one-hot encoding (with $K_h$ and $K_A$ denoting atom and bond types, respectively). $\mathbf{e}_\mathbf{x}$ is kronecker function, i.e. the projection from a class index $\mathbf{x}=j$ to a one-hot vector $\in \mathbb{R}^K$ with the $j$-th value equal to 1. We will revise the manuscript to improve clarity as requested. Q5: Molecular Docking Study and Baselines We thank the reviewer for this important point about training data differences. Following this suggestion, we trained a version of our model on PDBbind from scratch (120 epochs over 1.5 days) to enable a more direct comparison. \| \| DiffDock (850 epochs) \| Ours (120 epochs) \| \|---\|---\|---\| \| RMSD < 2Å (%) \| 38.0 \| 17.1 \| \| RMSD < 2Å & PB-Valid (%) \| 12.7 \| 15.4 \| Although the comparison remains imperfect, the results are still informative, for our primary goal was to demonstrate that ours is the first with genuine docking capability that can repurpose an SBDD model for the docking task. This capability stems from our decoupled training strategy rather than architectural changes. We will add clarification to the manuscript. Q6: Novelty of Generated Compounds Thank you for this valuable suggestion. We have calculated comprehensive metrics to assess the novelty. As shown in the table below, MolPilot achieves the highest combined metric (0.864) among all methods, demonstrating its ability to generate novel, valid, and unique compounds. \|\|Uniq\|Valid\|Novel\|Combined (U×V×N)\| \|---\|---\|---\|---\|---\| \|AR\|0.924\|0.385\|1\|0.356\| \|Pocket2Mol \| 0.910 \| 0.677 \|1\| 0.616 \| \|TargetDiff \|1\| 0.812 \|1\| 0.812 \| \|DecompDiff\|0.899 \| 0.829 \|1\| 0.745 \| \|MolCRAFT\|0.841 \| 0.995\|0.983 \| 0.823 \| \|Ours\|0.898\|0.974\|0.987\|0.864\| In addition to these metrics, we have calculated the Fréchet ChemNet Distance (FCD), which measures distribution similarity between generated molecules and training distribution (similar to FID for images, lower is better). MolPilot achieves competitive FCD scores that demonstrate its ability to generate novel compounds while faithfully capturing the training distribution. \|Method \| AR \| Pocket2Mol \| TargetDiff \| DecompDiff \| MolCRAFT \| Ours \| \|---\|---\|---\|---\|---\|---\|---\| \|FCD\|23.5\|23.0\|21.0\|18.1\|14.2 \| 12.9 \| --- Rebuttal Comment 1.1: Comment: Thank you for your responses and clarifications. I have no further questions. --- Reply to Comment 1.1.1: Comment: We are glad to know that we have successfully addressed the concerns raised in your careful review, and we will incorporate these responses and clarifications into our revised manuscript. Thank you for your time and helpful comments, which have contributed to improving our paper.	null	null	null	null	null	null	null	null
Time-VLM: Exploring Multimodal Vision-Language Models for Augmented Time Series Forecasting	Accept (poster)	Summary: This paper proposes Time-VLM, a multimodal framework using pre-trained VLMs for time series forecasting. It introduces VAL, RAL, and TAL modules to consider the information from three different views. Experimental results show that it achieves good performance with high efficiency. It contributes to a possible new direction in multimodal time series modeling. ## Update After Rebuttal I've read the rebuttal and other reviewers' comments, and my final rating is weak accept. Claims And Evidence: The claim that fusing temporal, visual, and textual modalities improves forecasting accuracy is supported by ablation studies. The claims are almost correct. I don’t identify crucial technical errors within the paper. Methods And Evaluation Criteria: The methods of Time-VLM are primarily divided into the following components: - VAL’s Image Encoding: The frequency/periodicity-based time-series-to-image conversion aligns well with VLM requirements while retaining temporal relationships. - TAL’s Hybrid Prompts: Combining statistical features with domain-specific knowledge provides a pragmatic design for real-world deployment. - RAL’s Memory-Enhanced Modeling: The retrieval-augmented mechanism leverages historical patterns to enhance temporal understanding, offering a robust foundation for forecasting. These three components are fused via the vision-language model to produce the predictive output. The evaluation metrics used are standard in this field (MSE, MAE, SMAPE, MASE, OWA), and the datasets (ETT, Weather, Electricity, Traffic, M4) are comprehensive and widely recognized. Theoretical Claims: N/A Experimental Designs Or Analyses: Overall, the experiments are thorough and well-structured, addressing key aspects of time series forecasting and multimodal learning. While the results are promising and the approach demonstrates strong potential, further exploration in more datasets and diverse real-world scenarios could provide additional insights. Nonetheless, the evaluation is solid and offers a convincing case for the effectiveness of the proposed framework. Supplementary Material: The appendix covers sufficient content to complement the main body. Relation To Broader Scientific Literature: This work aligns with recent efforts to integrate foundation models into time series analysis (e.g., Time-LLM, LLMTime) but stands out by uniquely addressing multimodal fusion. It advances the field by demonstrating how VLMs can be effectively adapted for time series forecasting, bridging gaps between modalities. Essential References Not Discussed: To the best of my knowledge, there are a series of existing studies discussing multimodal time series analysis [1, 2]. It would be good to discuss several of them for a more thorough comparison. [1] Y. Jiang et al. Multi-modal Time Series Analysis: A Tutorial and Survey. arXiv. [2] H. Liu et al. How Can Time Series Analysis Benefit From Multiple Modalities? A Survey and Outlook. arXiv. Other Strengths And Weaknesses: Overall, the insight of fusing textual and visual information with time series is interesting. The Time-VLM model can effectively address the complicated relationships among these three modalities. The experiments can verify the efficacy of these modalities. Despite the above merits, the paper can be improved in the following aspect: 1. The projection from the text/images to the time series space needs more interpretation. Can the paper provide some case studies for a better illustration? 2. According to Table 1 to Table 3, the proposed model can achieve good performance in zero/few-shot settings. However, the results in Table 4 and 5 are not significant, i.e., only limited improvements on the full-shot setting. Can the author clarify this point? In other words, if we have enough data, we don’t need other modalities anymore? 3. How about the efficiency of the proposed model? Do the authors evaluate different model size of Time-VLM on these datasets? How is the sensitivity to the parameter size? Generally the model size should largely impact the model performance. Other Comments Or Suggestions: N/A Questions For Authors: Please make rebuttal to the weaknesses. I’ve listed several questions there. Thank you. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: > Q1: Add the latest references related to multi-modal time series > A1: Thank you for your reminder. Our manuscript now includes two recent comprehensive surveys on multi-modal time series analysis [1,2], which we have integrated into both the Introduction and Related Work sections. These references help contextualize our work within current research trends and highlight important methodological connections. [1] Y. Jiang et al. Multi-modal Time Series Analysis: A Tutorial and Survey. [2] H. Liu et al. How Can Time Series Analysis Benefit From Multiple Modalities? A Survey and Outlook. > Q2: The projection from the text/images to the time series space needs more interpretation. Can the paper provide some case studies for a better illustration? > A2: Thank you for mention this important question. We have discussed a lot about this point, you can refer to Q3/A3 (Reviewers 6Pe4 / gzkF), hope to address your concern. > Q3: According to Table 1 to Table 3, the proposed model can achieve good performance in zero/few-shot settings. However, the results in Table 4 and 5 are not significant, i.e., only limited improvements on the full-shot setting. Can the author clarify this point? In other words, if we have enough data, we don’t need other modalities anymore? > A3: Thank you for your question. The experimental results indeed support this observation. However, it is worth noting that Time-VLM still outperforms Time-LLM despite having significantly fewer parameters. Our conclusion is that when time series data is limited, visual and textual transformations can compensate for the lack of information, though time series data remains the most critical factor. When the time series data is sufficiently diverse and abundant, the model can learn effectively from the time series alone. Currently, Time-VLM research is constrained by the lack of high-quality multi-modal time series datasets. Existing text and image data are generated, with real-world multi-modal datasets—such as medical scenarios combining ECG time series, textual diagnoses, and other modalities—the fusion of these data types could yield better performance even in full-shot settings, as different modalities would complement each other more effectively. > Q4: How about the efficiency of the proposed model? Do the authors evaluate different model size of Time-VLM on these datasets? How is the sensitivity to the parameter size? Generally the model size should largely impact the model performance. > A4: The model size of Time-VLM is determined by its underlying VLM architecture. We evaluated four variants: ViLT-, CLIP-, BLIP-2-based implementations, and a custom model. Experiments show that larger models do not perform better. Since time series data is relatively sparse compared to multimodal image-text data, excessively large VLMs are prone to overfitting and slower efficiency. Among the tested versions, the ViLT- and CLIP-based configurations achieve the best trade-off between efficiency and performance.	Summary: Time-VLM is a groundbreaking framework that leverages pre-trained VLMs to unify temporal, visual, and textual data for time series forecasting. Key innovations include adaptive time-series-to-image conversion (VAL), memory-enhanced temporal modeling (RAL), and contextual prompt generation (TAL). The experiments demonstrate superior performance in few-shot and zero-shot settings, with efficiency gains compared to Time-LLM. This work opens a new paradigm for multimodal time series forecasting. Claims And Evidence: The claims are compelling. Ablation studies (Table 6) strongly support the multimodal synergy claim, as removing any modality degrades forecasting accuracy. Time-VLM's efficiency is notable, reducing parameters 20× compared to Time-LLM (Table 7) yet maintaining competitive performance, with inference speed metrics further affirming it. Results on zero-shot cross-domain tasks (Table 3) validate its generalization ability. Overall, the evidence substantiates the approach's effectiveness. Methods And Evaluation Criteria: The methods are technically sound. VAL's time-series-to-image conversion retains temporal relationships, suiting VLMs. TAL's hybrid prompts combine statistical and domain knowledge practically. RAL's memory-enhanced modeling uses historical patterns for forecasting. Multimodal fusion of RAL, VAL, and TAL modalities captures diverse patterns, improving accuracy. Evaluation is comprehensive, with standard metrics and diverse datasets. Theoretical Claims: No theoretical claims. Experimental Designs Or Analyses: The experiments are comprehensive and well-executed, spanning key aspects such as long/short-term forecasting, few/zero-shot prediction, ablation studies, model analysis, visualization case studies, and hyperparameter sensitivity. Supplementary Material: The appendix encompasses detailed information, including descriptions of datasets, hyperparameter settings, training procedures, comprehensive results, visualization case studies, and discussions on future work. Relation To Broader Scientific Literature: This work aligns with recent efforts to integrate foundation models into time series analysis (e.g., Time-LLM, LLMTime) but stands out by uniquely addressing multimodal fusion. It advances the field by demonstrating how VLMs can effectively adapt to time series forecasting, bridging gaps between modalities. Essential References Not Discussed: 1) Vision Language Models Are Few-Shot Audio Spectrogram Classifiers (NeurIPS Workshop 2024): This work evaluates zero-shot capabilities of LMMs for audio classification using spectrogram images and textual prompts. While related, Time-VLM uniquely addresses forecasting-specific challenges (e.g., periodicity-aware image encoding in VAL), highlighting its broader applicability. 2) Training-Free Time-Series Anomaly Detection: Leveraging Image Foundation Models (Arxiv 2024): This work focuses on zero-shot anomaly detection using visual representations. Discussing it would further emphasize Time-VLM’s unique contributions in multimodal forecasting and its efficiency compared to larger LMMs. Other Strengths And Weaknesses: Strengths: 1) Novel use of VLMs for time series, enabling semantic context injection. 2) Strong empirical validation across diverse domains. Weaknesses: 1) Scalability: Exploring larger VLMs (e.g., LLaVA, GPT-4V) could enrich textual context and further improve performance, offering a promising avenue for future work. Other Comments Or Suggestions: Please refer to the weakness. Questions For Authors: Please refer to the weakness. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: > Q1: Scalability: Exploring larger VLMs (e.g., LLaVA, GPT-4V) could enrich textual context and further improve performance, offering a promising avenue for future work. > A1: Thank you for your suggestion. We empirically evaluated VLMs across different scales, ranging from smaller architectures like ViLT (143M) to larger ones such as BLIP-2 (3.75B). Our experiments revealed two key findings: 1. Diminishing Returns on Scale: Larger models demand substantially more computational resources without delivering performance gains. 2. Overfitting Tendency: On benchmarks like the ETT datasets, we observed rapid training loss reduction alongside increasing validation loss, indicating overfitting. Based on these results, we adopted a more compact VLM to optimize the trade-off between efficiency and effectiveness. We hypothesize that the rich multimodal priors from large-scale pretraining may be unnecessarily complex for our current datasets (ETT, Traffic, Weather, Electricity), which are relatively small-scale.	Summary: This paper proposes Time-VLM, a multimodal framework that leverages vision-language models to encode temporal, "visual" and textual modalities for enhanced time series forecasting. Specifically, RAL encodes and saves time series into a memory bank for further interaction with multi-modal embedding. VAL encodes time series to multi-dimensional representations and TAL generates time series descriptions. "vision" and textual features are processed with frozen pretrained VLMs to obtain informed meta representations. Fused with temporal features, the Time-VLM achieves superior performance on various experiment settings. Claims And Evidence: Yes. Claims are clear and well supported. Methods And Evaluation Criteria: Yes, methods and evaluation criteria make sense in this area. Theoretical Claims: N/A Experimental Designs Or Analyses: Yes, experients are sound and comprehensive. Supplementary Material: Yes, review the code in the supplementary material. Relation To Broader Scientific Literature: Contribute to multi-modal time series analysis via combining temporal, visual and textual modalities Essential References Not Discussed: N/A Other Strengths And Weaknesses: Strength: 1. The n-dimensional representation of time series is good. Instead of merely plotting the time series, it allows for a more effective utilization of the vision encoder. 2. Comprehensive and complete experiments. 3. The framework is new to this field. Weakness: 1. The textual encoder component follows Time-LLM, and based on your ablation study, its contribution appears marginal. There is room for improvement in this area. 2. The n-dimensional representation of time series and its description are loosely connected. Directly utilizing a pretrained VLM may reduce effectiveness. 3. The “visual” representation of time series is difficult for human perception to comprehend. The visualization in C.1 lacks meaningful interpretation. Other Comments Or Suggestions: N/A Questions For Authors: 1. Would using a pretrained VM combined with a pretrained LM, instead of a pretrained VLM, better enhance your visual and textual inputs? 2. Since you mentioned foundation models for time series, could they offer stronger encoding capabilities and enhance your pipeline? Ethical Review Concerns: N/A Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Thank you for recognizing the method design, complete evaluation and unique innovation of our paper. Below are our responses to your major questions. > Q1: Textual Encoder Limitations Analysis > A1: We systematically investigated the limitations of textual encoders in VLMs through three complementary analyses: 1. Input Length Analysis: We evaluated three VLMs with progressively longer maximum text input lengths—ViLT (40 tokens), CLIP (77 tokens), and BLIP-2 (512 tokens)—and observed no improvement in forecasting performance despite increased model capacity. Instead, larger models exhibited lower efficiency, with significantly slower inference and training speeds. 2. Custom VLM Analysis: We implemented a Custom implementation on single VM (ViT-B/16) + LM (BERT-Base) on traffic datasets. However, experiments revealed that it underperformed native VLMs. \| Horizon \| Time-VLM (ViLT) \| Time-VLM (Custom) \| \| --- \| --- \| --- \| \| 96 \| 0.148 \| 0.158 \| \| 192 \| 0.193 \| 0.206 \| \| 336 \| 0.243 \| 0.258 \| \| 720 \| 0.312 \| 0.334 \| \| Avg \| 0.224 \| 0.239 \| 3. Embedding Space Divergence: As we discussed in Q3/A3 of Reviewer 6Pe4, The t-SNE visualization demonstrates that: - Text embeddings (blue) from COCO-Text form distinct clusters separated from time-series data distributions (ETT/Traffic/ECL), confirming poor semantic alignment. - Visual embeddings (green) from COCO-Image naturally encompass time-series features, validating that pixel-space representations better preserve temporal dynamics. This reveals a lack of effective cross-modal alignment. Crucially, the inherent divergence between image, text, and time-series modalities—compounded by their distinct training data distributions—hinders performance without explicit alignment mechanisms. 4. Future Potential: Time-VLM is a self-enhanced paradigm that operates without real image/text data—both are generated from raw time series. We believe that with a high-quality dataset covering real-world multimodal time-series data (e.g., ECG time series paired with medical images and diagnostic reports), Time-VLM’s potential could be fully unlocked. At that stage, modalities could complement each other more effectively. > Q2: The n-dimensional representation of time series and its description are loosely connected. Directly utilizing a pretrained VLM may reduce effectiveness. > A2: Your concern is right. However, our approach does not aim to map time series directly to text. Instead, we project them into a joint text-image multi-modal space, leveraging the complementary strengths of both modalities. For a deeper discussion on this methodology, please refer to Q3/A3 (Reviewer 6Pe4). > Q3: The “visual” representation of time series is difficult for human perception to comprehend. The visualization in C.1 lacks meaningful interpretation. > A3: I fully understand your concerns. In response, we added an insightful analysis in Q3/A3 (Reviewer 6Pe4), showing that the pre-training knowledge from the VLM aligns with the time series domain. Additionally, our Time-VLM's image generation framework integrates innovative techniques to better align the distribution of the VLM’s input while maximizing temporal information retention: 1. Frequency Domain Information Injection: - High-frequency components appear as fine-grained textures - Low-frequency components form broad color gamut distributions 2. Multi-Scale Period Encoding: - Cosine/sine functions encode periodic patterns (e.g., daily/weekly cycles) - Represented through distinct spatial patterns in the image 3. Interpolation Alignment Mechanism: - Bilinear interpolation ensures smooth pixel transitions - Sudden time-series changes correspond to sharp color intensity variations 4. Color Semantic Mapping: - Dark blue → low values; light yellow → high values - Gradient transitions directly indicate trend directions We acknowledge that visual interpretability remains a challenge and plan to explore this further in future work. > Q4: Would using a pretrained VM combined with a pretrained LM, instead of a pretrained VLM, better enhance your visual and textual inputs? > A4: This is an interesting idea, and we have explored it experimentally. You can find details in Q1/A1 and Q3/A3 (Reviewer 6Pe4). > Q5: Since you mentioned foundation models for time series, could they offer stronger encoding capabilities and enhance your pipeline? > A5: As discussed in Q1/A1 (Reviewer 6Pe4), Time-VLM and time-series foundation models follow different paradigms. However, we may explore building a pre-trained vision-language-enhanced foundation model once high-quality multimodal time-series datasets become available. --- Rebuttal Comment 1.1: Comment: Thank you to the author for the response. It addressed most of my concerns. I will keep my scores.	Summary: The paper introduces Time-VLM, a multimodal time series forecasting framework that leverages pre-trained Vision-Language Models (VLMs) to integrate temporal, visual, and textual information. By combining retrieval-augmented learning, vision-based encoding, and text-based contextualization, Time-VLM enhances forecasting performance, particularly in few-shot and zero-shot settings. Claims And Evidence: Overall, the claims made in the paper are clear. Methods And Evaluation Criteria: Yes, the proposed methods and evaluation criteria are appropriate for the problem of time series forecasting. Theoretical Claims: The paper does not contain any theoretical claims that require formal proof verification. Experimental Designs Or Analyses: I have reviewed the experimental design and analyses. To further establish the validity of the results, additional comparisons with other models that perform well in zero-shot and few-shot forecasting would be necessary. Supplementary Material: I have reviewed the supplementary material, particularly the additional experiments. Relation To Broader Scientific Literature: This paper contributes to the broader scientific literature by exploring multimodal time series forecasting with pre-trained Vision-Language Models (VLMs). While previous works have integrated either text or vision with time series forecasting, this study is one of the first to leverage both modalities simultaneously. Essential References Not Discussed: The paper would benefit from citing and discussing prior works on zero-shot and few-shot forecasting, particularly those related to foundation models in time series forecasting. Several recent studies, such as CHRONOS, TimesFM, and MOIRAI, have explored the use of large-scale pre-trained models for improved generalization in forecasting tasks. Other Strengths And Weaknesses: Strengths 1. The paper presents a clear motivation and is well-structured, making it easy to follow. 2. The approach of transforming time series into visual cues and leveraging a memory bank for enriched feature extraction is novel. 3. The proposed method demonstrates strong performance across various time series forecasting scenarios, highlighting its effectiveness. Weaknesses 1. Comparison with Time Series Foundation Models: Recent foundation models for time series forecasting (e.g., CHRONOS, TimesFM, MOIRAI) have demonstrated strong zero/few-shot forecasting performance. A direct comparison with these models is necessary to validate the effectiveness of the proposed approach. 2. Instance Normalization and Misalignment: Since raw time series data undergoes normalization, but textual information is extracted from the unnormalized version, this may cause misalignment in feature representations. The paper should include experiments addressing this issue to ensure robustness. 3. Role of the Vision Encoder: It is unclear whether a pre-trained vision encoder can effectively process images generated from time series data. A more thorough evaluation is needed to justify its role. Additionally, the decision to freeze the vision encoder should be explained, and results from fine-tuning should be provided for comparison. 4. Lack of Component Analysis: While the paper provides extensive forecasting results, there is a lack of detailed ablation studies on key components. For example, the memory bank is a core part of the method, yet its contribution is not analyzed enough. Further component-wise evaluations would enhance the credibility of the approach. Other Comments Or Suggestions: N/A Questions For Authors: Please refer to the Weaknesses. Code Of Conduct: Affirmed. Overall Recommendation: 2	Rebuttal 1: Rebuttal: Thank you for recognizing the clear motivation, method design, and rigorous evaluation of our paper. Below we endeavor to address your questions. > Q1: Comparison with Time Series Foundation Models > A1: We appreciate your suggestion. However, Time-VLM fundamentally differs from foundation models (e.g., CHRONOS, TimesFM, MOIRAI) in its learning paradigm: While the latter rely on external datasets for pre-training, Time-VLM uses only the target dataset. By generating text and visual modalities, it augments raw time series without external knowledge, enabling efficient fine-tuning and cross-dataset zero-shot learning. However, we added a comparison of Time-VLM (5% few-shot) vs. foundation models (zero-shot) on ETT datasets. Results show Time-VLM achieves lower MSE across all datasets, validating its effectiveness under data scarcity. \| Methods \| Time-VLM \| Moirai \| Chronos \| TimesFM \| \| --- \| --- \| --- \| --- \| --- \| \| ETTh1 \| 0.442 \| 0.475 \| 0.560 \| 0.489 \| \| ETTh2 \| 0.354 \| 0.379 \| 0.392 \| 0.396 \| \| ETTm1 \| 0.364 \| 0.714 \| 0.636 \| 0.434 \| \| ETTm2 \| 0.262 \| 0.343 \| 0.313 \| 0.320 \| > Q2: Instance Normalization and Misalignment > A2: We added ablation experiments on Weather dataset to evaluate text normalization’s impact. Results show that normalized text reduces MAE by 1.29%, underscoring the importance of cross-modal alignment. We will fix this in final version. \| Horizon \| Time-VLM (Raw) \| Time-VLM (Normalized) \| \| --- \| --- \| --- \| \| 96 \| 0.160 \| 0.159 \| \| 192 \| 0.203 \| 0.201 \| \| 336 \| 0.253 \| 0.249 \| \| 720 \| 0.317 \| 0.312 \| \| Avg \| 0.233 \| 0.230 \| > Q3: Role of the Vision Encoder and Freezing Rationale > A3: We conducted an analysis to evaluate how pre-trained VLMs can be applied to time series forecasting. Specifically, we sampled 200 image-text pairs from MSCOCO (VLM’s pre-training dataset) and 60 samples each from time series dataset (ETT, Traffic, Weather, ECL). Using t-SNE, we visualized four embedding types in 2D space: 1. Multi-modal embeddings from COCO-Pair samples through VLM ⇒ representing VLM’s pre-training knowledge 2. Multi-modal embeddings from time series-generated image-text pairs through VLM ⇒ representing Time-VLM’s augmented knowledge 3. Visual embeddings from COCO-Image samples through ViT ⇒ representing visual knowledge from a single VM 4. Text embeddings from COCO-Text samples through BERT ⇒ representing text knowledge from a single LM Key findings from the visualization https://anonymous.4open.science/r/Time-VLM/ts_embeddings_with_coco_samples.png: 1. COCO-Image features (green) fcluster centrally, surrounded by time-series features (ETT: yellow/orange, ECL: purple, etc.), confirming intrinsic visual-temporal similarity. This aligns with VisionTS [1], where visual features (pixel intensity variations, repeating patterns, color consistency, and edge transitions) directly map to temporal behaviors (value fluctuations, periodicity, stable segments, and outliers/abrupt changes, respectively). This explains why time series imaging [2] has emerged as a hot research direction. Our image generation process further advances this explicitly encoding frequency/periodicity and using interpolation/color semantics to preserve temporal information. 2. COCO-Text features (blue) show clear separation with time-series clusters, highlighting modality gaps. 3. COCO-Pair features (red) achieve maximal overlap with time-series data, demonstrating cross-modal complementarity - text semantics enhance visual-temporal alignment. This motivates Time-VLM. Compared to Time-LLM and VisionTS which utilize a single modality projection, we argue that projecting time series into multi-model embeddings is more plausible. Time-VLM's remarkable zero-shot and few-shot learning capabilities primarily stem from the pre-trained VLM's knowledge. Regarding freezing the visual encoder, we did extensive experiments, which revealed that unfreezing led to training instability (e.g., overfitting on small datasets like ETT). Since the VLM has already achieved cross-modal alignment, freezing the encoder allows us to reuse this capability while avoiding excessive training overhead, we only add a simple fusion layer that is time-efficient for alignment. [1] M. Chen et al. VisionTS: Visual Masked Autoencoders Are Free-Lunch Zero-Shot Time Series Forecasters [2] J. Ni et al. Harnessing Vision Models for Time Series Analysis: A Survey. > Q4: Lack of Component Analysis > A4: We expanded ablation studies on the memory bank. Results on the Weather dataset (MSE) confirm both local and global memory are critical: \| Horizon \| Full Model \| w/o Local Mem \| w/o Global Mem \| \| --- \| --- \| --- \| --- \| \| 96 \| 0.160 \| 0.185 \| 0.165 \| \| 192 \| 0.203 \| 0.235 \| 0.210 \| \| 336 \| 0.253 \| 0.295 \| 0.265 \| \| 720 \| 0.317 \| 0.375 \| 0.330 \| \| Avg \| 0.233 \| 0.273 \| 0.243 \|	null	null	null	null	null	null
Efficiently Access Diffusion Fisher: Within the Outer Product Span Space	Accept (poster)	Summary: The diffusion Fisher information matrix (or just 'diffusion Fisher') provides useful quantitative information about the sensitivity of diffusion model log-likelihoods to small changes in state, and can be exploited to (among other things) evaluate sample likelihoods and guide diffusion models to generate higher-quality samples. The authors observe that a special property of the diffusion Fisher allows it to be computed more efficiently than is possible with the naive auto-differentiation-based approach. Moreover, they show that their approach is much faster than an existing alternative approach for computing (the trace of) the diffusion Fisher, which involves taking the Jacobian-vector product (JVP). Claims And Evidence: Yes. The authors' work is based on a simple theoretical idea, which they clearly prove. They support their claim of practical usefulness with a variety of numerical experiments, which involve both evaluating likelihoods and guiding the output of diffusion models to be higher-quality. Methods And Evaluation Criteria: Yes, the authors' methods and evaluations (principally, using the diffusion Fisher for what it's usually used for, and showing that their computations are fast compared to the previous SOTA) make sense. Theoretical Claims: The authors' theoretical claims are simple and easy to verify. Experimental Designs Or Analyses: The authors' experiments appear sound and yield reasonable-looking results. Supplementary Material: No. Relation To Broader Scientific Literature: The authors' work relates to the diffusion Fisher, which has various well-known applications to evaluating likelihoods and guiding diffusion models. More broadly, it relates to a large body of work concerning evaluating the quality of the samples of diffusion models, and guiding them to produce better samples. Essential References Not Discussed: No references come to mind. Other Strengths And Weaknesses: The paper is well-written and the main theoretical idea is clear. The authors' evaluations are easy to understand and clear, although it would be helpful if more examples (along the lines of Figs 2 and 4) were shown in the SI. Other Comments Or Suggestions: line ~ 208, "detail discussions" -> "a detailed discussion" Questions For Authors: The authors' proposed methods involve some approximation (see, e.g., line 375). Are there cases where these approximations are expected to break down, and this method is not expected to give good results? In general, are there any obvious issues associated with using or scaling up these methods for computing the diffusion Fisher (or certain related quantities, like its trace)? As a related point, Proposition 6 appears to show potentially bad behavior when $\sigma_t \approx 0$. Code Of Conduct: Affirmed. Overall Recommendation: 5	Rebuttal 1: Rebuttal: Thank you for your appreciation of our work. We will answer your questions one by one regarding these suggestions/questions. > Answer to Suggestion 1: The authors' evaluations are easy to understand and clear, although it would be helpful if more examples (along the lines of Figs 2 and 4) were shown in the SI. While we consider the theoretical analysis of the diffusion Fisher to be the primary contribution of this work, we agree that additional visual illustrations, such as those in Figures 2 and 4, would further enhance clarity. We will include more examples in the Supplementary Information (SI) as part of our revision. > Answer to Suggestion 2: line ~ 208, "detail discussions" -> "a detailed discussion" We apologize for this oversight. We have now corrected the syntax error and conducted a thorough proofreading of our work. > Answer to Question 1: The authors' proposed methods involve some approximation (see, e.g., line 375). Are there cases where these approximations are expected to break down, and this method is not expected to give good results? In the DF-EA method, we introduce an approximation technique for the adjoint term (around line 375). These approximations are likely to be inaccurate in the following scenarios: - When $t$ is very large, the $x$-prediction part in the approximation is less accurate because of the large noise scale. - When $t$ is very small, the approximation error bound stated in Proposition 6 will increase due to the singularity issue, and the approximation will lack an accuracy guarantee. We will discuss on this singularity issue in detail in Question 3 In practice, we apply DF-EA in the range from $t=0.7$ to $t=0.3$. This range also aligns with the recommended adjoint region of the original adjoint methods. > Answer to Question 2: In general, are there any obvious issues associated with using or scaling up these methods for computing the diffusion Fisher (or certain related quantities, like its trace)? - Obvious issue: Our methods are derived exclusively on the classical diffusion process and thus cannot be directly extended to settings where the diffusion process is modified, such as cases involving additional consistency-model-type distillation [1], Schrödinger-Bridge-type endpoint alignment [2], non-Gaussian transition kernels [3], or flow rectification [4]. - Scaling-up: Theoretically, both the training and sampling phases of our DF-TM and DF-EA exhibit linear complexity growth with respect to dataset scale and data dimensionality. Experimentally, our approach performs well on commercial-grade diffusion models such as SD2-base and large-scale datasets like Laion-2B. Therefore, our method indeed has scalability. [1] Frans, Kevin, et al. "One step diffusion via shortcut models." ICLR 2025. [2] De Bortoli, Valentin, et al. "Diffusion schrödinger bridge with applications to score-based generative modeling." NeurIPS 2022. [3] Yoon, Eun Bi, et al. "Score-based generative models with Lévy processes." NeurIPS 2023. [4] Liu, Xingchao, et al. Flow Straight and Fast: Learning to Generate and Transfer Data with Rectified Flow. ICLR 2022. > Answer to Question 3: As a related point, Proposition 6 appears to show potentially bad behavior when $\sigma_t \approx 0$. Note that Proposition 6 will be ill-defined due to division-by-zero when $t=0$ since $\sigma_0 = 0$. This concern is also raised by Reviewer V5LL. We argue that this problem, which has been referred to as the singularity issue in previous literature [1][2], stems from the inherent characteristics of diffusion models rather than flaws in our derivations. Theoretically, the diffusion model has an inherent singularity property when $t_{\min} \to 0$. This implies that many quantities associated with diffusion models become ill-defined in the vicinity of $t_{\min} = 0$. This phenomenon, previously explored in [1] and [2], is once again recognized in the context of diffusion Fisher through our analysis. A deep theoretical exploration of the singularity problem remains an open question within the diffusion model field. Practically, we implement the approach used in [3] and [4], where the diffusion sampling path is ended at $t_{\min} = 0.005$ instead of $t_{\min} = 0$. This method circumvents potential bad effects resulting from the singularity issue. We briefly discussed this singularity issue on line 1242 of the original paper. In our revision, we will provide a more detailed discussion and clarification of our handling of this issue. [1] Zhang, Pengze, et al. "Tackling the singularities at the endpoints of time intervals in diffusion models." CVPR 2024. [2] Yang, Zhantao, et al. "Lipschitz singularities in diffusion models." ICLR 2024. [3] Song Y, Dhariwal P, Chen M, et al. Consistency Models ICML 2023. [4] Lu, Cheng, et al. "Maximum likelihood training for score-based diffusion odes by high order denoising score matching." ICML 2022.	Summary: This paper introduces a novel formulation of the diffusion Fisher (DF) information in diffusion models by expressing it as a weighted sum of outer products of the score function and initial data, thereby revealing that DF lies in a space spanned by specific outer-product bases dependent solely on the initial distribution and noise schedule. This formulation enables the development of two efficient approximation algorithms—one for computing the trace of DF and another for its matrix-vector multiplication—with rigorously established error bounds, significantly reducing computational costs compared to traditional auto-differentiation methods. Additionally, the paper derives a corollary for the optimal transport property of the diffusion-ODE deduced map and validates this property through numerical experiments on various noise schedules, demonstrating enhanced accuracy in tasks like likelihood evaluation and adjoint optimization. Claims And Evidence: I have a problem with the paper's main claim that JVP cannot be calculated effectively, which motivates the authors to train an additional network. More specifically, they claim that the time complexity is $O(d^2)$ and infeasible. However, both Pytorch and JAX provide forward-mode autodiff, which can be used to calculate JVP very efficiently (e.g. Pytorch with torch.func). Loosely, it requires only 2 forward passes, which is faster than a single optimization step (1 forward, 1 backward at least) on the same network. If the model evaluation is required anyway, then the overhead is just 1 forward pass. Thus, training a network to calculate the JVP seems unfavorable and unscalable. Even without forward-mode autodiff, how about approximating it with numerical methods? They may not be accurate, but I think it is a reasonable baseline that needs presenting. Methods And Evaluation Criteria: They make sense to me. Theoretical Claims: I checked the theoretical claims, though not their proofs in detail. I do not find any problems. Experimental Designs Or Analyses: I do not have problems with them. Supplementary Material: No, I did not review the supplementary material. Relation To Broader Scientific Literature: Authors proposed a new way to calculate the trace of diffusion Fisher. Essential References Not Discussed: Not that I know of. Other Strengths And Weaknesses: Even without considering the problems listed in Claims And Evidence. Training a separate nontrivial network for the use cases listed in the paper feels too heavy. I suggest the authors justify the additional cost better with more practical and popular use cases. Other Comments Or Suggestions: Given my concerns stated before, I cannot recommend acceptance of this paper. However, there are claims that I enjoy learning, e.g. Prop 1, and the paper is well-written and easy to follow. Questions For Authors: 1. The adjoint optimization is an interesting topic, which I do not know very much about. Is it true that the prior methods all use the highly inefficient way of calculating the JVP? I wish the authors could go into more detail here, as I think this setting/use case has the most potential in practice. