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AdaWorld: Learning Adaptable World Models with Latent Actions | Accept (poster) | Summary: This paper focuses on learning world models from general videos. Unlike previous approaches that solely rely on video-based learning, this work extracts latent actions in a self-supervised manner and leverages action information for large-scale world model pretraining. With the aid of latent actions, the model can efficiently transfer actions across different contexts and adapt to new environments with limited interactions. Comprehensive experiments are conducted across multiple environments to validate the effectiveness of AdaWorld.
Claims And Evidence: This work claims that by learning latent actions:
1. AdaWorld can directly transfer actions to different contexts.
2. It can efficiently adapt into specialized world models with limited interactions and fine-tuning.
The authors validate these claims through experiments and visualizations. Figure 2 demonstrates action transfer to support Claim 1, while Table 1&2 showcases the model's rapid adaptation capabilities. Compared to other conditioning methods, AdaWorld achieves superior performance.
Methods And Evaluation Criteria: The method employs a β-VAE to learn latent actions and a conditional diffusion model for video generation. The evaluation primarily focuses on the consistency and quality of generated videos, with FVD and ECS serving as reasonable metrics.
Theoretical Claims: No theoretical claims.
Experimental Designs Or Analyses: The paper evaluates the approach through both quantitative and qualitative experiments. Tables 1 & 2 validate the advantages of prediction under the action latent space. Overall, the experimental setup is reasonable. However, it lacks visualization or feature similarity analysis of the learned action latent representations.
Supplementary Material: The supplementary materials provide additional details and visualized examples.
Relation To Broader Scientific Literature: This paper follows a similar idea to Genie, aiming to learn action latents in a self-supervised manner to improve world model learning. Additionally, the approach of learning difference information between two given frames is commonly used in the robotics field.
Essential References Not Discussed: NA
Other Strengths And Weaknesses: 1. The learned latent actions seem quite similar to those in Genie and Genie2, primarily representing simple movements such as up, down, left, and right. However, they struggle to effectively capture complex and long-range motion representations.
Other Comments Or Suggestions: 1. The paper validates the benefits of the learned world model through visual planning. A more convincing approach could be testing in robotics simulators, where a goal image is provided for generation, followed by evaluating the corresponding planning performance using a video-action model.
2. Providing an analysis of the action latents would make the findings more convincing.
Questions For Authors: 1. From the visualizations, a decline in generation quality over time can be observed. How does the model perform when generating longer temporal sequences?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thanks for the constructive feedback. We answer each question below and will include all results and discussions in the revision.
> A visualization or feature similarity analysis of the action latents.
**R4-1**: As suggested, we randomly collect 1000 samples for each action from three environments (Habitat, Minecraft, DMLab) and use UMAP projection [1] to visualize them [[LINK](https://icml2025-1014.github.io)]. The visualization shows that the same actions, even from different environments, are clustered together, which validates the context-invariant property of our latent actions. Note that noise exists because the action inputs cannot be executed in certain states (e.g., cannot go ahead when an obstacle is in front). We also compare the latent action autoencoder trained with a different hyperparameter choice in the right figure. Although a lower $\beta$ results in more differentiable latent actions, it also reduces action overlap across environments thus sacrificing disentanglement ability.
> This paper follows a similar idea to Genie, aiming to learn action latents in a self-supervised manner to improve world model learning. Additionally, the approach of learning difference information between two given frames is commonly used in the robotics field.
**R4-2**: While the concept of latent action is not new, we are the first to find its usefulness in world model pretraining. Unlike existing works that mainly adopt a discrete action set for imitation learning or playability, we propose a continuous latent action space that enables more effective adaptation. As mentioned in Sec. 2.3, our design also enables several unique applications compared to prior works like Genie, such as action composition and clustering.
> The learned latent actions seem quite similar to those in Genie and Genie2, primarily representing simple movements such as up, down, left, and right. However, they struggle to effectively capture complex and long-range motion representations.
**R4-3**: Unlike Genie, which is limited to 8 fixed actions, we develop a continuous latent action space that can express a wide range of diverse actions. Compared to Genie’s discrete design, our model can capture and transfer more nuanced actions (Table 1). Since our model is pretrained with various kinds of actions, adapting it to a new environment is akin to matching the corresponding latent actions for the action space, which leads to better simulation quality (Table 2). We also add some action transfer results showing that our model captures complex actions [[LINK](https://icml2025-1014.github.io)].
Regarding the range of actions, our current model opts for frame-level control to achieve finer granularity. In future work, we will explore extending our general training recipe to long-range settings, e.g., predicting multiple frames with one latent action.
> Visual planning evaluation in robotics simulators, where a goal image is provided for generation, followed by evaluating the corresponding planning performance using a video-action model.
**R4-4**: Thanks for the suggestion. We use the 100 robosuite control tasks from the VP2 benchmark [2] to evaluate the effectiveness of our method in robotic tasks. We focus on a compute-efficient setting and finetune our pretrained world model and the action-agnostic baseline for only 1k steps. The finetuned models are then used to perform goal-conditioned model predictive control following the official protocol of the VP2 benchmark. The success rates are reported below:
| | robosuite |
| :--- | :---: |
| Act-agnostic | 14% |
| AdaWorld | **61%** |
The results demonstrate that our action-aware pretraining significantly enhances robot planning performance with limited finetuning steps. We will experiment with more robotic environments in the revision.
> How does the model perform when generating longer temporal sequences?
**R4-5**: The current model can be stably controlled for about 20 frames. Generating longer sequences is likely to result in quality degradation. While this paper mainly focuses on enabling adaptable world models, we believe our study complements other progresses in this field. We will explore potential solutions for long-horizon rollouts in future work.
[1] UMAP: Uniform Manifold Approximation and Projection for Dimension Reduction
[2] A Control-Centric Benchmark for Video Prediction | Summary: The authors propose a method to incorporate latent actions into the pre-training stage of World-models allowing for more efficient adaptation to downstream tasks. The authors curate a dataset spanning from ego perspectives and third-person views to virtual games and real-world environments. Finally, they evaluate their model on action transfer, model adaptation and visual planning.
Claims And Evidence: Yes the authors' claims are evidence backed. The action aware pre-training does show promising results in action transfer, model adaptation and visual planning.
Methods And Evaluation Criteria: The authors mention using two action tokens $a_{t:t+1}$ during the latent action autoencoding but they mention that they use $a_{t+1}$ to approx the posterior. What do the authors do with $a_{t}$ ? Also the authors mention that in the action aware pretraining, the next frame is predicted based on a sequence of the latent actions. Which latent action $a_{t+1}$ or $a_{t}$? These details need to be carefully described and mathematically formulated instead of just via text.
Theoretical Claims: NA
Experimental Designs Or Analyses: In line 317-319 authors say that "We randomly initialize action embeddings for the action-agnostic
video pretraining baseline." However in lines 282-285 the authors say "pretrain a world model that shares the same architecture as AdaWorld but does not take latent actions as conditions." These two statements seem inconsistent.
Supplementary Material: Yes the appendix. All of it.
Relation To Broader Scientific Literature: The proposed action aware pre-training is quite novel although encoding latent actions from videos is not.
Essential References Not Discussed: NA
Other Strengths And Weaknesses: NA
Other Comments Or Suggestions: NA
Questions For Authors: see above
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thanks for the helpful feedback. We answer each question below and will include all results in the revision.
> The authors mention using two action tokens $a_{t:t+1}$ during the latent action autoencoding but they mention that they use $a_{t+1}$ to approximate the posterior. What do the authors do with $a_{t}$? Also the authors mention that in the action-aware pretraining, the next frame is predicted based on a sequence of the latent actions. Which latent action $a_{t+1}$ or $a_{t}$? These details need to be carefully described and mathematically formulated instead of just via text.
**R3-1**: Sorry for the confusion. The $a_{t}$ ensures that the total number of tokens is aligned between $t$ and $t+1$, simplifying the implementation of spatiotemporal attention. Let $f_{t}$ and $f_{t+1}$ represent image tokens and [;] denote concatenation operation. The spatial attention can be formulated as:
[$f_{t}$’;$a_{t}$’] = SpatialAttn([$f_{t}$;$a_{t}$]),
[$f_{t+1}$’;$a_{t+1}$’] = SpatialAttn([$f_{t+1}$;$a_{t+1}$]),
and the temporal attention can be formulated as:
[$f_{t}$’;$f_{t+1}$’] = TemporalAttn([$f_{t}$;$f_{t+1}$]),
[$a_{t}$’;$a_{t+1}$’] = TemporalAttn([$a_{t}$;$a_{t+1}$]).
After encoding, all tokens except for the $a_{t+1}$ will be discarded, and we only project $a_{t+1}$ to estimate the posterior. Formally,
[$\mu$;$\sigma$] = FC($a_{t+1}$).
Thus, for two consecutive frames $f_{t:t+1}$ in the video sequence, the corresponding latent action is predicted from $a_{t+1}$. We will revise this part accordingly and open-source all code for reproducibility.
> In line 317-319 authors say that "We randomly initialize action embeddings for the action-agnostic video pretraining baseline." However in lines 282-285 the authors say "pretrain a world model that shares the same architecture as AdaWorld but does not take latent actions as conditions." These two statements seem inconsistent.
**R3-2**: Our latent action is concatenated with the timestep embedding and CLIP image embedding in the original SVD, which is equivalent to adding a linear projection layer to these two layers. For the action-agnostic baseline, we use the same architecture but input zeros into the additional linear projection during pretraining. When adapting to the discrete action space, the inputs are chosen from an action codebook. We utilize the averaged latent actions to initialize the embeddings of this codebook. Since the latent actions are not learned in the action-agnostic baseline, we initialize its action codebook with random parameters. We will clarify this in the revision.
---
Rebuttal Comment 1.1:
Comment: I thank the authors for clarifying their approach. I will maintain my previous score. | Summary: This paper proposes a pretraining framework for learning world models that can generalize to various contexts. AdaWorld first learns a latent action representation using an unsupervised forward prediction objective. Subsequently, AdaWorld learns an autoregressive world model that conditions on latent actions to produce future frames. Interestingly, AdaWorld finds that the learned latent actions are context-invariant, allowing for transfer between contexts. AdaWorld is evaluated on a variety of downstream tasks in action transfer, model adaptation, and visual planning.
Claims And Evidence: Yes, the paper claims that the learned world model can generalize to new, unseen contexts. The experiments show that by applying latent actions from one demonstrations, AdaWorld can generalize the same behavior to generate behavior for a unseen scene conditioned on just a single frame. There are also experiments demonstrating AdaWorld's capabilities on visual planning and adaption. However, these experiments are not as comprehensive and could use additional comparisons to state-of-the-art baselines.
Methods And Evaluation Criteria: Yes, the proposed method is sound and the evaluation is based on standard metrics used in the literature.
Theoretical Claims: There are no theoretical claims and proofs.
Experimental Designs Or Analyses: To evaluate their approach, they measured AdaWorld's ability to generalize to new contexts on a single demonstration. The paired data between LIBERO and Something Something v2 is reasonable. Also the evaluation environments used are quite common in the literature.
Supplementary Material: I did review the supplementary material, specifically the model details and some analysis on the action clustering as well as the qualitative rollout visualizations.
Relation To Broader Scientific Literature: The proposed work is relevant to literature in latent action models and learning from actionless videos including LAPO and Genie among others. The proposed method of learning a latent action space to guide world model generation is sound and a good idea.
Essential References Not Discussed: [1] Ye, Seonghyeon, et al. "Latent action pretraining from videos." arXiv preprint arXiv:2410.11758 (2024).
[2] Menapace, Willi, et al. "Playable video generation." Proceedings of the IEEE/CVF Conference on Computer Vision and Pattern Recognition. 2021.
Other Strengths And Weaknesses: Strengths:
- Paper is well written and easy to follow
- Implementation details and framework is described thoroughly
- AdaWorld has diverse set of applications in task transfer and visual planning
Weakness:
- Method is technically not very novel. Prior work has already proposed latent action models in LAPO and Genie and similarly there is a plethora of work on generative video models
- No state-of-the-art baselines. Baseline methods are mostly ablations or modifications to the approach (e.g. predicting optical flow as pretraining objective) so the comparison is quite weak
- It would be nice to incorporate some baselines on controllable video generation to highlight that AdaWorld is more adaptable than prior works as a result of the learned latent action space.
- The data diversity experiments seem a bit orthogonal to the purpose of the paper and is not really an ablation. The action-agnostic video pretraining is more of an ablation than an actual baseline.
Other Comments Or Suggestions: See weaknesses and questions section.
Questions For Authors: Question:
- How does the latent action model avoid collapse, e.g. how do you ensure that the decoder or the forward dynamics model in this case does not just pass f_t through and learn a policy on the demonstration data?
- In Figure 4, what is meant by context-invariant? Does that mean the same latent actions are applied to autoregressively predict the future frames across each of these environments?
- Why do you think optical flow as a condition is not as powerful as image reconstruction?
- Does the average embedding also work in continuous control environments? The highlight example seems to be only in the Procgen discrete action space setting.
- What is the pretraining data for the main set of experiments? Do those use the full OpenX and Retro datasets for pretraining the latent actions?