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Thank you for your valuable feedback! We will answer your concerns/questions one by one. > Concern 1: I have a problem with the paper's main claim that JVP cannot be calculated effectively, they claim that the time complexity is $O(d^2)$... Please allow me to humbly clarify that we didn't claim a single JVP's time complexity to be $O(d^2)$. Instead, we stated that calculating the diffusion Fisher trace using JVPs has an $O(d^2)$ complexity. The reason is that to obtain each diagonal element of the diffusion Fisher matrix, one JVP operation is needed. As computing the full trace demands all $d$ diagonal elements and each JVP has $O(d)$ complexity, the total complexity for $d$ JVPs is $O(d^2)$. In the context of accessing the diffusion Fisher trace, previous methods rely on $d$ JVP operations. In contrast, our DF-TM method only requires one forward pass through the learned trace network to access the diffusion Fisher trace, which is notably more efficient than the traditional multiple-JVP approach. In the adjoint scenario, previous methods use a JVP to compute the adjoint term. Our DF-EA approximation method eliminates this JVP, making it marginally more efficient than the traditional method. Furthermore, accessing the diffusion Fisher via JVP is a black-box approach without any accuracy guarantee. Conversely, our DF-TM and DF-EA methods exploit the analytical structure of the diffusion Fisher and offer theoretical guarantees. > Concern 2: how about approximating it with numerical methods?... While numerical methods for JVP and trace evaluation are inaccurate and inefficient in high-dimensional scenarios, as discussed in line ~1281. We appreciate your suggestion and agree that incorporating these as baselines enhances the clarity of our experiments. So, we've added two numerical methods, Finite Difference and Hutchinson's Trace Estimation, as baselines in the toy NLL evaluation experiment: Table 2: The relative error of NLL evaluation. \|Methods\|t = 1.0\|t = 0.8\|t = 0.6\|t = 0.4\|t = 0.2\|t = $t_{\min}$\| \|-\|-\|-\|-\|-\|-\|-\| \|Finite Difference\|20.54%\|44.57%\|60.68%\|79.53%\|83.08%\|94.87%\| \|Hutchinson\|11.28%\|10.01%\|16.12%\|23.79%\|53.02%\|71.85%\| \|JVP\|6.68%\|5.79%\|10.46%\|20.13%\|51.14%\|70.95%\| \|DF-TM (Ours)\|3.41%\|4.56%\|4.13%\|4.28%\|5.33%\|5.81%\| It is shown that our DF-TM outperforms these numerical methods. > Concern 3: Training a separate nontrivial network for the use cases listed in the paper feels too heavy... - In adjoint applications, our DF-EA is training-free. - In NLL evaluation, our DF-TM incorporates an additional trace matching network, only bringing moderate costs: - The trace network is scalar-valued and demonstrates a much faster convergence compared to the main network, as shown in Fig. 1. In Laion-2B dataset, the main network of SD-1.5 needs 100,000 GPU hours, while the trace network only 3000, just 3% of the main network's training cost. - The trace network shares the same input as the diffusion network, allowing it to use a shared backbone of $\epsilon_\theta$ for feature extraction, and only necessitates the training of an output head. We plan to explore and implement this promising approach in our future research. Thus, DF-TM can leverage off-the-shelf pretrained diffusion models and only needs to train a small trace network as a "plug". > Question 1: Is it true that the prior methods all use the highly inefficient way of calculating the JVP... In prior adjoint methods [1][2], a JVP operation is required at each step. Usually, these methods use the official PyTorch auto-differentiation tools to compute the JVP. Our DF-EA approximation method circumvents the need for this JVP calculation, though the efficiency gain is limited. The main advantage of DF-EA in adjoint optimization lies in its accuracy, leading to better scores and visual effects, as demonstrated by the qualitative comparison in Fig. 4 and the quantitative comparison in Fig. 3. In the revision, we'll add more details on prior adjoint methods and their applications. [1] Pan, Jiachun, et al. "Towards accurate guided diffusion sampling through symplectic adjoint method." arXiv preprint arXiv:2312.12030 (2023). [2] Blasingame, Zander W., and Chen Liu. "AdjointDEIS: Efficient gradients for diffusion models." NeurIPS 2024. --- Rebuttal Comment 1.1: Comment: Thanks for the clarification. My concerns have been resolved, and I have raised my score accordingly. --- Reply to Comment 1.1.1: Comment: Dear Reviewer mnN8, Thank you very much for your thoughtful evaluation. We are incredibly grateful for your discerning insight, reflecting your deep understanding and high standards. Your positive assessment means a great deal to us. If you have any further suggestions for how we can improve our work and potentially improve your evaluation, please do let us know! Best regards! Wishing you a good day.	Summary: This paper addresses the challenge of efficiently accessing the diffusion Fisher information (DF) in diffusion models (DMs). Based on the analytical formulation of the diffusion Fisher, the authors propose two novel algorithms: DF Trace Matching (DF-TM) for efficiently estimating the trace of the DF, and DF Endpoint Approximation (DF-EA) for efficient matrix-vector multiplication with the DF. DF-TM trains a neural network to estimate the diffusion Fisher while DF-EA approximates the drift term through the learned score function. The paper provides theoretical error bounds for these approximations and showcases their superior accuracy and reduced computational cost in experiments on likelihood evaluation and adjoint optimization. Furthermore, leveraging their outer-product formulation, the authors show that their approach can be used to numerically verify the OT property of the diffusion-ODE derived map under various conditions. ## Update after rebuttal - Most concerns have been clarified during the rebuttal. - As an empirical likelihood estimation method, the proposed method showed improved accuracy based on low-dimensional experimental results. However, the practical significance of the method, based on the presented empirical evidence (Fig 2-4), remains somewhat unclear to me. - The error bounds appear vacuous due to singularity. However, I admit that this issue originates from a fundamental limitation inherent to diffusion models—specifically, the singularity associated with the denoising score matching objective—rather than a flaw unique to the proposed method. - Overall, I view this paper as borderline. However, considering its potential to inspire future research in the community, I would be supportive of acceptance if the other reviewers believe it's worth publishing. Claims And Evidence: Yes. Methods And Evaluation Criteria: Yes, it makes sense. Theoretical Claims: Yes, I checked the proofs for Proposition 1 & 2. Experimental Designs Or Analyses: - In the toy problem reported in Table 2, it is unclear how the ground truth NLL is obtained. Supplementary Material: There is no supplementary material. Relation To Broader Scientific Literature: This paper proposes a novel approach to estimate the diffusion Fisher. Essential References Not Discussed: N/A Other Strengths And Weaknesses: Strength - The proposed DF-TM is efficient and effective in terms of estimating the likelihood of an observed sample. - The proposed method enables OT verification of diffusion models, which is an interesting application. Weaknesses - The bound in Proposition 5 is vacuous especially when t is small. NLL evaluation requires integration over [0, T] which means the overall approximation error bound of NLL will blow up. - In the Dirac setting that the authors focus on, the direct likelihood evaluation becomes almost trivial. The likelihood of an observed $x$ is zero if $x$ is not one of the $y_i$; is 1 / N i f $x$ is one of the $y_i$. Therefore, there is a gap from the typical challenges in generative modeling where the data distribution is general and we have only finite data samples. The paper should focus on the actual setting in the generative modeling. - In the adjoint improvement task, the visual quality gain from proposed DF-EA adjoint is negligible. Other Comments Or Suggestions: - Line 145: “outer-product sums We first” needs a period → “outer-product sums. We first”. - Line 153: “in (Lu et al., 2022a)”. Please use inline citation when it is part of the sentence. - Eq. (7) uses the second derivative to represent Hessian which is confusing. Please check out the standard the notation for [Hessian matrix](https://en.wikipedia.org/wiki/Hessian_matrix). Questions For Authors: - The valuable setting in generative modeling is where we have finite samples from the general data distribution. Can the authors extend Proposition 4,5,6 for this setting? - In the toy problem, how do you compute the ground truth NLL from the dataset? Code Of Conduct: Affirmed. Overall Recommendation: 2	Rebuttal 1: Rebuttal: Thank you for your valuable feedback! We will answer your weaknesses/questions one by one. > Weaknesses 1: The bound in Proposition 5 is vacuous when t is small... It is true that as $t$ approaches $0$, the bound in Proposition 5 will be ill-defined and blow up due to division-by-zero. This concern is also raised by Reviewer a1EQ. We argue that this problem, which has been referred to as the singularity issue in previous literature [1][2], stems from the inherent characteristics of diffusion models rather than flaws in our derivations. A deep exploration of the singularity problem remains an open question, which we will investigate in our future works. Practically, we adopt the approach in [3], where the diffusion sampling path ended at $t_{\min} = 0.005$ instead of $t_{\min} = 0$. This circumvents potential blow-up effects of singularity issues and results in a well-defined bounded NLL. We briefly discussed this singularity issue on line 1242 of the original paper. In our revision, we will provide a more detailed discussion and clarification of our handling. [1] Zhang, P, et al. Tackling the singularities at the endpoints of diffusion models. CVPR 2024. [2] Yang, Z, et al. "Lipschitz singularities in diffusion models." ICLR 2024. [3] Song, Y, et al. Consistency Models ICML 2023. > Weaknesses 2: In the Dirac setting, the likelihood evaluation becomes trivial... We derive the theory within the Dirac setting to simplify the formulations and make them easier to follow. We also present the derivations under the general setting in the appendix. Remarkably, both the Dirac and general settings yield the same forms for the DF-TM and DF-EA methods. All derivations within the Dirac setting can be straightforwardly adapted to the general setting by replacing discrete summations with general integrals. The underlying ideas and mechanisms are identical. The Dirac case can be regarded as a collection of finite Monte-Carlo samples drawn from a general distribution. In the mean-field limit, the Dirac case converges to the general case. To prevent misunderstandings, we will revise all propositions in the main body of the paper to the general setting. > Weaknesses 3: In adjoint task, the visual quality... In Fig. 4, the DF-EA method contributes to (left) a higher Laion-Aes score, as evidenced by a smoother visual effect, and (right) a higher pick-score, reflected in enhanced colorfulness and more detailed features. Since visual effects can be subjective, we also present a quantitative demonstration of the score improvement brought about by DF-EA in Fig. 3. > Suggestions: Line 145...Line 153...Eq. (7)... We apologize for the oversights. We have now corrected the typographical errors and adopted standard Hessian notation for Eq. 7: $\left(F_t(x_t,t)\right)_{i,j} := - \frac{\partial^2 \log q_t(x_t, t)}{\partial x_t^{(i)} \partial x_t^{(j)}}$, where $x^{(i)}$ denotes the i-th element of vector $x$. > Question 1: ...Can the authors extend Proposition 4,5,6 for this setting? Yes, our Proposition 3,4,5,6 can be extended to the general setting and result in the same DF-TM and DF-EA method. Suppose we have $m$ samples from a general initial distribution $q_0$. - Proposition 3 (general version): The trace of the diffusion Fisher for the diffused distribution $q_t$, where $t\in(0,1]$, is given by: $ \mathrm{tr}\left(F_t(x_t,t)\right) = \frac{d}{\sigma_t^2} - \frac{\alpha_t^2}{\sigma_t^4}\left[ \int w(y) \|\|y\|\|^2dq_0(y) - \left\\|\int w(y) y dq_0(y)\right\\|^2 \right] $ - Proposition 4 (general version): $\forall (x_t, t) \in \mathbb{R}^d \times \mathbb{R}^{+}$, the optimal $t_\theta(x_t, t)$ trained by Algo. 1 are equal to $\frac{1}{d}\int w(y) \|\|{y}\|\|^2 dq_0(y)$. - Proposition 5 (general version): The approximation error of DF-TM is at most $\frac{\alpha_t^2}{\sigma_t^4}\delta_1 +\frac{1}{\sigma_t^2}\delta_2^2$. - Proposition 6 (general version): The approximation error of the DF-EA linear operator, is at most $\frac{\alpha_t^2}{\sigma_t^3}(2\mathcal{D}_y^2+ \sqrt{d}\delta_2)$ Note that, in Proposition 5 & 6, the approximation error induced from the finite number of $m$ samples is absorbed into $\delta_1$ and $\delta_2$. We'll include the general-version propositions and their proofs in the revision. > Question 2: In the toy problem, how do you compute the ground truth NLL from the dataset? In the toy experiment, we adopt the method in [1] and approximate the true NLL following Eq. 13. We use Euler discretization over 1000 timesteps for simulation and 5000 data samples per timestep to approximate the right-hand side term of Eq. 13. This setup aims to ensure NLL approximation accuracy. We apologize that the description in line ~1096 is rather simplistic. In the revision, we will provide a more comprehensive description. [1] Lu, Cheng, et al. Maximum likelihood training for score-based diffusion odes by high order denoising score matching. ICML 2022. --- Rebuttal Comment 1.1: Comment: Thank you for the clarification. However, I believe further clarification on the singularity issue is still necessary. - For the Dirac setting, the singularity at time 0 is inherent, which cannot be addressed as discussed in [1]. However, this is not the case for general data distributions with finite second moments. - To illustrate concretely, consider a simple example where the data distribution is Gaussian $p_0(x) \sim \mathcal{N}(0, I)$ and linear noise schedule $\sigma(t)=t$. The score function at time t is $\nabla\log p_t(x_t)= - \frac{1}{1+t^2}x_t$, which is well-defined for all t. There is no singularity in this setting, even at 0. Therefore, it is unclear to me why the provided results of the general version (finite second moments) have singularity at time 0. - Therefore, I would like to request the authors to write down the concrete derivations for the general setting and point out the source of singularity in the general setting. It would also be helpful if you could work through the Gaussian example above and indicate why (or why not) the singularity appears. - Regarding the cited references, - The intrinsic singularity issue discussed in [1] appears only in the Dirac setting. - [2] only focuses on the singularity issue caused by specific noise schedule and network preconditioning. - Thus, neither reference fully accounts for the singularity behavior in the general finite-moment case discussed in this paper. - BTW, Eq. (12) it appears to be a placeholder ("general setting") without an actual expression. Please correct this for completeness. [1] Zhang, P, et al. Tackling the singularities at the endpoints of diffusion models. CVPR 2024. [2] Yang, Z, et al. "Lipschitz singularities in diffusion models." ICLR 2024. --- Reply to Comment 1.1.1: Comment: Dear Reviewer V5LL We sincerely appreciate your profound reflection on the theory of diffusion models. Your concerns regarding the singularity issue of diffusion models demonstrate a deep understanding of this complex field, and we highly value your insights. We will first conduct a comprehensive analysis of the two primary sources of the singularity problem in diffusion models when $t \to 0$. Subsequently, we will provide a detailed examination of your example. Two sources of singularity: - Source 1: Discontinuity of the data distribution, leading to the ill-defined score $\nabla\log p_0(x_0)$. Due to the Radon–Nikodym theorem [1], $p_0$'s log-density function must be absolutely continuous (a.c.) with respect to the Lebesgue measure on $\mathbb{R}^d$ to ensure a well-defined score $\nabla\log p_0(x_0)$. Notably, having finite second moments is not enough to guarantee that a distribution has a well-defined score. Distributions with finite second moments can still possess discontinuous components. Absolutely continuous property is needed to cut off this source of singularity. - Source 2: The design of $\epsilon$-prediction of diffusion models parameterization, leading to divide-by-zero of $\sigma_0$. Current diffusion models generally do not use the network to directly match the score $\nabla\log p_t(x_t,t)$. Instead, they use a network $\epsilon_\theta(x_t,t)$ to match a scaled version of the score, specifically $\epsilon^{\}(x_t,t)=-\sigma_t\nabla\log p_t(x_t,t)$, which is known as $\epsilon$-prediction. The score approximated by the learned network is then $\nabla\log p_t(x_t,t) =-\frac{\epsilon^{\}(x_t,t)}{\sigma_t}\approx-\frac{\epsilon_\theta(x_t,t)}{\sigma_t}$. The score $\nabla\log p_t(x_t,t)$ near $t=0$ can be theoretically obtained by calculating $\lim_{t\to 0}-\frac{\epsilon^{\}(x_t,t)}{\sigma_t}$. However, both $\lim_{t\to 0}\epsilon^{\}(x_t,t)=0$ and $\lim_{t\to 0}\sigma_t=0$, making this limitation hard to get. Moreover, we also do not have access to $\epsilon^{\}(x_t,t)$ in practice. We can only approximate it via $\epsilon_\theta(x_t,t)$. Due to the network's matching error, $\epsilon_\theta(x_t,t)$ may not converge to $0$ as $t\to 0$. This is precisely why calculating the score or other quantities using the learned $\epsilon_\theta(x_t,t)$ near $t=0$ leads to a blow-up divide-by-zero result. Most existing off-the-shelf pretrained diffusion models, such as SD-15, SD-2base, SD-XL, and PixArt-$\alpha$ all adopt the $\epsilon$-prediction parameterization. Hence, our analysis on diffusion Fisher primarily focuses on this widely-adopted scenario and encounters the singularity issue. In practice, our DF-TM and DF-EA algorithms end the sampling path at $t_{\min}=0.005$, bypassing the singularity issue. [1] Folland G B. Real analysis: modern techniques and their applications[M]. John Wiley & Sons, 1999. > Question 1:* consider a simple example where the data distribution is Gaussian $p_0(x) \sim \mathcal{N}(0, I)$ ... Your derivation is correct. When the data distribution is Gaussian, i.e., $p_0(x)\sim\mathcal{N}(0, I)$ and $\sigma_t = t$. The score is always well-defined as $\nabla\log p_t(x_t,t)=-\frac{1}{1 + t^2}x_t$. This analytical score has no singularity issue because $\lim_{t\to 0}\nabla\log p_t(x,t)=\lim_{t\to 0}-\frac{1}{1 + t^2}x=-x$ for any $x$. However, if we use $\epsilon$-prediction to learn this score, a troublesome singularity issue will occur. The $\epsilon$-prediction scaled score takes the form of $\epsilon^{\}(x_t,t) = -\sigma_t\nabla\log p_t(x_t,t)=\frac{t}{1 + t^2}x_t$, which converge to $0$ as $t\to 0$. But the learned $\epsilon_{\theta}(x_t,t)$ will have matching errors compared to $\epsilon^{\}(x_t,t)$ and will not be exactly $0$ as $t\to 0$. To estimate the score $\nabla\log p_t(x,t)$ as $t\to 0$ in practice, we can only calculate $\lim_{t\to 0} \frac{\epsilon_{\theta}(x_t,t)}{\sigma_t}$, which results in a divide-by-zero error. In summary, in this Gaussian case, the underlying analytical score has no singularity issue. However, attempting to obtain it through an $\epsilon$-prediction network gives rise to singularity issues. Unfortunately, in practice, we do not know the analytical score; we only know the learned $\epsilon$-prediction network. > Question 2: BTW, Eq. (12) it appears to be a placeholder ("general setting") without an actual expression... Thanks for your suggestion. We follow your kind advice to write out the detailed definition of the general finite second moments distributions as follows: $$ q_0\in \mathcal{P}(\mathbb{R}^d),\quad \int_{\mathbb{R}^d} \|\|x\|\|^{2} q_0(x)dx<\infty $$ We will fix this in our revision. If Reviewer V5LL still has further concerns, we would appreciate it if you could update them in the Rebuttal Comment. We are more than willing to provide further detailed responses. Wish you a happy day!	null	null	null	null	null	null	null	null
IRBridge: Solving Image Restoration Bridge with Pre-trained Generative Diffusion Models	Accept (poster)	Summary: This work presents an image restoration framework IRBridge. IRBridge connects the bridge model with the diffusion process of the generative diffusion model by introducing a transition equation, thereby enabling direct utilization of the pre-trained generative model for image inpainting. This methods transforms the state of the bridge model into that of the generative diffusion model through forward and backward transitions, and then exploits the powerful prior knowledge of the generative model for image inpainting. The experiments in the paper demonstrate that IRBridge performs better in various image restoration tasks and exhibits superior robustness and generalization capabilities. Claims And Evidence: Yes, this work presents a rather detailed theoretical derivation process of the transition equation and a reasonably well-structured introduction to the framework construction of the IRBridge. Methods And Evaluation Criteria: Yes, this work presents a relatively rich set of comparative experiments to verify the performance of IRBridge and conducts a certain degree of analysis on the experimental details. Theoretical Claims: Yes, I perused the introduction of the bridge model in the article and the theoretical derivation process of the transition equation thus elicited. Apart from some minor issues (detailed in suggestions), the argumentation is relatively sound. Experimental Designs Or Analyses: Yes, I perused the work's elaboration on the setup of the experiment, the implementation method of the comparative experiment, and the analysis of other details of the experiment. Specific issues regarding the experimental section can be found in the "weaknesses" part. Supplementary Material: Yes, I perused the entire supplementary material, encompassing more detailed proofs, the specific setup of the experiments, as well as the supplementary experimental results and other such contents. Relation To Broader Scientific Literature: In response to the task of image restoration, previous research aimed to more intuitively simulate the transition from low-quality images to high-quality ones. The advancements in generative diffusion models, such as various types of diffusion models, have demonstrated remarkable potential in this tasks. The bridge model has attracted attention as it simulates the stochastic process between two distributions or fixed points. Essential References Not Discussed: No, the paper makes a relatively comprehensive citation of the literature. Other Strengths And Weaknesses: Strengths: 1. The IRBridge framework is novel. It obviates the need to train models from scratch for each degradation type and directly leverages pre - trained generative diffusion models, remarkably reducing the training cost. 2. Through the proposed transition equation, IRBridge can adapt to diverse image restoration tasks and permits the adjustment of hyperparameters during inference to optimize performance. 3. The paper validates the performance and robustness of IRBridge through reasonable comparative experiments, and its performance surpasses that of off-the-shelf methods. Weeknesses: 1. In this work, the selection of hyperparameters is based on empirical methods rather than systematically determining the optimal choices. This brings certain limitations when dealing with some complex degradations or in practical applications. 2. In Figure 3, the innovative points of the article are not well highlighted within the framework of the IRBridge. For instance, the role played by the transition equation in the IRBridge could be emphasized. Other Comments Or Suggestions: 1. There are some inconsistencies in expression. For instance, the vast majority uses ‘timesteps’, while in some places ‘time steps’ is used. It is recommended to maintain consistency here. 2. In the left-hand image of Figure 5, it is rather difficult to discern the values on the abscissa of the two pictures. The numerical range of the timesteps here is of crucial importance. Questions For Authors: 1. Although the IRBridge reduces the need to train models from scratch, multiple iterations are still required during the inference process, especially when dealing with high-resolution images. Is there any comparison or analysis regarding the consumption of computational resources? 2. Is there a test on the image restoration effect of the IRBridge in more complex degradation scenarios? For example, the results of tasks such as real-world degradation tasks to further validate the practicality of the model. 3. Has the work considers reducing the dependence on the initial state estimation by introducing additional prior information from different perspectives (such as degradation models or image structural information)? Or can the estimation errors of the initial state be gradually corrected through iterative optimization? If the weeknesses and questions be adequately resolved, I would be delighted to increase my score. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We are grateful for your positive review! We will carefully address your concerns below. Q1: Empirical selection of hyperparameters We acknowledge that this is a limitation of IRBridge, and we offer two key insights. + As shown in Appendix C, while different choices of timesteps can significantly affect the intermediate states of the diffusion trajectory, their impact on final results is generally limited. This suggests that although we may not adopt theoretically optimal inference hyperparameters, the actual performance loss is often acceptable (~5%). Based on our experience, the hyperparameters used for the inpainting task are effective for most tasks, and we refer it as a default setting. + Recent works have provided ways to systematically optimize hyperparameters under certain metrics. For example, LDSB [1] recently proposed using local Schrödinger bridge to optimize the diffusion coefficients. IRBridge can benefit from it to obtain optimal hyperparameters in the context of relative entropy minimization. While optimal hyperparameters are attainable, we believe that the cost of complex optimization is not cost-effective, as manually designed parameters are typically sufficient. Q2: Inference efficiency and computational resources. In our implementation, we use the SD1.5 model, which processes approximately 7.14 steps per second on a 512×512 image using an RTX 3090 GPU, consuming around 6300MB of VRAM. In [THIS TABLE](https://anonymous.4open.science/r/IRBridge-4181/asserts/table3.md) , we present the performance and inference time of IRBridge under different inference steps. Encouragingly, even with a 75% reduction in inference steps, IRBridge shows minimal performance drop (less than 3%) while significantly reducing inference time (14.2s → 3.4s), demonstrating its potential for improving inference efficiency. Future work can also focus on compression of the pretrained model to further enhance the inference efficiency. Q3: Generalization for real-word degradation. We present the evaluation results on real-world datasets in [THIS TABLE](https://anonymous.4open.science/r/IRBridge-4181/asserts/table2.md). We utilized no-reference image quality metrics to evaluate the performance of the methods. As shown in the table, IRBridge demonstrates a clear advantage over other training-from-scratch methods in real-world scenarios. Compared to the latest method, DCPT (ICLR 2025), IRBridge still achieves a better performance (with average 5.6% performance improved), highlighting its superior performance under real-world conditions. We attribute these improvements to the pretrained generative prior that equips the model with stronger generalization capability. Visual examples are provided [HERE](https://anonymous.4open.science/r/IRBridge-4181/asserts/real/show.md). Q4: Has the work considers reducing the dependence on the initial state estimation by introducing additional prior information from different perspectives? We would like to clarify that, mathematically the dependence on the initial state is solely determined by β in Eq.7. In principle, we only consider the case where β takes its minimum value, as this theoretically implies minimal reliance on x0. However, we are open to the idea of retaining some prior information to reduce dependence on x0. For example, given a known degradation model, a plug-and-play (PnP) [2] style approach can be adopted to enforce observation consistency at each iteration step, thereby reducing the degrees of freedom in estimation. Similarly, in the case of image inpainting, we can follow the strategy of RePaint [3] by directly replacing the corresponding pixels in the generated x0 with the uncorrupted pixels from the original LQ sample, thus lowering the reliance on the model’s estimate of initial state. Q5: Can the estimation errors of the initial state be gradually corrected through iterative optimization? Diffusion-based image generation and restoration methods can generally be viewed as progressively refining their estimate of the initial state during the reverse iteration process. IRBridge, by nature, leverages a pretrained generative model to simulate the reverse process of a restoration bridge. As such, its inference procedure inherently serves to iteratively correct the estimation error of the initial state. Q6: Inconsistences in expression and the quality of images and tables. We sincerely appreciate the reviewer’s thoughtful suggestions! We will address these issues in the revised version. These constructive suggestions are invaluable for enhancing the overall quality of our work. [1] Finding Local Diffusion Schrodinger Bridge using Kolmogorov-Arnold Network, CVPR 2025 [2] Denoising Diffusion Models for Plug-and-Play Image Restoration, CVPR2023 [3] RePaint: Inpainting using Denoising Diffusion Probabilistic Models, CVPR 2022 --- Rebuttal Comment 1.1: Comment: The reviewer sincerely thanks the authors for their rebuttal. After carefully reading the rebuttal, most of my concerns have been solved. However, when I check the show.md, there are lots of blurred points in the output image. Please discuss the potential reasons. Moreover, failure cases should also be showed and discussed. --- Reply to Comment 1.1.1: Comment: We appreciate your insightful feedback! Next, we will address your concerns point by point. Q1: Blurred points in the output image A1. We acknowledge that some output images do exhibit blurriness, and we offer two explanations for this: + 1) The encoding-decoding loss of the VAE. The Stable Diffusion model we use (similar to most large-scale pretrained generative models) relies on a VAE to compress images to alleviate the computational load during pretraining. However, the VAE inevitably loses some high-frequency details. While we exclude the errors introduced by the VAE when computing quantitative metrics, these losses are still reflected in the visualized results. To address this issue, we suggest that the VAE can be fine-tuned to mitigate the errors. For example, [1] proposed a Detail Refinement Module (DRM) to enable direct encoder-to-decoder information transformation through a skip connection. Similarly, [2] introduced a Structure Correction Module (SCM) to reverse VAE-induced distortions. We believe that similar approaches could be adopted to correct the errors introduced by the VAE. To validate our claim, we performed a simple fine-tuning of the VAE and presented the visual results in [Fig. 1](https://anonymous.4open.science/r/IRBridge-4181/asserts/reply.md). We simplified the aforementioned approaches by concatenating encoder features of the LQ image to the corresponding decoder layers, and used a zero-initialized convolutional layer to project the output. As shown, even this simple fine-tuning strategy significantly improves the fidelity of fine details in the output images. In future work, we plan to explore more effective ways to enhance the VAE and make it better suited for IR tasks. + 2) The impact of the training data. The visual results we present are generated by models trained on synthetic datasets. These datasets use hand-crafted degradation models to simulate image degradation, which still exhibit a non-negligible gap from real-world degradations. Although IRBridge demonstrates better generalization to real-world scenarios compared to other methods, we acknowledge that the influence of training data still persists in IRBridge. Some subtle degradations may not be completely removed. Q2: Failure cases should also be showed and discussed. Thanks for pointing that out! We acknowledge that IRBridge has some failure cases. As shown in [Fig.2 and Fig.3](https://anonymous.4open.science/r/IRBridge-4181/asserts/reply.md), we present two extreme failure cases. + 1) Inconsistent color tones. Due to the generative nature of our model and the stochastic inference process (induced by noise added during the forward transition), it tends to produce diverse outputs. In extreme cases, this may result in color tones that are significantly inconsistent with the target image. While this does not affect the visual quality of the output or the performance on downstream tasks (such as object detection), it does lead to a drop in fidelity. Given that our current model is trained purely with the generative objective of DDPM and does not incorporate any restoration-specific priors, we believe that explicitly injecting degradation-related priors could help constrain the model’s degrees of freedom and reduce such inconsistencies (as mentioned in the response to Q4 in the initial review). + 2) Performance bottleneck caused by the quality of training data. In certain datasets (such as the ITS subset of RESIDE), the ground truth images themselves contain degradations, which can mislead the model during training. In our case, since the target images were captured under foggy conditions, IRBridge inherits the imperfect priors present in the original dataset, making it unable to completely remove the degradations. Fortunately, the two failure cases mentioned above are not common. Among all the samples in the low-light enhancement task, only the example shown exhibits a noticeable tonal discrepancy, the rest of the output samples are all consistent with the ground truth. In the revised version, we will add a new section in the appendix to discuss the failure cases and explore potential solutions. We sincerely appreciate your constructive feedback! If you have any further concerns, please don’t hesitate to reach out — we will do our utmost to respond as promptly as possible. Once again, we truly appreciate your positive and constructive feedback! Your suggestions have been tremendously helpful in improving the quality of our manuscript and have also deepened our understanding of the proposed work. [1] Multimodal Prompt Perceiver: Empower Adaptiveness, Generalizability and Fidelity for All-in-One Image Restoration, CVPR 2024 [2] GenDeg: Diffusion-Based Degradation Synthesis for Generalizable All-in-One Image Restoration, CVPR 2025	Summary: This paper argues that the existing diffusion-based restoration methods are based on the standard diffusion process and cannot intuitively simulate the transition from low-quality images to high-quality images. To solve this problem, the bridge model is used. Subsequently, the paper extends the bridge model to the all-in-one image restoration task and conducts experiments. Claims And Evidence: This paper highlights that, it: 1. connects the diffusion model and bridge model in the context of image restoration. 2. trains an all-in-one image restoration bridge. 3. demonstrates its effectiveness. I agree that the first point is the contribution and highlight of this paper, but I disagree with the last two points. The reasons are as follows: - This paper does not clearly show what difficulties must be solved in training an all-in-one image restoration bridge. A model concurrently trained on multiple datasets can achieve somewhat good restoration performance. I don't think `training an all-in-one image restoration model` can be regarded as a contribution. - This paper only compared its method with very few methods. The experiments are seriously insufficient. Methods And Evaluation Criteria: Using pre-trained generation models makes sense in the all-in-one image restoration task. The test benchmark selected in this paper is also representative. Theoretical Claims: The proof of Proposition 3.1 is correct in my view. Experimental Designs Or Analyses: The ablation experiments in this paper are extremely comprehensive, but the comparison with other methods in the main experiment is seriously insufficient. For example, - RDDM [1] and DiffUIR [2]. They modified the forward and reverse formulas of the Diffusion Model and were able to transition from low quality images to high quality images. This paper should compare with them. - DCPT [3]. As a concurrent work, the performance of this paper should be on par with DCPT. (However, based on the results in the main experiment, I strongly suspect that the method proposed in this paper will not be able to achieve the effect of DCPT.) [1] Residual Denoising Diffusion Models. CVPR 2024. [2] Selective Hourglass Mapping for Universal Image Restoration Based on Diffusion Model. CVPR 2024. [3] Universal Image Restoration Pre-training via Degradation Classification. ICLR 2025. Supplementary Material: I mainly paid attention to the theoretical proof in Appendix A and the experimental setup in Appendix D. The theoretical proof is correct, but I have some questions about the experimental setup, please see `Questions For Authors`. Relation To Broader Scientific Literature: I believe the method proposed in this paper is helpful for other ill-posed inverse problems. Essential References Not Discussed: N/A Other Strengths And Weaknesses: Weakness I question the significance of the problem addressed in this paper. ResShift [1], RDDM [2], and DiffUIR [3] have effectively achieved diffusion from low-quality images, providing a better alignment with the physical dynamics of the image restoration process. Furthermore, DiffUIR [3] has also been tested for all-in-one image restoration. The problem tackled in this paper appears somewhat gradual. [1] ResShift: Efficient Diffusion Model for Image Super-resolution by Residual Shifting. NeurIPS 2023. [2] Residual Denoising Diffusion Models. CVPR 2024. [3] Selective Hourglass Mapping for Universal Image Restoration Based on Diffusion Model. CVPR 2024. Other Comments Or Suggestions: Table 1. Why the `Type` is vertical??? Questions For Authors: 1. In lines 319-320, this paper claims that "although IRBridge is not explicitly trained for image restoration tasks". However, Sec.4.1 also claims that "degraded images are directly used as conditions for ControlNet". ControlNet is not trained? or ControlNet is not trained for image restoration? What is the function of this ControlNet? (I notice that Appendix D.1 says that "integrate conditional guidance into the pre-trained Stable Diffusion". However, it just trains image restoration. ) 2. Appendix D.2 does not describe how the training and test sets of the desnowing dataset are divided. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We sincerely appreciate your insightful review and valuable comments! We will carefully address your concerns below. Q1: Insufficient comparative experiments. We have added a [QUANTITATIVE COMPARISON](https://anonymous.4open.science/r/IRBridge-4181/asserts/table1.md) between IRBridge and the suggested methods across different tasks. Since the training code for DCPT has not been released, we directly used the pretrained model provided by the authors for comparison. All results are reported at a unified resolution of 512×512 to ensure a fair comparison. The proposed IRBridge outperforms existing methods on most tasks. While it may underperform on deterministic metrics like PSNR and SSIM due to its generative nature and output diversity (e.g., slight tonal shifts from ground truth), these variations rarely affect perceptual quality, though they impact sensitive metrics. In contrast, IRBridge consistently achieves better FID scores (lower average ~4.97), highlighting its strength in capturing data distribution. Moreover, we present the quantitative results of IRBridge on real-world datasets in [THIS TABLE](https://anonymous.4open.science/r/IRBridge-4181/asserts/table2.md). IRBridge outperforms the latest method DCPT, achieving an average performance improvement of approximately 5.6%. These results demonstrate the generalization ability of IRBridge. Q2: The problem tackled in this paper appears somewhat gradual. We thank the reviewer for their thoughtful comments, and we provide insights from both theoretical and practical perspectives. + Theoretically. The mentioned methods, similar to IRSDE, can be regarded as defining a stochastic differential equation (SDE) that describes the transformation from LQ images to HQ counterparts. They typically train models to estimate the score of the corresponding reverse SDE for image restoration. In contrast, our method explores the use of score estimators from generative SDEs (pretrained DMs) to estimate the score of these SDEs. By leveraging a generative model capable of estimating $p(x_{0} \| x_t^, x_{lq})$, IRBridge can directly solve the reverse SDE defined by methods like IRSDE and GOUB. + Practically.* Our method is the first to enable bridge methods to directly leverage pretrained DMs, whose priors not only reduce the training burden but also provide better generalization (+5.6% vs DCPT in real-world scenarios) , as demonstrated in Q1. Moreover, IRBridge effectively decouples training and inference: by leveraging a DM conditioned on LQ images, IRBridge can solve alternative forms of restorative SDEs, without being constrained to specific diffusion coefficients, enabling greater flexibility. Q3: The role of ControlNet and training issues. The employed ControlNet integrates guidance information from the degraded image, ensuring that the model is directed to generate the desired x0. From another perspective, ControlNet can indeed be seen as performing implicit image restoration, as it models $p(x_{hq} \| x_t^, x_{lq})$. However, we emphasize a fundamental distinction:* ControlNet is trained via conditional score matching, following standard diffusion. Our ControlNet is trained to estimate the score of the SDE associated with a generative diffusion, whereas restoration bridge methods like GOUB are trained to estimate the score of their restorative diffusion . Moreover, these methods also use LQ images as condition for the model to enhance performance. We clarify that IRBridge does not focus on the training of the model itself, yet we acknowledge that its performance depends on the underlying model. The ControlNet we used is a relatively coarse implementation, and other conditional control methods (like UniCon[1]) remain applicable to IRBridge, for fine-tuning the generative model. Future work can explore more effective conditional guidance strategies and guidance modules tailored for IR tasks. Q4: Training an all-in-one image restoration bridge cannot be considered a highlight contribution. We agree that training an all-in-one model on multiple degradation datasets can achieve good results. However, we want to clarify that the main contribution of IRBridge lies in enabling the solution of IR bridges through pre-trained DMs for the first time, rather than training an all-in-one model. Typically, training an all-in-one model requires merging multiple datasets to handle diverse image types, leading to high computational costs. In contrast, IRBridge allows direct leverage of generative priors, significantly lowering the training effort (discussed in Section 4.2). Q5: Table quality and missing details. The desnowing dataset contains 50k samples in both the training and testing sets. We will correct the visual quality of the tables and figures and address the missing details in the revised version. Thanks pointing that out! [1] A Simple Approach to Unifying Diffusion-based Conditional Generation, ICLR 2025 --- Rebuttal Comment 1.1: Comment: I appreciate the author's rebuttal, which answered many of my questions, but I still have some issues: 1. The results of DiffUIR do not seem to be presented in [QUANTITATIVE COMPARISON](https://anonymous.4open.science/r/IRBridge-4181/asserts/table1.md), please add it in time. 2. I noticed that the author emphasized the superiority of the IRBridge in the FID indicator. But when the number of test samples is small, such as Rain100H has only 100 test images and LoLv1 has only 15 test images, the FID indicator is not accurate enough. On the RESIDE SOTS test set (with nearly 500 test images), the FID of IRBridge is also similar to that of DCPT-PromptIR. It seems that IRBridge has not increased significantly compared with DCPT, but has large-scale parameters of pre-trained generative models. 3. I am very curious about the evaluation of `generalization` mentioned in this rebuttal. The generalization research of image restoration models is very important, which may be further emphasized in the experimental section of this paper. For now, I tend to raise the score to 2.5, which means "but could also be accepted" part of the `Overall Recommendation:`. If the authors address my above issues and modify this paper accordingly, I think this paper will meet the acceptance criteria of the ICML conference. --- Reply to Comment 1.1.1: Comment: We appreciate your positive feedback! Next, we will address your concerns point by point. Q1. The results of DiffUIR. A1. We apologize for the delay. We have now included a [QUANTITATIVE COMPARISON](https://anonymous.4open.science/r/IRBridge-4181/asserts/table1.md) with DiffUIR. As shown, IRBridge outperforms DiffUIR across all tasks, with particularly notable improvements in PSNR (+0.606) and FID (−8.872), demonstrating the superiority of our method. Q2. Evaluation of IRBridge Using FID. A2. We sincerely appreciate you pointing this out! We acknowledge the limitation of FID when evaluated on small-scale datasets. In response, We have included additional comparison results on the OutdoorRain [1] dataset, a combined low-light enhancement dataset, and a combined dehazing dataset. Specifically, for the low-light enhancement task, we combined the test set of LOL v1, the training set of LOL v2 [2], and its test set, resulting in a total of 1,115 samples. For dehazing, we merged the original SOTS with the Unannotated subset from RESIDE-β (4,808 samples), resulting in a total of 5,308 samples. Since some of the data lacks ground-truth annotations, we computed the FID using the GT images from the OTS dataset. To the best of our knowledge, DCPT has not been pre-trained on OutdoorRain or LOL v2, and neither has our model, which ensures a fair comparison. The results are as below: \| Dataset \| OutdourRain (2700 Samples) \| Combined LOL (1115 Samples) \| Combined RESIDE (5308 Samples) \| \| -------------- \| ------------------------------ \| ------------------------------ \| ------------------------------ \| \| Method \| PSNR / SSIM / LPIPS / FID \| PSNR / SSIM / LPIPS / FID \| FID \| \| DCPT-Restormer \| 26.79 / 0.8198 / 0.161 / 35.85 \| 24.01 / 0.8641 / 0.059 / 47.55 \| 24.98 \| \| DCPT-PromptIR \| 27.33 / 0.8257 / 0.154 / 30.87 \| 23.87 / 0.8597 / 0.062 / 46.33 \| 25.64 \| \| IRBridge \| 28.57 / 0.8678 / 0.153 / 24.59 \| 25.19 / 0.8967 / 0.058 / 35.87 \| 17.23 \| On larger-scale datasets, IRBridge achieves better performance (Avg. PSNR +5.03%, SSIM +4.7%) compared to DCPT, and achieves a more significant FID improvement (-8.41) on the image dehazing task, demonstrating its effectiveness. Q3. Large-scale parameters of pre-trained generative models. A3. We acknowledge the increased parameter count introduced by the use of pre-trained DMs, which will be a focus of our future work. However, we would like to emphasize that IRBridge offers significantly more efficient training compared to DCPT. Specifically, our model was trained for 10k iterations with a batch size of 12 on a single 3090 GPU, whereas DCPT was trained for 750k iterations with a batch size of 32 on 4 NVIDIA L40 GPUs. Compared to DCPT, our method is actually much more cost-efficient. Q4. The evaluation of generalization A4. We greatly appreciate your constructive feedback! Following your suggestion, we will discuss the generalization capability in the revised `Experiments` section from two perspectives: + Cross-domain Generalization. As mentioned in the paper (Section 4.2), models trained solely on a face dataset using IRBridge demonstrate better generalization to other domains (including indoor and outdoor scenes) compared to models trained from scratch. This highlights IRBridge’s ability to leverage pre-trained priors for improved cross-domain performance, which is important for image restoration tasks, as many IR datasets are limited to specific domains. + Generalization to Real-world Scenarios. We will include in the revision a quantitative comparison between IRBridge and other methods (including the recent DCPT) on real-world datasets such as RealRain-1K, RealSnow, and RTTS, to demonstrate the generalization capability of IRBridge in real-world scenarios. Additionally, we will provide visual results in `Appendix E` to offer an intuitive illustration of its performance under real-world conditions. [1] Heavy Rain Image Restoration: Integrating Physics Model and Conditional Adversarial Learning [2] From Fidelity to Perceptual Quality: A Semi-Supervised Approach for Low-Light Image Enhancement We sincerely thank the reviewer for recognizing our work and for raising the score after our response! Your encouragement means a great deal to us. We also greatly value the comments from the other reviewers and have addressed each of them in the revised manuscript. We hope these improvements will help all reviewers better appreciate the value of our work.	Summary: This paper introduces a new approach for leveraging pre-trained generative diffusion models in image restoration bridges. Traditional image restoration bridge models require training from scratch for each degradation type, making them computationally expensive. This work aims to eliminate that requirement by integrating generative priors into the restoration process. Claims And Evidence: The claims are generally well-supported by evidence, with mathematical analysis and empirical validation. Methods And Evaluation Criteria: Yes, the proposed methods and evaluation criteria are well-aligned with the problem of image restoration. Theoretical Claims: The proof for Proposition 3.1 appears to be correct and complete. Experimental Designs Or Analyses: The designs and analyses appear sound, but some evaluations rely on synthetic degradations, which might not capture the full complexity of real-world scenarios. Supplementary Material: Yes, I reviewed the supplementary material. Relation To Broader Scientific Literature: The paper synthesizes and extends prior work in diffusion-based image generation and restoration bridges by introducing a transition equation that leverages pre-trained generative priors—building on foundational ideas from diffusion models (e.g., Sohl-Dickstein et al., Ho et al.) and restoration frameworks (e.g., IR-SDE, GOUB) to eliminate the need for training separate models for each degradation type. Essential References Not Discussed: None. Other Strengths And Weaknesses: It combines ideas from diffusion-based generative modeling and image restoration bridges by introducing a transition equation that leverages pre-trained generative priors. Its empirical evaluations across multiple restoration tasks demonstrate improved performance and generalization, and the theoretical derivations are presented rigorously. Other Comments Or Suggestions: The method relies on manual hyperparameter tuning for timestep scheduling, and further evaluations on real-world degradations would strengthen its practical relevance. In my view, the main novelty of this paper lies in the transition equation. How does the proposed transition equation differentiate IRBridge from existing image restoration approaches, and in what ways does it offer an advantage over prior diffusion-based restoration methods? Some typos, for example "Critial timsteps" should be "Critical timesteps" in several figures and sections. The iterative nature of IRBridge may lead to slower inference, making it essential to quantify its efficiency. Assessing the trade-off between accuracy and speed would offer valuable insights for practitioners when choosing between IRBridge and other restoration methods. Questions For Authors: Please see the above comments. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We sincerely appreciate your insightful comments! We will address your concerns point by point. Q1: Evaluations on real-world scenarios. We present the [EVALUATION RESULTS](https://anonymous.4open.science/r/IRBridge-4181/asserts/table2.md) on real-world datasets (RealRain-1K for deraining, RealSnow for desnowing, and RTTS for dehazing). As these datasets lack ground truth, we utilized widely-used no-reference image quality metrics (MUSIQ, BRISQUE, NIQE) to evaluate the performance of the methods. As shown in the table, IRBridge demonstrates a clear advantage over other training-from-scratch methods in real-world scenarios. Compared to the latest method, DCPT (ICLR 2025), IRBridge still achieves a better performance (with average 5.6% performance improved), highlighting its superior performance under real-world conditions. We attribute these improvements to the pretrained generative prior that equips the model with stronger generalization capability. Visual examples are provided [HERE](https://anonymous.4open.science/r/IRBridge-4181/asserts/real/show.md). Q2: Inference efficiency. We acknowledge that the iterative nature of IRBridge makes it less suitable for real-time processing. However, its high flexibility allows for improving efficiency by reducing the number of inference steps. We present the performance and inference time of IRBridge under different numbers of inference steps (on a 3090 GPU processing standard 512×512 resolution images). The [TABLE](https://anonymous.4open.science/r/IRBridge-4181/asserts/table2.md) shows that even with a 75% reduction in inference steps, the performance degradation remains minimal (< 3%), demonstrating it’s potential for lowering inference overhead. Additionally, future work could focus on distillation and compression of the pretrained generative model to further reduce the computational complexity of IRBridge and improve its inference efficiency. Q3: Manual Hyperparameter Tuning. We acknowledge that it is a limitation of IRBridge. To address this, we offer two insights: + 1) Manual configuration as a practical solution. In Appendix C, we show the impact of timestep selection strategies across different tasks. Our experiments indicate that although timestep selection impacts intermediate states, it has a minimal effect (~5%) on final performance, suggesting manual tuning is both sufficient in most scenarios. Based on our experience, the timestep schedule used in inpainting task tends to work well for most tasks, which is referred as the default setting. + 2) Systematic hyperparameter selection. Several approaches can provide more principled strategies for selecting optimal parameters under specific considerations. For example, the recent work LDSB [1] proposes using a path prediction network to estimate more suitable diffusion coefficients via a local Schrödinger bridge, thereby improving the performance of pretrained DMs. Similarly, for IRBridge, one could explore optimal timestep scheduling under the context of minimizing relative entropy. For a trade-off between cost and performance, we still recommend using manually selected parameters. Pursuing complex optimization for marginal performance gains is not cost-effective. Q4: How does the transition equation differentiate IRBridge from other approaches, and in what ways does it offer an advantage over diffusion-based IR methods? We would like to elaborate on the contributions of IRBridge from both theoretical and practical perspectives. + 1) Theoretically. IRBridge supports bridging two distinct diffusion processes that share the same endpoints. In contrast to previous IR bridge methods, IRBridge does not define a specific diffusion process tailored for restoration. Instead, it leverages the transition equation to ”substitute“ a pretrained DDPM model in place of a specially trained score network for solving the corresponding SDE. To our knowledge, this is the first work to introduce a pretrained generative model into such bridge-based restoration frameworks, breaking the limitation of prior approaches that require training models from scratch. + 2) Practically. The incorporation of pretrained generative priors endows IRBridge with stronger generalization capabilities, especially in complex scenes or across different data domains. In Q1, we demonstrated the superior generalization ability of IRBridge compared to other bridging methods in real-world scenarios. Additionally, as discussed in Section 4.2, the pretrained model provides a strong initialization, enabling IRBridge to achieve nearly twice the training efficiency compared to methods trained from scratch (e.g., GOUB). Q5: Correction of some typos. We will thoroughly check for spelling errors in the subsequent revision to improve the quality of our manuscript. Your feedback is invaluable for improving our work! [1] Finding Local Diffusion Schrodinger Bridge using Kolmogorov-Arnold Network, CVPR 2025 --- Rebuttal Comment 1.1: Comment: Thanks for the authors' detailed responses. The evaluations in real-world scenarios and the explanation on contributions has addressed my concerns. However, the inference efficiency and the manual hyperparameter tuning remain complex and non-trivial, which I believe are still significant limitations of the work. That said, considering the improvements and clarifications provided, I am willing to raise my score. --- Reply to Comment 1.1.1: Comment: We sincerely appreciate the reviewer’s positive feedback on our work and the increased recommendation score after our response ! We acknowledge that the manual inference hyperparameters currently used in IRBridge are not theoretically optimal. However, we have identified systematic methods to obtain optimal settings under specific considerations. From a cost-effectiveness standpoint, we still advocate for using manually tuned hyperparameters, as they already deliver strong performance with minimal overhead. In terms of inference efficiency, diffusion-based methods are indeed less competitive than regression-based models due to their inherently iterative inference paradigm. Nevertheless, IRBridge has demonstrated the ability to reduce the number of inference steps by flexibly adjusting diffusion parameters, enabling a significantly faster inference process with only minimal performance degradation. Moreover, future work can focus on model distillation and compression to further reduce its computational burden. Once again, we truly appreciate your insightful and constructive comments, which have helped us further improve our work. We will incorporate your suggestions and revise the manuscript accordingly in the next version.	Summary: Traditional image restoration bridge models require training from scratch for each degradation type, limiting efficiency and generalization. Meanwhile, pretrained generative diffusion models are underutilized due to mismatched intermediate states between generative and restorative diffusion processes. This work proposes a transition equation that connects two diffusion processes with the same endpoint distribution. Based on the equation, the IRBridge framework is introduced to directly utilize generative models for image restoration tasks. ## update after rebuttal I appreciate the authors’ detailed response. My main concern regarding the experiments, including the baseline methods and reported performance gains, still remains. Therefore, I maintain my score of 2. Claims And Evidence: Yes, the claims made in the submission are supported by evidence. Methods And Evaluation Criteria: Overall, the proposed method and evaluation criteria, including the benchmark dataset, are reasonable. However, the size of the test data is not specified. Additionally, based on the images in the paper, it appears that the method only supports fixed-size inputs. The authors should provide more detailed explanations on this aspect. Theoretical Claims: Yes, I checked the correctness of the theoretical proofs presented in the paper. I did not identify significant errors. Experimental Designs Or Analyses: Yes, I have reviewed the validity of the experiment design and analysis. Supplementary Material: Yes, I have reviewed the supplementary materials. The supplementary materials provide some implementation details (core code). Relation To Broader Scientific Literature: The core contribution of the paper further enhances the effectiveness of using pretrained diffusion models to complete image restoration. Essential References Not Discussed: Yes, the related works are essential to understand of the context for the key contributions of the paper. Other Strengths And Weaknesses: Strengths: 1. The proposed transition equation concept remove restrictive assumptions in prior work. Eliminating per-degradation training aligns with real-world needs for scalable solutions, making the approach both practical and original in application design. 2. Demonstrates state-of-the-art performance on 6 restoration tasks, with potential for immediate use in photography and autonomous vehicles. 3. The paper is well-structured, with method descriptions presented in a logical and layered manner. Weaknesses: 1. The method is based on IR-SDE and GOUB, with pretrained diffusion priors introduced to enhance performance. However, the performance gains from these priors are unclear. Results on some datasets are missing, and the performance improvement in Deraining and Image Inpainting is very limited. 2. The authors should provide the resolution of the test images and the inference efficiency, as these are important for image restoration tasks. 3. Although the authors have tested six image restoration tasks, the comparisons on these tasks are not sufficiently comprehensive. The authors should compare their method with the latest works. Other Comments Or Suggestions: N/A Questions For Authors: Please see the weaknesses. Code Of Conduct: Affirmed. Overall Recommendation: 2	Rebuttal 1: Rebuttal: We are grateful for your valuable comments, which are helpful for improving our manuscripts. Below, we will address your concerns point by point. Q1: Test image resolution and supported resolution. To ensure a fair comparison, we conducted all comparison experiments at a 512×512 resolution in our paper. However, it should note that the resolution supported by IRBridge depends on the model it employs. For SD1.5’s UNet, it supports resolutions in multiples of 64. Inspired by WeatherDiff, we developed an overlapping patches partitioning scheme to support inputs of arbitrary resolutions. We present [VISUAL EXAMPLES](https://anonymous.4open.science/r/IRBridge-4181/asserts/real/show.md) of IRBridge processing arbitrarily high-resolution real-world images, highlighting its ability to effectively handle high-resolution images without causing performance degradation. Q2: Inference efficiency of IRBridge. With the default setting of 100 inference steps, IRBridge takes about 14.2 seconds to process a 512 resolution image, running at 7.18 steps per second. Notably, since IRBridge decouples model training from inference, it allows flexible specification of both the diffusion coefficients and the number of inference steps. In [THIS TABLE](https://anonymous.4open.science/r/IRBridge-4181/asserts/table3.md) , we present the inference time and quantitative results of IRBridge under different step settings. It is worth noting that even with a 75% reduction in inference steps (14.2s -> 3.4s of inference time), IRBridge still maintains comparable performance (<3% average drop), demonstrating its potential for more efficient inference. Q3: The performance gains from pretrained diffusion priors. The performance gains brought by pretrained priors can be attributed to three main aspects: + 1) Improved Generalization. Pretrained models provide general knowledge about a wide range of image distributions, enhancing the model’s ability to generalize to various scenarios. IRBridge demonstrates better generalization across different data domains compared to methods trained from scratch (as shown in Fig.7). Furthermore, we present the results of IBridge on real-world datasets (see Q4), showing its superior performance compared to other methods, further supporting our claims. + 2) Faster Convergence. As shown in Section 4.2, IRBridge benefits from a favorable initialization provided by the pretrained model, leading to nearly twice the training efficiency compared to training-from-scratch methods such as GOUB. + 3) Better Robustness. Even though we simply adopted a ControlNet trained with a DDPM objective, its performance still outperforms methods trained specifically to estimate the score of a particular SDE. This demonstrates that the pretrained generative prior provides IRBridge with more robust representations, thereby enhancing its overall performance. Q4: Comparison on more datasets and with the latest methods. We provide [QUANTITATIVE RESULTS](https://anonymous.4open.science/r/IRBridge-4181/asserts/table1.md) of IRBridge compared with recent methods, including ResShift [1], RDDM [2], DiffUIR [3], and DCPT [4], across different tasks. Additionally, we present the [QUANTITATIVE RESULTS](https://anonymous.4open.science/r/IRBridge-4181/asserts/table2.md) of IRBridge and the aforementioned methods on real-world degraded datasets, covering image deraining, desnowing, and dehazing. IRBridge outperforms other bridging methods, achieving an average improvement of approximately 3.23% over the latest bridge method DiffUIR, demonstrating that the pretrained generative prior significantly enhances model robustness. Furthermore, IRBridge achieves an overall improvement of about 5.60% over the recent method DCPT on real-world scenarios, confirming that the introduced prior in IRBridge improves the model's generalization across different degradation conditions. We present [VISUAL EXAMPLES](https://anonymous.4open.science/r/IRBridge-4181/asserts/real/show.md) of IRBridge processing real-world degraded images. Q5: The size of the test data is not specified. We present the complete number of training and testing samples for the datasets used in the table below. \| Datasets \| Training samples \| Test Samples \| \| - \| - \| - \| \| Rain100H \| 1800 \| 100 \| \| RESIDE \| 72,135 \| 4,322 \| \| Snow100K \| 50,000 \| 50,000 \| \| Raindrop \| 861 \| 58 \| \| LOL \| 485 \| 15 \| \| CelabA-HQ \| 20,000 \| 20,000 \| We thank the reviewer for the thorough review. These detailed suggestions are invaluable for improving the quality of our manuscript. [1] ResShift: Efficient Diffusion Model for Image Super-resolution by Residual Shifting. NeurIPS 2023 [2] Residual Denoising Diffusion Models. CVPR 2024 [3] Selective Hourglass Mapping for Universal Image Restoration Based on Diffusion Model. CVPR 2024 [4] Universal Image Restoration Pre-training via Degradation Classification. ICLR 2025. --- Rebuttal Comment 1.1: Comment: Thank you for the detailed responses, which have addressed most of my concerns. In the initial version, the method was compared with only two bridging models per task, which I found insufficient. Although the authors have added several recent methods for comparison, the performance improvements in some tasks—such as SSIM and LPIPS on Rain100H, Snow100K, and RESIDE—remain marginal. Taking into account the completeness of the experiments, the method’s performance and efficiency, as well as the evaluations from other reviewers, I decided to maintain my original score. --- Reply to Comment 1.1.1: Comment: Thanks for your valuable feedback. We would like to reiterate and clarify several important points. Q1: The performance improvement. A1. So far, we have conducted comprehensive comparisons with other bridge methods, including IRSDE (ICML 23), GOUB (ICML 24), ResShift (NeurIPS 23), RDDM (CVPR 24), and DiffUIR (CVPR 24). We clarify that IRBridge achieves consistent performance advantages over the latest bridge method DiffUIR across all tasks, with an average improvement of approximately: - PSNR↑: +2.37% - SSIM↑: +0.79% - LPIPS↓: −7.86% - FID↓: −30.39% Even compared to the recent DCPT (ICLR 2025), IRBridge achieves an average performance gain of nearly 5.6% in real-world scenarios. These quantitative results strongly demonstrate the performance improvement brought by introducing pretrained generative priors in IRBridge. In addition, we would like to clarify the significance of the performance improvements. According to the results reported in the original papers: > 1. DiffUIR-L (CVPR 24) improves upon RDDM (CVPR 24) across all tasks by (avg. PSNR +0.818 / 3.05%, SSIM +0.0 / 0.0%) > > 2. GOUB-SDE (ICML 24) improves upon IRSDE (ICML 23) on the image deraining task by (PSNR +0.31 / 0.97%, SSIM -0.0013 / -1.41%, LPIPS -0.001 / -2.12%, FID -0.5 / -2.68%). Therefore, the performance gain of our method is in fact noticeable. Q2: Efficiency. A2 (1) Training Efficiency. Benefiting from the generative prior, IRBridge achieves significantly higher training efficiency. + Compared to the recent pretrained method DCPT, IRBridge requires only 10K training iterations with a batch size of 12 on a single RTX 3090 GPU, whereas DCPT is trained for 750K iterations on 4×L40 GPUs. + Compared to bridge models trained from scratch, IRBridge still demonstrates superior efficiency—for instance, its actual training time is less than 50% of that of GOUB (1 days 3090 GPU vs. 2.5 days 3090 GPU), while achieving better performance. A2 (2) Inference Efficiency. Although IRBridge incorporates a pretrained model leading to a relatively larger parameter count, it allows for flexible adjustment of diffusion process during inference, which enables the use of fewer sampling steps to improve inference efficiency. In contrast to other bridge methods that typically adopt relatively fixed iteration steps, IRBridge can achieve shorter inference time in practice. We present a comparison of inference efficiency with GOUB on a single RTX 3090 GPU in the table below: \| Method \| Inference Speed \| Inference Steps \| Inference Time \| \| -------- \| ------------------- \| --------------- \| -------------- \| \| GOUB \| 8.10 iter / sec \| 100 \| 11.3s \| \| IRBridge \| 7.18 iter / sec \| 25 \| 3.4s \| While each inference step in IRBridge takes longer, the reduced number of steps leads to more efficient overall inference (11.3s -> 3.4s). Based on the above rebuttal, we believe your concerns have been substantively addressed. Finally, we still hope you would kindly reconsider your score. We would like to once again express our sincere thanks for your time and effort in reviewing our work. Your comments have been highly constructive and instrumental in improving the quality of our manuscript.	null	null	null	null	null	null
Compression for Better: A General and Loss-Driven Compression Framework	Reject	Summary: This paper introduces LLC, a LossLess model Compression framework that specifies the permissible error range for lossless model compression through higher-order error bound analysis. LLC is applied to both quantization and decomposition, achieving notable compression results without compromising performance. Update After Rebuttal: In summary, ensuring lossless compression requires that Eq. 7 remains negative and that a solution exists at each layer. The activation value is influenced by input, while the sign of each parameter is determined post-quantization. However, the paper does not address how the existence of a solution is guaranteed. Additionally, the interaction between layers is captured by the second-order Hessian. While the gradient may dominate, this does not imply that the off-diagonal elements of the Hessian have no effect on the results. Prior works, such as BRECQ and QDrop, have explored this aspect, and I do not see a significant theoretical distinction in this paper. After considering the feedback from other reviewers, I have decided to maintain my score. Claims And Evidence: The paper’s claims are supported by experimental results. However, further theoretical validation would strengthen the argument. Methods And Evaluation Criteria: The proposed method is interesting, especially in considering the direction of compression error. Theoretical Claims: I have reviewed the theoretical derivation and found some issues. In particular, I question whether each layer, such as a convolutional layer, can always be represented as \frac{\partial l_k}{\partial h_i} \cdot \delta_i, as assumed in the paper. This directly affects the correctness of the scalar product formulation in Equations (7) and (8), as well as the implementation in the algorithm. The authors may need to provide additional mathematical justification for this step. Experimental Designs Or Analyses: i. Are the calibration dataset and test dataset different? How does the calibration dataset compare to those used in other baseline methods? ii. Does "drop-rate" refer to the compression ratio of model weights? Supplementary Material: I reviewed the supplementary material. Relation To Broader Scientific Literature: This work is relevant to the field of model compression. Essential References Not Discussed: None. Other Strengths And Weaknesses: None Other Comments Or Suggestions: The theoretical foundation of the paper is not entirely rigorous (see theoretical claims). With layer-wise error accumulation, it is unclear whether a lossless compression solution always exists. Specifically, since quantization affects subsequent layers, its joint influence should be considered. However, Equation (3) and subsequent analysis are based on individual sum of error, do not seem to account for this. Moreover, this work presents counterintuitive results. The authors may provide additional details or consider open-sourcing their implementation. Questions For Authors: a) The authors use gradient-based criteria. In the case of quantization, does 2-bit quantization always satisfy the error bound based only on the gradient, as shown in Figure 1? If not, how is lossless compression ensured? b) What are scale_input and scale_weight in Algorithm 1? Do they refer to the scaling factors used for floating-point to integer conversion? What is the exact role of noise in Algorithm 1? The description of the algorithm should be corrected and clarified. c) The authors should specify the layer-wise bit-width and rank configurations for lossless compression. Within a given layer, do all weights share the same bit-width? Code Of Conduct: Affirmed. Overall Recommendation: 2	Rebuttal 1: Rebuttal: Q1: About convolution representation. A1: 1. The convolution layer can be expressed in the first-order differential form[2]. This first-order approximation is applicable to any differentiable operation unit (including conv layers, etc.), and its effectiveness comes from the differentiability assumption of neural networks[1]. The following is a simple proof, Assume that the output $h_i$ of a conv layer is defined by the convolution: $ h_i = (w * x)_i =\sum_j w[i - j]x_j $ where $x$ is the network input, $w[i - j]$ represents the convolution kernel weights, and we introduce a new index $j$ to denote the input position corresponding to kernel computation. $h_i$ is the activation at position $i$. Suppose the input $x$ is perturbed by a small amount $\delta$, i.e., $x \rightarrow x + \delta$. Then, the new convolution output becomes: $ \tilde{h}_i = (w * (x+\delta))_i = \sum_j w[i - j]\Bigl(x_j + \delta_j\Bigr) $ Due to the linearity of convolution, we can split the above sum: $ \tilde{h}_i = \sum_j w[i - j]x_j +\sum_j w[i - j]\delta_j = h_i + (w * \delta)_i $ Thus, the perturbation is: $ \Delta h_i = \tilde{h}_i - h_i = (w * \delta)_i $ To be consistent with the notation in the paper, we denote: $ \delta_i = (w * \delta)_i $ This means that the input perturbation $\delta$ is weighted by the kernel $w$ to yield the output perturbation $\delta_i$. Assuming the loss function $l_k$ is differentiable with respect to the activation $h_i$, a first-order expansion gives: $ l_k(h_i + \Delta h_i) \approx l_k(h_i) + \frac{\partial l_k}{\partial h_i}\Delta h_i $ Replacing $\Delta h_i$ with $\delta_i$ yields: $ \Delta l_k \approx \frac{\partial l_k}{\partial h_i} \cdot \delta_i $ For a detailed derivation and differentiation, please refer to https://www.jefkine.com/general/2016/09/05/backpropagation-in-convolutional-neural-networks/. [1]Goodfellow I et al. Deep learning[M]. Cambridge: MIT press, 2016. [2]Dumoulin V. A guide to convolution arithmetic for deep learning[J]. arXiv preprint 2016. Q2: About accumulation joint impact. A2: The accumulation of layer-wise errors comes from the off-diagonal elements of the Hessian matrix in the second-order terms. Through extensive experimentation, in the first-order neighborhood, we have found that the impact of the second-order terms on the loss is smaller than $10^{-5}$, and the layer-wise accumulated error is similarly smaller than $10^{-5}$. Because the computation of second-order terms is time-consuming, LLC neglects these terms. The joint impact and the summation of multiple errors that you referred to are typically results when the second-order terms dominate, which is different from LLC’s approach. Q3: About the calibration and drop-rate. A3: The calibration dataset is completely different from the test dataset. We follow the existing mixed precision quantization work and keep the calibration set consistent with the existing methods[Zhang et.al]. Drop-rate refers to the compression rate of the model weights. Q4: About the error boundary. A4: After extensive experiments, we have found it is less common for layers quantized to 2 bits. 2-bit quantization does not always satisfy the gradient-based error bound. As shown in Fig 1, when the error caused by ultra-low bit is large, the first-order term still dominates, but the error introduced by the second-order term is non-negligible ($10^{-2}$), it may not ensure lossless compression. This issue has been addressed in the LLC limitation section. Therefore, in such cases, it is necessary to additionally analyze the impact of the high-order term on the model, which is also the next research direction of LLC. Since the purpose of LLC is to ensure losslessness and select a suitable bit width for the layer, if LLC cannot ensure lossless compression under ultra-low bits, it usually increases the bit width (2bit->4bit) to minimize the loss. The experimental results are detailed in Reviewer 7rwL A2. Q5:About noise. A5:$scale_{input}$ and $scale_{weight}$ are the scaling factors used for the FP to Int conversion. In Alg 1, the role of the noise is twofold: (a)During the calibration process, the noise is used to compute the magnitude of quantization errors to ensure that they remain within the differential neighborhood; (b)During the quantization process, the noise represents the quantization error and must remain opposite to the gradient direction. We have updated the algorithm and clarified the symbols. Q6: About configuration. A6: LLC adopts a layer-wise quantization approach, where all weights in a given layer use the same bit-width. This is consistent with existing work. For specific configurations of bit-width and rank, we plan to gradually release the code to provide more information. We have updated the paper as you suggested. However, due to ICML's rebuttal policy, the updated paper will be presented later. I hope the reply can address your concerns and look forward to your feedback.	