- What part of the model ensures that the learned latent actions are clustered semantically? Is it the beta-VAE term that controls the amount of disentanglement in thel latent space? Again, is this only application in the discrete domain? Is there any evidence that this holds in continuous environments?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thanks for the thoughtful feedback. We answer each question below and will include all results in the revision.
> Compare to state-of-the-art baselines.
**R2-1**: To demonstrate the generality of our method, we use iVideoGPT as a state-of-the-art baseline. iVideoGPT is an action-controlled world model with an autoregressive Transformer architecture. It is pretrained by action-agnostic video prediction and adds a linear projection to learn action control during finetuning. For fair comparison, we implement a variant by conditioning iVideoGPT with our latent actions during pretraining. We resume from the official OpenX checkpoint and do not finetune its tokenizer. After pretraining iVideoGPT and our action-aware variant on OpenX for 10k extra steps, we finetune each model with robot actions for 1k steps on BAIR robot pushing dataset. The result is shown below:
| | PSNR ↑ | LPIPS ↓ |
| :--- | :---: | :---: |
| iVideoGPT | 16.69 | 0.221 |
| iVideoGPT + AdaWorld | **17.33** | **0.207** |
In our paper, we also compare Genie's latent action setting. The results validate our superior adaptability compared to recent arts.
> Discuss LAPA and PVG. Method is technically not very novel.
**R2-2**: Our key innovation is to incorporate action information into world model pretraining, which significantly enhances its adaptability. To achieve this, we extract continuous latent actions as a scalable condition for our world model. While prior works have studied latent actions, they mainly focus on imitation learning (LAPA, LAPO) and playability (PVG, Genie). As a result, they use discrete latent actions, which struggle to express various actions and fall short in adaptation. As mentioned in Sec. 2.3., our continuous design also enables several unique applications.
> How does the latent action model avoid collapse?
**R2-3**: Our model is less likely to collapse for three main reasons. (1) A large portion of our data is collected randomly. Thus, our model must learn from latent actions. Otherwise, it has no way to predict the next step. (2) Our data contains thousands of environments, making learning a shared action space easier than remembering all behaviors as a decoder policy. (3) The parameter $\beta$ is adjusted to allow sufficient information to pass the bottleneck, ensuring that the latent actions capture meaningful information.
> In Figure 4, what is meant by context-invariant?
**R2-4**: The latent action sequence from the source video is directly applied to the target scene for autoregressive prediction, where the same actions are replicated even when context is totally different.
> Why optical flow as a condition is not as powerful as image reconstruction?
**R2-5**: The dense and uniform optical flow is highly sensitive to spatial and structural misalignment. In contrast, our latent action can adaptively allocate its capacity to represent the most critical actions, making it more robust in recognizing misaligned actions [[LINK](https://icml2025-1014.github.io)].
> Does the average embedding also work in continuous control environments?
**R2-6**: While the average embedding is not directly applicable, AdaWorld still exhibits strong adaptability for continuous action spaces. To verify this, we use nuScenes, an autonomous driving dataset where the vehicle takes continuous displacements at each timestep, as a typical example. During adaptation, we add a two-layer MLP to map actions to the latent action interface. The interface can also be efficiently initialized by finetuning the MLP with minimal action-latent action pairs (3k steps take less than 30 seconds on a single GPU). The result is shown below:
| | PSNR ↑ | LPIPS ↓ |
| :--- | :---: | :---: |
| Act-agnostic | 20.86 | 0.475 |
| Flow | 20.94 | 0.462 |
| Discrete | 21.28 | 0.450 |
| AdaWorld | **21.60** | **0.436** |
We also plot the PSNR curves [[LINK](https://icml2025-1014.github.io)], where AdaWorld adapts more rapidly in all cases. **R2-1** also shows that our method works for another world model with continuous control, while **R4-4** shows that AdaWorld enables better planning for robot arms.
> Pretraining data for main experiments.
**R2-7**: Except for Table 4, all models are pretrained on the data mixture specified in Appendix A.2, including the full OpenX and Retro datasets.
> What part ensures that the latent actions are clustered semantically? Is it the beta-VAE term that controls the amount of disentanglement? Is it only an application in the discrete domain?
**R2-8**: The semantic clustering and disentangling ability result from the low dimensionality of latent actions and the regularization on posterior distributions. The parameter $\beta$ controls the disentanglement of latents [[LINK](https://icml2025-1014.github.io)] (see **R4-1**). This ability also holds for continuous actions. As [[LINK](https://icml2025-1014.github.io)] shows, continuous actions can be effectively disentangled and transferred across contexts. | Summary: This paper introduces AdaWorld, a world model learning approach that leverages self-supervised latent action extraction from videos to capture key transitions. It also introduces an autoregressive world model (single-frame SVD) conditioned on these latent actions and historical frames, enabling transfer and learning of new actions.
Claims And Evidence: The paper largely supports its claim regarding action/motion representation learning. However, since it is presented as a world model, it differs from traditional world models where direct user input (e.g., via keyboard or mouse) influences predictions. Instead, this approach requires a reference video to guide actions in the generated video. It would be helpful for the authors to clarify how the model can achieve similar controllability to Genie or OASIS at inference time.
Methods And Evaluation Criteria: The proposed method makes sense, as learning motion representation through pretraining a latent action autoencoder and applying it to a one-frame denoising diffusion model is a reasonable approach. However, I have some concerns regarding the training data and process (see the section below).
Regarding the evaluation criteria, I am skeptical about the robustness of the ECS metric based on I3D features for assessing action/motion transfer in open-domain scenarios. A more comprehensive user study may be necessary to better evaluate the effectiveness of action/motion transfer.
Theoretical Claims: The theoretical claims appear to be valid. However, I have some concerns about whether the latent action autoencoder effectively captures important actions. Smooth transitions between frames, such as a character simply moving forward, dominate the sequence, whereas sudden transitions, like jumping or performing distinct actions, constitute only a small fraction of the total frames. Yet, during training, it seems that f_t and f_{t+1} are sampled uniformly. This raises the question of whether smooth transitions should be considered "actions" or merely "motion."
Experimental Designs Or Analyses: For the comparison methods, I suggest that the authors include motion transfer approaches, as referenced earlier. Also consider add user study for action transferring performance.
Supplementary Material: I have read the appendix.
Relation To Broader Scientific Literature: This paper is related to to diffusion models, world models, and action-driven video generative models.
Essential References Not Discussed: A group of motion transfer methods are missing for inference:
Space-Time Diffusion Features for Zero-Shot Text-Driven Motion Transfer, CVPR 2024
MotionClone: Training-Free Motion Cloning for Controllable Video Generation, ICLR 2025
Other Strengths And Weaknesses: Strengths: Modeling action or motion using latent representations is a crucial challenge in world models, and this work takes a promising direction by expanding the action vocabulary beyond traditional action-labeled approaches. The proposed method—first learning to extract latent actions and then incorporating them into diffusion models—seems well-motivated and conceptually sound.
Weakness: Please refer to the sections above, as well as the "Questions for Authors" section, for my specific concerns and areas where further clarification is needed.
Other Comments Or Suggestions: None.
Questions For Authors: 1. In Figure 3, the input appears to be the next frame f_{t+1}, but this seems to result in a reconstruction rather than a next-frame prediction. Based on the text in Line 248, the last frame in the memory is used as the condition image, which suggests it might be f_t instead?
2. The current approach seems to entangle motion with structural elements, leading to a strong similarity in overall flow between the source and target videos. It would be helpful for the authors to discuss potential limitations of this, particularly in scenarios where the source and target videos are misaligned due to differences in camera poses or character locations. Can the method still function effectively under such conditions?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thanks for the insightful feedback. We answer each question below and will include all results in the revision.
> The model requires a reference video to guide actions. Clarify how the model can achieve similar controllability to Genie or OASIS at inference time.
**R1-1**: Our world model does not necessitate a reference video for prediction. As shown in Sec. 3.2, our model can be efficiently adapted to various action inputs. After adaptation, our model can be directly controlled by raw actions (e.g., Minecraft actions like OASIS) without using reference videos. Moreover, as mentioned in Sec. 2.3, one can easily obtain a customizable number of control options by clustering latent actions from videos.
> A user study may be necessary to evaluate the effectiveness of action/motion transfer.
**R1-2**: We conduct a user study with the baselines as requested. We follow the same setup in Sec 3.1 and generate 50 video pairs on LIBERO and SSv2, respectively. We then invite four volunteers to judge whether the action is successfully transferred. The success rates are reported below:
| | LIBERO | SSv2 |
| :--- | :---: | :---: |
| Act-agnostic | 0% | 1% |
| Flow | 2% | 10.5% |
| Discrete | 3.5% | 21.5% |
| AdaWorld | **70.5%** | **61.5%** |
The results indicate that our interface can transfer actions more effectively, especially on LIBERO, where the robot actions are more nuanced.
> Include motion transfer approaches for comparison.
**R1-3**: Thanks for the suggestion. First, we want to emphasize that our paper aims to develop a highly adaptable interface for world models. In contrast, motion transfer methods mainly rely on transferring video-level feature maps, which are not applicable for interactive control and are not suitable for action adaptation. It is also notable that our action transfer ability does not require strictly aligned spatial structures, which is much more flexible than common motion transfer settings (see **R1-7** below).
Due to time limit, we compare the suggested MotionClone using 32 official demos released on its GitHub page. To avoid potential bias, we crop them to square and ensure that the text at the top is excluded. We use AdaWorld to autoregressively predict 16 frames and resize them to MotionClone’s resolution. Since ground truth target videos are not available, we invite four volunteers for a user study. As a result, AdaWorld is preferred 21.09% of time in action transfer accuracy, showing our ability to perform motion transfer tasks (though optimizing video-level motion transfer is not our main purpose).
> Whether the latent action autoencoder effectively captures important actions. During training, smooth transitions between frames dominate the sequence, whereas sudden transitions constitute only a small fraction of the total frames. Whether smooth transitions should be considered "actions" or merely "motion".
**R1-4**: We add more action transfer results to show the capability of our latent action autoencoder [[LINK](https://icml2025-1014.github.io)]. Without any special handling of training data, our model can effectively capture and transfer sudden transitions. Rebalancing the training data may further enhance the learning of these transitions. Note that the latent action autoencoder is encouraged to encode the most critical actions due to the information bottleneck, while minor motions and background changes that can be predicted by the decoder are likely not to be encoded.
> Missing motion transfer references.
**R1-5**: We have included the two references in the related work and will update them accordingly in the revision.
> The input frame in Figure 3.
**R1-6**: Sorry for the confusion. Figure 3 illustrates our training process, where $f_{t+1}$ is the frame to be denoised and is used to generate latent actions. During inference, $f_{t+1}$ is not used and the predictions are made based on past frames. The control interface can take latent actions transferred from other videos, selected from a known set, or raw actions after efficient adaptation. We will clarify this in the revision.
> Can the method still function effectively when the source and target videos are misaligned due to differences in camera poses or character locations?
**R1-7**: Unlike typical motion transfer settings, our method does not require strong spatial alignment to capture actions. As shown in this [[LINK](https://icml2025-1014.github.io)], our latent actions can effectively recognize and transfer actions from various poses and embodiments. Moreover, we want to clarify that the main objective of this work is to develop a generally adaptable world model rather than maximize action representation precision. Although our latent action may not faithfully represent all kinds of actions, it is general enough to serve as a unified interface for pretraining, which significantly improves the adaptability of world models compared to existing training methods. We will add more results in the revision. | null | null | null | null | null | null |
RE-IMAGINE: Symbolic Benchmark Synthesis for Reasoning Evaluation | Accept (poster) | Summary: This paper introduces R E -I MAGINE: a framework to characterize a hierarchy of reasoning ability in LLMs, alongside an automated pipeline to generate problem variations across all the levels of the hierarchy. By altering problems in an intermediate symbolic representation, RE-IMAGINE generates arbitrarily many problems that are not solvable using memorization alone. Reductions in performance can be observed when the models are queried with problem variations.
## update after rebuttal
I keep my score positive for this paper.
Claims And Evidence: Not for all.
Problematic claim: these variations have been developed in an ad hoc manner, lacking a systematic hierarchy.
Some datasets also have a systematic hierarchy such as GPQA.
Methods And Evaluation Criteria: It makes sense.
Theoretical Claims: 1. the use of theory on "counterfactual" (for generating level 3 questions)
A counterfactual is a hypothetical scenario that describes what would have happened if a different decision or condition had occurred, contrary to what actually happened in real-world. While in the existing questions, they do not present real-world questions, making the questions of level-3 more like intervention. Maybe creating an scenario which would never happend in real-world could alleviate this issue.
2. The validity of the method might be influenced by the correctness of the NL-symbolic-NL process.
A wrong python program can also produce the same answer as the ground truth.
Experimental Designs Or Analyses: 1. the evaluation on the created benchmarks on various domains is somewhat sound.
2. More analyses are needed.
All experiments are about evaluation on the created benchmark (too much content is used for this part). Some analyses should be incorprate to investigate the relationship of question in different level. For example, whether training on level-3 questions can help answering level-2 questions.
More popular LLMs should be adopted for analysis, such as Qwen.
Error studies should be done to analyse why LLMs perform worse on hader questions.
Case studies are also required.
Supplementary Material: The supplementary material is not provided in this submission.
Relation To Broader Scientific Literature: It might influence the evaluation of LLMs.
Essential References Not Discussed: None
Other Strengths And Weaknesses: None
Other Comments Or Suggestions: None
Questions For Authors: Please refer to the weaknesses above.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: # Response to Claims And Evidence: Some datasets also have a systematic hierarchy such as GPQA
The hierarchy in GPQA represents the difficulty of the **original problems**, whereas the hierarchy we introduce in Re-Imagine defines reasoning complexity through **variations of problems** from existing, well-established benchmarks.
We believe that Level-3 mutations align with counterfactual reasoning based on Pearl’s ladder of causation—**how our belief about the occurrence of event Y changes if event X had value x’ instead of x**. In Figure 1, for example, we present: "Janet bakes muffins with 2 eggs... Assume Janet no longer bakes muffins, how much money does she make every day?" Here, the observed outcome (event Y) is Janet’s daily earnings, while the causal factor (event X) is whether she bakes muffins or not. The logical facts are structured as a math problem, and Level-3 mutations modify one of these facts by introducing an additional assumption.
We agree with the reviewer that creating scenarios unlikely to occur in the real world, such as "Assume Janet bakes muffins using 10,000 eggs every day," can be highly interesting. Thanks to the modular plug-and-play design of our pipeline, we encourage the community to implement mutations of their interest to thoroughly assess models' reasoning abilities.
---
# Response to Theoretical Claims 2: NL-symbolic-NL process
We recognize that the accuracy of NL-symbolic-NL translation is critical. Therefore, for benchmarks requiring full NL-symbolic-NL translation, such as GSM8K, we employ four methods to ensure the correctness of the mutated QA pairs and report results with quantified noise:
- **NL-symbolic:** We select Python solutions that not only produce the correct answer but also ensure that all constant variables in the code (root nodes in the computational graph) align with the numbers in the question, and vice versa (see lines 246-249, left column, in the main paper).
- **Symbolic-NL:** to ensure the accuracy of the symbolic-to-NL translation, we prompt GPT-4o a second time to back-translate the mutated math problem into Python by modifying the original question’s Python solution. The generated code must produce an execution result that matches the ground truth answer of the mutated question (see line 220-224, right column, in the main paper).
- **Manual Quality Check:** we manually check the quality of the mutated QA pairs and report the error rate in each mutation (see line 227-235, right column, in the main paper).
- **Report Results with Quantified Noise:** we show the error rate of the mutated data when reporting the model's performance (see Figure 2).
---
# Response to Experimental Designs Or Analyses 2: Error analysis of the relationship of questions across levels, and training on level-3 questions.
We emphasize that this study primarily focuses on introducing the reasoning hierarchy, the benchmark mutation pipeline, and evaluating models' zero-shot and few-shot performance on dataset mutations. Model training is beyond the scope of this paper. However, thanks to the scalability of our proposed pipeline, we are expanding training set mutations to investigate whether exposing models to mutated questions during training can enhance their reasoning abilities. However, the results will not be included in this paper.
In Appendix B.2, we present experiments in an in-context learning setting, revealing that (1) simply replacing the original demonstrations in the context with mutated ones does not improve models’ reasoning accuracy. However, (2) models perform significantly better on generated test set variations when provided with both original and mutated examples as demonstrations. These findings offer insights for future model-training experiments.
---
# Response to Experimental Designs Or Analyses 3: More popular LLMs should be adopted for analysis, such as Qwen
We conduct additional experiments with a broader range of popular LLMs, and the observations in the paper still hold for these new models.
**Loop** (mutations Raw, JunkHint, JunkNoHint, readOriginal, WriteOriginal, Xoriginal)
- QwQ-32B: 75.9% 76.7% 66.5% 63.67% 39.59% 36.33%
- R1-Distill-Llama-70B: 75.10% 62.45% 49.80% 60.41% 49.39% 48.57%
**CruxEval** (mutations Raw, Mutate String (L2), Mutate Value (L2), Redefine Function (L2), Replace Operator (L2), Swap Conditional (L2))
- GPT-4.5: 45.5% 23.55% 32.45% 29.79% 29.14% 32.06%
- GPT-o3-mini: 56.88% 35.95% 59.82% 56.35% 58.52% 50%
**GSM8K** (mutations Raw, SampleValues, OverWriteValue, UselessInfo, AddDependence, InsertConditional)
- qwq-32b 100 98.2 92.6 99.1 59.6 95.6
- r1-distiall-qwen-32b 98.3 93.5 85.9 97.6 63.2 85.0
- GPT-o3-mini 97.4 90.3 84.02 93.5 77.3 91.6
- GPT-4.5 97.45 89.76 81.28 95.47 61.54 89.28
Additional experiments are ongoing. We will include performance results for qwq, r1-distill-qwen, GPT-o3-mini, and GPT-4.5 across all four benchmarks in the camera-ready, and an error analysis in the Appendix. | Summary: To identify whether the performance improvement of LLMs on public benchmarks such as GSM8K indeed comes from the stronger reasoning capabilities or results from mere memorization of training cases, the authors propose RE-IMAGINE to automatically make multi-level modifications to questions in the existing benchmarks. The authors employ RE-IMAGINE to generate problem variations based on 4 benchmarks and observe performance drop of LLMs on the problem variations, which is said to indicate the model reliance on recalling training data.
## Update after rebuttal
Most of my concerns are solved. I have raised my score from 2 to 3.
Claims And Evidence: The paper makes two primary claims: 1) RE-IMAGINE can automatically generate multi-level problem variants, thereby extending existing datasets and mitigating data leakage during training; 2) The performance gap between raw questions and their variants suggests that LLMs rely on recalling training data.
* **Evidence for claim 1:** The authors claim that RE-IMAGINE is a general framework and an automated pipeline. But how to operate the first step, language-to-symbolic transformation, is task-specific and requires manual intervention. And whether or why the mutation mentioned in the paper is general and can be applied to other domain is not clear. The mutation seems to need humans to manually define and restrict the modification types. For example, for the "Sample Values", if the values are numbers, boolean, or strings, the mutation may be different. The authors should provide more details on the generalization of the proposed method and how much manual work is necessary to adopt it in a new dataset. If this framework requires manual redesign of step 1 and step 2 for each new dataset, I think the applicability of this framework is insufficient.
* **Evidence for claim 2:** I doubt whether the experimental results sufficiently support claim 2.
* Most modifications introduced by RE-IMAGINE significantly increase the complexity of the problems. The UselessInfo operation at level-2 introduces an extra node in the computation graph, and level-3 modifications add reasoning steps. Consequently, the observed decline in model performance could be attributed to either the increased difficulty of the problems or the model's reliance on memorized training data and poor generalization. Previous studies, such as [1] and [2], have shown respectively that irrelevant information and additional reasoning steps can negatively impact model performance.
* The SampleValues modification at level-2, which involves integer and float values fluctuating within the range of [-10, 10], preserves the problem's difficulty. This suggests that the performance drop in this case may indeed reflect the model's dependence on training data for reasoning. However, this conclusion is not novel, as [3] has already demonstrated in GSM8K that LLMs are sensitive to minor changes in variable values and names, leading to performance degradation.
* So to robustly support claim 2, the authors need to disentangle the effects of increased problem difficulty from the model's reliance on training data. Without this clarification, the claim remains partially unsubstantiated.
Methods And Evaluation Criteria: RE-IMAGINE supports automated data generation through a pipeline involving: language-to-code transformation, mutations of symbolic representations and code-to-language transformation. The idea is simple and clear. However, the authors should provide more details on the generalization of the proposed method and how much manual work is necessary to adopt it in a new dataset.
The evaluation metric includes model accuracy towards raw questions and the question variations. Besides, in Sec 4.3, the authors also involve the metric of sufficiency / necessity inconsistency, which is proposed in [4]. I recommend that the authors provide a more detailed explanation of the experimental setup and the methodology for this metric in the paper. Currently, the paper merely references [4], which may confuse readers unfamiliar with the prior work.
Theoretical Claims: The paper introduces a hierarchical framework to evaluate the reasoning ability of models. While this framework is inspired by the hierarchical structure proposed by Pearl in the context of causality, I find the connection between this framework and causality to be unclear. In other words, could you justify why this particular framework was chosen or how it is fundamentally linked to causality?
Experimental Designs Or Analyses: See Claims and Evidence, ablations for the effects of mutations on question difficulties are needed.
Supplementary Material: Although the authors provide a hyperlink, the link is just [https://github.com](https://github.com). I have no access to their code or data.
Relation To Broader Scientific Literature: The paper discusses a crucial problem concerning the evaluation of LLM reasoning capabilities, which is how to identify genuine reasoning and merely recalling training data. This has long been a hotly-debated question in the community of LLM reasoning. Here are some literatures recommended for reference under the topic:
* Reasoning Elicitation in Language Models
via Counterfactual Feedback, Hüyük et al., 2024, https://arxiv.org/abs/2410.03767
* Counterfactual Memorization in Neural Language Models, Zhang et al., 2023, https://arxiv.org/abs/2112.12938.
* Faith and Fate: Limits of Transformers on Compositionality, Dziri et al., 2023, https://arxiv.org/abs/2305.18654
* Case-Based or Rule-Based: How Do Transformers Do the Math?, Hu et al., 2024, https://arxiv.org/abs/2402.17709
* Towards a Mechanistic Interpretation of Multi-Step Reasoning Capabilities of Language Models, Hou et al., 2023, https://arxiv.org/abs/2310.14491
Essential References Not Discussed: The related work section is missing in the paper, and my primary concern is that the unique contribution of this work beyond the following previous work is unclear. While the paper focuses on automatically modifying public datasets, with GSM8K being a central dataset, several highly relevant studies are not discussed or cited. These include:
* GSM-IC [1] shows that irrelevant context can degrade LLM performance.
* iGSM [2] introduces a synthetic pipeline which captures parameter dependencies in a symbolic structure.
* GSM-HARD [9] modify parameter values to be much bigger than in the original dataset.
The contributions beyond the above work and GSM-Symbolic [3] should be more clearly discussed.
Other Strengths And Weaknesses: Strengths:
* The paper discusses a crucial problem of how to identify memorization and genuine reasoning in LLMs.
* The presentation of the work is very clear and well-structured, making it accessible to readers.
* Several modifications introduced in RE-IMAGINE, particularly at level-3, appear to be novel to the best of my knowledge. These modifications have the potential to increase the difficulty of the dataset and mitigate the impact of data leakage.
Weaknesses：
* My primary concern revolves around (1) the novelty of the proposed methods.
* The techniques at level-2 have been previously explored in related works [1, 2, 3].
* While some methods at level-3 are indeed novel, they do not maintain the same level of problem difficulty as the original tasks. As a result, the observed decline in LLM performance cannot be solely attributed to memorization, as suggested in the 'Claims and Evidence' section. This limits the strength of the conclusions drawn regarding the reliance of LLMs on memorization for answering questions.
* And (2) the generalization of the proposed method. (See the first point in 'Claims and Evidence')
Other Comments Or Suggestions: Here are some typos:
1. line 019 right: "Traditionally, the **evaluation** of reasoning **evaluation** in LLMs" -> "evaluation of reasoning abilities"
2. line 078 right: "The proposed hierarchy has three levels of increasingly difficulty" -> "increasing difficulty" ?
Questions For Authors: 1. Please explain about how the pipeline can work accross domains and how much human efforts are needed to adopt this pipeline on different datasets.
2. Please explain more about the cause of performance decreasing. Whether the performance of the model has declined comes from the difficulty of the problem itself, rather than the difference between "memory" and "reasoning".
3. Please explain the novelty of these mutation and your overall framework.
4. How do the three level are related to the three level in causal ladder?
The overall reference:
[1] Large Language Models Can Be Easily Distracted by Irrelevant Context, Shi et al., 2023, https://arxiv.org/abs/2302.00093
[2] Physics of Language Models: Part 2.1, Grade-School Math and the Hidden Reasoning Process, Ye et al., 2024, https://arxiv.org/abs/2407.20311
[3] GSM-Symbolic: Understanding the Limitations of Mathematical Reasoning in Large Language Models, Mirzadeh et al., 2024, https://arxiv.org/pdf/2410.05229
[4] Reasoning Elicitation in Language Models
via Counterfactual Feedback, Hüyük et al., 2024, https://arxiv.org/abs/2410.03767
[5] Counterfactual Memorization in Neural Language Models, Zhang et al., 2023, https://arxiv.org/abs/2112.12938.
[6] Faith and Fate: Limits of Transformers on Compositionality, Dziri et al., 2023, https://arxiv.org/abs/2305.18654
[7] Case-Based or Rule-Based: How Do Transformers Do the Math?, Hu et al., 2024, https://arxiv.org/abs/2402.17709
[8] Towards a Mechanistic Interpretation of Multi-Step Reasoning Capabilities of Language Models, Hou et al., 2023, https://arxiv.org/abs/2310.14491
[9] PAL: Program-aided Language Models, Gao et al., 2023, https://arxiv.org/abs/2211.10435
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank the reviewer for the detailed feedback.