Summary: This paper proposes a general theoretical framework to achieve lossless compression. The paper uses a loss-driven framework to specify the error range each layer's weight and activation can tolerate. A model compression scheme such as quantization or decomposition can therefore be searched within the error ranges. ## update after rebuttal After checking other reviews and the author's reply, I still think the theortical framework proposed in this work is overly simplified when dealing with piecewise linear activation functions and dealing with cross-layer correlations. The experimental results are also weak in supporting the effectiveness of the proposed work. I retain my score of weak rejection. Claims And Evidence: The derivation of the paper is based on the assumption that the function of the neural network is inherently smooth and differentiable, yet as most models are using ReLU activations, it is unsure if the smoothness condition still holds given the piece-wise nature of the ReLU function. In the noise neighborhood mapping, the treatment in Equ. (5) appears to consider the perturbations in different layers are independent. As this holds for weight perturbation, activation perturbation is correlated to the perturbations in earlier layers. It is not sure how this correlation is taken into the account. Methods And Evaluation Criteria: Loss is reported as the main criteria in the experiments. This makes sense given the target of the propose dmethod is to achieve a lossless compression. However, it appears that a smaller loss does not always lead to a better performance, and the performance improvement over baseline methods is limited. This implies that the objective of controlling loss difference may not be practically useful. Theoretical Claims: Given the assumptions made in the paper, the theoretical derivation of the LLC framework appears to be correct. Experimental Designs Or Analyses: It is unclear which part of the dataset is used for calibrating the noise bound and which part is used for reporting the experiment results. It is mentioned in Sec. 5.1 that "the validation set" is used for calibration, which is a doubtful choice. If the validation set is used for both noise bound calibration and performance evaluation, the proposed method may subject to overfit, where the noise bound is ony effective on the calibration dataset but not generalize. Additionally, the noise bound computation and the optimization within the bound is complicated and may be costly. The cost is only reported for SVD experiments but not for quantization experiments. Supplementary Material: No supplementary material provided Relation To Broader Scientific Literature: This paper follows the line of work that use Taylor Expansion based criteria to estimate the impact of model compression noise to the model loss. Unlike previous work that tries to minimize the loss differnet, this work derives a noise boundary that guarantee a smaller loss. This prespective is novel and not explored before. Essential References Not Discussed: Reference adequate Other Strengths And Weaknesses: Besides what is mentioned previously, the data source of Fig. 1 is also unclear. It is not clear how the noise boundaries in Fig. 1 are computed and what is it's impact on the method. Other Comments Or Suggestions: No other comments Questions For Authors: Is the proposed method overfitting to the calibration dataset? Code Of Conduct: Affirmed. Overall Recommendation: 2	Rebuttal 1: Rebuttal: Q1: About Smoothness Condition. A1: Except at the zero point, ReLU is smooth and differentiable in most regions; its non-differentiability occurs only when the activation value is exactly zero. Since real-world datasets (e.g., ImageNet) typically feature continuous distributions, the activations input to ReLU are also mostly continuous real numbers. This implies that the probability of activations being exactly zero is extremely low, and thus the piecewise nature of ReLU has a negligible impact on the overall optimization process. Therefore, ReLU does not invalidate the overall smoothness assumption, and the theoretical derivation of LLC remains valid. Bengio, Y. On the Number of Linear Regions of Deep Neural Networks. [NIPS2014] Q2: About the correlation of layers. A2: In Equation 5, we have accounted for the inter-layer perturbation correlations, mathematically manifested as the effect of the off-diagonal elements of the second-order Hessian matrix (denoted as $H_{i,j} = \frac{\partial^2 f}{\partial x_i \partial x_j}$). This term reveals some dependency among layers. Q3: About limited loss improvement. A3: 1. First of all, from the perspective of the improvement, the loss improvement is competitive. For example, in ResNet18, as shown in the following table, the data in the table represents the improvement compared with the original model after compression, and the larger the value, the better. HAWQ has a smaller improvement over LLC. The improvement compared with other methods is also competitive. ResNet18\|Acc. Drop$\uparrow$\|Loss. Drop$\uparrow$ -\|-\|- HAWQ\|-0.21%\|-0.74% ACIQ\|-0.14%\|-0.22% LLC\|-0.02%\| +0.13% 2. You mentioned that smaller loss does not always seem to lead to better performance. This is because you have already believed that loss (cross entropy, sequence cross entropy, AUC error, etc.) cannot represent the performance of the model. But in fact, cross entropy or accuracy are all performance indicators that can evaluate the model. You agree with LLC's theoretical framework for loss. As you mentioned, loss is the main criterion in the experiment. Therefore, in LLC's experiments, loss (cross entropy, sequence cross entropy, AUC error, etc.) is mainly used to measure the performance of the model in different tasks. For more discussion on loss, please refer to the answer to m1Ar reviewer. Looking forward to your discussion with us. Q4: About calibration set. A4: Following existing pipelines, we use the ImageNet validation set to assess the noise boundary and the test set for performance evaluation. Since the validation and test sets contain entirely different data, the calibration set is used solely for computing quantization parameters and error boundaries, thus avoiding overfitting to the calibration data. All experimental results in the paper are based on the test set. Q5: About the noise boundary. A5: The data source of Figure 1 is calculated by Eq. 6. In the early stage, we conducted a lot of experiments to calculate the compression boundary. That is, control the size of the introduced noise, measure the applicable range of the differential expansion, and observe the change in loss. The purpose is to analyze the relationship between the introduced noise and the higher-order terms. For example, when the error introduced by the weight is less than 8e-3, the first-order gradient is the main factor affecting the compression performance. Specifically, in this experiment, we mainly perturb the ResNet18, ResNet34, ResNet50, Bert and other models with different error sizes. After the perturbation, different error ranges for the first-order and second-order terms are obtained. The calculation of the noise boundary of the second-order term is complicated. We use the Lanzcos algorithm to restore the second-order Hessian term as much as possible. The calculation time takes several days and the cost is high. However, after repeated experiments, we found that the impact of the second-order term is small within the range of $8\times10^{-3}$, and the time cost is large. Therefore, LLC ignores the calculation of the second-order term and focuses on the first-order term. At the same time, LLC calculates the cost of the noise boundary of the first-order term is extremely small, which takes only about 3-4 minutes. The experimental hardware uses NVIDIA A800 GPU. We show the cost of the quantization experiment in the table below. LLC has higher efficiency in both quantization and decomposition. Model \|ResNet18\|ResNet34\| ResNet50\|BERT -\|-\|-\|-\|- Time(min)\|8.42\|12.66\|14.99\|17.34 We have added the above experimental results to the original text and added a description of the noise boundary in Figure 1 based on your comments. Due to the rebuttal policy of ICML, we are currently unable to display the original paper publicly. This paper will be provided in subsequent stages. Thank you for your suggestions and hope that our answer can address your concerns. Looking forward to your feedback.	Summary: This paper presents a novel theoretical framework, LossLess Compression (LLC), which provides a principled approach to model compression while ensuring that the model’s loss remains unchanged or even decreases after compression. Through extensive experimentation, LLC demonstrates its effectiveness in achieving lossless model compression across various architectures and datasets, achieving compression ratios of up to 70% while maintaining or improving model performance. Update after rebuttal: The author only solved part of my confusion. The authos fails to demonstrate its effectiveness in diffusion models and large multimodal models. I still maintain my decision to weak reject. Claims And Evidence: Claim: "LLC can achieve compression without performance degradation across all models and datasets". The claim that LLC universally prevents degradation is not fully proven: some results (e.g., Table 4, ResNet-18) show minor drops in accuracy after compression. The paper does not explore cases where compression might exceed the lossless threshold, potentially leading to degradation. In addition, the authors does not apply their method to LLM and diffusion models. Claim: "LLC can always find an optimal compression ratio that reduces loss". This claim that loss after compression is always lower than before is too strong. While some cases show lower loss post-compression, this is not universal across all models and datasets. The mathematical formulation relies on first-order analysis, which may not fully capture second-order or higher-order compression effects, particularly in extreme compression scenarios. Methods And Evaluation Criteria: 1. Need for more diverse models. LLC is claimed to be a general framework, but testing on only a handful of architectures does not guarantee universal applicability. It is necessary to test on LLM and diffusion models. 2. The framework assumes first-order approximations are sufficient, but extreme compression (e.g., 1-bit quantization or ultra-low-rank decomposition) might violate these assumptions. Theoretical Claims: The paper formulates model loss as a function of compression noise using total differential, which neglects the second-order terms. It assumes that the Hessian contributions are always negligible, which may not hold in cases where compression induces significant changes. The bit-width selection problem in mixed-precision quantization can be efficiently solved as a grouped knapsack problem. However, the knapsack formulation assumes that bit-width choices per layer are independent, but in reality, inter-layer dependencies exist (e.g., some layers are more robust to quantization than others). Experimental Designs Or Analyses: No extreme compression analysis (e.g., 1-bit quantization, rank-1 decomposition). LLC assumes first-order approximations are sufficient, but no tests explore when this breaks down (e.g., 1-bit quantization or extreme low-rank factorization). No layer-wise sensitivity analysis. Different layers in deep networks tolerate compression differently, but the paper does not analyze which layers benefit most from LLC. Limited model diversity. The paper does not evaluate LLM and diffusion models. These models behave differently than CNNs/RNNs, and LLC may not generalize to them. Supplementary Material: There is no supplementary material. Relation To Broader Scientific Literature: 1. Reformulate quantization as a grouped knapsack problem, which reduces search complexity compared to heuristic-based approaches like HAWQ. Unlike BRECQ, LLC does not require fine-tuning, making it computationally cheaper. 2. Extend loss-sensitive compression methods by providing an explicit mathematical formulation (via total differentials) to define the safe compression region. Unlike HAWQ, LLC does not require second-order Hessian computation, making it computationally cheaper. 3. Provide an explicit compression boundary formulation, improving interpretability compared to prior empirical loss landscape studies, such as Parr & Howard (2018), Ghorbani et al. (2019), Li et al. (2018). Essential References Not Discussed: The paper compares against HAWQ (ICCV'19) but ignores HAWQ-V3 [ICML'21], which further improved Hessian-based bit-width selection. Other Strengths And Weaknesses: Strengths: 1. The paper introduces a novel formulation for compression via total differential analysis, which explicitly models the effect of compression-induced perturbations on the loss function. 2. Unlike many heuristic-based quantization and decomposition methods, LLC derives explicit mathematical conditions under which compression can be performed without increasing loss. 3. Reformulating quantization bit-width selection as a grouped knapsack problem is a novel idea that improves efficiency compared to brute-force search approaches (e.g., HAWQ’s bit-width exploration). Weakness: 1. Overclaimed about universal loss reduction. The paper does not analyze when LLC fails to maintain loss, making the "universal loss reduction" claim too strong. 2. Lack of analysis for extreme compression scenarios. LLC assumes that first-order approximations are sufficient, but this may not hold for aggressive quantization (e.g., 1-bit, 2-bit). The paper does not test LLC at very low bit-widths, making it unclear whether LLC remains lossless under extreme compression. 3. The competing baselines are proposed in several years ago. The authors should compare their method with the latest baselines. Other Comments Or Suggestions: No Questions For Authors: No Code Of Conduct: Affirmed. Overall Recommendation: 2	Rebuttal 1: Rebuttal: Q1:About when LLC cannot reduce loss A1:Regarding the limitations of LLC, we emphasize that the loss reduction achieved by LLC is not exaggerated but based on strictly defined mathematical conditions. This sentence has been mentioned in the advantages of the paper you commented on: LLC has clear mathematical conditions. As described in the paper, LLC can reduce the loss of the model in the differential neighborhood; in section 3, we discussed the effective conditions in the noise neighborhood mapping, which require that the perturbation is small enough to ensure the effectiveness of the total differential expansion. Only in such a differential neighborhood can LLC guarantee the reduction of loss. Once the perturbation exceeds this neighborhood, the influence of high-order terms becomes significant, and LLC can no longer guarantee the reduction of loss, making the total differential analysis no longer applicable, and further analysis of high-order terms is required. Therefore, the effective conditions of LLC are the effective conditions of the total differential expansion. When the significant error caused by extreme compression is introduced, the total differential analysis is difficult to apply, and LLC cannot maintain the loss, which is also mentioned in the limitations of the paper. Q2:About extreme compression and sensitivity analysis A2:Our algorithm is still based on mixed-precision compression, and we use quantization as an example for explanation. First, the purpose of LLC is to find the bit width that can reduce the model loss, so the bit width selected is different according to the tolerance of the layer. LLC is best-effort, that is, when the layer can be extremely compressed (meeting the neighborhood condition), LLC will compress it to ultra-low bits. Taking VGG13 as an example, the following table shows the loss changes of LLC for quantization of the 4th and 8th layers, VGG13(L:1.2726) \|8bit\|4bit\|2bit\|1bit -\|-\|-\|-\|-\| L(#8) \| 1.2689 \| 1.2603 \| 1.2599 \| 2.1599 L(#4) \| 1.2711 \| 1.2709 \| 1.9961 \| 2.6634 The error caused by 1bit significantly exceeds the neighborhood range of these two layers, so 1bit compression cannot be performed. LLC will increase the bit width to 2bit compression. At this time, the eighth layer meets the neighborhood condition and the loss is reduced. However, the fourth layer still exceeds the neighborhood range, resulting in increased loss. Therefore, 4bit compression is finally selected for this layer. This example demonstrates that layers with larger error neighborhoods benefit most from LLC. Secondly, LLC defines "aggressive compression" based on the impact of low-bit errors on the model's loss. Since different layers have varying tolerances to compression, when the error introduced by 2-bit quantization remains within the first-order differentiable neighborhood, LLC can achieve loss reduction with 2-bit compression. As shown in Table 2 of the original paper, some models maintain lossless performance even after 2-bit compression. Q3: About inter-layer dependency A3: Mathematically, the inter-layer dependency primarily stems from the off-diagonal elements $H_{i,j} = \frac{\partial^2 f}{\partial w_i \partial w_j}$ of the second-order Hessian matrix. However, experimental results indicate that within the first-order neighborhood, the contribution of the second-order terms is negligible, and the first-order terms remain dominant. Consequently, within this neighborhood, LLC can reasonably neglect inter-layer dependencies, effectively transforming the bit-width selection problem in mixed-precision quantization into an approximately independent grouped knapsack problem. Q4: About comparison A4: The following table is a comparison with the latest baseline method. LLC is competitive and the accuracy drop is still minimal. ResNet50 \| Orgin Acc. \| Quant Acc. \| Error \| Model Size -\|-\|-\|-\|- HAWQV3[ICML'21] \| 77.72 \| 77.58 \| -0.14 \| 24.5 Qdrop[ICLR'22] \| 76.8 \| 76.65 \| -0.15 \| 24.5 PTMQ[AAAI'24] \| 76.8 \| 76.52 \| -0.28 \| 24.5 LLC \| 75.06 \| 75.04 \| -0.02 \| 24.5 The following table shows LLC's performance on Tinyllama compression on MMLU. LLC still improves accuracy while reducing loss. Due to rebuttal policy we were unable to submit the latest paper, but more results and details have been added to the original paper. LLM\| STEM \| Hum. \| Social. \| Other \| Acc. \| SFT Loss -\|-\|-\|-\|-\|-\|- Orgin \| 26.938 \| 24.378 \| 30.971 \| 26.681 \| 26.904 \| 1.769011 LLC \| 27.469 \| 24.846 \| 31.199 \| 26.959 \| 27.29 \| 1.763389 Due to our lack of familiarity with the neighborhood characteristics of the diffusion model, coupled with the limitations of rebuttal time and calibration datasets, it is currently difficult to quantify and analyze the diffusion model within a limited time. We plan to explore this direction in future work, and hope you understand. Thank you for your suggestions and we look forward to receiving your feedback.	Summary: The paper proposes a general model compression framework named LossLess Compression theoretical framework(LLC), which focuses on reducing the model loss for better model performance. By considering quantization and decomposition as adding noise to the model weights and activations, the loss introduced by model compression on the whole dataset can be represented. With the analytic experiments, the authors find that the first-order term of the Hessian matrix has dominant influence on the loss. Therefore, the higher-order terms of the Hessian matrix is omitted for efficiency in the LLC framework. The authors evaluate the performance of LLC with model quantization and decomposition on both computer vision and natural language processing datasets. As shown in the results, the models compressed with LLC mostly achieves lower loss values compared with the baseline models. Claims And Evidence: Yes. The results show that LLC with quantization and decomposition achieve lossless compression as claimed on different models and datasets. Methods And Evaluation Criteria: Whether the proposed methods make sense depends on the mathematic proofs. I'm not a math expert. Please refer to other's comment. The evaluation criteria including the datasets, models and metrics are reasonable for me. Theoretical Claims: The mathematical proofs for Equation 1,2,...,6 seems reasonable to me. For the remaining proofs, which corresponds to the core design of LLC, please refer to other's comment. Experimental Designs Or Analyses: The results show that LLC with quantization and decomposition achieve lossless compression as claimed on different models and datasets. While it doesn't show outstanding performance in the comparison experiments as shown in Table 3 and 6. In the Table 6, the MobileNet-V2 with LLC achieves the accuracy of 71.89%. It is lower than that of HAWQ (72.90%), which is published in 2019. There should be more comparison results with the state-of-the-art compression methods. Supplementary Material: This paper doesn't have supplementary material. Relation To Broader Scientific Literature: The proposed LLC framework aims to achieve lossless compression. With LLC, the compressed model can even achieve lower loss value compared with the full-precision model. It shows that compression not always leads to degradation, which is the key contribution of the paper. Essential References Not Discussed: None. Other Strengths And Weaknesses: Strengths: 1.The paper provides pseudo code to describe the methods. 2.The time cost of the proposed compression method is relatively low. Weaknesses: 1.There is no illustration about the proposed method to help the reader understand. 2.Inconsistent text format. (page 5) Other Comments Or Suggestions: None. Questions For Authors: 1. As shown in the Table 3, LLC achieves lower loss values but lower accuracy on mobilenet-v2 compared with HAWQ. How to explain the phenomenon? 2. It shows that lower loss value doesn't indicate higher accuracy. Do you think the loss value is a good evaluation metric? Why? Code Of Conduct: Affirmed. Overall Recommendation: 2	Rebuttal 1: Rebuttal: Q1: About the evaluation metrics in Table 3. A1: First, in Table 3, the decrease in loss value represents the decrease in cross entropy. Cross entropy and accuracy represent different evaluation methods. Compared with accuracy, cross entropy can compare the closeness between the probability distribution predicted by the model and the true distribution. That is to say, cross entropy can more carefully reflect the performance of the model on different samples, not only whether it is correct or not, but also the degree of certainty of the prediction. At the same time, accuracy will be dominated by the performance of most categories. Compared with HAWQ, although LLC has a slightly lower accuracy, LLC performs better than HAWQ under the evaluation standard of cross entropy. This shows that lower loss values can reveal more detailed improvements in the probability distribution of the model. Secondly, compared with the original model Mobilenet-v2, LLC not only outperforms the original model in accuracy, but also has a lower cross entropy than the original model. HAWQ outperforms the original model only in the accuracy evaluation metric, but is lower than the original model in the cross entropy evaluation metric. Q2: About loss and accuracy. A2: 1. Different focus. Loss functions remain a valid evaluation metric, such as cross-entropy, sequence cross-entropy, and AUC error, among others. We believe that both cross-entropy and accuracy reflect model performance, regardless of good or bad, but they emphasize different aspects. For our work, as described in Q1, loss functions like cross-entropy are better suitable, making them a more appropriate evaluation standard. 2. Generality metric. As mentioned in the paper, we aim to develop an evaluation method that is applicable to different tasks and technical frameworks to validate the universality of LLC. Since different tasks or models may employ diverse evaluation metrics, and the loss function, as an inherent property of the model, can uniformly reflect the model’s performance across various tasks, using loss as the evaluation metric is the best choice for verifying the universality of LLC. 3. LLC does not target specific forms of loss, but it can steadily reduce losses. LLC is a compression method for loss reduction, that is, compression may lead to performance improvement. In order to prove the versatility of LLC, LLC has been verified on different tasks, data sets, and compression methods. More importantly, there are differences in the loss indicators used in different tasks in this paper, but LLC can achieve the reduction of loss after compression, proving that it is independent of the loss function. Theoretical analysis and experimental results can show that, under the differential framework, LLC implements a method for reducing loss after compression for a variety of losses (cross entropy, sequence cross entropy, AUC error, etc.) and compression techniques (quantization and decomposition). In other words, LLC also provides an explanation for the performance improvement after compression, which is also used as a guide for future compression work. 4. Reasonableness of loss evaluation. Regarding evaluation metrics, we believe that the loss value best reflects the effectiveness of LLC. Because the starting point of LLC is the analysis of model loss, the purpose is to reduce the loss values (cross entropy, sequence cross entropy, AUC error, etc.) on different tasks. It is undeniable that most papers with theoretical analysis start with loss, and theoretical analysis ultimately achieves the purpose of reducing loss. However, in the experiment, although these works may have advantages in other indicators, they avoid the evaluation of loss (such as HAWQ, etc.). So are there certain flaws in such theoretical verification? If these works lead to higher model loss, does it mean that there are certain flaws in the theoretical analysis and it does not match the experimental results? Based on the above concerns, we use loss to evaluate and verify the rationality of the theory, despite similar papers avoiding experiments on loss. Thank you for your valuable feedback. We are honored to discuss this issue with you and look forward to your further comments.	null	null	null	null	null	null
Splitting & Integrating: Out-of-Distribution Detection via Adversarial Gradient Attribution	Accept (poster)	Summary: The authors propose a post-hoc detector, which is an interesting approach, especially given that post-hoc methods generally struggle with robustness against adversarial examples. Their lightweight architecture allows for easy retraining and is practical for deployment. In particular, their method involves splitting the model’s intermediate layers and iteratively updating adversarial examples layer by layer. They then combine the attribution gradients from each intermediate layer along the attribution path from the adversarial examples to the actual input, producing accurate explanations for both in-distribution (ID) and out-of-distribution (OOD) samples. The method is well-supported with formulas and explanations. When compared to other post-hoc methods, it shows some improvements in terms of accuracy, though the improvements are limited. The appendix includes ablation studies that demonstrate the importance of layer-splitting, providing experimental support. Additionally, they report the frames per second of their method, which is on the lower end. The underlying main related work is GAIA [1] and gradient-based OOD detector and [2] for the Axioms and theoretical foundations. The code is developed independently, though OpenOOD, the standardized benchmark for OOD tasks, could have yielded similar results. The work has some weaknesses, such as a limited description of the attack method, and the related work section could be strengthened with more citations. [1] https://arxiv.org/pdf/2311.09620 [2] https://arxiv.org/pdf/1703.01365 ## update after rebuttal I upgrade my score from weak accept to accept. The author(s) showed additional experiments comparing with SCALE, a sota method, where their method is performing better. Claims And Evidence: - They supported their claims experimentally. - not problematic. Methods And Evaluation Criteria: It is not clear to me, why they compared with these post-hoc detectors, although there are more. Theoretical Claims: At proof 2: It is claimed that OOD samples are overconfident in prediction. This is not clear to me, because adversarial examples are can be also very confident. I am not sure if in ln 259 (right column) holds the inequality. Experimental Designs Or Analyses: It is unclear why other methods, such as SCALE, which is one of the most recent approaches, were not included in the comparison. Supplementary Material: Contains an ablation study, which supports their method experimentally. Relation To Broader Scientific Literature: Post-hoc OOD detectors are important and very vulnerable to adversarial example. Essential References Not Discussed: - OOD standard framework: https://github.com/Jingkang50/OpenOOD or https://arxiv.org/pdf/2306.09301 - FGSM attack: https://arxiv.org/abs/1412.6572 or even https://arxiv.org/pdf/2306.09301 Other Strengths And Weaknesses: Strengths: - The focus on post-hoc OOD detection methods, which are at the forefront of OOD detection research, is a notable strength of this work. - The gradient-based approach presented offers a promising and potentially robust method for this problem, making it a strong candidate in the field. Weaknesses: - The term "adversarial noise" may be a misnomer. Typically, "noise" refers to random fluctuations, whereas an adversarial example is a deliberate manipulation of the input. The definition provided in Equation 3 closely resembles the FGSM attack, but it is not properly cited. - In the experimental setup, the attack parameters remain unspecified. Equation 4 introduces a hyperparameter for perturbation strength, but it is unclear whether the perturbation is sufficiently strong to evaluate the method's robustness accurately. - There is no ablation study regarding the effect of adversarial perturbation strength, making it difficult to assess the impact of this variable. - Equation 1 could be enhanced by referencing relevant literature, such as [1]. [1] https://arxiv.org/pdf/2306.09301 Other Comments Or Suggestions: - In Table 2, the value 88.21 should not be bolded for the proposed method, as Rankfeat demonstrates stronger performance. This issue can be easily addressed. - ln 208 - typo: balck --> black Questions For Authors: Dear author(s), thank you for your insightful paper on this important topic. I have a few questions: - What is the rationale behind comparing to the selected post-hoc detectors? Are there more recent methods that could also be considered for comparison? - Is it accurate to state that the attack is essentially an FGSM attack? - Would it be possible to conduct an ablation study to analyze the effect of varying the strength of the generated perturbations? Wouldn't this useful for your method and missing to your ablation study in the appendix? Or do you think that this ablation study is unnecessary and why? After discussion, I might update my score. I hope for insightful discusses. Ethical Review Concerns: none Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: Theoretical Claims: We appreciate the reviewer's suggestions. Our mathematical proofs are all grounded in theoretical foundations. Regarding the reviewer's concern about "OOD samples being overconfident in prediction," we have cited (Nguyen et al., 2015; Hein et al., 2019) on lines 161-164 in our manuscript to support this claim. This perspective is also accepted by GAIA, as illustrated in Figure 1 of the GAIA paper. We hope our response has addressed the reviewer's concerns. Weaknesses: 1. We appreciate the reviewer’s suggestion. Indeed, replacing "noise" with "perturbation" better reflects the deliberately manipulated nature of adversarial attacks. Regarding Equation 3, it can be extended as an untargeted BIM (Basic Iterative Method) attack, meaning that the adversarial example's label differs from the original label and does not need to be manipulated to a specific category. Notably, the difference between BIM and FGSM lies in the iterative process: FGSM generates adversarial examples with a single-step update, whereas BIM performs multiple iterations and projects the perturbations within a predefined bound to control the magnitude of the disturbance. To help readers understand the concept of adversarial attacks (especially BIM), we cited Kurakin et al. (2018) [1] as a reference on line 190. But regarding the understanding of Equation 3, we find the reviewer’s suggestion very constructive, and we will cite [1] at Equation 3 to further support the explanation. [1] Kurakin, A., Goodfellow, I. J., & Bengio, S. (2018). Adversarial examples in the physical world. In Artificial intelligence safety and security (pp. 99-112). Chapman and Hall/CRC. 2. We appreciate the reviewer’s suggestion. For the adversarial attack hyperparameters in Equation 3, we used a learning rate $\eta$ of 0.001 and a fixed number of attack step $T=2$. For the parameter $\epsilon$ in Equation 4, since it is jointly controlled by the learning rate and the attack step, and we have fixed the number of attack step in our experiments, we conduct an ablation study on the hyperparameter learning rate $\eta$ to investigate the impact of different perturbations on our method. For details on the ablation experiment, please refer to Q3 in Questions For Authors. 3. Please refer to Q3 in Questions For Authors 4. We referred to the definition of OOD detection in GAIA [2] to propose our Equation 1. Indeed, we highly appreciate the reviewer’s constructive suggestions. As an open-source and comprehensive OOD detection framework, the OpenOOD has made significant contributions to OOD research. We will refine our manuscript by incorporating the definition of OOD detection at Equation 1 in OpenOOD. [2] Chen, J., Li, J., Qu, X., Wang, J., Wan, J., & Xiao, J. (2023). Gaia: Delving into gradient-based attribution abnormality for out-of-distribution detection. Advances in Neural Information Processing Systems, 36, 79946-79958. Other Comments Or Suggestions: 1&2. We sincerely thank the reviewer for pointing out the errors, and we have addressed this issue. Questions For Authors: Q1. For the selection of post-hoc detectors, we referred to the baselines set in GAIA, which includes gradient-based OOD detection methods such as GAIA and GradNorm, as well as feature representation-based methods like Rankfeat and React, and output-based methods such as MSP and ODIN. Regarding the inclusion of additional comparison methods, we are open to the reviewer’s suggestions and are willing to compare our method with the latest 2024 baseline "SCALE", the results are in the link: https://anonymous.4open.science/r/S-I-F6F7/rebuttal/additional_exp_result.md. It can be seen that our method has better performance than SCALE on each OOD dataset. Using CIFAR100 as the benchmark and a learning rate of 0.001, our method shows a 65.32% improvement in FPR95 and a 28.37% improvement in AUROC compared to SCALE. Q2. In fact, this attack is essentially a BIM attack. Please refer to our response in Weaknesses 1, which we hope will resolve the reviewer's concerns. Q3. We appreciate the reviewer's suggestions and are happy to conduct an ablation study on the learning rate to explore the impact of different perturbation magnitudes on our method. In the Table at link: https://anonymous.4open.science/r/S-I-F6F7/rebuttal/additional_exp_result.md, we vary the learning rate in the range {0.0005, 0.001, 0.0015, 0.002}. It can be seen that our method consistently achieves high AUROC and low FPR95 scores across all OOD datasets under different settings. The performance remains stable, with only marginal fluctuations observed. This demonstrates that our method is robust to learning rate selection and can generalize well without requiring sensitive hyperparameter tuning. We sincerely hope that our response has addressed the reviewer's concerns. We would be truly grateful if the reviewer would consider adjusting the score accordingly.	Summary: This paper addresses the challenge of out-of-distribution (OOD) detection in deep learning by proposing S & I, a novel method based on layer Splitting and gradient Integration via Adversarial Gradient Attribution. While existing gradient-based methods struggle to distinguish OOD samples due to non-zero gradient behaviors, especially in high-dimensional spaces with noisy in-distribution (ID) samples, S & I improves detection by iteratively updating adversarial examples layer by layer and integrating attribution gradients along the attribution path. Experimental results on CIFAR100 and ImageNet demonstrate that S & I outperforms state-of-the-art OOD detection methods, enhancing model robustness and security in unknown and dynamic data environments. ## update after rebuttal I thank the authors for their rebuttal, which has addressed my concerns. I am now pleased to change my recommendation from weak reject to weak accept. Claims And Evidence: Yes, the claims are supported by clear and convincing evidence. Methods And Evaluation Criteria: Yes, the proposed method and evaluation criteria make sense for the problem. Theoretical Claims: I reviewed all the theorems and proofs in the paper and, to the best of my judgment, they appear to be correct. However, there is a possibility that I may have misunderstood something. Experimental Designs Or Analyses: I reviewed the experimental design, including the datasets, models, baselines, and evaluation metrics, and did not identify any obvious issues. Supplementary Material: Yes, I reviewed all sections of the appendix. Relation To Broader Scientific Literature: The key contributions of the paper align with the broader out-of-distribution (OOD) detection literature, particularly in the area of gradient-based OOD detection methods. Essential References Not Discussed: To the best of my knowledge, all relevant works necessary for understanding the paper’s key contributions are properly cited and discussed. Other Strengths And Weaknesses: Other Weaknesses: 1. The proposed method does not appear to significantly outperform the baseline method, GAIA. To better assess the significance of the improvements, it would be beneficial to repeat the experiments multiple times and report the mean and variance of the results. 2. The paper lacks ablation experiments to evaluate the impact of different components in the proposed method. Conducting such experiments would help clarify the contributions of each part of the proposed approach. 3. There is no analysis of the computational complexity of the proposed method compared to the baselines. Providing a complexity analysis would offer valuable insights into its efficiency and practicality for real-world applications. Other Comments Or Suggestions: No other comments. Questions For Authors: I am willing to raise my scores if the authors address the following questions: 1. Does the proposed method demonstrate a significant improvement over the baselines? 