---
# Response to weakness 1: Novelty and the Influence of the Question Difficulty
## (1) Novelty and contribution:
In summary,
* We present the reasoning ladder for LLMs, which systematically defines different levels of reasoning difficulty. This framework establishes **a unified reasoning hierarchy that integrates both previously studied mutations and the new mutations** introduced in our work. (Please refer to our response to Q1 for further explanation of the reasoning ladder.)
* Alongside the reasoning hierarchy, we introduce— to the best of our knowledge—**the first scalable mutation generation pipeline that applies across multiple benchmarks and tasks**. This framework enables the creation of an arbitrary number of mutations at each level of the hierarchy for existing benchmark problems. (We elaborate on the scalability further in our response to Weakness 2.)
Compared to the previous studies,
* We pointed out that **previous work is primarily limited to Level-2 mutations** ([1,2,3,9]), which evaluate a model's ability to generalize beyond existing benchmarks while preserving the original reasoning path of the questions.
* Huyuk et al. [4] explored a level-3 mutation, Bi-Counterfactual. However, like previous studies on level-3 mutations, their approach heavily relies on manually crafted patterns and rule annotations. To the best of our knowledge, **no scalable solution has been proposed for generating problem variations across different reasoning levels spanning multiple benchmarks and tasks**.
## (2) Disentangle the decline in model performance from the question difficulty:
We use GSM8K as an example. We quantitatively define the difficulty of a numerical question reasoning using the number of calculation steps in the code snippet, following iGSM [2]. We compute the average accuracy of each model across examples with varying numbers of calculation steps. Given the large number of models tested, we aggregate their results and present the overall average accuracy in the following table. We included detailed results for each model respectively in the Appendix of the paper.
| Intervention Type | 2 steps | 3 steps | 4 steps | 5 steps | 6 steps |
|-------------------|------|------|------|------|------|
| Raw | 0.95 | 0.94 | 0.84 | 0.91 | 0.83 |
| SampleValues | 0.87 | 0.84 | 0.75 | 0.74 | 0.80 |
| UselessInfo | 0.91 | 0.90 | 0.90 | 0.81 | 0.88 |
| CounterFactual | 0.74 | 0.71 | 0.75 | 0.62 | 0.67 |
| InsertConditional | 0.62 | 0.68 | 0.65 | 0.61 | 0.57 |
| AddDependence | 0.57 | 0.47 | 0.46 | 0.45 | 0.42 |
From the table we make three key observations:
* In nearly all scenarios, **even when tested on examples with the same number of calculation steps, models consistently perform worse on the mutated sets compared to the original test set**.
* Compared to Level-2, Level-3 mutations present a significantly greater challenge. Especially, **the accuracy on Level-3 mutations with just two calculation steps is lower than on Raw test examples with six calculation steps with a significant margin.**
---
# Response to weakness 2: Generalization of the method
The pipeline requires three types of adapters: Question-to-Symbolic Adapters, Symbolic Representation-to-Mutation Adapters, and Mutation-to-Natural Language Question Adapters. The pipeline is designed in a **modular plug-and-play fashion**, making **all adapters both reusable and customizable**. Users can either utilize existing adapters if they meet their needs or modify them to suit their specific dataset or domain. The estimated manual effort required for **adapter customization** is based on the four domains we implemented:
* Question to Symbolic Adaptor: **Prompts Writing**.
* Symbolic Representation to Mutation Adapter: **Write around 50 lines of code** to define the mutation of the symbolic representation.
* Mutation to Natual Language Question Adaptor: **Write around 100 lines of code for model prompting** to translate the mutation to natural language.
**We replaced the word "automatic" with the more precise term "scalable" in the paper.**
---
# How do the three levels relate to the causal ladder?
The key connection between Pearl's ladder and our framework is the problem's computation graph, which can be understood as a causal model in Pearl's framework. Each problem in a benchmark can be interpreted as a single realization of the graph with specific node values. Experiment associated with different perturbations in such graph can be related to operations in Pearl's ladder of causation. For instance, computing the effect in the outcome of the change in one leave node maps to the definition of a counterfactual. Note, however, that that not all mutations in the three levels have a causal counterpart (like adding an irrelevant piece of information or changing an operation). In this sense our framework can cover a broader definition of reasoning in each level.
---
Rebuttal Comment 1.1:
Comment: I appreciate your additional experiments and justifications, especially about `Disentangle the decline in model performance from the question difficulty`. I want to further confirm how you define "steps" in this experiment. I am still concerned that the number of calculation steps do not actually represent the genuine difficulty. For example, in the case of “UselessInfo”, adding an irrelevant node does not increase the number of calculation steps, but it does make the question harder as shown in [1].
My understanding about the definition of the calculation step is as follows (I use Figure 1 in your original paper as an example):
* SampleValues: the difficulty is maintained, no problem.
* UselessInfo: add extra node, but not increase calculation step?
* AddDependence: add 1 extra node, increase 1 calculation step, no problem.
* InsertConditional: add 1 extra node, I’m not sure how the number of calculation steps change.
* CounterFactual: add 1 extra node, increase 1 calculation step, no problem.
* Bi-CounterFactual: add 3 extra node, I’m not sure how the number of calculation steps change.
---
Reply to Comment 1.1.1:
Comment: We thank the reviewer's response!
The reviewer's interpretation of the calculation step was mostly accurate. We provide further clarification on the three mutations that the reviewer is uncertain about:
* **UselessInfo**
**[Mutated question]**: Janet’s ducks lay 10 eggs per day. She eats 4 for breakfast and bakes muffins with 2. She sells the remainder for $3 per fresh duck egg. **Janet plans to save these money for a new dress.** How much in dollars she makes every day?
**[Mutated code]**:
```python
eggs = 10
breakfast_eggs = 4
muffin_eggs = 2
remainder = eggs - breakfast...
price = 3
sales = price * remainder
# The useless Info
# Note that, the added number is sampled. In other examples, it may not be 0.
# In Figure-1 in the paper, we missed '+0'. We already updated the figure.
dress = sales + 0
return sales
```
**[Difficulty Changes]**: The mutation adds an extra calculation step. To clarify, in the table, all examples in UselessInfo contain **one additional reasoning step** compared to the Raw examples. However, this extra step does not impact the calculation of the final answer. Therefore, according to our definition, we still consider UselessInfo to be a **Level-2 mutation**.
* **InsertConditional**
**[Mutated question]**: Janet’s ducks lay 10 eggs per day. She eats 4 for breakfast and bakes muffins with 2. She sells the remainder for $3 per fresh duck egg. **Janet only sells eggs if her ducks lay at least 16 eggs in a day.** How much in dollars she makes every day?
**[Mutated code]**:
```python
eggs = 10
breakfast_eggs = 4
muffin_eggs = 2
remainder = eggs - breakfast...
price = 3
# The inserted Condition
if eggs > 16:
sales = price * remainder
else:
salse = 0
return sales
```
**[Difficulty Changes]**: Compared to the original problem, the mutation introduced an if-else operation. To clarify, in the table, all examples in InsertConditional contain **one additional reasoning step** compared to the Raw examples.
* **Bi-CounterFactual** is equivalent to **CounterFactual**, as in our PN/PS experiments, the 'Raw' questions were also transformed into binary questions. Therefore, the additional reasoning step introduced by Bi-CounterFactual is the assumption of a value change.
We want to emphasize that testing reasoning is inherently an adversarial task. A model capable of reasoning through a problem should perform equally well across a diverse range of its variations. Our work paves the way for defining and implementing these variations at scale. In our paper, **we presented multiple variations designed to evaluate the model’s reasoning ability from different perspectives, going beyond just differentiating it from memorization** (SampleValues). For example:
* UselessInfo: assesses the model’s ability to disregard irrelevant information.
* Level-3 mutations: assess the models’ ability to accurately integrate new information and logic into existing problems. While these mutations introduce an additional operation that could increase difficulty, we argue that:
* (1) if a model has truly learned basic math, adding one more step should not significantly alter the problem’s complexity, and
* (2) the ability to envision an alternative scenario is a fundamental aspect of reasoning, which these mutations are specifically designed to test.
We promise to include the discussion about the problem difficulties in the updated version of the paper. | Summary: The paper mainly introduces a benchmark synthesis pipeline for math and coding reasoning problem. The proposed pipeline can make modifications of the original benchmark (question, answer) pairs to make it a different (potentially more challenging) instance. The main motivation is to evaluate the true reasoning ability of the models other than memorizing training set. The pipeline comprises 3 steps: (1) NL-to-code transformation (2) make changes to the code/computation graph (3) transform back from code to NL. The results show that models usually yield worse performance on the synthesis benchmarks.
## Update after rebuttal
Overall I think this work is a moderate extension of the Gsm-symbolic paper; I will keep my already possitive rating
Claims And Evidence: The claim is: fixed benchmarks are not good enough as there can be leakage, so we need this benchmark systhesis tool to alter the original benchmark to get more faithful evaluation results
I feel the "sysnthesis" part is clear and the results well supports the claim, we observe quite some drops when altering the original question, even if it is just changing values or adding irrevant information; (earlier work such as [1] also have this observation and applied similar techniques);
However, the claim that this can be a useful "benchmark" is unclear; the main goal of a benchmark is to evaluate performance accross different models, however, if the synthesis is not deterministic, it is not possible to compare results with previously reported scores from other models; if we fix the synthesis, then the problem goes back to a "fixed" benchmark with potential leakage once released;
If the authors can show that even though the synthesis is not deterministic, some metric e.g., the drop of performance, can still be robust enough to have comparison across different models, the contribution of this paper would be more clear.
---
Reference:
[1] Mirzadeh, Iman, et al. "Gsm-symbolic: Understanding the limitations of mathematical reasoning in large language models." arXiv preprint arXiv:2410.05229 (2024).
Methods And Evaluation Criteria: Some important technical details seems to be not explained (or hard to find), this includes: What exact models are used for
(1) NL-to-code
(2) Computation graph parsing
(3) code-to-NL
Theoretical Claims: N/A
Experimental Designs Or Analyses: Solid
Supplementary Material: N/A
Relation To Broader Scientific Literature: This is related to, and can be viewed as an expansion of: Mirzadeh, Iman, et al. "Gsm-symbolic: Understanding the limitations of mathematical reasoning in large language models." arXiv preprint arXiv:2410.05229 (2024).
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: # Response to Claims And Evidence: Robustness to stochastic synthesis
We believe there may be a misunderstanding about the experimental setup. To clarify:
* **All models in the paper are tested on the same generated benchmark instantiation**, ensuring fair comparison between models.
* We also report the **statistical accuracy of models on GSM8K numerical answer predictions in Figure 7**. The bar plot presents the average accuracy and variance for each model, tested on 10 test variations per mutation, sampled using 10 different seeds. Importantly, these 10 test variations are identical across all models in this experiment. The results show the robustness of the metric to stochastic synthesis.
We thank the reviewer for pointing out the unclear instructions on how to evaluate using dynamic benchmarks like Re-Imagine. We will add the following clarification to the paper:
*For a fair comparison, all models should be tested using the same data. In practice, to evaluate using dynamic benchmarks like Re-Imagine, we recommend that researchers: (1) sample multiple test variations initially; (2) record and report the random seeds in publications or repositories; (3) report the statistical accuracy on the sampled test variations for both baseline models and proposed approaches.*
# Response to Methods And Evaluation Criteria: What exact models are used for (1) NL-to-code (2) Computation graph parsing (3) code-to-NL?
We use language models only in the NL-to-code and code-to-NL steps. All mutations to symbolic representations (ie. computation graphs) are performed explicitly by modifying the AST (abstract syntax tree https://docs.python.org/3/library/ast.html) data structure of the code according to user-defineable rules.
For NL-to-code and code-to-NL:
* GSM8K
* NL-to-code uses Mixtral-8x7B (see line 240-244, left-column in the main paper).
* Code-to-NL uses GPT-4o (see line 266-270, left-column in the main paper, Figure 13 and 14 in Appendix B).
* CLadder
* NL-to-code uses the causal engine offered in the original CLadder benchmark (see line 1124 in Appendix C).
* Code-to-NL uses Meta-Llama70BInstruct (see line 1140 in Appendix C).
Loop and CruxEval start from the symbolic representation, so the NL-to-code and Code-to-NL steps are skipped; thus, applying Re-Imagine to these benchmarks does not require use of any models.
---
Rebuttal Comment 1.1:
Comment: (copying official comment here so authors can see this) Thanks authors for the rebuttal. Overall I think this work is a moderate extension of the Gsm-symbolic paper; I will keep my already possitive rating | Summary: This work creates a framework for LLM reasoning evaluationexpands and scales up LLMs reasoning evaluation by means of an automated pipeline that converts benchmark problems into symbolic representations and then back again, and a 'mutations' step to create variations in pre-existing questions to further test reasoning capabilities.
Claims And Evidence: The mutation step in particular offers a great way to augment data and benchmarking for LLMs. This is a versatile tool that uses powerful symbolic reasoning tactics to test reasoning.