2. How do the different components of the proposed method contribute to its overall performance? 3. How does the computational complexity of the proposed method compare to that of the baselines? Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We thank the reviewer for the valuable suggestions. We provide the following responses to the questions in “Questions For Authors”. Q1: We would like to clarify that the insignificant improvement of our method on CIFAR100 does not mean limited effect, but means that our method can achieve the same or even slightly better performance than GAIA on small datasets. Besides, we would like to emphasize that our approach demonstrates significant improvements on the larger-scale ImageNet dataset. This distinction highlights the strength of our method in addressing the challenges of OOD detection in large-scale environments, which is a critical focus of our work. We also want to clarify that current OOD detection metrics such as FPR95 and AUROC have already achieved promising performance across many benchmark datasets. However, our approach prioritizes robustness and reliability in large-scale scenarios like ImageNet, where these challenges become more pronounced. We are pleased to highlight the significance of our method through the practical task of plant OOD detection. Firstly, we selected the ImageNet dataset as the in-distribution (ID) dataset. To perform the plant OOD detection task, we chose the iNaturalist dataset as the OOD dataset. Specifically, we manually selected 110 plant categories from the iNaturalist dataset and randomly sampled 10,000 images for these categories. The related experimental codes and results can be found in our anonymous GitHub repository (https://anonymous.4open.science/r/S-I-F6F7/additional_OOD_samples/). The entire work is fully open-source. The detected OOD samples are stored in the "additional_OOD_samples" folder. Interestingly, the OOD samples detected from the iNaturalist dataset are all plant species that are not present in the ImageNet dataset, demonstrating the effectiveness of our method in plant OOD detection tasks. This result can be further explained by the dataset characteristics: ImageNet is a general-purpose image classification dataset, while iNaturalist focuses on biodiversity and covers a wide range of fine-grained species. For certain visually similar plant categories, such as the Violet category in ImageNet and the Viola sororia category in iNaturalist, conventional OOD detection methods like MSP, ODIN, and GradNorm struggle to distinguish them and often classify OOD samples as ID categories. However, our method can accurately distinguish fine-grained plant species, as evidenced in the additional_OOD_samples folder. We provide the following example for the reviewers’ reference: Detection of angiosperms: The following link shows an OOD sample detected from the iNaturalist dataset, belonging to the Lotus corniculatus category (https://anonymous.4open.science/r/S-I-F6F7/additional_OOD_samples/b51107eaf0608d345a265f623c776706.jpg). The corresponding ID sample from the ImageNet dataset, belonging to the Rapeseed category, is available at this link: (https://anonymous.4open.science/r/S-I-F6F7/ImageNet_rapeseed/1.png). By comparing these two images, it becomes evident that the visual differences between them are minimal, making it challenging for humans to distinguish visually similar plant species. However, our method effectively identifies fine-grained plant species, which has significant real-world implications, such as discovering new plant species or protecting endangered plant populations. Regarding the inclusion of additional comparison methods, we are open to the reviewer’s suggestions and are willing to compare our method with the latest 2024 baseline "SCALE". It can be seen that our method has significantly better performance than SCALE on each OOD dataset. For more details, please refer to Q1 in Questions For Authors at Reviewer 5PTw Q2: We sincerely express that we have provided ablation experiments of the adversarial attack module and layer splitting module in Part B of the supplementary material. By comparing Table 4 and Table 5, it can be proved that adversarial attack module plays an important role. Similarly, by comparing the ablation experiments in Table 3 and Table 5, it can be proved that the layer splitting module also plays an important role. We hope our response can address the reviewer's concerns. Q3: We kindly acknowledge that we have provided a comparison of computational costs in Part C of the Supplementary Materials. We measure the efficiency of our methods using the frame per second metric in Table 6. It can be observed that on the ImageNet dataset, our method is slightly slower than GAIA. However, from the perspective of the main experimental metrics, FPR95 and AUROC, on the ImageNet dataset, our method achieves significant performance improvement. Compared to the computationally similar RankFeat method, our approach not only achieves faster runtime efficiency but also provides more accurate OOD detection. Therefore, we believe the computational cost of our algorithm is an acceptable trade-off. --- Rebuttal Comment 1.1: Comment: After reading the rebuttal, I still have the concern that the proposed method does not significantly outperform the baseline method -- GAIA. Thus, I keep my original scores. --- Reply to Comment 1.1.1: Comment: We appreciate the reviewer’s continued engagement and thank you again for the thoughtful feedback. We would like to respectfully clarify our position regarding the performance improvements over GAIA and the broader contribution of our method. First, as previously noted in the rebuttal, our method demonstrates clear and consistent advantages over GAIA on complex, large-scale datasets such as ImageNet. While improvements on relatively saturated benchmarks like CIFAR-100 may appear marginal due to diminishing returns, on ImageNet, our method consistently outperforms GAIA by over 1%, which we believe is a significant improvement given the maturity and strength of GAIA as a baseline. Moreover, we believe that in the OOD detection field, performance gains are naturally converging, and incremental improvements over strong baselines should be interpreted in the context of both theoretical innovation and robustness to real-world scenarios, not just raw numerical margins. From a theoretical standpoint, we identify a fundamental limitation in GAIA—its use of an ad-hoc attribution baseline (x=0), which lacks generality and may lead to task-dependent misclassifications. In contrast, our method introduces a principled, adversarial-based attribution baseline that is supported by rigorous mathematical reasoning. This not only addresses the attribution inconsistency issues in GAIA but also provides a more robust theoretical foundation for OOD detection, especially under complex distribution shifts. Practically, our method’s value is further demonstrated in a real-world plant OOD detection scenario, where fine-grained distinctions between highly similar species are essential. In such cases, our method successfully identifies subtle inter-class differences that conventional methods often miss. We believe this kind of performance is not only evidence of superiority but also shows how our approach bridges the gap between academic research and real-world deployment, such as in biodiversity conservation. In addition, we respectfully note that the reviewer's concerns in Questions 2 and 3 regarding the contributions of individual components and computational complexity have already been addressed in our original supplementary material. Specifically, Part B contains ablation studies of the adversarial attack and layer splitting modules, while Part C compares the computational efficiency with relevant baselines. We hope this clarifies any remaining concerns. Finally, our method also surpasses the latest 2024 baseline SCALE across multiple datasets, as shown in the table below. This reinforces our claim that our approach is both competitive and forward-looking in this fast-evolving research area. \| Dataset/Model \| Methods \| SVHN \| SVHN \| LSUN \| LSUN \| TinyImageNet \| TinyImageNet \| Places \| Places \| Textures \| Textures \| AVG \| AVG \| \|---\|---\|---\|---\|---\|---\|---\|---\|---\|---\|---\|---\|---\|---\| \| \| \| FPR95↓ \| AUROC↑ \| FPR95↓ \| AUROC↑ \| FPR95↓ \| AUROC↑ \| FPR95↓ \| AUROC↑ \| FPR95↓ \| AUROC↑ \| FPR95↓ \| AUROC↑ \| \| CIFAR100/ResNet34 \| Our \| 15.68 \| 97.06 \| 33.29 \| 94.18 \| 63.71 \| 89.17 \| 16.73 \| 97.17 \| 15.82 \| 97.09 \| 29.05 \| 94.93 \| \| CIFAR100/ResNet34 \| SCALE \| 87.3 \| 74.07 \| 84.8 \| 72.3 \| 74.55 \| 79.64 \| 89 \| 70.08 \| 83.16 \| 73.66 \| 83.76 \| 73.95 \| We sincerely hope that the reviewer can reconsider the significance of our contributions and possible score adjustment, both in terms of performance and theoretical advancement.	Summary: This paper proposes a method called S&I (Splitting and Integration) for improving out-of-distribution (OOD) detection in deep neural networks. S&I introduces two components: (1) layer splitting, which decomposes intermediate layers of the network to iteratively update adversarial examples and reduce gradient instability, and (2) gradient integration, which aggregates attribution gradients along the attribution path from adversarial examples to the input. Experimental setup is followed a previous work GAIA and experiments were conducted across various ID/OOD datasets. Claims And Evidence: not all, see the weaknesses Methods And Evaluation Criteria: yes Theoretical Claims: yes Experimental Designs Or Analyses: yes Supplementary Material: yes Relation To Broader Scientific Literature: The paper could has broader scientific impact on OOD detection, especially for understanding the gradient-based methods, and provides new idea about the OOD detection. Essential References Not Discussed: no Other Strengths And Weaknesses: Strengths: 1. The paper is well organized and easy to read. 2. The paper provides a theoretical analysis of the proposed method. 3. Experiments were conducted on standard protocols and across many benchmarks. Weaknesses: 1. The paper only has marginal improvement over GAIA in average, reflecting that the proposed method is less effective. 2. The motivation is less convincingly described, for the main argument “the non-zero gradient behaviors of OOD samples do not exhibit significant distinguishability”, only a visualization in Fig.2 is presented to support it. Is there any statistic evidence? Considering the marginal accuracy improvement over GAIA, it is highly possible that such a key argument does not in practice, or this may not be the key defect for GAIA. ==================== post rebuttal ======================= After read the rebuttal, the reviewer maintains the initial recommendation. Other Comments Or Suggestions: The FPR numbers in the brackets of abstract and end of section 1 are not easy to understand, suggesting to remove them. Questions For Authors: Can the method extend to other gradient based OOD methods? GAIA was published on 2023, how about the performance compared the state of the art gradient based OOD methods? For the argument presented in this paper “the non-zero gradient behaviors of OOD samples do not exhibit significant distinguishability”, it is unclear how the proposed S&I conquer this problem. Code Of Conduct: Affirmed. Overall Recommendation: 2	Rebuttal 1: Rebuttal: Other Strengths And Weaknesses Weakness1：We thank the reviewer for the valuable comment. We would like to clarify that the insignificant improvement of our method on CIFAR100 does not mean limited effect, but means that our method can achieve the same or even slightly better performance than GAIA on small datasets. Besides, we would like to emphasize that our approach demonstrates significant improvements on the larger-scale ImageNet dataset. This distinction highlights the strength of our method in addressing the challenges of OOD detection in large-scale environments, which is a critical focus of our work. We also want to clarify that current OOD detection metrics such as FPR95 and AUROC have already achieved promising performance across many benchmark datasets. However, our approach prioritizes robustness and reliability in large-scale scenarios like ImageNet, where these challenges become more pronounced. We are pleased to highlight the significance of our method through the practical task of plant OOD detection. For details, please see our response to Reviewer SPNg in Q1. Weakness2：Thanks to the reviewer for the suggestion. We would like to clarify that this view is one of the motivations of our paper. In lines 194-197, we explained that the attribution-based OOD detection method such as GAIA is developed based on the baseline selection of $x'=0$. GAIA checks OOD samples by counting the distribution of non-zero attribution gradients, so the highly OOD nature represented by non-zero attribution gradients has been proven. However, using the black image with x=0 as the baseline will make it difficult to retain the original semantic information of the sample when attributing, and it is easily disturbed by noise, which will cause deviations when counting non-zero attribution gradients, reducing the accuracy of OOD detection. Adversarial samples can retain the semantic information of samples while introducing minimal perturbations, so we designed an adversarial attribution-based OOD detection method by layer splitting and attribution integration, corresponding to the pseudo code of lines 409-414. Since non-zero gradient represents a high confidence OOD sample probability (as expressed by GAIA), it is obvious that the accuracy of calculating non-zero gradient will significantly affect the accuracy of OOD detection. This is the starting point for designing our method, and the performance improvement in extensive experiments (especially on large-scale ImageNet) has proven that our method can more accurately calculate the attribution gradient (i.e., we can obtain more accurate non-zero and zero gradient distribution) to obtain better OOD detection performance. Other Comments Or Suggestions For the FPR numbers in brackets, we hope that the following explanation can help the reviewer’s understanding. Referring to Table 1, we can see that the backbone models are ResNet34 and WRN40, respectively. Therefore, the FPR numbers in brackets represent the results on the WRN40 model. We promise to revise the text to avoid ambiguity. Questions For Authors Q1: Our method can be easily extended to other gradient-based OOD detection methods. By introducing adversarial samples as a baseline, the gradient calculation can be stabilized and noise interference can be reduced. This strategy can be applied to other gradient-based methods (such as GradNorm, GAIA, etc.) to enhance the distinguishability of gradient patterns by generating adversarial samples, thereby improving detection robustness. In addition, layer splitting can alleviate the problem of gradient explosion or cumulative error in deep networks by analyzing the gradient sensitivity of different layers in a hierarchical manner. This module can be independently integrated into other methods, such as decomposing by layer when computing gradient importance and optimizing the detection logic by leveraging the characteristics of different layers (e.g., low-level textures and high-level semantics). Q2: Regarding the inclusion of additional comparison methods, we are open to the reviewer’s suggestions and are willing to compare our method with the latest 2024 baseline "SCALE" [1], the results are in the link: https://anonymous.4open.science/r/S-I-F6F7/rebuttal/additional_exp_result.md. It can be seen that our method has better performance than SCALE on each OOD dataset. Using CIFAR100 as the benchmark and a learning rate of 0.001, our method shows a 65.32% improvement in FPR95 and a 28.37% improvement in AUROC compared to SCALE. [1] Xu, K., Chen, R., Franchi, G., & Yao, A. (2023). Scaling for training time and post-hoc out-of-distribution detection enhancement. arXiv preprint arXiv:2310.00227. Q3: Please see the clarifications in Weakness 2. We sincerely hope that our response has addressed the reviewer's concerns. We would be truly grateful if the reviewer would consider adjusting the score accordingly.	Summary: This paper proposes S & I (Splitting and Integrating), a gradient-based out-of-distribution (OOD) detection method that builds on gradient attribution techniques by leveraging adversarial attacks to refine feature explanations. The core idea is to split neural network layers and iteratively integrate attribution gradients across layers to obtain more robust feature representations for distinguishing between in-distribution (ID) and OOD samples. The approach is empirically validated with strong results, particularly on large-label-space datasets like ImageNet. The authors argue that this method improves model robustness and security in dynamic data environments. --- ## Update after rebuttal As mentioned below, I am happy with the authors response. I will maintain my initial score (Weak Accept). --- Claims And Evidence: Some of the claims made in this submission are that: 1. Adversarial gradient attribution improves OOD detection over GAIA. Although, experiments across multiple datasets strengthen this claim, the paper does not provide an ablation study that isolates the specific impact of adversarial baselines. 2. The paper argues that different network layers focus on different types of features (textures, semantics, etc.), and thus should be split rather than treated uniformly. Unfortunately, the claim lacks theoretical justification beyond intuition. An ablation study comparing different numbers of layer splits (e.g., one split, two splits, all layers) would clarify how much splitting contributes to performance. 3. The authors argue that gradients from different layers should be integrated iteratively to prevent instability. Here too, an ablation comparing results with vs. without integration would clarify how much gradient integration itself improves detection accuracy. 4. It is not clear how much additional overhead does layer-splitting and gradient integration introduce. This also begs the question of whether the method be used efficiently for large architectures. Methods And Evaluation Criteria: The evaluation criteria are mostly appropriate but have gaps. More specifically, I found the methods and evaluation protocol used to be mostly reasonable but I think that additional computational and statistical validation is needed for a complete assessment. For instance, no computational efficiency analysis (runtime/memory overhead) is done to evaluate the efficiency of the proposed framework. No real-world OOD cases (e.g., adversarial or domain-shifted OOD data) are studied to further strengthen the claims made in the paper. Theoretical Claims: The theoretical claims in the paper are mostly plausible but lack full mathematical rigor and empirical validation. The proof that adversarial baselines improve gradient attribution follows a logical argument but does not include empirical verification to confirm that adversarial perturbations consistently enhance feature sensitivity. The claim that layer splitting improves stability is based on heuristic reasoning rather than a formal mathematical justification, as it lacks a precise metric for instability. Similarly, the argument that gradient integration reduces noise assumes variance reduction but does not provide explicit variance bounds or an empirical demonstration of this effect. Finally, the proof that the proposed OOD scoring function is optimal assumes that OOD samples always yield stronger gradients, which is not universally true and requires further validation across diverse datasets. Strengthening these claims with statistical validation, variance analysis, and empirical testing would improve the paper’s theoretical foundation. Experimental Designs Or Analyses: The framework proposed by the authors follows standard OOD detection practices, but there are some critical gaps in validation. While the experimental design follows standard OOD detection protocols, it lacks statistical efficiency benchmarks, ablation studies, and failure case analyses. Addressing these issues would improve confidence in the results. For instance, the method introduces adversarial perturbations + layer-wise gradient integration, which may be computationally expensive, but fails to report per sample inference time analysis and a comparative analysis against baselines. I wish also there were more experiments isolating the effects of adversarial attribution, layer splitting, and gradient integration. Conducting such an ablation study can show which component contributes most to performance gains. Supplementary Material: I didn't get the chance to go over the supplemental material. Relation To Broader Scientific Literature: The paper refines gradient-based OOD detection by incorporating adversarial perturbations and layer-wise gradient integration, linking it to prior work in feature attribution, adversarial attacks, and hierarchical feature processing. While novel, it lacks comparisons to some closely related methods that could strengthen its scientific positioning. For instance, this method is related to energy-based OOD scoring (Liu et al., 2020) and Mahalanobis distance-based scoring (Lee et al., 2018) due to the fact that it scores OOD samples based on gradient density rather than activation energy or distance metrics, but no such comparison is considered in the paper. Essential References Not Discussed: The paper introduces valuable refinements to gradient-based OOD detection but does not cite some key works on gradient stability, adversarial attribution, feature disentanglement, and alternative OOD scoring methods. Addressing these gaps would strengthen its scientific positioning and clarify how it improves upon prior approaches. On gradient-based OOD detection, the work doesn't cite [1], and concerns expressed in [1] seems to contradict some claims made in this current work. On adversarial perturbations, the work doesn't consider the fact that adversarial perturbations may distort attribution maps, as discussed in [2]. Experimentally validating that the attribution gradients of adversarial examples that are integrated in the model do not affect feature quality might be useful. [1] Gradient Stability in OOD Detection (Serrà et al., Hooker et al.) [2] Adversarial Perturbations for Attribution (Etmann et al., Dombrowski et al.) Other Strengths And Weaknesses: The paper is original, practical, and well-explained, but lacks computational efficiency analysis, broader comparisons, and ablations. These missing elements weaken confidence in the method’s impact, but addressing them could make it a strong contribution. Other Comments Or Suggestions: Some equations are referenced without clear explanation of their role in derivations. Please consider adding a short remark before or after. Also, some figures lack descriptive captions. It'd be useful if the authors could clearly explain what is being shown in gradient attribution maps. Questions For Authors: The paper presents a creative combination of adversarial perturbations and layer-wise gradient attribution, making a valuable contribution to gradient-based OOD detection. The methodology is clearly explained and has potential real-world applications. However, the significance of performance improvements, computational cost, and comparison to alternative OOD methods remain unaddressed. Adding runtime benchmarks, broader method comparisons, and failure case analyses would significantly strengthen the paper. Some of the key strengths of this paper are: 1.) using adversarial perturbations as baselines rather than standard black images (as in GAIA), which seems to be a novel refinement over GAIA, and 2.) the proposed method improves OOD detection without retraining, making it feasible for real-world deployment in settings like medical imaging or security applications. The ability to work with pre-trained networks increases its usability for practitioners. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Claims And Evidence: 1. We sincerely state that in Section B of the supplementary materials, we have provided ablation experiments for the adversarial attack module and the layer splitting module. By comparing Table 4 and Table 5, it can be demonstrated that the adversarial attack module plays a significant role in our method. 2. We would like to point out that the statement, "different network layers focus on different types of features (textures, semantics, etc.)" is both intuitive and theoretically supported, as demonstrated in numerous studies [1][2]. GAIA assumes that all intermediate layers have the same influence on the feature maps, which contradicts the hierarchical feature distribution inherent in neural networks. Compared to GAIA's uniform treatment of all layers during attribution, our proposed layer splitting theory offers an innovative contribution by more precisely capturing the feature sensitivity of different layers. Finally, the ablation experiments shown in Table 3 and Table 5 of the supplementary materials already demonstrate that the layer splitting module plays a crucial role in our method. [1] Zeiler, M. D., & Fergus, R. (2014). Visualizing and understanding convolutional networks. ECCV 2014. [2] Yosinski, J., Clune, J., Nguyen, A., Fuchs, T., & Lipson, H. (2015). Understanding neural networks through deep visualization. ICML Workshop on Deep Learning. 3. We would like to point out that comparing the ablation experiments with and without integration does not align with the principles of discrete path integration. According to the formula in line 282: $A=L\left(f\left(x_T\right)\right)-L\left(f\left(x_0\right)\right)=\sum_{i=0}^{T-1} \frac{\partial L\left(f\left(x_{i}\right)\right)}{\partial x_i}\left(x_{i+1}-x_i\right)$, the attribution result $A$ is expressed as the cumulative sum of gradient changes along each point on the path. If layer-by-layer integration is not used and the attribution is only calculated based on the changes between the start and end points, the gradient variations along the path are ignored. This results in an inaccurate attribution gradient distribution, making it impossible to perform the OOD detection task properly, let alone improve detection accuracy. 4. We sincerely state that in Section C of the supplementary materials, we have provided a comparison of computational costs. We use the frames per second (FPS) metric in Table 6 to evaluate the efficiency of the methods. We believe the computational cost of our algorithm is an acceptable trade-off. Methods And Evaluation Criteria Please refer to point 4 in the Claims and Evidence section for the efficiency analysis. We are also pleased to highlight the significance of our method through the practical task of plant OOD detection. For details, please see our response to Reviewer SPNg in Q1. Theoretical Claims We would like to clarify that we have provided extensive mathematical proofs as the theoretical foundation for our method (including but not limited to the claims and proofs of Theorem 1 and Theorem 2). We use Equation 3 to ensure that the adversarial perturbation consistently enhances feature sensitivity. Equations 9 and 10 formally derive the layer splitting strategy from a mathematical perspective. Experimental Designs Or Analyses The analyses of time efficiency, ablation studies, and real-world OOD cases can be found in the above rebuttals. Relation To Broader Scientific Literature We would like to clarify that energy-based OOD scoring has already been used as a baseline for comparison in our paper on line 371, and our method demonstrates significantly better performance. As for Mahalanobis distance-based scoring, since it is an earlier work and it seems that no clear citation link has been provided by the reviewer, we have not included it as a comparison target. We compare our method with the latest 2024 baseline "SCALE". It can be seen that our method has better performance than SCALE on each OOD dataset. For more details, please refer to Q1 in Questions For Authors at Reviewer 5PTw Essential References Not Discussed We appreciate the reviewer's addition; however, it seems that no clear citation link of the two references has been provided. If the reviewer could supply the link, we would be happy to discuss these works. Other Strengths And Weaknesses The efficiency analysis, comparison experiments, and ablation studies can be found in the above rebuttals. Other Comments Or Suggestions We appreciate the reviewer’s suggestions, and we will improve the presentation of the formulas and figures to enhance the clarity of the paper. Questions For Authors The time efficiency analysis, comparison experiments, and real-world OOD case analysis can be found in the above rebuttals. We sincerely hope that our response has addressed the reviewer's concerns. We would be truly grateful if the reviewer would consider adjusting the score accordingly. --- Rebuttal Comment 1.1: Comment: I thank the reviewers for the effort and time they put into the rebuttal. I am happy with the answers and will my original score.	null	null	null	null	null	null
The Devil Is in the Details: Tackling Unimodal Spurious Correlations for Generalizable Multimodal Reward Models	Accept (poster)	Summary: The paper addresses the challenge of unimodal spurious correlations in Multimodal Reward Models (MM-RMs), particularly how these models fail to generalize to out-of-distribution (o.o.d.) data. These spurious correlations occur when models over-rely on text-only features, which hold in the training distribution but fail in o.o.d. settings. The authors introduce a “Shortcut-aware” MM-RM learning algorithm that dynamically identifies and reweights samples where unimodal shortcuts fail, thus promoting a stronger multimodal understanding. Experimental results show improvements in generalization and performance across various tasks, suggesting that this approach is effective in reducing the impact of unimodal biases. Claims And Evidence: The claims about unimodal spurious correlations limiting MM-RMs’ generalization to o.o.d. data are supported by experimental evidence, particularly the cross-distribution tests. However, the discussion could benefit from more detailed analysis on the theoretical aspects of why the proposed approach outperforms other methods, especially in terms of sample reweighting. The evidence is generally convincing, but the connection between the empirical findings and the theoretical foundations could be made clearer. Methods And Evaluation Criteria: The proposed methods, specifically the Shortcut-aware learning algorithm and the use of the Shortcut-Failure Coefficient (SFC), are appropriate for the problem of improving generalization in multimodal models. The experimental design, including cross-distribution and downstream performance evaluations, is well-suited to test the algorithm’s robustness. However, while the evaluation metrics like SFD (Shortcut-Failure Degradation) are useful, they might need further justification in terms of how they specifically relate to the real-world applicability of MM-RMs. Theoretical Claims: The paper introduces some theoretical concepts like the Shortcut-Failure Coefficient (SFC), but does not provide a full theoretical proof of how this approach leads to better generalization. This is an area that could use more depth, particularly regarding how the shortcut-aware approach compares to standard training regimes in a formal theoretical context. Experimental Designs Or Analyses: The experimental setup appears solid, with a clear focus on cross-distribution and real-world applicability. The use of multiple datasets (VLFeedback, POVID, RLHF-V) strengthens the claims about generalization. Supplementary Material: Yes. Relation To Broader Scientific Literature: The work is well-grounded in the current literature on reward models and multimodal learning. The authors effectively position their work within the context of previous research on unimodal biases and generalization in MM-RMs. Essential References Not Discussed: No. Other Strengths And Weaknesses: A key strength of the paper is its novelty in tackling unimodal spurious correlations in multimodal models. The Shortcut-aware algorithm is a promising contribution that addresses a clear gap in the current research. However, the paper could be clearer in its discussion of how the proposed method compares quantitatively to other established methods for multimodal model generalization. The evaluation could also benefit from more rigorous analysis of the trade-offs between in-distribution and out-of-distribution performance. Other Comments Or Suggestions: The paper is well-written but could improve in terms of theoretical clarity, especially concerning the Shortcut-aware algorithm’s formal underpinnings. It might also be helpful to include more experimental results on how the algorithm performs across a broader range of real-world scenarios, particularly in domains outside of vision-language models. Questions For Authors: 1. How do you justify the use of the Shortcut-Failure Coefficient (SFC) as a meaningful metric for measuring the failure of unimodal shortcuts? 2. Could you provide a more detailed theoretical analysis of how the Shortcut-aware algorithm ensures better generalization in multimodal settings? Would other debiasing techniques, such as invariant risk minimization, perform similarly in your setup? Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Thank you for your recognition of the strengths of our work. We address your concerns as follows. C1: More detailed analysis on the theoretical aspects of why the proposed approach outperforms other methods. C2: Justify the use of SFC as a meaningful metric for measuring the failure of unimodal shortcuts. A1-2: Thank you for your interest in our theoretical analysis. Below is a more detailed justification: - Information-theoretically, SFC quantifies text-only shortcut insufficiency for prediction. SFC = $\frac{L_t}{L_t + L_m}$ estimates $\frac{H(Y\|T)}{H(Y\|T) + H(Y\|T,V)}$ assuming optimized losses approximate entropy terms. Defining $\rho = \frac{I(V,Y\|T)}{H(Y\|T)}$ as visual modality's normalized information contribution, we derive: $SFC \approx \frac{1}{2-\rho}$. This establishes SFC as monotonically increasing with $\rho$, providing principled foundation for reweighting based on visual information's unique contribution. - Our method connects with group DRO [1], with each sample representing a group without explicit labels. We hypothesize that worst-case group probability depends on the degree to which samples cannot be predicted using text information alone, aligning with our observations of Shortcut-Failure Degradation. By defining weights as $w(x, y) = \frac{SFC(x, y)}{\mathbb{E}{(x, y)} [SFC(x, y)]}$, we shift from $P_{train}$ to $Q$ where $\frac{dQ}{dP_{train}}(x, y) \propto w(x, y)$. These weights positively correlate with optimal weights minimizing worst-case risk, reducing generalization gaps while maintaining computation efficiency. We will expand this analysis in the future revision. C3: While the evaluation metrics like SFD are useful, they might need further justification in terms of how they specifically relate to the real-world applicability of MM-RMs. A3: Thank you for this important point about SFD's real-world relevance. SFD quantifies MM-RM performance when text shortcuts fail - a scenario critical for practical applications. Consider a concrete example: an MM-RM might learn to prefer "long, descriptive captions" as a text shortcut, but would fail when deployed to a domain where caption quality depends on visual grounding (e.g., medical imaging). SFD measures how severely the MM-RM fails in such scenarios. We'll add more discussion about SFD's practical implications in our next revision. C4: The evaluation could also benefit from more rigorous analysis of the trade-offs between in-distribution and out-of-distribution performance. A4: We appreciate your insightful comments. Our experiments reveal a nuanced balance: while the proposed algorithm slightly reduces IID accuracy (91.4→90.2), it achieves an absolute gain in OOD scenarios (68.1→78.5)—a critical robustness improvement. This trade-off aligns with our expectations: suppressing text-only shortcuts weakens overfitting to dataset-specific biases, which marginally impacts IID performance but significantly enhances generalization. We will provide more detailed discussion in our revision. C5: The paper could be clearer in its discussion of how the proposed method compares quantitatively to other established methods for multimodal model generalization. A5: Thank you for your valuable suggestion. We would like to clarify that the research landscape shows an imbalance: text-only RM generalization are well-studied [2] while MM-RMs remain under-explored despite their growing importance. Our work addresses this gap by identifying and mitigating unimodal spurious correlations that significantly impair MM-RM generalization, establishing new understanding in this emerging area. C6: Would other debiasing techniques, such as invariant risk minimization, perform similarly in your setup? A6: While IRM and related work inspire us, we believe that direct application of IRM would be infeasible in our setup: 1) IRM requires multiple training environments with explicit distribution shifts. In contrast, real-world RMs are typically trained on a single environment due to practical constraints in data collection [3]. Therefore, our setup limits the training data to a single environment, while our method circumvents this by implicitly defining "environments" per sample via SFC. 2) IRM and similar algorithms involve bi-level optimization with second-order gradients, challenging to optimize for large models like InternVL2-8B due to computational overhead and optimization instability. Our approach instead builds on ERM with sample-wise risk reweighting, ensuring compatibility with existing training frameworks and efficient backpropagation. [1] Sagawa, Shiori, et al. "Distributionally robust neural networks for group shifts: On the importance of regularization for worst-case generalization." ICLR, 2020. [2] Yang, Rui, et al. "Regularizing hidden states enables learning generalizable reward model for llms." NeurIPS 2024. [3] Ouyang, Long, et al. "Training language models to follow instructions with human feedback." NeurIPS 2022.	Summary: This paper highlights how unimodal spurious correlations reduce generalization in multimodal reward models. In cross-distribution tests, MM-RMs trained on large, seemingly robust datasets still fail to generalize in unseen environments, primarily because they exploit textual cues rather than genuinely integrating vision and language. The paper proposes a “Shortcut-aware” algorithm that dynamically weights training examples where text-only reasoning fails, thereby forcing the model to rely more on multimodal inputs. Empirical results show that this method improves out-of-distribution accuracy while modestly sacrificing in-distribution performance, leading to better overall robustness and downstream task performance. 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: NA Essential References Not Discussed: NA Other Strengths And Weaknesses: Strengths: 1. The paper identifies a very practical gap in multimodal reward modeling: many so-called multimodal models mainly leverage textual signals, limiting their reliability on unseen data. 2. The proposed dynamic reweighting mechanism, which highlights cases where text-only responses fail, is conceptually straightforward but shows notable gains in generalization, a good example of tackling “shortcut learning” with minimal changes to the overall architecture. Weaknesses: 1. While the paper presents a creative fix, it does not introduce new core ML techniques or theory. The reweighting approach, although usefu, mostly builds on known dynamic data debiasing heuristics. 2. There is little formal treatment of how or why the method shifts model capacity away from text-only cues toward genuinely multimodal representations. This lack of theoretical grounding might limit the paper’s appeal. 3. The problem is demonstrated in the context of MM-RMs for reward modeling. Extensions to tasks like sequence generation, multi-turn conversation, or reinforcement learning from (truly) diverse signals remain unexplored. 4. Although the empirical results are valuable, the paper’s novelty is mainly spotting a subtle problem in multimodal RMs and offering a practical fix. From a rigorous ML research perspective, it may be viewed more as an engineering improvement rather than breaking fresh ground in ML methodology. Other Comments Or Suggestions: NA Questions For Authors: See Weaknesses Above. Ethical Review Concerns: NA Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Thank you for your recognition of the strengths of our work. We address your concerns as follows. C1: While the paper presents a creative fix, it does not introduce new core ML techniques or theory. C2: From a rigorous ML research perspective, it may be viewed more as an engineering improvement rather than breaking fresh ground in ML methodology. A1-2: We sincerely thank you for recognizing our method’s creativity and for the thoughtful critique. We appreciate the chance to clarify our contributions. - We systematically reveal unimodal spurious correlations as a critical bottleneck in MM-RM generalization - a novel insight in multimodal alignment. While prior works address single-modality biases (e.g., text-length bias [1]), we uniquely demonstrate how modality gaps fundamentally drive models toward text-only shortcuts, even in multimodal training paradigms. This discovery exposes a critical blind spot in existing approaches and establishes a new research direction for multimodal robustness. - We propose a principled framework anchored in the Shortcut-Failure Coefficient (SFC), which dynamically quantifies modality reliance through dual-branch interaction. Unlike heuristic reweighting methods, SFC leverages intrinsic modality conflicts to identify samples requiring multimodal integration. Our cross-distribution evaluation protocol and Shortcut-Failure Degradation metric further provide standardized tools for diagnosing generalization failures, enabling systematic comparisons in future work. - We conduct rigorous experiments to analyze the impact of text-only shortcuts on generalization and demonstrate the real-world effectiveness of our approach. Our method not only achieves significant generalization gains (e.g., +10.4 average OOD accuracy) but also improves performance on real-world downstream tasks (e.g., +6.5 on LLaVA-Bench). These results underscore that our approach is not just a heuristic but a principled framework toward more robust multimodal systems. While building on existing ML components, our work establishes a new paradigm for analyzing and mitigating modality-specific biases - a fundamental challenge as multimodal systems scale. We believe these contributions meaningfully advance the development of robust multimodal alignment. C3: There is little formal treatment of how or why the method shifts model capacity away from text-only cues toward genuinely multimodal representations. This lack of theoretical grounding might limit the paper’s appeal. A3: Thank you for your interest in the theoretical analysis of our approach. Due to space limitations, we follow ICML’s guidelines and recommend that you refer to our response to Reviewer Rc2L, where we provide a theoretical analysis of how our SFC measure quantifies the insufficiency of text-only shortcuts for prediction from an information-theoretic perspective. Additionally, we analyze how sample reweighting can shift the training distribution to optimize worst-case OOD risk. This theoretical foundation illustrates how our method reallocates model capacity away from text-only cues toward genuinely multimodal representations. C4: The problem is demonstrated in the context of MM-RMs for reward modeling. Extensions to tasks like sequence generation, multi-turn conversation, or reinforcement learning from (truly) diverse signals remain unexplored. A4: We appreciate the reviewer's concern about the scope of our work. We would like to clarify that while our experiments focus on MM-RMs as the implementation context, the implications and applications of our findings are much broader. Reward models serve as preference modeling tools that guide AI responses across various paradigms. As essential components shaping AI behavior in both training and inference stages, they directly connect to tasks including the sequence generation, conversation, and RL applications the reviewer mentioned: 1. Our experiments demonstrate how MM-RMs improve model outputs through Best-of-N selection at test time across diverse benchmarks including MM-Vet, Llava-Bench, and MMHal-V. These benchmarks specifically evaluate capabilities in visual recognition, OCR, instruction following, and complex reasoning - all essential components of effective sequence generation and conversational AI. 2. We have supplemented our initial experiments with additional results showing how our improved MM-RMs enhance policy models when used in RL training loops. The policy models trained with our shortcut-aware MM-RMs demonstrate significant performance improvements across the same benchmarks. \|\|MM-Vet\|Llava-bench\|MMHal-V\| \|-\|-\|-\|-\| \|Policy (InternVL2-8B)\|43.4\|73.3\|3.26\| \|Policy + RL (w/ Standard MM-RM)\|43.5\|76.3\|3.46\| \|Policy + RL (w/ Shortcut-aware MM-RM)\|44.1\|77.8\|3.58\| Please let us know if you have any additional questions. [1] Chen, Lichang, et al. "Odin: Disentangled reward mitigates hacking in rlhf." ICML 2024.	Summary: This paper reveals that multimodal reward models (MM-RMs) are struggling to address out-of-distribution (OOD) input queries and identify the unimodal spurious correlation (text-only reliance behavior of MM-RMs) as the main cause of this issue. The authors provide some hypotheses behind this issue and propose to leverage this bias to dynamically reweight the per-sample loss based on the expertise of text-only and multimodal reward models. This shortcut-aware multimodal reward modeling induces better OOD generalization of the reward model and improves downstream open-ended question-answering tasks through best-of-N inference protocol. Claims And Evidence: The main claim is that the poor OOD generalization capability of MM-RMs is due to the text-only shortcut, and this claim was validated through systemic empirical evaluation. Methods And Evaluation Criteria: The proposed method and evaluation protocol are both reasonable enough to make a persuasive empirical validation. Theoretical Claims: There are no theorems. Experimental Designs Or Analyses: The experiments are intuitively designed and valid to investigate the authors' hypotheses, but there is a slight concern about the volume of the experiment (which will be covered in the strengths and weaknesses section). Supplementary Material: I took a look at the data statistics. Relation To Broader Scientific Literature: There have been many attempts to leverage biases (by modeling them with an auxiliary model) to mitigate biases from the main branch network [Bahng et al. 2020; Jung et al. 2023]. This work presents a simple yet effective application of this kind of approaches in the multimodal reward modeling regime. - [Bahng et al. 2020] Learning De-biased Representations with Biased Representations - [Jung et al. 2023] Fighting Fire with Fire: Contrastive Debiasing without Bias-free Data via Generative Bias-transformation Essential References Not Discussed: The authors properly cited essential references. Other Strengths And Weaknesses: ## Strengths * The presentation quality is excellent. * The main hypothesis -- MM-RMs' poor OOD robustness is due to text-only shortcuts -- is well-supported by extensive intermediate experiments. * The authors try to further dive into the reason behind the phenomenon (text-only shortcuts) by providing some conjectures (information imbalance between modalities and so on). ## Weaknesses * Although the authors provide rich analysis to strengthen the motivation and rationale behind the method development, one concern is that they only validate their approach with InternVL2-8B. It is not sure that the proposed method can be applied to other model architectures / model sizes. * The proposed method hosts an additional large language model branch to model the text-only shortcut bias. This will significantly increase the amount of resources required during reward modeling, and the authors do not provide cost comparison between standard reward modeling and their proposal. Other Comments Or Suggestions: * I would recommend the author to remove the negative sign from equation (6) and equation (7). In its current form, the statement "A sample with a higher SFC value indicates that the text-only branch struggles to model preferences, suggesting that multimodal fusion is crucial for robust learning, thus receiving an increased weight ..." is wrong because the higher value of SFC means text-only branch produces large preference loss (the logarithm of sigmoid is range from -inf to 0). If the negative signs in Eq (6) and (7) are removed, the above explanation will be correct. * It would be great if the authors could further provide some justifications for the proposed metric Shortcut-Failure Degradation (SFD). Is it correlated with other robustness metrics? or is it just for measuring the degree of text-only shortcut bias inside of MM-RMs? # Post-rebuttal > The authors' rebuttal is quite professional and addresses some of my concerns successfully. I will be thinking about editing my initial review and rating after carefully going through other rebuttal contents to other reviewers (but will not require any additional details or raise questions from/to authors). -> After looking through the other reviews and rebuttals, I want to adhere to my current rating -- Weak Accept -- by echoing the concerns raised by `hs7o ` while acknowledging some unique insights provided by this work. Questions For Authors: See the above reviews. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Thank you for your recognition of the strengths of our work. We address your concerns as follows. C1: Although the authors provide rich analysis to strengthen the motivation and rationale behind the method development, one concern is that they only validate their approach with InternVL2-8B. It is not sure that the proposed method can be applied to other model architectures / model sizes. A1: We appreciate the reviewer's concern about the broader applicability of our method. To address this point, we have conducted additional experiments on other base models: 1. InternVL2-2B (Model Backbone: InternLM2-Chat-1.8B) \|Training Set\|IID Accuracy ($\Delta$)\| OOD Accuracy ($\Delta$)\| \|-\|-\|-\| \|VLFeedback\|84.5 (-1.9)\|81.1 (+3.5)\| \|POVID\|99.8 (-0.3)\|53.7 (+8.4)\| \|RLHF-V\|84.0 (-1.8)\|60.9 (+7.3)\| 2. InternVL2-4B (Model Backbone: Phi-3-Mini-128K-Instruct) \|Training Set\|IID Accuracy $\Delta$\| OOD Accuracy $\Delta$\| \|-\|-\|-\| \|VLFeedback\|85.6 (-1.5)\|81.4 (+1.5)\| \|POVID\|99.5 (-0.5)\|60.4 (+10.1)\| \|RLHF-V\|79.3 (-0.6)\|66.4 (+8.7)\| $\Delta$ measures the accuracy differential between Shortcut-aware MM-RM and Standard MM-RM. The results demonstrate that our method generalizes well across different model architectures and parameter scales, confirming that the effectiveness of our approach extends beyond just InternVL2-8B. C2: The proposed method hosts an additional large language model branch to model the text-only shortcut bias. This will significantly increase the amount of resources required during reward modeling, and the authors do not provide cost comparison between standard reward modeling and their proposal. A2: Thank you for raising this important concern about computational resources. We would like to clarify two key points: 1. The additional text-only branch is only present during the training phase. During inference, this branch is completely removed, meaning our approach has identical computational requirements to standard multimodal reward modeling when deployed in practice. 2. The additional computational overhead is comparable to what's already widely accepted in language model alignment research (similar to DPO [1] algorithms that also use a reference model). In the context of the overall model development pipeline (especially compared with pre-training stage), this marginal increase is quite modest. C3: I would recommend the author to remove the negative sign from equation (6) and equation (7). A3: Thank you for your thorough review of our paper—your attention to detail is valuable for improving our work! We apologize for the typo error you identified. We will correct this mistake in future versions of the paper to ensure mathematical consistency with our textual statement. C4: It would be great if the authors could further provide some justifications for the proposed metric Shortcut-Failure Degradation (SFD). Is it correlated with other robustness metrics? or is it just for measuring the degree of text-only shortcut bias inside of MM-RMs? A4: Thank you for raising this important question about the justification of our SFD metric. We would like to clarify that: - SFD addresses the specific challenge of unimodal spurious correlations in MM-RMs. By calculating the accuracy difference between shortcut-success samples and shortcut-fail samples, SFD directly quantifies how much a multimodal model relies on text-only shortcuts. This makes it a tailored metric for diagnosing unimodal bias, unlike general robustness metrics that might conflate multiple failure modes. - While SFD isn't directly equivalent to existing metrics, it shares conceptual grounding with worst-group accuracy [2][3][4], where the shortcut-fail subset represents our "worst group" in the multimodal generalization context. Both metrics prioritize performance on challenging subgroups where biased correlations lead to failures. Just as worst-group accuracy penalizes models exploiting majority-group features, SFD penalizes over-reliance on text shortcuts that may dominate training but fail during test phase. We will elaborate on these connections in our revision. C5: There have been many attempts to leverage biases to mitigate biases from the main branch network [Bahng et al. 2020; Jung et al. 2023]. A5: Thank you for pointing out the pioneering papers related to our research direction! We will cite them in the future version of our paper. Please let us know if you have any additional questions. [1] Rafailov, Rafael, et al. "Direct preference optimization: Your language model is secretly a reward model." NeurIPS, 2023. [2] Sagawa, Shiori, et al. "Distributionally robust neural networks for group shifts: On the importance of regularization for worst-case generalization." ICLR, 2020. [3] Nam J, Kim J, Lee J, et al. "Spread Spurious Attribute: Improving Worst-group Accuracy with Spurious Attribute Estimation." ICLR, 2022. [4] Chaudhuri, Kamalika, et al. "Why does throwing away data improve worst-group error?." ICML, 2023.	Summary: The paper proposes to improve the generalization of Multimodal Reward Models (MM-RMs) by addressing the issue of unimodal spurious correlations. It introduces a Shortcut-aware MM-RM learning algorithm that dynamically reweights training samples to emphasize multimodal understanding, reducing reliance on text-only shortcuts. Experiments show the effectiveness in generalization, downstream task performance, and scalability. Claims And Evidence: The authors demonstrate through cross-distribution transfer experiments that standard MM-RMs struggle with generalization due to unimodal spurious correlations. They introduce the Shortcut-Failure Degradation (SFD) metric to quantify this issue and show that their proposed algorithm reduces SFD values, indicating better generalization. However, it would be more demonstrative if the authors could conduct evaluations on more benchmarks like MMMU and MMStar. Methods And Evaluation Criteria: Yes Theoretical Claims: The paper does not present any formal theoretical proofs. All equations and definitions are checked. Experimental Designs Or Analyses: All experiments are checked. For the results on Table 2, have the authors tried to combine these three training datasets to train the MM-RM? Would combining preference datasets obtained through different construction methods help, or would they interfere with each other? Supplementary Material: I reviewed all parts of supplementary material. Relation To Broader Scientific Literature: This paper attempts to addresses a critical limitation of existing MM-RMs by proposing a novel learning algorithm that enhances generalization. A more-robust MM-RMs can enhance the alignment of MLLMs. Essential References Not Discussed: N/A Other Strengths And Weaknesses: - Strengths: The introduction of the SFD metric provides a new way to diagnose and measure the impact of unimodal spurious correlations. - Weaknesses: The paper focuses on a specific type of spurious correlation (text-only shortcuts) and may not address other forms of spurious correlations that could exist in multimodal data. Additionally, the method relies on the availability of multimodal preference datasets, which may not always be practical in real-world applications. Other Comments Or Suggestions: It would be helpful to include a comparison with other state-of-the-art methods for improving generalization in multimodal reward models. Questions For Authors: - Can the Shortcut-aware learning algorithm be extended to address other forms of spurious correlations beyond text-only shortcuts? If so, what modifications would be required? - How does the method handle scenarios where multimodal preference datasets are limited or unavailable? Are there any alternative strategies to ensure robust generalization in such cases? - Could we potentially avoid phenomena like text-only shortcuts by better constructing the Preference dataset? Or could this improve the generalization performance of the MM-RMs trained with it? Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Thank you for your recognition of the strengths of our work. We address your concerns as follows. C1: It would be more demonstrative if the authors could conduct evaluations on more benchmarks like MMMU and MMStar. A1: Thank you for your concern about benchmark evaluation. We clarify that our assessment focuses on MM-RMs' ability to select highest-quality responses generated by a VLM. Unlike traditional multiple-choice benchmarks, we deliberately selected free-response benchmarks (MM-Vet, Llava-bench, and MMHal-V) for a more appropriate evaluation. Nevertheless, your suggestion is insightful. We conducted additional evaluations on VL-RewardBench, a benchmark designed to assess MM-RMs. \|Method\|Hallucination\|Reason\|General\|Overall\| \|-\|-\|-\|-\|-\| \|MM-RMs (VLFeedback)\|\|\|\|\| \|Standard\|56.9\|55.7\|41.0\|54.2\| \|Shortcut-aware\|65.0\|61.0\|44.8\|61.0\| \|MM-RMs (POVID)\|\|\|\|\| \|Standard\|84.6\|56.6\|63.9\|74.5\| \|Shortcut-aware\|85.7\|57.9\|62.3\|75.2\| \|MM-RMs (RLHF-V)\|\|\|\|\| \|Standard\|65.3\|57.2\|33.3\|58.6\| \|Shortcut-aware\|75.8\|58.8\|48.1\|67.4\| C2: For the results on Table 2, have the authors tried to combine these three training datasets to train the MM-RM? A2: Thank you for this insightful suggestion. We conducted an additional experiment combining equal samples from the three datasets (15K total) for MM-RM training. The evaluation results demonstrated that training with the mixed dataset yielded performance that fell between the individual datasets: \|Training Set\|MM-Vet\|Llava-bench\|MMHal-V\| \|-\|-\|-\|-\| \|VLFeedback\|49.0\|80.5\|3.70\| \|POVID\|46.7\|69.6\|3.43\| \|RLHF-V\|39.9\|73.1\|3.55\| \|Mixture\|47.3\|76.5\|3.53\| This finding suggests that while combined preference datasets provide diverse training signals, they may partially interfere with each other due to differences in methodologies and preference distributions. C3: Can the Shortcut-aware learning algorithm be extended to address other forms of spurious correlations beyond text-only shortcuts? If so, what modifications would be required? A3: Thank you for raising an important point about the generalizability of our approach. While our experiments focused on text-only shortcuts due to their prevalence in MM-RMs, the framework's design is intentionally modality-agnostic and can be extended to other forms of spurious correlations with two key modifications: 1. Proxy Adaptation: Replace the text-only proxy with a problem-specific proxy (e.g., image-only) to isolate the target spurious feature. 2. Dynamic Reweighting: Compute failure signals analogously to Eq. 5 (SFC) for the new proxy, then reweight samples where the proxy struggles. The core mechanism (shifting focus to "hard" multimodal cases) remains unchanged. We will explicitly discuss this generality in our revisions to highlight the framework's broader applicability. C4: It would be helpful to include a comparison with other state-of-the-art methods for improving generalization in multimodal reward models. Thank you for your valuable suggestion. We clarify that while text-only RM generalization is well-studied, MM-RMs face a critical research gap despite growing importance. Due to space limitations, we follow ICML’s guidelines and recommend that you refer to our response to Reviewer Rc2L (C5). C5: How does the method handle scenarios where multimodal preference datasets are limited or unavailable? Are there any alternative strategies to ensure robust generalization in such cases? A5: Thank you for raising this practical consideration. We'd like to clarify that: * Preference datasets are fundamentally necessary for RM development, not a limitation specific to our method but rather an inherent requirement of the existing paradigm itself. Any approach to developing MM-RMs will require some form of preference data to learn what constitutes high-quality responses. * A key strength of our approach is that it improves bias mitigation without requiring additional data beyond what existing methods already use. Without these innovations, addressing generalization issues would demand significantly more labeled data. C6: Could we potentially avoid phenomena like text-only shortcuts by better constructing the Preference dataset? Or could this improve the generalization performance of the MM-RMs trained with it? A6: Thank you for highlighting dataset quality as another path to improving generalization. While more balanced datasets can help mitigate shortcuts, achieving truly unbiased data demands extensive human verification to eliminate subtle shortcut patterns—an inherently challenging task. Our solution addresses this without requiring additional data collection or expensive curation. It works with existing datasets to reduce shortcut learning, offering immediate benefits while minimizing costs. Rather than competing with dataset improvements, our method complements them, strengthening any preference dataset—including those refined in the future. Please let us know if you have any additional questions. --- Rebuttal Comment 1.1: Comment: Thank you for the detailed responses. I’ve updated my score to Weak Accept. One more question: Do you plan to open-source your model to benefit the community? --- Reply to Comment 1.1.1: Comment: We sincerely appreciate you for raising your score. As for your question, we are committed to open-sourcing both our model and code to contribute to the research community.	null	null	null	null	null	null
Otter: Generating Tests from Issues to Validate SWE Patches	Accept (poster)	Summary: This paper introduces a novel code agent specifically designed to generate test cases for real-world repositories, comprising a localizer, action planner and generator. A variant of the agent executes all but one of these components and picks the best results using some heuristics and execution feedback. The resulting agent achieves state of the art performance on the related SWT-bench and high performance on the similar benchmark introduced by the authors for the same purpose, TDD-Bench. Claims And Evidence: Several claims regarding related work are mentioned further below. Claims regarding state-of-the-art performance appear well-founded. Methods And Evaluation Criteria: The authors introduce fail to pass (FTP) scores and a tddScore, which is the multiplication of the FTP score with the % of changed lines covered. While the latter is an interesting score, many readers are more familiar with line coverage and may be interested in having line coverage displayed along FTP and tddScore. Theoretical Claims: No theoretical claims made/checked. Experimental Designs Or Analyses: While the proposed method proposes interesting components to combat likely issues with test generation, from a scientific perspective I feel there is a lack of rigor in assessing the individual component's impact (listed below in more details). No ablation on the localization, planner, test generator component In Section 4.1 a Localizer is introduced, and it is introduced that only the top 10 retrieved files are passed to the LLM. It would be interesting to see an ablation here on how the choice of less or more files influences the model performance (either qualitatively or quantitatively). Also hallucinated file names are not dropped but replaced with minimal edit distance files. Why was this introduced and can the authors provide examples or statistics on how frequent such hallucinations are (and how useful their replacement is)? The same holds for the planner component - the model revises its plan 5 times. Why this many times? Finally the test generator extracts file structure and imports for the model. How exactly is the "test structure" extracted? What happens when this is not provided to the LLM? No analysis of relevance for various fixing steps The authors introduce the above mentioned hallucination replacer and an import fixer (Section 4.1 Test Generator). It would be interesting to see their impact, i.e. how many instances would fail if not for these components? No analysis of heterogenous prompts vs temperature The authors mention they use 5 heterogenous prompts at temperature 0 for their models because this proved useful in early experiments. It would be interesting to see concrete examples of how this change improves the method or some quantitative comparison of performances. Supplementary Material: Yes. I skimmed through the definition of TDD Bench, the scripts defining Otter and the generated test cases attached. - The Otter_Otter++ implementation is barely documented, the README lacks descriptions. It would be preferrable to have a single script that performs the benchmark, the submitted code only features a heap of python files to be executed after one another. - Please note the Python version and dependencies for Otter, ideally as a requirements file, package or docker environment. - Please outline the format of the Generated Test jsons - The LICENSE of SWE-bench appears to be missing from the adaptation for TDD-bench - The top-level Instruction.txt refers to Otter(v5). What is this v5 referring to? Relation To Broader Scientific Literature: The approach is similar to the mentioned AEGIS. However, the field of repository-level test case generation is evolving and it is interesting to see different proposals for code agents for test generation (similar to code agents for code repair). In section 4.1 "Test generator", the authors claim that Mundler et. al. attempt to generate diffs directly, however telling from the corresponding paper, Mundler et.al. actually introduce a custom diff format in their zero-shot setups that mainly asks the model to generate complete functions and where to insert them, similar to the method that the authors propose. The agents do not generate diffs either but are equipped with different editing tools. I suggest the authors adapt these claims accordingly or clarify how they consider their method to differentiate. In Section 6.4, the authors moreover claim that "two of [Mundler et al.'s] approaches use a golden patch in the prompt". Could the authors clarify which methods these are? For Otter++, an execution feedback oracle is used, concretely, the best model generation is picked based on execution logs in the final setting. While this is similar to the LIBRO setting in Mundler et. al., it is a clear advantage over their analysed code agents which do not have access to a correctly set-up environment and the test results. The authors may consider mentioning this, since it may be a contributing factor to their superior performance. Essential References Not Discussed: None that I am aware of. Other Strengths And Weaknesses: The paper introduces a novel and interesting follow-up for the work of Mundler et. al., demonstrating a variety of components designed for addressing common issues during test generations. Other Comments Or Suggestions: Table 8 is barely readable when printed on paper, I suggest to make it slightly larger. Questions For Authors: Please see my open questions in the above fields. Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: a) Reporting Coverage: We will add a coverage column to Table 1. \| Model \| Approach \| Coverage \| \|-\|-\|-\| \| Mistral \| Zero-shot \| 60.6 \| \| \| Otter \| 70.5 \| \| \| Otter++ \| 70.4 \| \| GPT-4o \| Zero-shot \| 60.0 \| \| \| Otter \| 70.6 \| \| \| Otter++ \| 71.5 \| b) Ablation: We have conducted a detailed analysis of Otter tests in response to Reviewer G2zQ's comments (see- Analyze Otter-generated tests) and have modified our ablation study to further break down self-reflective action planning (Reviewer BFCj- Clarification on Ablation). File Retrieval: We evaluated the effect of the number of localized files on the results and found it to be minor: Focal (#of files, accuracy) = {(5, 82.4%), (10, 82.4%), (15, 83.3%)} Test (#of files, accuracy) = {(5, 69.9%), (10, 70.6%), (15, 71.9%)} Hallucination: The localizer makes two LLM calls during which hallucinations can occur. In the first call, we drop hallucinated file names. In the second call, we replace hallucinated file names with existing ones to ensure our pipeline functions correctly. \| Type \| LLM Call \| #of Hallucinations Happen \| #of fail-to-pass \| in %\| \|-\|-\|-\|-\|-\| \| Focal \| 1 \| 19 \| 8 \| 42.1 \| \| \| 2 \| 5 \| 3 \| 60.0 \| \| Test \| 1 \| 39 \| 22 \| 56.4 \| \| \| 2 \| 5 \| 4 \| 80.0 \| The results show that our proposed technique helps Otter achieve better performance. For example, if we didn’t replace the hallucinated file name in the 2nd call of test localization (the last row), we would have lost 5 samples because our pipeline would have exited with an error. Replacing the hallucinated name generated 4 fail-to-pass tests for those samples. Plan revision up to 5 times: The model does not always revise the plan 5 times. If the model is satisfied before making 5 calls, it does not make further revisions. Figure 4 shows that the LLM is usually satisfied within 2 calls. Our approach could go beyond 5 calls, but considering the cost and time, we limit the number of plan revisions to 5. Test File Structure: It contains lines where classes and functions are defined. We build the test file structure by omitting lines that do not define a new class or function. Note that 72.8% tests are new, and test file structure is necessary for those tests. LLMs are unable to indicate the position of new tests without it. c) Analysis for various fixing steps: We have already added the results in Table 2 for the import fixer. We will lose 11 and 4 instances with GPT-4o and Mistral-large, respectively. We address the hallucination above. d) Heterogenous Prompts vs Temperature: We make multiple LLM calls in different stages and multi-sampling in each stage will exponentially increase the test counts. To compare heterogenous prompting with temperature, we generated 5 samples at high temperature (1.0) in our last LLM call in Test Generator phase of Otter (our best solution). Though the average number of fail-to-pass test goes up (117.8 vs 116.6), the Top-5 and Top-1 (using Otter++ ranker) results remain lower (Top-5: 173 vs 197 and Top-1: 146 vs 166). That means heterogenous prompting boosts up the overall ensemble performance if we compare at the same number of samples. e) Diff format: The custom-diff has similarities to our approach. However, the model needs to perform additional tasks such as writing the file name, change type, and line number in response to one LLM call. Additionally, to instruct the model to generate a specific format, the authors had to include an example that is not relevant to the issue itself. In our generation step, the model only needs to generate the test (and prior function name for positioning new tests). f) Usage of patch in Mundler et al.'s: Thank you for pointing this out. Figure 12 of the SWT-Bench paper presents the prompt that was used for ZeroShotPlus and LIBRO. Line 7 indicates that the “proposed patch” has been used to generate the test. We mistakenly thought this refers to the golden patch, which we now realize is not the case. We will fix this statement in the paper. g) Execution feedback: Otter++ uses execution logs on the current code base and gains an advantage in the final selection stage. We will mention the use of feedback as a contributing factor to the superior performance of Otter++. Note that Otter does not use any execution logs, yet it still performs significantly better than LIBRO (25.4% vs 15.2% in Table 3). h) Supplementary Material: We will improve the Otter repository as suggested. We removed the license following the ICML author instructions. We will address this in our open-source version. V5 is our internal name used for Otter; we apologize for the confusion it caused. --- Rebuttal Comment 1.1: Comment: I thank the authors for their extensive additional experiments and corrections. > Though the average number of fail-to-pass test goes up (117.8 vs 116.6), the Top-5 and Top-1 (using Otter++ ranker) results remain lower (Top-5: 173 vs 197 and Top-1: 146 vs 166). Can you please elaborate this a bit further? Does this not simply imply that the ranker is not very good? It seems high temperature/heterogenous prompts does not make a significant difference before the ranker. I think heterogenous prompts is a good idea to increase sample diversity but temperature should not be so simply discarded without convincing evidence of its inferiority. This should be discussed more in the next revision. I think the paper is potentially interesting to the test generation community when the discussed changes are incorporated and accordingly raised my score. --- Reply to Comment 1.1.1: Comment: Thank you for your comment! We agree that the question of high temperature vs. heterogeneous prompts deserves more discussion in the revised paper. We will make sure the revised paper includes that. We expanded the experiment from our previous author response: \| Setting \| Individual Performance \| Max \| Average \| Top-1 \| Oracle \| \|-------------------------------------------\|------------------------------------------\|-----\|---------\|-------\|--------\| \| 5 heterogeneous prompts (Otter++) \| 141,110,115,107,110 \| 141 \| 116.6 \| 166 \| 197 \| \| 5 high-temperature samples (temp=1.0) \| 111,118,126,121,113 \| 126 \| 117.8 \| 146 \| 173 \| \| 5 = 1 greedy + 4 high-temperature samples \| 141, 111,118,126,121 \| 141 \| 123.4 \| 152 \| 183 \| \| 10 = 5 heterogeneous + 5 high-temperature \| 141,110,115,107,110, 111,118,126,121,113 \| 141 \| 117.2 \| 168 \| 218 \| Here, the Top-1 column shows "fail-to-pass @ 1" based on our actual ranker, whereas the Oracle column shows "fail-to-pass @ N", i.e., the result if we had a perfect ranker. Heterogeneous prompts yield better results than high-temperature samples in both the Top-1 column and the Oracle column. This is evidence that the difference indeed comes from the diversity of heterogeneous prompts and is not ranker specific. The difference between the Top-1 and the Oracle column is almost the same in the first three rows (i.e., all settings with 5 samples). That said, there is still room for improvement in the ranker, as illustrated by the last row. In the last row, an oracle that could reliably choose among all 10 samples would perform amazingly well, motivating further work on better rankers.	