Methods And Evaluation Criteria: Because the mutation part to me is the best methodological novelty of this paper, I would personally like to see more comprehensive testing on the mutations, apart from the selective manual verification you did.
Theoretical Claims: None
Experimental Designs Or Analyses: The work does not do experimentation on how models perform on their framework versus other reasoning evaluation methods (like those referenced in the related works section from from Mirzadeh et al., Lewis & Mitchell, or Gonzalez & Nori). Extremely thorough model testing (Figure 2) and benchmark usage (code benchmarks).
Supplementary Material: Skimmed through it.
Relation To Broader Scientific Literature: Generally speaking, the thing I find least convincing is the reason *why* this framework is needed overall. The mutation step is interesting, but is the symbolic conversion approach better than simpler mutation methods? This isn't particularly addressed experimentally. Of course, it makes sense logically that symbolic conversion would allow for better code/math mutations. But this can be formally shown.
Essential References Not Discussed: I think one aspect you didn't really cover is the adversarial nature of a lot of the testing that is done in this field. The mutations could include something like robustness testing. Also, similar works to be cited would be DreamCoder and SATNet.
Other Strengths And Weaknesses: Weaknesses: should directly compare against related works methods to show concrete improvements.
Strength: very thorough testing of diverse domains, datasets, ablations (in appendix) and mutation types. Interesting findings about complex reasoning and weaknesses of these LLMs
Other Comments Or Suggestions: I think pages 2-4 need some editing. There seems to be accidentally duplicated paragraphs (the Judea Pearl quotes, the definitions of the layers etc)
Questions For Authors: All prompts are done with zero-shot prompting. Did you look at all at few-shot?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: # Response to Experimental Designs Or Analyses and Weaknesses: should directly compare against related works methods to show concrete improvements
We highlight that **the goal of Re-Imagine is to establish a unified reasoning hierarchy that integrates both previously studied mutations and the new mutations introduced in our work**.
We re-implement the two most widely studied mutations from previous work—UselessInfo and SampleValues—while scaling them up to the entire GSM8K test set. Since no prior studies have focused on evaluating models' reasoning abilities through mutations in the other three benchmarks—Loop, CruxEval, and CLadder—there is no meaningful mutations to be included in the framework.
---
# Response to Experimental Relation To Broader Scientific Literature: Why Symbolic Representation?
The primary reason for introducing the executable symbolic representation is to obtain ground truth answers for the mutated examples in a deterministic manner. For instance, if the symbolic representation is a Python code snippet, the answer to the mutated question is derived by executing the mutated code. As a result, both the symbolic-to-mutation and mutation-to-answer modules in the pipeline are deterministic. The other two modules—NL-to-symbolic and mutation-to-NL question—rely on LLMs. Given that LLMs have demonstrated relatively high reliability and robustness in NL-to-code and code-to-description tasks, the accuracy of these two modules is generally satisfactory. On top of these, for each LLMs-based module, we conduct verifications to further guarantee the mutations accuracy:
* NL-to-symbolic: see lines 246-249, left column, in the main paper.
* Symbolic-to-NL question: see line 220-224, right column, in the main paper.
**In conclusion, executable symbolic representations enable us to break down the mutation process into smaller steps that are either deterministic or easily handled by LLMs, and can be thoroughly verified.** In addition, the symbolic representation gives us greater control over the mutation generation process. **We can explicitly define and study different types of mutations.**
We are unclear about which "simpler mutation methods" the reviewer is referring to. We assume they might be methods that generate mutated QA pairs directly using LLMs without the assistance of symbolic representations. However, as shown in the paper, LLMs struggle with answering mutated questions, and relying on them to generate ground truth answers for mutated questions can be risky. Additionally, there are no reliable validation methods to verify the accuracy of the generated mutations. We are open to further discussion if the reviewer provides more details about the simpler mutation methods they have in mind.
---
# Response to Experimental Questions For Authors: Zero-shot Only?
For all four benchmarks, we adopt the standard in-context learning methods commonly used in the original benchmarks. In previous studies, zero-shot learning has been most widely used in CLadder, CruxEval, and Loop, while 8-shot learning has been the most common setup for GSM8K. We replicate this configuration in our experiments. In Appendix B.2, we further extend our experiments to explore the impact of different types of in-context learning examples on answering mutated GSM8K questions.
---
# Response to repeated text in pages 2-4
We did not find any repeated paragraphs or quotations as mentioned by the reviewer (any specific line number references to this would be greatly appreciated); however, we appreciate the note and have performed an additional pass editing this section for proofreading and clarity. We acknowledge that the typesetting of the table and caption may have led to some confusion or re-reading of earlier text, and we improve the layout for the camera-ready submission. | null | null | null | null | null | null |
Improving the Effective Receptive Field of Message-Passing Neural Networks | Accept (poster) | Summary: This paper introduces an architecture called Interleaved Multiscale Message-Passing Neural Networks (IM-MPNN) to address limitations in traditional Message-Passing Neural Networks (MPNNs), particularly the problem of over-squashing and the limited Effective Receptive Field (ERF). The key issue identified is that MPNNs struggle to capture long-range dependencies in graph-structured data due to an exponentially decaying influence of distant nodes, similar to the ERF limitations in Convolutional Neural Networks (CNNs).
## update after rebuttal
I keep my score, given the introduced addtional computation load, which may offset the performance gain. Also, it is not quite clear on how to choose the right scales for graphs.
Claims And Evidence: The linear graph analysis (Section 3.1) assumes a simple topology, and the diffusion model (Section 3.2) relies on Laplacian-based assumptions. These may not fully generalize to complex, real-world graph structures. Table 6 shows increased runtimes with more scales. The claim of "maintaining computational efficiency" is supported by complexity analysis (O(|V| + |E|)), but practical runtime impacts are underexplored, especially for large-scale graphs.
Methods And Evaluation Criteria: The IM-MPNN design is well-motivated, addressing over-squashing by expanding ERF through multiscale processing—a direct analogy to CNN solutions. The benchmarks (LRGB, heterophilic datasets, graph transfer) are appropriate.
Theoretical Claims: There is no proof in this paper.
Experimental Designs Or Analyses: The experimental designs are appropriate, including relevant datasets for evaluations. But more compasions with baselines on different benchmarks are needed.
Supplementary Material: I reviewed Appendix B, Table 6.
Relation To Broader Scientific Literature: This paper mainly builds on the idea of increasing the ERF of CNN, and adapts it to graphs. Based on that, this work extends several key ideas in GNN research, i.e., oversquashing, Hierarchical GNNs, and Long-Range Dependencies.
Essential References Not Discussed: Most relevant references are cited.
Other Strengths And Weaknesses: Strengths:
1. The multiscale interleaving approach is a novel synthesis of CNN-inspired ERF enhancement, distinct from existing over-squashing solutions.
2. Improving ERF addresses a fundamental GNN limitation.
3. The proposed multiscale interleaved MP approach is well-presented and easy to follow.
Weaknesses:
1. It lacks comparisons with other approaches addressing the oversquashing problem, e.g., re-wiring.
2. Runtime increases with scales (Table 6), which suggest a trade-off not fully addressed, potentially limiting scalability for massive graphs.
3. The ERF analysis could explore more graph topologies or non-diffusion-based MPNNs to strengthen generality.
Other Comments Or Suggestions: 1. Explain what different colors mean in Figure 1.
2. Figure 2, Line 67, "The the" -> "Then the"
3. Line 138, "nodes features the ℓ-th hidden layer" -> nodes features of the ℓ-th hidden layer
Questions For Authors: 1. Line 323-329, it is said to address the three questions in the experiments, and it is better to refer the question when discuss the corresponding results.
2. Table 1 and 2, it seems that the performance is not necessarily increasing with scales, can the authors further elaborate on this? How to choose the right scales for different graphs?
3. Can the authors compare the multiscale interleaved message passing with other approaches of addressing oversquashing, such as rewiring?
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: We thank Reviewer UcQT for their thoughtful and constructive feedback, and for acknowledging our work being *well-motivated*, *well-presented*, *distinct from existing solutions*, and *addressing a fundamental GNN limitation*. We are pleased to address your comments in detail below.
1. **Regarding comparison with rewiring:** During the rebuttal phase, we have experimented with a couple of methods that address oversquashing. The first is Graph U-Net, a hierarchical architecture that uses stages of pooling and unpooling to operate on different scales of the graph, with the main difference from IM-MPNN being that the U-Net approach only considers pairs of scales at a time. The second is DRew, a multi-hop method that utilizes rewiring, and we have chosen it because its implementation is compatible with the LRGB codebase, and because of its strong baseline performance. DRew was originally trained with the LRGB official hyperparameters, and not with the better-tuned ones presented in Toenshoff et al. (2023). Hence, for a fair comparison, we've rerun the experiments with those, changing only the width of the network to stay within the 500k parameter budget. The results for Graph U-Net, DRew, and our IM-GatedGCN are reported in the table below, further highlighting its effectiveness.
| Method | PascalVOC-SP |
|---|---|
| Graph U-Net | 0.1801+-0.0055 |
| DRew(GatedGCN) | 0.3909+-0.0051 |
| IM-GatedGCN | 0.4332+-0.0045 |
2. **Regarding runtime:** Thank you for the comment. We agree with the Reviewer that our IM-MPNN framework increases running times, as discussed in Section 4.3 reported in Appendix B (Table 6). However, Table 6 compares it to vanilla MPNNs, which are very fast and simple. It is expected that more complex architectures will require longer running times. For instance, on PascalVOC-SP, we measured a training runtime of 119.84 seconds using DRew-GatedGCN, while our IM-GatedGCN (with 4 levels) requires 31.72 seconds. That said, we agree that a leaner and faster method inspired by the interleaving multiscale principle is a promising direction for future work.
3. **Regarding the extension of the ERF analysis to more graph topologies:**
The ERF analysis that we present in Section 3.2 relies on the connection between the combinatorial Laplacian being a discretization of the continuous Laplacian for some geometry. This connection is rather general and can hold for geometric problems characterized by graphs resembling an unstructured mesh discretizing a continuous domain. Figure 1, for example, presents such a mesh, discretizing a circular domain using triangulation. One can locate the nodes in space such that the combinatorial Laplacian (which is defined by the connectivity alone) will be equivalent to a finite element (FEM) discretization of a (minus) analytical Laplacian operator. Finite elements methods can discretize arbitrary domains in various dimensions, using quite a few types of elements and their mixes (triangular, rectangular, tetrahedral, etc.). Hence, since our analysis fits any FEM discretization (because it approximates a continuous equation in (10)), it is rather general, at least for geometric problems, and not limited only to a structured regular grid. Furthermore, the discussion in Section 4.1 regarding the scales will hold for any Finite Element discretization, as the discretization operators are scaled by the size of the elements (equivalent to $h^2$ in the paper). On the other hand, graphs are indeed more general than unstructured meshes, but we believe that our analysis gives intuition and motivation to use our method in such cases as well.
4. **Regarding lines 323-329 and addressing the three questions in the experiments:** While not explicitly answering these questions, we believe our experiments are constructed in a way that answers them. That is, Section 5.2 answers (i), and Sections 5.1 and 5.3 answer (ii) and (iii). We revised the text of the results section to reflect it more explicitly.
5. **Regarding typos and editorial suggestions:** Thank you for pointing those out. We have fixed our paper according to your guidance.
----
We hope that you find our responses satisfactory, and that you will consider revising your score. | Summary: This work proposes a hierarchical coarsening method during GNN message passing in order to increase the effective receptive field while reducing over-squashing. The method is compared against datasets within the Long Range Graph Benchmark.
Claims And Evidence: The experimental results well demonstrate the claims. Particularly with Figure 7, the IM-GCN shows strong performance on the given long-range dependence prediction task as the scale increases.
Methods And Evaluation Criteria: The methods and evaluation make sense for the problem.
Theoretical Claims: The paper doesn’t put a large emphasis on theoretical findings.
Experimental Designs Or Analyses: The experimental designs are standard for graph learning problems. Hierarchical MPNNs should be included in the experimental results, as these works are very closely related to the idea of graph coarsening.
Supplementary Material: I read through the entirety of the appendix.
Relation To Broader Scientific Literature: This work positions itself within the important discussion about the limitations of MPNNs, specifically about over-smoothing and over-squashing. The depth of graph models is limited by these factors. Therefore, works investigating ways to remedy these problems are important for the field.
Essential References Not Discussed: Most relevant references are discussed. One major work for hierarchical representations is DiffPool [1]. For hierarchical graph transformers, which utilize graph coarsening, another work to consider is ANS-GT [2].
[1] Ying, Zhitao, et al. "Hierarchical graph representation learning with differentiable pooling." Advances in neural information processing systems 31 (2018).
[2] Zhang, Zaixi, et al. "Hierarchical graph transformer with adaptive node sampling." Advances in Neural Information Processing Systems 35 (2022): 21171-21183.
Other Strengths And Weaknesses: The interleaved multiscale message passing is straightforward. Some extra discussion and comparison to hierarchical MPNNs would be important to highlight the differences to IM-MPNNs. As the paper is currently written, the novelty of this work is not entirely clear.
Other Comments Or Suggestions: See questions. I would increase my score with strong answers to my questions.