Summary: This paper introduces Otter, a system for generating tests from issue descriptions to validate software engineering (SWE) patches. Unlike prior work that focuses on generating tests for existing code, Otter addresses the scenario where a code patch does not yet exist, supporting test-driven development (TDD) and validation of SWE agents. The system takes an issue description and original code as input, and generates tests that should fail on the old code but pass on the new code after the issue is resolved. Claims And Evidence: The paper's main claims are supported by evidence. Methods And Evaluation Criteria: The methods and evaluation criteria are generally appropriate for the problem: - The TDD-Bench-Verified benchmark is a reasonable extension of SWE-bench Verified with additional quality filters. - The tddScore metric combines fail-to-pass behavior with code coverage, which is appropriate for evaluating test quality. - The comparison with existing approaches (SWE-Agent+, LIBRO, etc.) provides context for Otter's performance. However, there are some limitations: - The paper would benefit from more qualitative analysis of the generated tests to understand their characteristics beyond just pass/fail rates. - The evaluation focuses primarily on Python repositories, which may limit generalizability. Theoretical Claims: The paper doesn't make significant theoretical claims requiring formal proofs. Experimental Designs Or Analyses: The experimental design is generally sound: - The comparison with baselines uses the same dataset and evaluation metrics. - The ablation studies help understand component contributions. - The data contamination analysis addresses potential concerns about model memorization. Supplementary Material: The supplementary material contain additional details on the TDD-Bench-Verified dataset, example prompts, and implementation details of Otter. This material supports the claims in the main paper. Relation To Broader Scientific Literature: The paper positions itself well within the literature on test generation and SWE agents. It builds upon: - SWE-bench and SWE-bench Verified for issue resolution benchmarking - Recent work on LLM-based SWE agents (SWE-Agent, CodeR, SpecRover) - Test generation systems like LIBRO Essential References Not Discussed: As mentioned above, the following references are essential to understanding the context but are not cited: ``` [1] Wang X, Gao P, Meng X, et al. (2024) "AEGIS: An Agent-based Framework for General Bug Reproduction from Issue Descriptions" - This work directly addresses bug reproduction from issue descriptions using a multi-agent framework, which is highly relevant to Otter's goals. [2] Lin Y, Ma Y, Cao R, et al. (2024) "LLMs as Continuous Learners: Improving the Reproduction of Defective Code in Software Issues" - This paper explores similar problem space of reproducing issues from descriptions. [3] Ehrlich R, Brown B, Juravsky J, et al. (2025) "CodeMonkeys: Scaling Test-Time Compute for Software Engineering" - This work presents related approaches for test generation that would provide important context. ``` Other Strengths And Weaknesses: Strengths: - The paper addresses an important practical problem in software engineering - generating tests from issue descriptions before patches exist. - The comprehensive evaluation across multiple models and comparison with existing approaches provides a clear picture of Otter's capabilities. - The introduction of TDD-Bench-Verified is a valuable contribution to the research community. Weaknesses: - Limited novelty: The primary novelty is in the combination of existing techniques rather than fundamentally new approaches. - Incomplete ablation studies: While Table 2 shows component contributions, more detailed analysis of the novel components (especially the self-reflective planning) would strengthen the paper. - Limited qualitative analysis: Beyond pass/fail rates, deeper analysis of test characteristics would be valuable. - Missing comparisons with concurrent work: The paper doesn't compare with or discuss several highly relevant recent papers in the same problem space. Other Comments Or Suggestions: - The paper would benefit from more examples of generated tests in the main text. - The paper should address how Otter might be integrated into existing developer workflows. Questions For Authors: See about "Other Strengths And Weaknesses". Code Of Conduct: Affirmed. Overall Recommendation: 2	Rebuttal 1: Rebuttal: a) Limited novelty: Our approach introduces self-reflective action planning for generating bug-reproduction tests, which is a novel application in this problem setting. Our approach also incorporates heterogeneous prompting for multi-sampling, which is shown to be better than multi-sampling at higher temperatures. Although applying static analysis for repairing name-related errors, prompt design, and rule-based checking are not new, we have adapted them to work well in our problem setting. Together these features enable our approach to achieve significantly better results than the techniques presented by Mundler et al. b) Incomplete ablation studies: We have modified and restructured the ablation study to place more focus on self-reflective action planning (See reviewer BFCj “Clarification on Ablation”). We have added the last two rows in the following table (Table 2 in the paper): Row 2 shows the number of fail-to-pass tests obtained if plan refinement is disabled; Row 3 shows the results obtained if we do not provide the model with valid and invalid action lists. \| Model \| Component \| Approach \| # of fail-to-pass \| tddScore \| Change in tddScore% \| \|:-:\|:-:\|:-:\|:-:\|:-:\|:-:\| \| GPT-4o \| Action Planner \| Otter - Action Planning (complete) \| 110 \| 23.6 \| -19.7 \| \| \| \| Otter - Plan Refinement (Just 1 attempt) \| 130 \| 27.5 \| -6.5 \| \| \| \| Otter - Action Validation \| 120 \| 25.7 \| -12.6 \| In Figure 4 of the paper, we present the number of turns taken in the “reflect and improve the plan” step. In the following table, we show the total number of actions proposed by the model in the final stage and how the performance changes with it. We find that the number of actions tends to be around 1-3, with no clear correlation between the number of actions and whether the test ultimately satisfies the fail-to-pass criterion. \| #of Action \| #of Sample \| #of fail-to-pass \| in % \| \|-\|-\|-\|-\| \| 1 \| 18 \| 7 \| 38.9 \| \| 2 \| 157 \| 49 \| 31.2 \| \| 3 \| 258 \| 78 \| 30.2 \| \| 4 \| 15 \| 7 \| 46.7 \| \| 5 \| 1 \| 0 \| 0 \| c) Limited qualitative analysis: We have added a detailed analysis of the Otter-generated test in response to Reviewer G2zQ (Analyze Otter-generated tests). We discuss how performance changes with mislocalization, the test status on the current codebase, and the type of change (new/modified). d) Missing comparison with concurrent work: Thank you for pointing out the references to Aegis, EvoCoder, and CodeMonkeys. All three of them are highly relevant to our work, as they involve generating reproduction tests from issues. We will make sure to cite and discuss them. [1] Aegis: Our related-work section already cites and discusses this paper. [2] EvoCoder: This paper proposes the interesting idea of using experiences from prior issues to help with the latest issue at hand, which is complementary to Otter. Unlike our work, the generated tests are not integrated with the existing CI pipeline. Furthermore, the experiments do not use execution-based metrics, making it hard to compare empirically. [3] CodeMonkeys: This paper leads with inference scaling and patch generation. It appeared on arXiv on Jan 24, 2025, and we did not realize its test-generation contributions until after we had submitted our work to ICML on Jan 30. CodeMonkeys iteratively and jointly improves a patch with a test, which is interesting and complementary to Otter. Unlike our work, their experiments do not evaluate the fail-to-pass rate nor coverage of generated tests. e) Example & Integrating Otter: Thank you for your suggestions. We will add more examples in the main text. We envision two ways of integrating Otter into existing developer workflows. First, Otter can run on a new issue to propose a test, which the stakeholders can use to clarify requirements for the desired behavior after issue resolution and, following that, a developer can use the test for test-driven development to resolve the issue. Second, Otter can be paired with a patch-generation solution (a "SWE agent") to create a PR that includes both a patch and a test. --- Rebuttal Comment 1.1: Comment: Thank you for the author's response. I appreciate the clarification regarding the novelty aspects of the paper. While these adaptations (self-reflective action planning for bug-reproduction tests and the heterogeneous prompting for multi-sampling) show thoughtful engineering and integration of techniques for this specific problem domain, I still believe the primary contribution lies in the effective combination of existing approaches rather than fundamentally novel methods. The significant performance improvements over Mundler et al. are certainly valuable, but my original assessment of the novelty limitation remains. Therefore, I will maintain my original score for the paper. --- Reply to Comment 1.1.1: Comment: Thank you for your comments, which will greatly help us to improve our work. We are happy to provide clarifications if you have any further concerns.	Summary: The study describes a system to produce tests from code issues by leveraging LLMs with rule-based analysis and multi-step process with feedback. In addition, the study provides an associated benchmark derived from the SWE-bench Verified benchmark for evaluating tests generated from issues. Claims And Evidence: Yes. Methods And Evaluation Criteria: Yes. Theoretical Claims: N/A Experimental Designs Or Analyses: I read the descriptions of the experiments. Supplementary Material: I reviewed the supplied code. Relation To Broader Scientific Literature: Test generation for issues is generally relevant. The workflow described combining LLMs with rule-based steps is interesting but could be presented better. Essential References Not Discussed: I do not identify and major omissions in the references. Other Strengths And Weaknesses: The study is fairly comprehensive and clear– describing the methodology, associated benchmark, and assessments of both (including cost). However, I think that one area of potential improvement is clarifying the ablation study to capture the effect of the novel components of the workflow (the rule based and reflective components) clearly. Other Comments Or Suggestions: Text and numbers in many of the figures are too small to read (Fig 4-8) In the future, please enable the submission status on the template. It makes it easier to review. The textual reference to Mundler et al. should be standardized: Mundler et al. 2024 The use of “cov” in the equations is confusing since usual “cov” refers to covariance. Table 2 is confusing but one that I am interested in. It looks like this is an ablation test focusing on the “fixing import” and “import at generation” steps for Otter. It’s hard to match where those are in Figure 1. It would be interesting (and increase the impact of the work) to explicitly split out between the LLM, LLM w/ feedback, and rule-based components. The other entries look like they are ablation tests for Otter++ and not Otter. Questions For Authors: Can you provide further detail into what the issue is with coverage on sympy and what you did for manual validation? When identifying “local files” how do you handle inheritance? E.g. if a class inherits a method from a parent class do you include both files? Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: a) Issue with Sympy Coverage: We use the Python coverage package in the TDD-Bench-Verified benchmark, which works well with Pytest. However, the Sympy project does not use Pytest for testing. Additionally, the coverage package may fail due to dependency issues. In Sympy, we were able to generate the coverage report but found that many fail-to-pass tests had zero coverage. We then manually checked several of the fail-to-pass tests and found inconsistencies in the coverage report. There were lines that were executed but not covered by the package. Therefore, we decided to exclude coverage from the TDD-Score metric for Sympy. b) Handling Inheritance: The Otter pipeline does not explicitly handle inheritance, but the localizer can include functions from the parent class if it deems them relevant to the issue description. In several instances, the localizer selects multiple functions from different files. Also, the localizer does not consider library functions because it only examines user-defined functions from the current repository. c) Clarification on Ablation: We apologize for the confusion with respect to Table 2, which presents the ablation study of Otter, not Otter++. Figure 2 offers an overview of Otter, which comprises three major components: localizers, a self-reflective action planner, and a test generator. Please see the modified ablation study for the GPT-4o model (the Mistral-large version will be added in the final release) in the table below. In the first group, we present the ablation on the action planner. The first row shows the results when the action planner is removed. The following two rows demonstrate the outcomes when action planning is retained, but action refinement and action validation input to the LLM are disabled. Note that without self-reflective action planning, we cannot refine our localizations. Therefore, we must present all the functions collected during focal and test localizations. In the second group, we present the ablation on the localizer. The table shows the results of omitting either or both localizations. We did not run self-reflection on partial or no localization because, without both localizations, self-reflective action planning does not add any value. The last two entries, “fixing import” and “imports at generation”, belong to our third component, the test generator. These are the only two rule-based entries. \| Model \| Component \| Approach \| # of fail-to-pass \| tddScore \| Change in tddScore% \| \|:-:\|:-:\|:-:\|:-:\|:-:\|:-:\| \| GPT-4o \| NA \| Otter \| 141 \| 29.4 \| NA \| \| \| Action Planner \| Otter - Action Planning (complete) \| 110 \| 23.6 \| -19.7 \| \| \| \| Otter - Plan Refinement (Just 1 attempt) \| 130 \| 27.5 \| -6.5 \| \| \| \| Otter - Action Validation \| 120 \| 25.7 \| -12.6 \| \| \| Localizers \| Otter - Focal Localization \| 115 \| 25.2 \| -14.3 \| \| \| \| Otter - Test Localization \| 107 \| 24.2 \| -17.7 \| \| \| \| Other - Focal & Test Localization \| 110 \| 24.2 \| -17.7 \| \| \| Test Generator \| Otter - Fixing Import \| 128 \| 26.7 \| -9.2 \| \| \| \| Otter - Imports at Generation \| 130 \| 26.7 \| -9.2 \| To clarify, Otter++ uses heterogeneous prompting and a rule-based ranker on execution logs. For heterogeneous prompting, we used the same prompts used for the ablation on Otter. Therefore, the execution log is not used by Otter.	Summary: The paper introduces Otter, an LLM-based solution that generates unit tests directly from issue descriptions before a code patch is written. This approach supports test-driven development scenario and reduces LLMs overfitting of unit tests to the specific focal code. Otter employs a self-reflective action planner to iteratively decide which code to read and how to construct meaningful tests. Additionally, Otter applies rule-based post-processing to fix missing imports and validate test correctness. To evaluate its effectiveness, the paper introduces TDD-Bench-Verified, a benchmark derived from SWE-Bench Verified, which measures test quality based on fail-to-pass rates. Empirical results show that Otter++ (an ensemble version of Otter) achieves a 37.0% fail-to-pass rate, outperforming previous methods like SWE-Agent+ (19.2%). Additionally, incorporating Otter-generated tests into automated patch validation improves precision from 60.8% to 91.9%, helping filter out incorrect fixes. The approach remains cost-effective, with test generation costing less than $0.10 per issue when using GPT-4o. Claims And Evidence: The claims are generally well supported by the evaluation, although the cost-effectiveness claim only takes into account the GPU inference costs but not the infrastructure for executing tests. Methods And Evaluation Criteria: The paper evaluates Otter’s test generation quality using fail-to-pass rates and TDDScore, both measured on the TDD-Bench-Verified dataset. The fail-to-pass rate directly assesses whether generated tests meaningfully capture the reported issue by failing on the buggy code and passing after the fix, with Otter achieving 31.4% (Otter) and 37.0% (Otter++) -- outperforming prior methods like SWE-Agent+ (19.2%). The TDDScore extends this evaluation by incorporating test adequacy, measuring whether the generated tests effectively cover relevant code changes. This metric provides a more granular evaluation of test quality, ensuring that the generated tests are both correct and comprehensive. For patch filtering, the paper measures how well Otter-generated tests improve precision and recall in validating patches using the SWE-Bench Verified dataset. The results show that filtering patches with Otter-generated tests increases precision from 60.8% to 91.9%, though recall drops to 33%, indicating a trade-off between accuracy and completeness. These results suggest that Otter-generated tests effectively eliminate incorrect patches while preserving some valid ones. Theoretical Claims: The Otter paper relies on empirical validation of its novel test generation approach, there are no theoretical proofs to verify. Experimental Designs Or Analyses: The Otter paper uses a structured ablation study to isolate the impact of key components, such as self-reflective action planning, focal/test localization, and import fixing. Removing action planning reduces fail-to-pass rates by 14–20%, while eliminating test localization leads to a steeper drop (up to 36%), confirming that each step significantly improves test quality. The study also shows that test localization contributes more than focal localization, suggesting that retrieving relevant tests is more critical for fail-to-pass success. While these results validate Otter’s design, a deeper breakdown of failure cases (e.g., incorrect test logic vs. mislocalization) would further clarify its contributions. In addition, it would be good to include alternative localization approaches -- for instance, using analysis of import statements, or based line test coverage (dynamic contexts). The paper also compares Otter against prior test-generation models on SWT-Bench Lite, showing that Otter++ (29.0%) outperforms SWE-Agent+ (19.2%) and Libro (15.2%), highlighting the benefits of self-reflection and execution-guided filtering over static LLM outputs. By evaluating Otter across TDD-Bench-Verified and SWT-Bench Lite, the study ensures its findings generalize beyond a single dataset. However, statistical significance testing is could also be conducted, making it more clear whether performance gains consistently hold across different types of issues. In addition, a comparison to other patch filtering techniques like those introduced in CodeT paper could be helpful. Supplementary Material: I reviewed generated tests, and instructions provided as well as the Otter++ code. Relation To Broader Scientific Literature: The Otter paper builds upon and extends prior research in LLM-driven test generation, automated software debugging, and self-correction. The techniques discussed in the paper are instrumental to building TDD-style SWE agents, where tests are generated upfront to guide issue resolution. This aligns closely with recent work in SWE-Agent, which explores GH issue resolution, SWT-Bench, which benchmarks test generation from issues, and CodeT, which to the best of my knowledge is the first to introduce the concept of test generation conditioned on the natural language problem description rather than focal code. Essential References Not Discussed: "CodeT: Code Generation with Generated Tests", B. Chen et. al Other Strengths And Weaknesses: Strengths: Otter’s focus on test generation from issues aligns with real-world SWE agentic workflows, making it highly applicable for automated debugging and test-driven development in software engineering. The introduction of TDD-Bench-Verified also provides a structured benchmark for evaluating fail-to-pass test generation, ensuring practical impact. Weaknesses The evaluation effectively quantifies success rates, but it does not deeply analyze why some generated tests fail (e.g., mislocalization, incorrect assertions, gaps in execution filtering, or patch applicability errors). A more detailed error categorization would provide stronger insights into where Otter struggles and how it can be further improved. Other Comments Or Suggestions: None Questions For Authors: The paper includes an ablation study evaluating the impact of test and focal localization on fail-to-pass rates, but could you provide further analysis on alternative localization strategies (e.g. based on imports or dynamic coverage context driven localization)? While the evaluation measures fail-to-pass success rates, it does not deeply analyze cases where Otter-generated tests fail to apply to patches. Have you experimented with alternative diff formats, can you break down these metrics for addition-only, patches, etc? A breakdown of these cases would help assess the robustness of Otter’s generated tests in practical debugging workflows. The study demonstrates that Otter-generated tests improve patch filtering, but have you compared Otter’s filtering mechanism to other patch ranking algorithms, such as those used in CodeT? How does Otter++ scale when increasing the number of generated tests per issue or expanding the number of candidate patches evaluated? Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: a) Alternative Localization Strategies: Thank you for your suggestion. To further assess the impact of localization, we re-ran Otter using oracle golden localizations for both focal and test functions. We did not observe any significant performance gain (32.5% vs 31.4% with GPT-4o) in the fail-to-pass rate. This indicates that Otter's localization is already good enough. Perfection is not required in this phase; for instance, it is fine to add a test to a different file than the golden test. b) Analyze Otter-generated tests: As per your suggestion, we have analyzed the Otter-generated tests using GPT-4o model from different perspectives, as outlined in the following table. We will include additional analysis in the final version of the paper. \| Perspective \| Category \| #of Sample \| #of fail-to-pass \| in %\| \|:-:\|:-:\|:-:\|:-:\|:-:\| \| Type of Test \| PatchExisting \| 122 \| 50 \| 41.0 \| \| \| AdditionOnly \| 327 \| 91 \| 27.8 \| \| Test on old Codebase \| Pass \| 69 \| 0 \| 0 \| \| \| AssertionFail \| 170 \| 97 \| 57.1 \| \| \| Fail \| 101 \| 40 \| 39.6 \| \| \| Error \| 109 \| 4 \| 3.7 \| \| Focal Localization \| Correct \| 370 \| 118 \| 31.9 \| \| \| Wrong \| 79 \| 23 \| 29.1 \| \| Test Localization \| Correct \| 317 \| 117 \| 36.9 \| \| \| Wrong \| 132 \| 24 \| 18.2 \| Modified/New: We see that the fail-to-pass rate is higher when patching an existing test than when adding a new test, which is expected because the model can have better context from the existing test. Writing a new test is inherently more difficult than modifying an existing test. Test on old codebase: It is expected that the test will fail on the old codebase. However, we found 69 samples in Otter where the test passed on the old codebase. Also, our analysis shows that tests with assertion failures have a higher success rate (57.1% fail-to-pass rate) compared to other groups. Focal Localization: We did not see much impact of focal localization on the performance, with 31.9% and 29.1% for correct and incorrect localization, respectively. Test Localization: Test localization has a significant impact on the performance (36.9% vs 18.2% for correct and incorrect localization). In our ablation study, we also found that test localization is more important than focal localization. Alternative diff: We did not explore alternative diff formats. Mundler et al. compared two diff formats in their paper and concluded that custom diff outperforms unified diff. Our approach shares some similarities with the custom diff format, as explained in response to reviewer ZeyC (Diff format). In brief, custom diff provides the file name, type of change (new/modified), position of the edit, and the complete class or function in response to a single call. We extract similar information from the LLM using multiple calls, while keeping the total number of calls low, with specialized prompts. This approach resulted in significantly better performance than those using different diff formats. c) CodeT Ranking: CodeT is not directly applicable to our current setup because we have multiple tests but not the solution. However, apart from filtering SWE-patches, we could use our tests to choose the best SWE-patch, which would be a good application of the Otter-generated tests. Following your suggestion, we have tried CodeT ranking on candidates from the top 3 leaderboard systems on SWE-Bench-Verified and observed 2% improvement. Note that some of these leaderboard solutions have already been through good rankers and used superior models. Improving upon these samples using a ranker may be difficult. We will add a discussion on CodeT ranking in the paper. d) Scaling of Otter++: Otter++ uses heterogeneous prompting and execution logs to select the best solution. Therefore, we cannot significantly increase the number of samples. Otter++ scaled well with samples up to 5, giving 0.5%-2.9% improvement. \| #of Candidate \| #of Fail-to-pass \| In % \| \|-\|-\|-\| \| 1 \| 141 \| 31.4 \| \| 2 \| 154 \| 34.3 \| \| 3 \| 157 \| 35.0 \| \| 4 \| 164 \| 36.5 \| \| 5 \| 166 \| 37.0 \| We conducted some experiments with temperature (see Reviewer ZeyC -Heterogeneous Prompts vs Temperature) to generate more samples, but we did not find it beneficial.	null	null	null	null	null	null
Geometric Resampling in Nearly Linear Time for Follow-the-Perturbed-Leader with Best-of-Both-Worlds Guarantee in Bandit Problems	Accept (poster)	Summary: The paper proposed some useful variants of the Geometric Resampling (GR) algorithm called Conditional Geometric Resampling (CGR) and those algorithms improve the sample complexity from O(K^2) to O(Klog(K)) in each round while keeping the BOBW guarantee for a certain perturbation distribution. The experiment result shows the proposed algorithms do perform well in the sample complexity and runtime while keeping a low regret while keeping the BOBW guarantee for a certain perturbation distribution. ## update after rebuttal I thank the authors for the response. Nothing major has changed, and I keep my score. Claims And Evidence: Yes, they claim the CGR algorithm has a great improvement compared to the GR algorithm and the experiments do show the improvement for runtime and sampling time. Methods And Evaluation Criteria: Yes, the paper says the reason that CGR achieves success is that CGR resamples the perturbation only from those satisfying a necessary condition for termination, and that makes sense. Theoretical Claims: Yes, such as Theorem 6. Experimental Designs Or Analyses: Yes, I checked Section 5. Supplementary Material: Yes, I checked the proof of the theorem stated in the main paper. Relation To Broader Scientific Literature: The paper proposed an experimental beneficial algorithm CGR and its method might have chances to be applied to other time-cost algorithms. Essential References Not Discussed: Not to my knowledge. Other Strengths And Weaknesses: The proposed algorithms greatly improve the sample complexity and runtime from previous GR algorithm. Other Comments Or Suggestions: Could you discuss more about the novelty of the proof of those regret theorems? It is unclear what technical contributions this paper adds. Questions For Authors: Are there any disadvantages of CGR to the other algorithms (such as Tsallis-INF)? Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: Thank you for taking the time to review our paper. We have addressed your question and comment below. Q1. Are there any disadvantages of CGR to the other algorithms (such as Tsallis-INF)? A1. Generally, we believe that CGR has no disadvantages over the conventional GR, as it is intuitively just cutting the redundant part of GR, and thus CGR is more effective on each metric. Although CGR overcomes the computational inefficiency compared with GR, it still inherits the general disadvantages of FTPL. This is mainly the difficulty of the theoretical analysis, such as the difficulty of the analysis for RV estimators and extensions to other settings. Q2. Novelty of the regret analysis. A2. Thanks for your comment. The main novelty in the regret analysis lies in the analysis of CGR II-B. The key difference in the regret analysis stems from the biased estimator, where the relevant term involves both $P(A_t)$ and $w_t$ differently from the original GR. By deriving a lower bound on $w_t/P(A_t)$, we obtained the desired result even with a smaller maximum number of resampling. While our current analysis is specific to the chosen definition of $A_t$ and the expression of $w_t$, we expect that similar results can be achieved in different settings beyond MAB by appropriately designing $A_t$ and selecting perturbations.	Summary: This paper studies FTPL for MAB problem. The authors first propose a general receipe for designing loss estimate procedure. Then they also give several concrete variants under this framework and shows that they enjoy certain improved time complexity while maintain the optimal BOBW guarantee. These theoretical findings are complemented by comprehensive numerical results. The proposed CGR I and II both bring improved empirical time complexity and regret compared to the conventional GR. Claims And Evidence: Yes Methods And Evaluation Criteria: Yes Theoretical Claims: I checked the main body which looks good to me. Experimental Designs Or Analyses: Yes Supplementary Material: Yes, the additonal experimental results. Relation To Broader Scientific Literature: potential audience: people studying bandits/RL/stats Essential References Not Discussed: n/a Other Strengths And Weaknesses: Strengths 1. Gives a new framework for loss estimate in FTPL. 2. Supporting empirical results. Other Comments Or Suggestions: n/a Questions For Authors: 1. any intuitions for why the new proposed scheme would give better empirical regret? Code Of Conduct: Affirmed. Overall Recommendation: 5	Rebuttal 1: Rebuttal: Thank you for taking the time to review our paper. We have addressed your question below. Q1. Any intuitions for why the new proposed scheme would give better empirical regret? A1. Generally, the variance of the estimator $\widehat{w_{t,I_t}^{-1}}$ introduces an additional regret term in the analysis, which is strongly related to the expected number of resampling in GR and CGR. Since the expected number of resampling is significantly reduced in CGR, the variance of $\widehat{w_{t,I_t}^{-1}}$ is also effectively reduced, compared with that of GR (as explained in Remark 2). Therefore, the regret from the estimation error of $w_{t,I_t}^{-1}$ gets improved effectively, which also leads to the improved theoretical guarantee in Theorem 5. --- Rebuttal Comment 1.1: Comment: I've read the response from the authors and also the communication between the authors and other reviewers. While this work is limited to MAB, personally I'm still impressed by a new recipe for design and analysis of FTPL, which expends the theoretical understanding on FTPL, so I would still like to support this paper and recommend acceptance.	Summary: The paper proposes a new estimation procedure based on conditional resampling to improve both theoretically and empirically the sample efficiency of FTPL while maintaining the regret guarantees. Claims And Evidence: Claims are supported by clear evidence. Methods And Evaluation Criteria: Evaluation criteria and methods make sense. Theoretical Claims: I have not checked the correctness of proofs. Experimental Designs Or Analyses: I checked all experimental designs and they look valid to me. Supplementary Material: I have not reviewed the supplementary. Relation To Broader Scientific Literature: The paper presents a significant result in FTPL literature. Essential References Not Discussed: Prior work discussion seems extensive. Other Strengths And Weaknesses: The conditional resampling is a refreshing idea to overcome potential computational issue in FTPL. Other Comments Or Suggestions: N/A Questions For Authors: How would the analysis change in the proposed sampling approach when extending from bandits to semi-bandits? Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: Thank you for taking the time to review our paper. We have addressed your question below. Q1. How would the analysis change in the proposed sampling approach when extending from bandits to semi-bandits? A1. The analysis would not change so much if we are just interested in extending our sampling approach to derive results similar to Neu and Bartók (2016) for semi-bandits. Still, their results are only for near-optimal regret bound in the adversarial setting, and extending the BOBW analysis to semi-bandits is significantly difficult. In general, the key to the BOBW analysis in FTPL and FTRL is obtaining a uniform bound on $-w_{t,i}'/w_{t,i}^{3/2}$. Thus, the expression of $w_{t,i}$ significantly impacts the regret analysis. In the semi-bandit setting, the arm selection probability vector $w_t$ no longer lies in the probability simplex since multiple arms can be selected in one round. As a result, several techniques used in Honda et al. (2023) and Lee et al. (2024) become no longer applicable. In addition, to obtain the desired results for CGR II-B, the events $A_t$ would need to be modified according to the behavior of $w_t$ in semi-bandits.	Summary: The paper proposes Conditional Geometric Resampling (CGR) to improve the computational efficiency of the Follow-the-Perturbed-Leader (FTPL) algorithm in the multi-armed bandit problem. By introducing a carefully selected, necessary stopping condition in the resampling process, CGR reduces the expected computational complexity of standard Geometric Resampling from the quadratic $O(K^2)$ expected per-round time to the near-linear $O(K \\log K)$ while guaranteeing the same best-of-both-worlds regret guarantees from Honda et al. (2023) and Lee et al. (2024). More precisely, three variants of CGR are introduced: CGR I, CGR II-unbiased, and CGR II-biased. These variants offer different trade-offs between computational efficiency and estimation bias. The authors provide both theoretical regret bounds and experimental results that demonstrate lower runtime and improved regret performance compared to previous approaches. Claims And Evidence: The theoretical claims are clearly stated with complete proofs. The claims on the empirical performance are also validated by appropriate experiments. Methods And Evaluation Criteria: Yes. Theoretical Claims: Yes, with more focus on the proofs of claims relative to the number of resampling iterations. Experimental Designs Or Analyses: My main concern about experiments is the omission of FTPL CGR II-B from the experiments other than the number of resampling. The reason provided by the authors is because the number of resampling is essentially indistinguishable from that of FTPL CGR II-U, and so the other experiments only consider the latter algorithm. However, it would still be interesting to observe whether the performance is indistinguishable with respect to other performance metrics too (at least for the experiments performed in this work). For instance, the indistinguishability seems to appear for large enough $K$, e.g. $K \\ge 32$, but the first experiment measuring the cumulative regret considers $K = 8$. Supplementary Material: Yes, with more focus on the proofs of claims relative to the number of resampling iterations. Relation To Broader Scientific Literature: The adoption of FTPL with geometric resampling to achieve best-of-both-worlds regret guarantees for multi-armed bandits has alredy been considered by previous work. The main contribution of this paper lies in the design of more clever conditional geometric resampling procedure that employ a carefully chosen necessary stopping condition. This allows an improved computational complexity with respect to other algorithms that achieve a similar regret performance. The authors are clear in the comparison with the main related work. Essential References Not Discussed: The authors seem to have covered the essential related work in their discussion. Other Strengths And Weaknesses: The main techincal contribution is the design of variants of and the consequent improvement in the computational complexity of FTPL while preserving BOBW guarantees. Regarding the regret analysis per se, there seems to be no significant difference compared to prior work. Nevertheless, the time performance is also a relevant factor in practice and the contribution in this direction is interesting. Other Comments Or Suggestions: - In the Problem Setup section, you define losses $\\ell_t$ in the adversarial setting as being possibly functions of the history of losses and chosen arms, but it seems that you may assume they depend on $(I\_1, \\dots, I\_{t-1})$ w.l.o.g. - Starting from Section 3, $\\sigma_i$ is introduced but it seems to also depend on the round $t$; making this dependence explicit (e.g., writing $\\sigma\_{i,t}$) is probably clearer. - Theorem 5 seems more of a remark than an actual theorem. - In Section 5, it would be clearer to also specify how the confidence intervals around the curves were chosen (e.g., standard deviation?). Questions For Authors: - What is the main technical difficulty in designing a variant of GR that is a sort of counterpart of Tsallis-INF with the Reduced-Variance estimator, especially compared to using importance weighting? - Did you actually run all the other experiments for FTPL CGR II-B on your own? If so, was there no meaningful difference compared to FTPL CGR II-U? Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: Thank you for your thorough review and valuable feedback on our work. We have addressed your questions and comments below. Q1. What is the main technical difficulty in designing a variant of GR that is a sort of counterpart of Tsallis-INF with the Reduced-Variance estimator, especially compared to using importance weighting? A1. The main technical difficulties in constructing the Reduced-Variance (RV) estimator for FTPL with GR are as follows: The RV estimators can take negative value, which makes the analysis significantly difficult. Owing to this issue, after Zimmert \& Seldin (2021) proposed RV estimator, there are still some papers on FTRL that only considers the Importance-Weighted estimator (Jin et al., 2023; Tsuchiya et al., 2023). Moreover, for FTPL with GR, since the importance weight $w_{t,i}^{-1}$ is replaced with $\widehat{w_{t,i}^{-1}}$, the design and analysis of the RV estimator is more challenging. Julian Zimmert and Yevgeny Seldin. "Tsallis-INF: an optimal algorithm for stochastic and adversarial bandits.'' JMLR, 2021. Tiancheng Jin, Junyan Liu, and Haipeng Luo. "Improved best-of-both-worlds guarantees for multi-armed bandits: FTRL with general regularizers and multiple optimal arms.'' NeurIPS, 2023. Taira Tsuchiya, Shinji Ito, and Junya Honda. "Best-of-Both-Worlds Algorithms for Partial Monitoring.'' ALT, 2023. Q2. Did you actually run all the other experiments for FTPL CGR II-B on your own? If so, was there no meaningful difference compared to FTPL CGR II-U? A2. We actually ran all the experiments for FTPL CGR II-B, including the pseudo regret for $K=8$ and $K=32$, running time for $K$ varying from $2$ to $128$, and the number of resampling for $K=8$ and $K=32$. We confirmed that there is no meaningful difference compared to FTPL CGR II-U. The detailed results can be found at the this link: https://anonymous.4open.science/api/repo/ICML2025_CGRII_Experiments-9807/file/additional_experiments.pdf?v=86d6493c Q3. Assumption on the losses in the adversarial setting: we may assume they depend on $(I_1,\ldots, I_{t-1})$. A3. Thank you for the comment. While we mentioned the loss may depend on both $\ell$ and $I$, this phrasing was introduced primarily to clarify that we consider an adaptive adversary rather than an oblivious one. Still, we understood that as pointed out it is indeed sufficient to consider the loss as a function of $I$'s as in the literature considering an adaptive adversary (Arora et al., 2012; Zimmert \& Seldin, 2021). We will modify the writing accordingly. Raman Arora, Ofer Dekel, and Ambuj Tewari. "Online bandit learning against an adaptive adversary: from regret to policy regret.'' ICML, 2012. Julian Zimmert and Yevgeny Seldin. "Tsallis-INF: an optimal algorithm for stochastic and adversarial bandits.'' JMLR, 2021. Q4. - Starting from Section 3, $\sigma_i$ is introduced but it seems to also depend on the round $t$; making this dependence explicit (e.g., writing $\sigma_{i,t}$) is probably clearer. - Theorem 5 seems more of a remark than an actual theorem. A4. We sincerely appreciate your helpful suggestion. We will modify the notation accordingly to improve clarity. Q5. In Section 5, it would be clearer to also specify how the confidence intervals around the curves were chosen (e.g., standard deviation?). A5. Thank you for the valuable suggestion. The confidence intervals in the experimental results represent the standard deviation. We will modify the writing to clarify it.	null	null	null	null	null	null