Questions For Authors: (1) How is the pairing set P constructed?
(2) As mentioned previously, this work seems to resemble hierarchical MPNNs. What makes this work novel and sufficiently different from existing hierarchical MPNNs?
(3) What could the reason that IM-GatedGCN outperformed IM-GAT, despite the vanilla GAT outperforming the vanilla Gated-GCN? Why would interleaved multiscaling be more suited on a GatedGCN than a GAT?
(4) An interesting idea from a recent work is to perform what they call asynchronous aggregation during message passing [3]. This method is able to increase the effective receptive field as well by selectively aggregating messages from a node’s k-hop neighborhood and adding delays on when to aggregate each message. What do you see as the benefits of hierarchical coarsening over an approach like this?
[3] Jialong Chen, Tianchi Liao, Chuan Chen, and Zibin Zheng. 2024. Improving Message-Passing GNNs by Asynchronous Aggregation. In Proceedings of the 33rd ACM International Conference on Information and Knowledge Management (CIKM '24). Association for Computing Machinery, New York, NY, USA, 228–238. https://doi.org/10.1145/3627673.3679778
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank Reviewer 1PKF for their thoughtful and constructive feedback. We are happy to read that you found our *claims well demonstrated* and that the *paper tackles a problem important for the field*, and we are pleased to address your comments in detail below.
1. **Regarding related hierarchical MPNNs (DiffPool and ANS-GT):** Thank you for pointing out these related works. DiffPool is a coarsening (pooling) method for graphs. In contrast, our proposed IM-MPNN utilizes coarsening operations as a building block, and its main contribution is in the way in which the hierarchical representations of graph features are processed. Thus, it is possible to use DiffPool within IM-MPNN as its coarsening operation instead of Graclus. We chose to work with Graclus thanks to its popularity. We have clarified this important distinction in our paper.
ANS-GT is a variation of graph transformers that uses a preprocessed graph coarsening within its attention mechanism. It differs from IM-MPNN in two ways: First, our IM-MPNN uses coarsening as part of a message-passing network. Second, it interleaves multiple coarsening levels instead of a single one. In our revised paper, we now added this discussion and citations to DiffPool and ANS-GT. Thank you.
2. **Regarding the difference from other hierarchical MPNNs:** To the best of our knowledge, this is the first MPNN-based method to use multiple graph scales during the entire processing stage of the neural network, which is different from U-Net based approaches that only consider pairs of scales at a time. We demonstrate that it outperforms the baselines on datasets that require long-range interactions, and inspired by your comment, we also include an empirical comparison to highlight the effectiveness of IM-MPNN compared with Graph U-Net, in the table below. We have included this discussion in our revised paper.
| Method | PascalVOC-SP|
|---|---|
| Graph U-Net | 0.1801+-0.0055 |
| IM-GatedGCN | 0.4332+-0.0045 |
3. **Regarding the pairing set P:** The pairing is done using the Graclus clustering, as discussed in our response to point 1. However, it is not limited to this specific method and can be obtained with other clustering methods as well. Following your question and a request from reviewer EHuP, we added more information about Graclus to the appendix.
4. **Reasoning on IM-GatedGCN vs. IM-GAT results:**
We agree with the reviewer that this is an interesting topic. However, we would like to point out that this is a phenomenon that can happen empirically. For example, in Table 5, we see that GPS+Performer+GCN outperforms GPS+Performer+GAT on three of the five datasets. Therefore, while this is interesting to explore, investigating it is out of the scope of this paper.
5. **Regarding asynchronous aggregation during message passing:** We thank the reviewer for bringing the work to our attention. The method, aAsyn, suggests a multi-hop aggregation in an asynchronous approach. We did not find the code for this method in order to compare results with it. Hence, we compared with DRew (Gutteridge et al., 2023), which is another multi-hop approach, as discussed in response to Reviewer UcQT, to show the benefits of IM-MPNN over it. We agree that aAsyn is relevant to our work, and we now cite and discuss it in our revised paper.
| Method | PascalVOC-SP |
|---|---|
| DRew(GatedGCN) | 0.3909+-0.0051 |
| IM-GatedGCN | 0.4332+-0.0045 |
----
We hope that you find our responses satisfactory, and that you will consider revising your score.
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Rebuttal Comment 1.1:
Comment: Thank you to the authors for their thoughtful response. I believe the extra discussion and comparison to other related baselines strengthens this work. I will update my score appropriately.
---
Reply to Comment 1.1.1:
Comment: We thank you for your positive feedback and for adjusting your score. We appreciate your thoughtful review and are happy you found the additional discussion and comparisons to clarify our work and strengthen it.
Sincerely, Authors | Summary: The paper addresses the challenges faced in capturing long-range interactions in GNNs due to limited effective receptive field of the message passing mechanism and proposes a novel architecture based on a hierarchical coarsening of graph to improve communication between distant nodes.
## update after rebuttal:
Following the clarifications and additional results provided by the authors during the rebuttal, I believe the complementary nature of the proposed approach could be valuable to the GNN community. Therefore, I have raised my score.
Claims And Evidence: - The main claim that the contribution of one node to another node's output decaying exponentially by the distance between them is shown and analyzed on different synthetic graph types.
- While the results in Table 3 show IM-MPNN to achieve the best performance, some more baselines reported in Table 5 seem to be more competitive, particularly CO-GNN. Although I understand all results can not be reported in the main paper due to space limitation, I believe comparison with most recent competitors such as CO-GNNs should be included in the main results table.
Methods And Evaluation Criteria: - The proposed technique is analyzed on different graph types and evaluated on relevant real-world benchmark datasets.
- IM-MPNN, while interesting, is more time consuming in practice although its time complexity is a linear factor of a regular MPNN. Since the predictive performance is competitve or only a small improvement over a baseline such as CO-GNNs , it would also be nice to see how IM-MPNN compares empirically to CO-GNNs (and/or other such competing methods in addition to basic MPNNs such as GCN already shown in Table 6) in terms of runtime.
Theoretical Claims: The theoretical claims seem correct but the mathematical details were not checked in detail.
Experimental Designs Or Analyses: The experiments and analyses are reasonably well designed and conducted.
Supplementary Material: The appendices was also reviewed.
Relation To Broader Scientific Literature: The paper offers a relatively new perspective on effectively enabling long range interactions whereas most existing solutions are based on re-wiring strategies or specifically designed architectures and thus adds value to the current GNN literature.
Essential References Not Discussed: None that I can recall.
Other Strengths And Weaknesses: **Strengths**: The paper provides an interesting perspective to an imporant problem in the GNN landscape, is well-written with illustrations aiding comprehension.
**Weaknesses**: Runtime for even 4 scale levels in hierarchical coarsening is realtively quite high. An empirical comparison of runtime between IM-MPNN and competitive baselines with similar performance such as CO-GNNs and evaluation on large-scale OGB datasets could be a valuable addition.
Other Comments Or Suggestions: A brief basic explanation of the method used to select nodes pairs for graph coarsening could be helpful for readers not familiar with Graclus algorithm.
Questions For Authors: 1. Would the number of scales (and the number of nodes in each scale level) be a hyperparameter to be tuned? Is there any guideline for its selection depending on some properties of the input graph? Does performance tend to level out or decrease if the number of scales are further increased?
2. How many layers did the IM-MPGNNs generally constitute of?
3. Can IM-MPNN use heterophily designated GNNs or others as the underlying MPNN? For example, IM-GATsep or IM-FAGCN? If so, how would they be expected to perform? Is IM-MPNN complimentary with any GNN backbone or is there a case where a certain type of GNN could be deterimental to IM-MPNN?
4. Since the performance of IM-MPNNs and CO-GNNs is similar, do IM-MPNNs hold any other advantages over CO-GNNs, such as efficiency?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We thank Reviewer EHuP for the thoughtful and constructive feedback and for finding our paper *interesting*, *well-written*, valuable to the current GNN literature, and offering a *different perspective on enabling long-range interactions*. We are pleased to address your comments in detail below.
All the results and discussions were added to our revised paper, and we think they improved our paper, thank you.
1. **Regarding organizing Table 5:** Our goal was to compare with multiple relevant methods, hence Appendix Table 5 includes 33 methods. Following your suggestion, CO-GNN is now included in Table 3 (main paper), as well as our IM-COGNN -- please see details below.
2. **Re runtimes:** We agree with that IM-MPNN increases runtime, as discussed in Section 4.3 and Appendix B (Table 6). However, IM-MPNN retains the asymptotic complexity of its backbone MPNN, typically linear in the number of nodes and edges, and Tables 1, 2, and 6 show that IM-MPNN significantly improves performance over its backbone. We also kindly note that methods like DRew (Gutteridge et al., 2023) requires higher runtimes. For example, on PascalVOC-SP, DRew-GatedGCN takes 119.84s vs. 31.72s for IM-GatedGCN (4 levels). Following your advice, we now report runtimes on the Questions dataset using 8-layer networks with 256 channels on an Nvidia A6000. The results demonstrate that our method achieves strong performance while keeping runtime comparable to methods like CO-GNN.
|Method|milliseconds per epoch|
|---|---|
|GCN|68.67|
|CO-GNN|211.43|
|FAGCN|104.85|
|GatedGCN|127.90|
|GAT|113.26|
|GPS(Performer+GCN)|412.07|
|GPS(Transformer+GCN)|Out of memory|
|IM-GCN (Ours)|151.74|
3. **Regarding comparison with CO-GNN:** We incorporated IM-MPNN into CO-GNN and found it further improves CO-GNN’s strong baseline, as shown in the table below.
|Method|Roman.|Amazon.|Mine.|Tolo.|Ques.|
|---|---|---|---|---|---|
|CO-GNN($\Sigma$,$\Sigma$)|91.57+-0.32|51.28+-0.56|95.09+-1.18|83.36+-0.89|80.02+-0.86|
|CO-GNN($\mu$,$\mu$)|91.37+-0.35|54.17+-0.37|97.31+-0.41|84.45+-1.17|76.54+-0.95|
|IM-CO-GNN($\Sigma$,$\Sigma$) (Ours)|92.08+-0.33|53.11+-0.59|95.79+-0.96|85.25+-1.03|80.49+-0.92|
|IM-CO-GNN($\mu$,$\mu$) (Ours)|92.00+-0.41|54.43+-0.41|97.39+-0.35|85.77+-1.05|78.92+-0.87|
4. **Regarding OGB dataset:** During the rebuttal, we ran experiments with a couple of IM-MPNN options on OGBN ARXIV. The results are reported in the table below, and they suggest that our approach is beneficial also for larger graphs.
|Method|OGBN Arxiv (Acc)|
|---|---|
|GCN|71.74+-0.29|
|GAT|71.95+-0.36|
|IM-GCN (Ours)|73.89+-0.21|
|IM-GAT (Ours)|73.87+-0.16|
5. **Regarding the Graclus algorithm:** Our focus was not on the coarsening method, as IM-MPNN can benefit from other approaches in the literature. However, we agree that an explanation is helpful and have added it to the revised paper. Thank you.
6. **Regarding number of scales:** The Reviewer is correct that the number of scales is a hyperparameter. Like width and depth in neural networks, performance eventually plateaus or drops, which can be due to several factors. First, to stay within a parameter budget, we reduce network width when increasing scales, which may limit performance. Second, adding more scales may offer no benefit once the interaction range is sufficient for the data. For example, on a graph with a diameter of 16 and 3 coarsening levels, a node at the coarsest scale may already span most of the graph, making further scaling unnecessary. Thus, the optimal number of scales depends on the graph’s diameter.
7. **Regarding the number of layers:** We use IM-MPNN to enhance MPNN backbones and therefore follow the hyperparameters from prior work. For example, in IM-GatedGCN on PascalVOC-SP, we use the GatedGCN settings from Toenshoff et al. (2023), including 10 layers.
8. **Regarding IM-MPNN with heterophily designated GNNs:** To address your insightful question, we provide results of IM-GATsep and IM-FAGCN on heterophilic datasets below. These show that IM-MPNN can enhance various MPNN backbones and improve their performance.
|Method|Roman.|Amazon.|Mine.|Tolo.|Ques.|
|---|---|---|---|---|---|
|GAT-sep|88.75+-0.41|52.70+-0.62|93.91+-0.35|83.78+-0.43|76.79+-0.71|
|FAGCN|65.22+-0.56|44.12+-0.30|88.17+-0.73|77.75+-1.05|77.24+-1.26|
|IM-GAT-sep (Ours)|89.93+-0.34|53.97+-0.58|96.15+-0.37|85.44+-0.40|77.92+-0.92|
|IM-FAGCN (Ours)|86.26+-0.44|52.81+-0.35|95.17+-0.84|84.49+-0.97|78.17+-1.06|
9. **Regarding IM-MPNNs and CO-GNNs:** CO-GNN is a strong method that explores learning MPNN actions. We see IM-MPNN as a complementary contribution, offering interleaved hierarchical processing that can be combined with CO-GNN. To demonstrate this, we now include IM-COGNN in the table above, showing that IM-MPNN can further enhance CO-GNN’s strong baseline.
---------
We hope that you find our responses satisfactory, and that you will consider revising your score.