Compositional Risk Minimization	Accept (poster)	Summary: This paper addresses compositional generalization by tackling compositional shift, where test data contains unseen combinations of attributes. The authors propose Compositional Risk Minimization (CRM), using additive energy distributions to model attributes and providing an alternative to empirical risk minimization. Their approach involves training an additive energy classifier and adjusting it for compositional shifts, with theoretical analysis showing extrapolation capabilities to affine hulls of seen attribute combinations. Experimental results on benchmark datasets demonstrate improved robustness compared to existing methods for handling subpopulation shifts. Claims And Evidence: The claims are supported by both theoretical and empirical evidence. Methods And Evaluation Criteria: Yes, the evalucation criteria (Average Accuracy and Worst Group Accuracy) makes sense. Theoretical Claims: The mathematical derivations and theoretical arguments seem rigorous upon initial examination. Experimental Designs Or Analyses: Based on my review of the experimental section, the empirical results support the paper's claims. Supplementary Material: I conducted a cursory review of the supplementary materials without performing an in-depth analysis. Relation To Broader Scientific Literature: The authors provide a thorough and systematically structured overview of previous work in this research area. Essential References Not Discussed: None Other Strengths And Weaknesses: Strengths: 1. The research tackles an important problem in compositional generalization with novel insights. 2. Clear implementation details and reproducibility through provided pseudocode. Weakness: Limited empirical comparisons against existing baseline methods Other Comments Or Suggestions: The authors use 'Compositional Risk Minimization' as the title. Could you explain the core concept of Compositional Risk Minimization using simple mathematical formulations? Please refer to the classical mathematical formulation of Empirical Risk Minimization (ERM). Questions For Authors: No Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: We thank the reviewer for their positive and insightful feedback! We now address the concerns raised by the reviewer ahead. 1. Limited empirical comparisons against existing baseline methods We have done extensive benchmarking of CRM with 6 widely used baselines in the literature of subpopulation shifts apart from ERM. Please check Table 5 in Appendix G.1, where we compare CRM with GroupDRO, LC, sLA, IRM, VREx, and Mixup. We find that CRM outperforms all the baselines across diverse benchmarks w.r.t. the worst group accuracy. Note that in the main body of the paper (Table 1), due to space constraints where we only compared with the best performing baselines (GroupDRO, LC, sLA). Also, note that our primary comparison baseline has been with GroupDRO, as it is the most effective method for addressing subpopulation shifts, hence it was the main focus of our work. We also included baselines like LA (Logit Adjustment) that share conceptual similarities with our approach. 2. The authors use 'Compositional Risk Minimization' as the title. Could you explain the core concept of Compositional Risk Minimization using simple mathematical formulations? Please refer to the classical mathematical formulation of Empirical Risk Minimization (ERM). The classical ERM objective can be stated as follows. $$ R_p(f) = \sum_{z \in \mathcal{Z}} p(z)R(f\|z)$$ where $R(f\|z) = \mathbb{E}_{p(x\|z)}[\ell(f(X),Y)\|z]$ and $p(z)$ is the training prior probability and $\mathcal{Z}$ is the set of all $d^m$ groups. If $\ell$ is the cross-entropy loss, then output of ERM (with no capacity constraints) matches the true $p(z\|x)$. Also, note that in the above summation $p(z)$ is zero on all groups that are not in the support of the training distribution. To tackle compositional distribution shifts, we want to learn predictors that minimize $$ R_q(f) = \sum_{z \in \mathcal{Z}} q(z)R(f\|z)$$ and not $R_p(f)$, which ERM minimizes. In the above objective $q(z)$ can be non-zero on groups $z$ that have zero probability under $p(z)$. Our results show that our approach outputs a predictor that provably minimizes risk under any compositional shift $R_q(f)$ and hence the name compositional risk minimization. Specifically, in Theorem 3, we showed that CRM outputs the Bayes optimal predictor and hence it provably minimizes $R_q(f)$ with a high probability, where $\ell$ is cross-entropy loss or $0/1$ loss, as long as the number of training groups grow as $O(md + dlog d)$. To clarify, our approach does not require us to explicitly compute the risk on the test distribution $R_q(f)$. For additive energy distributions, in the second step of CRM we adapt the $\hat{p}(z\|x)$ to $\hat{q}(z\|x)$ with the extrapolated bias $B^{\star}$, which equals the true test predictor $q(z\|x)$ (Theorem 2). Hence, CRM avoids the computation of $R_q(f)$. Thanks again for this interesting question! We will add this discussion to the paper as well. We are very open to further discussion and would be happy to address any remaining concerns.	Summary: This paper proposes compositional risk minimization (CRM), an approach to compositional generalization that is based on additive energy distributions. The intuition is to train an energy-based classifer on the training set, then modify it to account for known bias between the observed training and test distributions. The authors show a number of theoretical results as well as empirical results on benchmarks for subpopulation shifts. Claims And Evidence: Yes, all claims are supported with adequate theoretical and empirical evidence. Methods And Evaluation Criteria: The method is well constructed and the benchmarks are well chosen. Theoretical Claims: The proofs appear correct; no issues found. Experimental Designs Or Analyses: The experimental setup described in section 5.1 appears sound. Supplementary Material: I looked at the proofs and additional results; both appear to support the claims of the main text. Relation To Broader Scientific Literature: This work is related to prior work on compositionality with energy-based models. However, these works typically consider a generative setting; by contrast, the authors consider a discriminative setting and produce a novel set of theoretical results. Essential References Not Discussed: No missing references as far as I am aware. Other Strengths And Weaknesses: The paper is quite well written and presented. Experiments are conducted over a number of datasets. Overall, the authors present an interesting, fresh approach to compositional generalization. My main concern is whether the additive energy distribution assumption is realistic (beyond the particular subpopulation-shift setting considered in the experiments). It would be great to have additional discussion on this point. Other Comments Or Suggestions: Typos - "boradcasting" in Figure 1 caption Questions For Authors: What practical settings is the additive energy distribution assumption applicable to? For example, does it apply to the blue elephant on the Moon example laid out in the introduction? It's reasonable if it does not hold, but discussing the boundaries of when it holds would be good to include. Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: We thank the reviewer for their positive and insightful feedback! We will fix the typo in the caption of Figure 1, thanks for pointing this. We now address the concerns raised by the reviewer ahead. My main concern is whether the additive energy distribution assumption is realistic (beyond the particular subpopulation-shift setting considered in the experiments). It would be great to have additional discussion on this point. What practical settings is the additive energy distribution assumption applicable to? For example, does it apply to the blue elephant on the Moon example laid out in the introduction? It's reasonable if it does not hold, but discussing the boundaries of when it holds would be good to include. We believe that additive energy assumption is practical for settings where the image is aptly described by an AND operation among the attributes (and this applies to the blue elephant example). The summation of additive energies leads to a product of exponentials which act as a soft AND operation. Hence, each energy term contributes to checking one of the conditions in the AND operation. Regarding the specific image "blue elephant on the moon", let us start with a simplification of this image, "elephant on the moon". Then we have one energy term that detects elephant and the other energy term detects moon. However, let us now consider the original image "blue elephant on the moon". If we do a simple AND between detecting blue color, elephant, and the moon, then even the image "elephant on blue moon" will have the same energy (density) as the image "blue elephant on the moon", which is not desirable. But we can model this scenario using additive energy distribution by having energy components for each object-specific attribute. Hence, the final energy function becomes $E(x\|o, z)= \sum_{o_i} \sum_{z_{ij}} E_{ij}(x, o_i, z_{ij})$, where $o_i$ refers to the location of the $i^{th}$ object and $z_{ij}$ refers to the $j^{th}$ attribute for the $i^{th}$ object. This essentially allows us to "bind" the attribute information to an object and still model the overall distribution with additive energies. In the example above, we have one energy term for the object elephant with attribute blue, which gets added with the energy term for the object moon (with some default attribue value). Thanks again for this interesting question! A thorough investigation of this is a fruitful future direction. We are very open to further discussion and would be happy to address any remaining concerns.	Summary: This paper introduces a method for addressing compositional shifts in discriminative tasks. The authors propose a theoretical framework built on additive energy distributions, where each energy term represents an attribute. They introduce the discrete affine hull concept to characterize extrapolation capabilities. Their two-step algorithm first trains an additive energy classifier to predict attributes jointly, then adjusts this classifier for compositional shifts. Theoretical guarantees show that the proposed method can extrapolate to test distributions within the discrete affine hull of training distributions. Experiments on several benchmarks demonstrate the effectiveness of the proposed method. Pros: + The proposed method is well-motivated and reasonable, and builds on additive energy distributions that are studied in generative compositionality. + The proposed algorithm is practical and easy to implement. And the authors provide detailed implementation in the appendix. + The extensive empirical evaluation demonstrates consistent improvements across diverse benchmarks. Cons: - The additive energy assumption may be too limited for many real-world situations where different factors interact in complex ways rather than simply adding together. This could reduce how useful the approach is in practice. - The additive energy distributions were previously studied in generative compositionality, while the authors extend this framework to discrimination tasks. This is an incremental contribution and the novelty appears limited in scope. - The paper assumes access to attribute labels during training, which might not always be available in practice. Claims And Evidence: 1. The authors provide rigorous theoretical analysis with detailed proofs showing that the proposed method can generalize to novel attribute combinations within the discrete affine hull. 2. Empirical validation on several common benchmarks show the proposed method outperforms other baselines. Methods And Evaluation Criteria: 1. The proposed two-step algorithm is consistent with the theoretical framework. The proposed method is well-motivated and reasonable, and builds on additive energy distributions that are studied in generative compositionality. 2. The authors use average accuracy, group-balanced accuracy, and worst-group accuracy to evaluate performance. The evaluation is comprehensive. Theoretical Claims: The proofs appear mathematically sound. The theoretical analysis provides a sharp characterization of extrapolation, demonstrating that generalization beyond the discrete affine hull is fundamentally impossible. This establishes clear boundaries on what can be achieved in this domain. Experimental Designs Or Analyses: The experiments systematically demonstrate the advantages of the proposed method, especially on worst-group accuracy. The ablation studies clearly show the importance of the extrapolated bias term, which aligns with the theoretical framework. Supplementary Material: The appendix is comprehensive and provides strong support for the claims in the main paper. It provides detailed theoretical proofs for all theorems, and additional experimental results for each benchmark and compositional shift scenario. Relation To Broader Scientific Literature: 1. This work is built on additive energy distributions for generative tasks. The authors extend it to discriminative tasks. 2. The problem connects to out-of-distribution generalization and subpopulation shifts. The authors clearly articulate how compositional generalization relates to these established research areas. Essential References Not Discussed: The idea that compositional generalization can only be achieved within the discrete affine hull is analogous to the assumption in the following papers, which posit that the test distribution should lie within the convex hull of the training distributions: [1] Qiao, F., & Peng, X. Topology-aware Robust Optimization for Out-of-Distribution Generalization. ICLR 2023. [2] Yao, H., Yang, X., Pan, X., Liu, S., Koh, P. W., & Finn, C. Improving Domain Generalization with Domain Relations. ICLR 2024. Other Strengths And Weaknesses: Please see summary. Other Comments Or Suggestions: None. Questions For Authors: 1. The paper assumes attribute labels are available during training. Can the proposed method be adapted to settings where attribute labels are only partially available or must be inferred? 2. How does the computational complexity of the proposed method scale with the number of attributes and classes? Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We thank the reviewer for their positive and insightful feedback! We are glad they appreciate the technical soundness of our work, on both the theoretical and empirical front. We now address the concerns raised by them. > Additive Energy Distribution (AED) Limitations We emphasize that the benchmarks used to evaluate CRM are both realistic and widely adopted in the subpopulation shift literature. Since CRM consistently outperforms baselines, this suggests that AED assumption is not overly restrictive and can model realistic datasets effectively. We now clarify how AED models complex interactions between attributes. Note that AED does not imply additive interactions in data space ($x= \sum_{i} g(z_i)$) as in additive decoders (Lachapelle et al. 2024). Instead, it models the AND operation between attributes, as illustrated below via examples (check Appendix B for details). i) Consider images that contain a distinct object varying in shape, size, and color. At any pixel, it is unlikely that shape, color, and size attributes interact additively, rather their interactions are complex which can't be captured via additive decoders. However, under AED, interactions are modeled via an energy component per attribute: one detecting shape, AND another detecting color, AND a third detecting size. Together, these energy terms define the distribution of images conditioned on attributes. ii) An example from a different data modality is the the CivilComments benchmark, where the attributes toxic language (class label) and demographic identity (spurious attribute) interact non-trivially in text space. However, under AED, we can model their interactions via an energy component that checks whether the language is toxic, AND another energy component checks the demographic identity. > Novelty of the work We explain the key features that set this work apart. a) Discrete Affine Hull, a novel mathematical object: Existing AED works in generative compositionality lack theoretical guarantees for generalization beyond training data. To address this, we introduce a novel mathematical object, the discrete affine hull, which precisely characterizes extrapolation to new distributions for both discriminative and generative tasks. For instance, our theoretical guarantee states that it is possible to generalize from $O(md)$ groups to $d^m$ groups in both discriminative and generative tasks. b) Discriminative training without estimating partition function:* Compositionality in discriminative tasks is a major problem, and our work makes key advances. One way to learn a classifier is via generative classification (lines 171-190, right column), where we first train densities $\hat{p}(x\|z)$ on observed groups, estimate new densities via affine combinations, and then use Bayes rule to derive $\hat{p}(z\|x)$. While this guarantees generalization, it is impractical due to the intractable gradient estimation of log partition functions (line 193-207, right column). While CRM circumvents these issues and retains the same guarantees. > Prior work regarding convex hulls We thank the reviewer for pointing us to these references, and we are happy to cite and contrast with them. However, note that the densities from a new group $q(x\|z')$ in the affine hull cannot be expressed as a convex or even an affine combination of the densities. For details, see e.q. (22) in Appendix D.2, summarized below. $\log\big(q(x\|z')\big)= \sum_{z\in \mathcal{Z}^{\mathsf{train}}}\alpha_z \log p(x\|z) - R\big(\{\alpha_z\}_{z\in \mathcal{Z}^{\mathsf{train}}}\big)$ Thus, in our setting, only energy terms are expressed as an affine combination, and our guarantees apply to distributions that are outside the convex hull of the training distributions. > Missing attribute labels scenario We believe this is an exciting future work. Existing works such as XRM (Pezeshki et al. 2024) show how one can discover the environments and then use existing domain generalization methods that require environment labels. We believe it would be exciting to extend these works to infer spurious attributes directly in combination with our approach. > Computational complexity of CRM For CRM training stage 1 (e.q. 7), the cost for each step is similar to that of training an ERM-based classifier for predicting the group $z$, which is proportional to $\| \mathcal{Z}_{\mathsf{train}} \| \times m \times d$. In the training stage 2, we compute the extrapolated bias $B^{*}(z)$ (e.q. 11), and the cost is proportional to $\| \mathcal{Z}_{\mathsf{test}} \| \times \text{number of training samples} \times m \times d$. Observe that in the worst case scenario the number of classes for $z$ at test time is $d^m$, making inference cost $O(d^{m+1}m)$. Any method that predicts $z$ would have to compute a probability vector of size $d^m$ and thus spend at least $O(d^m)$ per inference. Thanks again for your constructive comments, and please let us know if there are any remaining concerns.	Summary: This paper addresses the compositional shifts, a hard type of sub-population shifts, and proposes compositional risk minimization. The method is well-motivated and some theoretical analyses are provided. Results on the sub-population shift benchmark are shown to support the proposed method. Claims And Evidence: - The compositional risk minimization method is reasonable and well-motivated. - The formulation of the compositional shift setting provides a foundation for further research. - Experimental results are good to support the method. Methods And Evaluation Criteria: The analysis and proposed algorithm are designed to handle multiple attributes, with the theoretical advantages being most relevant for this multi-attribute context. However, the experiments are limited to only 2~3 attributes. I suggest that the authors include empirical results with multiple attributes to better align with the theoretical analysis. Theoretical Claims: Correct Experimental Designs Or Analyses: I understand that the paper’s chosen disjoint setting adds a level of complexity. However, in real-world scenarios, it is often feasible to obtain a small number of samples for different attribute combinations (particularly with only two attributes, as in these experiments). The proposed method should also be evaluated in traditional settings where all attribute combinations have some representation. This would confirm that the method performs well without requiring group-dropping. Supplementary Material: Yes, I checked the additional experimental results. Relation To Broader Scientific Literature: This paper proposes a more efficient method for domain generalization. Essential References Not Discussed: None Other Strengths And Weaknesses: N/A Other Comments Or Suggestions: I would suggest the authors moving additional results into the main body. Questions For Authors: N/A Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We thank the reviewer for their positive and insightful feedback! We now address the concerns raised by the reviewer ahead. 1. The analysis and proposed algorithm are designed to handle multiple attributes, with the theoretical advantages being most relevant for this multi-attribute context. However, the experiments are limited to only 2~3 attributes. I suggest that the authors include empirical results with multiple attributes to better align with the theoretical analysis. Thanks for raising this issue, we would like to provide some clarifications regarding this. In our theoretical results (Theorem 2 & 3), the key finding is that if we observe $O(md + dlogd)$ groups at training time, then CRM would generalize to test distributions over all the $d^m$ groups. Note that the result considers the setting with multiple groups, which can arise from multiple attributes $m$ or from multiple values per attribute $d$. Hence, the theoretical advantages are not restricted to the multi-attribute scenario. In our experiments, we already consider several scenarios that go beyond few attributes and few groups. NICO++ dataset has 360 groups, CelebA (multiple spurious attribute case, Table 12, Appendix G.3) consists of 5 attributes and a total of 32 groups. In addition to this, we also provided experiments on synthetic data with varying $d$ ($m=2$ with $d$ up to 50 leading to 2500 groups) and varying $m$ ($d=2$ and $m$ up to $9$ leading a total of 512 groups) in Figure 9, Appendix G.6. In all these experiments CRM performs well thus aligning the behavior of the method with the theoretical claims. Finally, we also want to point the guarantees in Theorem 2 are applicable to settings with small number of groups as well, i.e., in the setting of datasets like Waterbirds CRM offers a non-trivial Bayes optimality guarantee when only three out of the four groups are observed at training time. 2. I understand that the paper’s chosen disjoint setting adds a level of complexity. However, in real-world scenarios, it is often feasible to obtain a small number of samples for different attribute combinations (particularly with only two attributes, as in these experiments). The proposed method should also be evaluated in traditional settings where all attribute combinations have some representation. This would confirm that the method performs well without requiring group-dropping. In the paper, we had already carried out a comparison in the traditional setting where all attribute combinations have some representation. These were presented in the rightmost column in Table 1, "WGA (no groups dropped)", as well as in Table 14 in Appendix G.5 which contains additional metrics. CRM remains competitive with the baselines in this scenario. This confirms that the method performs well also without requiring group-dropping. We also want to point that as the number of groups grow (due to increase in $d$ or $m$), it is natural to expect that we will be disjoint setting where no samples are available from any group. Also, given the page limit, several results currently are in the supplementary material and we will move some results to the main body in the future revision. If you want us to move some specific result to the main body, please let us know. Thanks again for your constructive comments! We are open to further discussion and would be happy to address any remaining concerns.	null	null	null	null	null	null
Continuous Visual Autoregressive Generation via Score Maximization	Accept (poster)	Summary: This paper presents a new continuous visual autoregressive generative framework, which prevents the information loss caused by vector quantization. This framework takes energy score as the training objectives, which is likelihood-free and easy to make probabilistic predictions in the continuous space. In addition, the authors conduct many experiments to demonstrate the effectiveness of the proposed method. ## update after rebuttal I appreciate the authors' thorough response and the effort they put into the rebuttal. My concerns have been resolved, thus, I raise my score to accept. Last but not least, the authors are encouraged to include experiments on ImageNet $512 \times 512$ conditional generation in the final version. Claims And Evidence: Strengths + The motivation of this paper is strong and meaningful. It is an imperative direction for visual generation. + Unlike quantization-based approaches, the proposed method can avoid the information loss. It is mainly supported by the superior results in Table 1. + Based on energy score, autoregressive models can achieve an efficient inference, due to it only needs a single forward pass for each token prediction. Weaknesses None Methods And Evaluation Criteria: Strengths + The proposed energy loss is simple and intuitive. It addresses the shortcomings of GIVT and diffusion loss. + The proposed method is easy to implement and easy to understand. Its effectiveness is validated by the results on ImageNet $256 \times 256$ conditional generation. Weaknesses - The random noise is drawn from a uniform distribution. What the principle for this choice is? If using a gaussian noise, is it ok? - Likewise, the masking ratio is sampled in the range of $[0.7, 1.0]$. It is not a default choice. What the principle for this choice is? Theoretical Claims: I have check the correctness of any proofs for theoretical claims. And I do not find any errors. Experimental Designs Or Analyses: Strengths + The conducted experiments can demonstrate the effectiveness of the proposed method. In addition, the ablation studies on $\alpha$ and CFG also highlight the suitable value of these hyperparameters. Weaknesses - In Table 1, it is essential to show the results of MAR and GIVT. They are two important baselines to compare. - In Figure 2, the speed for MAR maybe not correct. To my knowledge, the speed of MAR in Figure 2 is slower than MAR paper. Could you provide more details about inference settings? - This paper only shows the comparisons on ImageNet $256 \times 256$ conditional generation. It is better to show more results to assess the proposed method, like ImageNet $512 \times 512$ conditional generation. - The ablation studies are insufficient. It is better to investigate more settings, such as the choice of random noise and mask ratio. Supplementary Material: This paper does not have the supplementary material. Relation To Broader Scientific Literature: To my knowledge, the proposed method in this paper is new. Essential References Not Discussed: To my knowledge, there is no other references to be discussed. Other Strengths And Weaknesses: None Other Comments Or Suggestions: None Questions For Authors: I appreciate the effectiveness of the proposed method on image generation, although the experiments of this paper are insufficient. Thus, I prefer to rate this paper as weak accept. If authors addresses my concerns, I would like to raise my score. Code Of Conduct: Affirmed. Overall Recommendation: 4	Rebuttal 1: Rebuttal: We sincerely appreciate the Reviewer's time and efforts in reviewing our work. We provide discussions about the concerns as follows. > In Table 1, it is essential to show the results of MAR and GIVT. They are two important baselines to compare. We fully agree with the Reviewer and will include comparisons with MAR and GIVT in the main table. > In Figure 2, the speed for MAR maybe not correct. To my knowledge, the speed of MAR in Figure 2 is slower than MAR paper. Could you provide more details about inference settings? The difference in reported speeds arises from differing evaluation protocols: + In the MAR paper, the authors measure inference time using the maximum batch size and report the average time per image, which benefits from parallel computation. + In our experiments, we follow the more common practice of benchmarking with a batch size of 1 to reflect real-world deployment scenarios where latency matters. Under the setting of batch=1, MAR’s diffusion process incurs significant decoding latency due to its iterative nature. While increasing the batch size improves MAR’s throughput, EAR remains approximately 2× faster than MAR under maximum batch size conditions. > This paper only shows the comparisons on ImageNet 256x256 conditional generation. It is better to show more results to assess the proposed method, like ImageNet conditional generation. We appreciate the Reviewer’s valuable suggestion. We are currently conducting experiments on ImageNet 512×512 conditional generation to further validate the effectiveness of our method. These results will be included in the final version of our paper. > The ablation studies are insufficient. It is better to investigate more settings, such as the choice of random noise and mask ratio. We thank the Reviewer for pointing out these concerns. Regarding the mask ratio, we directly adopted the range of [0.7, 1] from MAR, without further tuning. Regarding the random noise, we empirically observe that uniform noise yields slightly better performance compared to Gaussian noise. Specifically, for EAR-B: w/o CFG, FID increases from 5.46 (uniform) to 5.74 (Gaussian); w/ CFG, FID increases from 2.83 (uniform) to 2.89 (Gaussian). We will ablate this choice in the revised manuscript.	Summary: This paper introduces a continuous visual autoregressive framework EAR. The approach is grounded in strictly proper scoring rules, which provide a statistical basis for evaluating generative models, and primarily utilizes an energy score-based training objective to handle continuous data without requiring likelihood estimation. Update after rebuttal: I appreciate the authors' efforts. The response has clarified some of the issues I raised and helped me better understand certain aspects of the work. However, taking into account the points raised by other reviewers, I do not find enough justification to change my overall assessment. Therefore, I will maintain my original rating. Claims And Evidence: Not clear enough. See weaknesses. Methods And Evaluation Criteria: Yes. Theoretical Claims: Yes. Eq (1) - Eq (7) are from existing papers. Experimental Designs Or Analyses: Yes. Supplementary Material: N/A. Relation To Broader Scientific Literature: The main framework is from VAR. This paper modifies some components. Essential References Not Discussed: No. Other Strengths And Weaknesses: Strengths: 1. The paper is the first to apply strictly proper scoring rules to continuous visual autoregressive modeling. 2. It offers a theoretical discussion on how different strictly proper scores, such as the energy score, can be leveraged as training objectives, unifying previous continuous autoregressive approaches like GIVT and diffusion loss under a common framework. Weaknesses: 1. The paper does not clearly justify why Strictly Proper Scoring Rules are used to analyze Continuous Visual Autoregressive Generation. While the paper mentions that “GIVT is confined to the pre-defined family of Gaussian mixtures,” this is not necessarily a drawback. Instead, it may be the result of deliberate selection by the GIVT authors after thorough comparisons. The paper fails to explain why this limitation is a concern and to motivate its ideas. 2. The authors claim that continuous AR is superior to discrete AR, but the performance of their proposed EAR (Table 1) does not consistently support this assertion. For instance, EAR underperforms compared to MAGVIT-v2. Moreover, the training cost of EAR is significantly higher than existing approaches: EAR requires 800 training epochs, whereas VAR only needs 200 to 350 epochs. 3. The experiments in pages 7-8 mainly include obvious experiments or hyperparameter tuning studies, without exploring more critical aspects, for example, temperature or random noise in the MLP generator. Other Comments Or Suggestions: See weaknesses. Questions For Authors: See weaknesses. Code Of Conduct: Affirmed. Overall Recommendation: 2	Rebuttal 1: Rebuttal: We sincerely appreciate the Reviewer's time and efforts in reviewing our work. We provide discussions about the concerns as follows. > While the paper mentions that “GIVT is confined to the pre-defined family of Gaussian mixtures,” this is not necessarily a drawback. Instead, it may be the result of deliberate selection by the GIVT authors after thorough comparisons. The paper fails to explain why this limitation is a concern and to motivate its ideas. We appreciate the reviewer’s thoughtful feedback. While we acknowledge that the Gaussian mixture assumption in GIVT may indeed represent a deliberate and well-justified choice for modeling continuous tokens, we respectfully disagree with the assertion that this assumption "is not necessarily a drawback". The fundamental limitation arises when using likelihood maximization to train continuous autoregressive models: the predictive distribution must be constrained to a predefined parametric family (e.g., Gaussian mixtures) to enable tractable likelihood estimation. While Gaussian mixtures may offer the best fit within this constrained framework, this approach inherently restricts the model’s ability to represent arbitrary target distributions—a limitation that cannot be fully mitigated by the choice of distribution family. In contrast, our proposed EAR framework circumvents this challenge through its inherently expressive architecture. By implicitly defining the predictive distribution via its sampling process, EAR avoids restrictive parametric assumptions and enables automatic learning of complex data distributions. We will clarify this distinction more explicitly in the revised manuscript to better motivate our method. > The authors claim that continuous AR is superior to discrete AR, but the performance of their proposed EAR (Table 1) does not consistently support this assertion. For instance, EAR underperforms compared to MAGVIT-v2. Moreover, the training cost of EAR is significantly higher than existing approaches: EAR requires 800 training epochs, whereas VAR only needs 200 to 350 epochs. We appreciate the reviewer’s attention to the empirical results. Our claim regarding the advantages of continuous AR modeling is primarily supported by the comparison in Figure 3, where EAR outperforms its discrete counterpart (using the VQ tokenizer in [1]). This demonstrates the benefits of continuous modeling when controlling for other architectural factors. Regarding MAGVIT-v2, we acknowledge that EAR currently uses a three-year-old continuous tokenizer architecture, which may limit its performance compared to state-of-the-art discrete tokenizers. We hypothesize that integrating a more advanced, fine-grained continuous tokenizer could better showcase the potential of continuous AR modeling. As for training efficiency, we agree that EAR currently requires more epochs due to the inherent complexity of learning continuous distributions without restrictive parametric assumptions. Future work could explore optimizations to reduce training costs while retaining EAR’s expressiveness. [1] High-Resolution Image Synthesis with Latent Diffusion Models. > The experiments in pages 7-8 mainly include obvious experiments or hyperparameter tuning studies, without exploring more critical aspects, for example, temperature or random noise in the MLP generator. We thank the Reviewer for pointing out these concerns. Regarding the temperature, we have tuned it on EAR-B and found that τ=0.98 works better than other choices. Regarding the random noise, we have conducted experiments comparing uniform noise and Gaussian noise, and observed that uniform noise leads to marginally better performance. We will include these ablation experiments in the revised manuscript.	Summary: This paper introduce energy-based autoregressive to train a continuous autoregressive models. The continuous model bypasses the traditional approach of using discrete representation to train an autoregressive model, therefore reduce the information loss during discrete quantization. The experiment shows the effectiveness of continuous autoregressive framework on imagenet compared to other models. ## update after rebuttal The novelty has partially resolved my concern. Therefore, I increase my score to weak accept. Please include the ablation for causal and full attention in your revised paper. Claims And Evidence: The paper is well-written and provide evidence to most of their claims. Methods And Evaluation Criteria: The evaluation follows standard protocol Theoretical Claims: There is no theoretical proof. The paper introduces strictly proper scoring rules and directly apply it to train autoregressive models. Experimental Designs Or Analyses: The experimental designs are sound and valid. Supplementary Material: There is no supplemental material Relation To Broader Scientific Literature: The strictly proper scoring rule is interesting, the paper is one of first work exploring this as loss for training autoregressive model. Essential References Not Discussed: The paper mentions all essential references. Other Strengths And Weaknesses: Strength 1. The idea of using strictly proper score as loss function for continuous autoregressive seems novel to me. This is the first work investigating this idea in visual autoregressive model. 2. The paper writing is clear and easy to understand. Weakness: 1. The ablation for masked autoregressive should be provided with causal and full attention like setting in MAR [1]. 2. The experiment in table 1 lacks of comparison with continuous AR like [1], [2]. The paper states that in [2] GMM could limit expressivity line 155 2nd column. However, the performance of proposed method still lag behind GIVT. The author should include the performance of [1] and [2] in the main table and make a comprehensive comparison. 3. Why the random noise in MLP is uniform but not normal. Why uniform is better choice ?. The author should ablate this choice. 4. The inference process is significantly affected by variance $\sigma$ in section 5.4. This could be similar to Truncated trick in Big GAN. How the author think about it ?. I would like to hear the author opinion. [1]: Autoregressive Image Generation without Vector Quantization [2]: GIVT: Generative Infinite-Vocabulary Transformers Other Comments Or Suggestions: No Questions For Authors: Please refer to the weakness Ethical Review Concerns: None Code Of Conduct: Affirmed. Overall Recommendation: 3	Rebuttal 1: Rebuttal: We sincerely appreciate the Reviewer's time and efforts in reviewing our work. We provide discussions about the concerns as follows. > The ablation for masked autoregressive should be provided with causal and full attention like setting in MAR. We thank the Reviewer for raising this concern. We will enrich the ablation studies and provide comparisons between causal and full attention. > The experiment in table 1 lacks of comparison with continuous AR like [1], [2]. The paper states that in [2] GMM could limit expressivity line 155 2nd column. However, the performance of proposed method still lag behind GIVT. The author should include the performance of [1] and [2] in the main table and make a comprehensive comparison. We will follow the suggestion and include comparisons with continuous AR models (MAR and GIVT) in the main table. We would also like to respectfully clarify that our method (EAR) does not lag behind GIVT in performance. Specifically: + Base-scale models: GIVT (304M params) achieves an FID of 3.35, while our EAR-B (205M params) achieves 2.83. + Large-scale models: GIVT-L (1.67B params) achieves an FID of 2.59, while our EAR-H (937M params) achieves 1.97. > Why the random noise in MLP is uniform but not normal. Why uniform is better choice ?. The author should ablate this choice. We empirically observe that uniform noise yields slightly better performance compared to Gaussian noise. Specifically, for EAR-B: w/o CFG, FID increases from 5.46 (uniform) to 5.74 (Gaussian); w/ CFG, FID increases from 2.83 (uniform) to 2.89 (Gaussian). We will report this comparison in the revised manuscript. 4. The inference process is significantly affected by variance σ in section 5.4. This could be similar to Truncated trick in Big GAN. How the author think about it? We would like to clarify that Section 5.4 actually presents results using an MSE loss function (rather than our proposed EAR method), which can be interpreted as modeling continuous token distributions with Gaussian distributions. In this setup, the standard deviation σ is specified during inference. Our experiments show optimal performance occurs around σ=0.4, likely because this value best matches the inherent variance of the continuous token distribution. The reviewer's analogy to BigGAN's Truncation Trick is indeed insightful - they share the commonality of potentially trading sample diversity for sample quality. The Truncation trick operates on latent space sampling, while the variance adjustment operates more directly on the predicted distribution's shape.	null	null	null	null	null	null	null	null

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