---
Rebuttal Comment 1.1:
Comment: I thank the authors for the clarifications and appreciate their effort in providing further experiments. The complementary nature of their proposed approach could be helpful to various types of GNN architectures for tackling different tasks. Therefore, I have raised my score.
---
Reply to Comment 1.1.1:
Comment: Thank you for your feedback and for raising your score. We are glad that our response helped clarify the complementary nature of our approach for different GNN architectures and that the additional experiments addressed your concerns.
Sincerely, Authors. | Summary: This paper proposes a new messages passing strategy to expand the receptive field of GNNs by transmitting information between graphs at multiple scales, and theoretical analysizes the influence decay of message passing along the path between nodes. The experiments are conducted on long-range graph benchmarks to validate the effectiveness of multiscale message interaction.
## update after rebuttal:
My concerns in the first review phase have been addressed by the authors with empirical justification, so I raised my score.
Claims And Evidence: Yes.
Methods And Evaluation Criteria: Yes.
Theoretical Claims: checked.
Experimental Designs Or Analyses: Yes. The experimental designs are sound, which follow the widely used protocals.
Supplementary Material: The entire supplementary.
Relation To Broader Scientific Literature: The key contribution of this work is to build message passing among multi-layered graphs, namely, original graph and its coarsened graphs at different scale, which shares idea with (Yang et al. "SeBot: Structural Entropy Guided Multi-View Contrastive
Learning for Social Bot Detection", in KDD'24), where the hierarchy of the graph in question is constructed with some coarsening method like structure entropy, but the messages are only allowed to transfer from higher level to low level (directionally).
Essential References Not Discussed: No.
Other Strengths And Weaknesses: Strengths:
1. The paper is well-written and easy to follow.
2. It is a good idea to establish short-cut message passing channels between long-range nodes via coarsened graphs.
3. The message passing interleaved among different scaled graphs is meaningful, leading to impressive results.
Weaknesses: Why the proposed method is superior to other methods that are also able to capture the long-range dependence on heterophilic graphs is not discussed.
Other Comments Or Suggestions: 1. Messages are constrained to pass through the coarsen graphs in the adjacent layers, why not passing messages between any pair of coarsened graphs (including the original one)? what is the benefit of the current choice?
2. It is somehow counterintuitive to adopt pairwise coarsening according to the topology of the heterophilic graphs, as there is a good chance for connected nodes in that setting that have different features/labels, but grouping them into one node as well as feature aggregation according to eq.(17) may lead to invalid node features. How can we explain the outperformance of IM-GNN in heterophilic graphs?
Questions For Authors: In Eq.(20), what are X_1 and X_2? Can it be formulated in the product of coarsening matrix and feature matrix, which I guess will be more neat.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We thank Reviewer U4Ms for their thoughtful and constructive feedback. We appreciate you finding our paper *well-written and easy to follow*, and that the proposed method is *meaningful* with *impressive results*, and we are pleased to address your comments in detail below.
1. **Regarding SeBot (Yang et al. 2024)**: Thank you for the reference. The hierarchical information processing in SeBot appears to be based on a Graph U-Net structure, focusing on how to perform coarsening between scales. In contrast, our IM-MPNN uses existing coarsening operations, and its contribution is in the unique multiscale interleaving approach to enhance the ERF of MPNNs, as reflected by the results in the Table below, where our method significantly outperforms Graph U-Net. It might be possible (and interesting to try) to use SeBot with IM-MPNN in future works. We added this discussion and a citation to SeBot in our revised paper.
| Method | PascalVOC-SP |
|---|---|
| Graph U-Net | 0.1801$_{\pm 0.0055}$ |
| IM-GatedGCN | 0.4332$_{\pm 0.0045}$ |
2. **Regarding other methods on heterophilic graphs:** Thank you for the suggestion. As noted by Reviewer EHuP, our IM-MPNN offers a different approach compared with existing methods, that rely mostly on rewiring or designated architectures, while our IM-MPNN offers a hierarchical approach to allow the propagation of information from distant nodes. Moreover, IM-MPNN can be combined with these methods, to further improve performance, as shown in our results provided in the response to Reviewer EHuP. We added the discussion and results to the revised paper.
3. **Regarding messages between any pair of coarsened graphs:** We appreciate the interesting question. We have tried similar ideas of passing information between different scales of the graph, which also adds to the computational complexity of the architecture. However, we did not see an improvement over the proposed interleaving approach.
4. **Regarding the coarsening of heterophilic graphs:** Thank you for the insightful question. We would like to kindly note that an IM-MPNN layer processes the original resolution features (as well as other scales) on their own, followed by their aggregation. Thus, in our IM-MPNN, we only add information to the original resolution node features, which are aggregated from distant nodes, using the Graclus pooling algorithm. We agree with the Reviewer that the specific choice of pooling and aggregation may be improved for heterophilic graphs, and it will be interesting to explore such approaches in future works. Finally, we note that our experiments consistently indicate that our IM-MPNN improves downstream performance, also in heterophilic graphs, including when combined heterophily-designated MPNNs, as shown in our added experiments in our response to Reviewer EHuP. We added this fruitful discussion to our revised paper. Thank you.
5. **Regarding Eq. (20):** Thank you for pointing out our typo, we have now corrected the equation according to your guidance, and it reads (apologies for the line separation. There were issues with Openreview's rendering of the equation):
$$x_{q=(i,j)}^{(s,\ell+1)} = \tilde{x}_{q=(i,j)}^{(s,\ell)}$$
$$+ W_{l2h}^{(s,\ell)}\frac{1}{2}(\tilde{x}_i^{(s-1,\ell)}+\tilde{x}_j^{(s-1,\ell)})$$
$$+ W_{h2l}^{(s,\ell)}\tilde{x}_{(q,p)}^{(s+1,\ell)}.$$
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We hope that you find our responses satisfactory, and that you will consider revising your score. | null | null | null | null | null | null |
Nonconvex Theory of $M$-estimators with Decomposable Regularizers | Accept (poster) | Summary: This paper challenges the results of Section 9 of Martin's textbook "High-dimensional statistics". Surprisingly, this paper is able to recover the results of Proposition 9.13 and Theorem 9.19 of "High-dimensional statistics" for nonconvex loss functions. Moreover, Theorem 3.3 in this paper extends the results of Theorem 1 in Po-Ling's nonconvex m-estimators work to the general norms. They also consider the corrected linear regression and l1-penalized Lasso estimator as two nonconvex samples
Claims And Evidence: Yes
Methods And Evaluation Criteria: Yes
Theoretical Claims: I have read the proof of this paper, and believe there are correct.
Experimental Designs Or Analyses: NA
Supplementary Material: NA
Relation To Broader Scientific Literature: NA
Essential References Not Discussed: NA
Other Strengths And Weaknesses: 1. Based on the definitions of stationary points (9), RSC condition(10) and $\tilde{\mathbb{G}}(\lambda_n)$, Theorem 3.1 in this manuscript recovers the results of Proposition 9.13 of Martin's textbook for any stationary points. Theorem 3.3 in this manuscript is an important result. Because they recover the convergence rate of Theorem 9.19 of Martin's textbook for any stationary points, and improve the Po-Ling's nonconvex results to any norms. Theorem 4.2 also recovers the previous results. Theorems 3.1 and 3.3 are quite novel and of significant to the community due to the importance of nonconvex research.
2. Theorem 4.2 only deals with the sub-Gaussian parameters which may be a weakness of this paper. The DNN is the popular nonconvex structure, but the examples section did not present the DNN case.
Other Comments Or Suggestions: NA
Questions For Authors: -Can we consider the other distributions for corrected linear regression?
-Can we use the DNN as the example?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: -Can we consider the other distributions for corrected linear regression?
Thanks for the question. (Rosenbaum & Tsybakov, 2010; Loh & Wainwright, 2012) have already studied the corrected linear regression, and they consider the sub-Gaussian parameters. This paper just follow them to use the exiting non-convex eample to illustrate our theory. It is interesting to consider the parameters that follow other distributions. But it is out of the scope of this paper.
-Can we use the DNN as the example?
Thanks for the question. We have tried DNN as an example. Unfortunately, DNN do not satifies the dual norm bound. Therefore, we can not apply our theory to DNN. One interesting future direction is to study the non-convex theory that can be applied to DNN. | Summary: This paper studies the theoretical properties of regularized M-estimators with decomposable regularizers under nonconvex loss functions. The authors extend existing results on convex regularized M-estimators to the nonconvex case, demonstrating that estimation errors remain within a restricted set and that convergence rates can still be recovered. They establish key theoretical guarantees, leveraging restricted strong convexity and decomposability conditions. The theoretical results are further supported by two concrete applications: corrected linear regression and the Lasso estimator under nonconvex loss functions. The findings significantly contribute to the understanding of high-dimensional statistical estimation in nonconvex settings.
Claims And Evidence: yes
Methods And Evaluation Criteria: yes
Theoretical Claims: I have checked the theories and found no errors.
Experimental Designs Or Analyses: No experiment
Supplementary Material: No Supplementary
Relation To Broader Scientific Literature: This work extends foundational results in high-dimensional statistics, particularly those of Negahban et al. (2009), Wainwright (2019), and Loh & Wainwright (2015). While these prior works focused on convex regularized M-estimators, the present paper generalizes the theory to nonconvex loss functions.
Essential References Not Discussed: no
Other Strengths And Weaknesses: Strengths
-Theoretical novelty: Extends convex M-estimator results to the nonconvex setting.
-Strong mathematical foundations: Proofs are detailed and rigorous.
-Relevance: The results have broad applications in high-dimensional statistics.
-Clarity: The paper is well-structured and clearly presents key results.
Weaknesses
-Theoretical focus: Lacks empirical validation, though this is not necessarily a major drawback given the paper's aims. -Assumptions: Some assumptions (e.g., decomposability, restricted strong convexity) may not always hold in practical settings, limiting applicability to certain problems.
Other Comments Or Suggestions: NO
Questions For Authors: -Can you comment on whether your results extend to more general forms of nonconvexity beyond those studied in the examples?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Can you comment on whether your results extend to more general forms of nonconvexity beyond those studied in the examples?
Thanks for the question. Our framework applies to a broad class of nonconvex loss functions; however, we require that the nonconvex loss satifies the dual norm bound.
---
Rebuttal Comment 1.1:
Comment: My questions have been addressed. Thanks for the reply. | Summary: This paper develops a theoretical framework for analyzing regularized M-estimators with decomposable regularizers. Extending prior work in convex settings, the authors establish that estimation errors remain in a restricted set and that convergence rates can be recovered despite the loss function's nonconvexity.
Claims And Evidence: yes
Methods And Evaluation Criteria: yes
Theoretical Claims: yes
Experimental Designs Or Analyses: NA
Supplementary Material: NA
Relation To Broader Scientific Literature: This paper is close to Wainwright (2019) and Loh & Wainwright (2015).
Essential References Not Discussed: No
Other Strengths And Weaknesses: Provides a significant theoretical extension from convex to nonconvex settings. Uses rigorous mathematical analysis to establish key results. Well-structured and clearly written, making the contributions accessible. Offers practical examples to illustrate the main theoretical findings. I think there is no significant weakness.
Other Comments Or Suggestions: The paper can benefit from a brief discussion on potential algorithmic implementations based on the theoretical results.
Questions For Authors: Are there any specific classes of nonconvex loss functions where your framework does not apply?
How sensitive are the key theoretical results to violations of the decomposability assumption?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: 1, The paper can benefit from a brief discussion on potential algorithmic implementations based on the theoretical results.
Thanks for the question. Our theoretical results show that the decomposable regularizers play the key role in facilitating convergence and improving generalization. So, it is important to develop the regularizers for the potential algorithmic implementations.
2, Are there any specific classes of nonconvex loss functions where your framework does not apply? How sensitive are the key theoretical results to violations of the decomposability assumption?
Thanks for the question. Our framework applies to a broad class of nonconvex loss functions; however, we require that the nonconvex loss satifies the dual norm bound. If the nonconvex loss does not satisfy the dual norm bound, our results do not hold. The decomposability assumption plays a crucial role in our results. If this assumption is violated, the key bounds and statistical guarantees may no longer hold. | Summary: The paper studies the high dimensional M-estimators for non-convex loss functions. The previous classical results only consider the convex cases. It is natural to consider the non-convex loss function in high dimensions. The motivation is strong. The central theoretical questions studied in this paper are whether we can extend the classical results from convex to non-convex cases. The paper shows the positive results which are quite interesting and the proof is easy to follow.
Claims And Evidence: The claims made in this paper are well-supported by rigorous mathematical derivations and proofs.
Methods And Evaluation Criteria: The methods employed in the paper are mathematically rigorous and appropriate for the problem setting.
Theoretical Claims: I carefully reviewed key results, including Theorem 3.1 and Theorem 3.3. The derivations are logically sound. The proofs appear correct, assuming the stated assumptions hold.
Experimental Designs Or Analyses: No
Supplementary Material: No
Relation To Broader Scientific Literature: (Loh & Wainwright, 2015) present the nonconvex results of regularized M-estimator with non-convex regularizers. This paper considers the nonconvex results of regularized M-estimator with decomposable regularizers.
Essential References Not Discussed: No
Other Strengths And Weaknesses: Strengths
Originality
The paper studies the important theoretical questions which are never covered by previous works. This paper is the original research.
Quality
The decomposable regularizers and restricted strong convexity are two key concepts that play the important roles in the high dimension statistics. The decomposable regularizers enforce that the estimated errors fall into a restricted set. Motivated by this, the restricted strong convexity is defined to show the property of strong convexity only along some directions. The classical results show that one can get the desired convergence rates of the estimated error. The basic assumptions are the convexity of loss functions. The paper aims to break the convex assumption and consider the non-convex settings. To address the questions, the paper is mainly based on the weaker RSC condition (Loh & Wainwright, 2015) than (4). The main results in this paper show that both the Proposition 2.2 and convergence rate of the estimated error in (Wainwright, 2019) still hold for any stationary points. The proof is simple and rigorous. The paper also use two non-convex examples to illustrate the theories. The overall quality is quite impressive.
Clarity
The motivation, the background and the main proofs are well organized and easy to follow.
Significance
The main results of this paper are important. They extend our knowledge on high dimensional M-estimators from classical convex to nonconvex cases. The significance is that they may motivate the other researchers to study more challenging non-convex loss functions.
Weaknesses
Although the results obtained this paper are important, I still have some questions for the authors:
1, What is the main difference between the proof of Theorem 2.7 in (Wainwright, 2019) and Theorem 3.3 in this paper? I think it is better to clarify this question in the paper, then the reader can quickly understand theorems and proofs.
2, What is the difference between the $\tilde{\mathbb{G}}(\lambda_n)$ defined in this paper and $\mathbb{G}(\lambda_n)$ defined in (Wainwright, 2019)? Why not use the original definition of $\mathbb{G}(\lambda_n)$ in (Wainwright, 2019)?
3, The first example is corrected linear regression. Why corrected linear regression model is non-convex and why do we need to enforce the constraint for parameter $\theta$?
Other Comments Or Suggestions: No
Questions For Authors: See the Weaknesses.
Code Of Conduct: Affirmed.
Overall Recommendation: 5 | Rebuttal 1:
Rebuttal: 1, What is the main difference between the proof of Theorem 2.7 in (Wainwright, 2019) and Theorem 3.3 in this paper? I think it is better to clarify this question in the paper, then the reader can quickly understand theorems and proofs.
Thanks for the question. The main difference between the proof of Theorem 2.7 in (Wainwright, 2019) and Theorem 3.3 in this paper is that the proof of Theorem 2.7 in (Wainwright, 2019) uses the RSC condition (4), while our proof of Theorem 3.3 relies on the RSC condition (10). The difference between (4) and (10) contributes the key difference between Theorem 2.7 in (Wainwright, 2019) and Theorem 3.3 in this paper.
2, What is the difference between the $\tilde{\mathbb{G}}(\lambda_n)$ defined in this paper and $\mathbb{G}(\lambda_n)$ defined in (Wainwright, 2019)? Why not use the original definition of $\mathbb{G}(\lambda_n)$ in (Wainwright, 2019)?
Thanks for the question. The $\tilde{\mathbb{G}}(\lambda_n)$ defined in this paper is for stationary points, while the $\mathbb{G}(\lambda_n)$ defined in (Wainwright, 2019) is for the unknown parameter. The price for recovering the Proposition 2.2 in (Wainwright, 2019) to nonconvex settings is that we have to redefine the $\tilde{\mathbb{G}}(\lambda_n)$ for stationary points.
3, The first example is corrected linear regression. Why corrected linear regression model is non-convex and why do we need to enforce the constraint for parameter $\theta$?
Thanks for the question. For the case of noisy or missing data, the most natural choice of the matrix $\hat{\Gamma}$ is not positive semidefinite, hence the quadratic loss appearing in the problem is nonconvex. (Rosenbaum & Tsybakov, 2010; Loh & Wainwright,
2012) have already shown the nonconvexity of this problem. Furthermore, when $\hat{\Gamma}$ has negative eigenvalues, the objective in (27) is unbounded from below. Hence, we enforce the constraint for parameter $\theta$. (Loh & Wainwright,
2012) have already done like this.
---
Rebuttal Comment 1.1:
Comment: Thanks author for the response. They have answered my questions well. I keep my positive score. | null | null | null | null | null | null |
Handling Imbalanced Pseudolabels for Vision-Language Models with Concept Alignment and Confusion-Aware Calibrated Margin | Accept (poster) | Summary: This paper proposes a novel approach to improving pseudolabels generated by vision-language models (VLMS). The authors identify two key errors which contribute to the degradation of pseudolabel quality: concept mismatch and concept confusion. Concept mismatch occurs when the class text name provides a description that is misaligned with the visual features. Concept confusion occurs when two (or more) classes contain significant overlap, and the text description fails to capture the most striking visual differences. To address these, the authors propose concept alignment, in which concept-mismatched classes are identified and their labels enhanced with an LLM, and the confusion-aware calibrated margin, in which a margin matrix is calculated per-class based on the inter-class similarity and class-wise detection confidence margin and integrated into the cross-entropy loss. The authors perform experiments in the unsupervised, semi-supervised, and transductive zero shot learning settings, and demonstrate improvement in fine-tuning across a wide variety of settings.
Claims And Evidence: Yes, the authors claims are well supported empirically.
Methods And Evaluation Criteria: Yes, the benchmark datasets and various fine-tuning settings make sense for the task.
Theoretical Claims: N/a
Experimental Designs Or Analyses: Yes, the experimental design and analysis is valid.
Supplementary Material: Yes, the supplementary material was reviewed in its entirety.
Relation To Broader Scientific Literature: Previous works, such as CPL, have investigated prompt-tuning to improve pseudolabeling by VLMs [A]. This work expands on this in a principled way through investigating what causes the misalignment between text and visual features, and directly addressing those with improvements.
[A] Candidate pseudolabel learning: Enhancing vision-language models by prompt tuning with unlabeled data. In Proc. of ICML.
OpenReview.net, 2024b
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: Strengths:
- The paper is well-written and easy to follow
- CAP achieves good performance in a wide variety of experimental settings, consistently improving the SOTA.
- The method is well-motivated based on empirical observations, and detailed analysis (e.g. density of confidence scores in Fig 4) support the authors principle claims.
Weaknesses:
- CAP is largely heuristic and involves several differing hyperparameters, however detailed ablations of these are not included.
Other Comments Or Suggestions: I find Figure 5 to be a little confusing; although the figure displays the entirety of the pseudolabel finetuning pipeline, the key components of CAP are not well highlighted. I think the figure should be simplified, and more emphasis should be placed on the components that are the authors contributions.
Questions For Authors: N/A
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thanks for your time and encouraging comments! We address each of your concerns below.
> **Q1:** Ablations of hyperparameters are not included
Following your suggestion, we have conducted ablations of several hyperparameters in CAP.
**Ablation of $t$**
In CAP, we use $t$ to identify concept mismatched classes. Below, we report the results under UL setting with different values of $t$.
*Table 1. Impact of threshold $t$.*
| | $t$ = $\frac{C}{14}$ | $t$ = $\frac{C}{12}$ | $t$ = $\frac{C}{10}$ (Default) | $t$ = $\frac{C}{8}$ | $t$ = $\frac{C}{7}$ |
|----------|---------|---------|------------------|---------|---------|
| **RESISC45** | 81.5 | 81.5 | 81.5 | 81.5 | 81.7 |
| **DTD** | 54.9 | 54.9 | 55.4 | 55.4 | 55.4 |
$C$ is the number of classes in the dataset. The results show that CAP maintains consistent performance across different threshold values.
**Ablation of $k$**
In CAP, we use $k$ to determine the number of pseudo labels generated for each class. Results of ablation of different values of $k$ under SSL setting are presented below.
*Table 2. Impact of pseudolabel number $k$.*
| | $k$ = 12 | $k$ = 14 | $k$ = 16 (Default) | $k$ = 18 | $k$ = 20 |
|----------|---------|---------|------------------|---------|---------|
| **RESISC45** | 82.9 | 83.0 | 83.3 | 83.5 | 83.1 |
| **DTD** | 61.5 | 61.1 | 61.3 | 61.1 | 60.6 |
The results demonstrate that CAP is generally robust to different choices of $k$.
**Ablation of $\tau$**
In CAP, we use $\tau$ as the confidence threshold to dynamically generate pseudolabels. We conducted experiments on different values of $\tau$ under UL setting. The results are as follows:
*Table 3. Impact of confidence threshold $\tau$.*
| | $\tau$ = 0.80 | $\tau$ = 0.82 | $\tau$ = 0.85 (Default) | $\tau$ = 0.87 | $\tau$ = 0.90 |
|----------|---------|---------|------------------|---------|---------|
| **RESISC45** | 80.9 | 81.2 | 81.4 | 80.5 | 81.6 |
| **DTD** | 55.9 | 56.3 | 57.1 | 56.4 | 56.7 |
The results confirm that our method is robust to changes in $\tau$.
> **Q2:** Confusing Figure 5
Following your valuable suggestion, we have revised Figure 5 to provide clearer visualization of CAP's key components while simplifying its overall presentation. The new figure is available at:
https://anonymous.4open.science/r/CAP-C642/framework_updated.pdf
We appreciate your insights and hope this revision improves clarity. We will incorporate all of the above experimental results and figures in the next version, and we welcome any additional feedback you may have! | Summary: This paper proposes a concept-adaptive pseudo-labeling framework to generate balanced pseudo-labels for fine-tuning vision-language models (VLMs) on downstream tasks.
In the first stage, the paper introduces concept alignment to address the issue of concept mismatch by assigning precise pseudo-labels to misclassified instances. In the fine-tuning stage, the paper proposes a confusion-aware calibrated margin, built upon logit adjustment, to mitigate concept confusion.
Experiments on six benchmarks demonstrate the effectiveness of the proposed approach, with ablation studies highlighting the contribution of each component.
## update after rebuttal
The authors have addressed my concerns, and I keep my initial positive rating.
Claims And Evidence: Yes
Methods And Evaluation Criteria: Overall, the technical contributions and evaluation are sound.
This paper focuses on fine-tuning VLMs for downstream tasks, specifically image classification, and conducts experiments on six benchmarks. The authors identify two key issues in generated pseudo-labels: concept mismatch and concept confusion. To address these issues, the paper proposes Concept Alignment (CA) and Confusion-Aware Calibrated Margin (CACM). The authors further support their approach with ablation studies under different datasets.
Theoretical Claims: N/A—this paper does not include theoretical proofs.
Experimental Designs Or Analyses: The proposed method is evaluated on six image classification benchmarks under SSL, UL, and TRZSL settings. Additional ablation studies on three datasets further demonstrate the effectiveness of the proposed components. Overall, the experimental setup and analysis are comprehensive and convincing.
One concern is the limited number (i.e., 4) of baselines for comparison. It would strengthen the paper if more baselines were included in the main results (i.e., Tab. 1).
Supplementary Material: Yes, the supplementary material has been reviewed. Key aspects examined include:
- Additional experimental results and extended ablation studies.
- Further implementation details, including hyperparameters and training settings.
Relation To Broader Scientific Literature: This paper addresses the issues of mismatch and bias in VLM-generated pseudolabels, contributing to broader research areas, particularly in VLM-based training and pseudo-labeling techniques. The proposed approach has the potential to improve the reliability of pseudo-labeling for various downstream tasks, extending its impact beyond image classification.
Essential References Not Discussed: No
Other Strengths And Weaknesses: Pros:
- Well-organized paper with clear motivation and strong writing.
- The proposed methods are effective and demonstrate SOTA performance.
Cons:
- As mentioned earlier, the number of compared baselines is limited—only four baselines are considered.
- The scope of evaluation is somewhat narrow. It would be more compelling if the method were tested on more challenging tasks, such as segmentation, rather than just image classification.
Other Comments Or Suggestions: N/A
Questions For Authors: See strengths and weaknesses.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thanks for your time and helpful comments! We address each of your concerns below.
> **Q1:** The number of baselines is limited
In our paper, we primarily compare against state-of-the-art methods **specifically designed for leveraging CLIP’s zero-shot capabilities** through pseudolabel generation. The number of such methods is relatively small—for instance, CPL only compares with three baselines.
To further enrich our comparisons, we have incorporated **general semi-supervised learning methods** as additional baselines, and the results under SSL setting are presented in the table below.
*Table 1. Comparison of different methods under SSL setting.*
| | RESISC45 | DTD | Flowers102 | EuroSAT |
|----------|---------|---------|------------------|---------|
| **FixMatch [1]** | 66.1 | 51.2 | 85.0 | 79.1 |
| **FreeMatch [2]** | 76.6 | 53.5 | 87.7 | 90.0 |
| **SoftMatch [3]** | 69.5 | 47.8 | 86.9 | 83.8 |
| **CAP (Ours)** | **83.3** | **62.3** | **90.0** | **92.8** |
The results show that CAP consistently outperforms these baselines on all datasets, with a significant improvement of 6.7% on RESISC45 and 9.8% on DTD.
[1] FixMatch: Simplifying Semi-Supervised Learning with Consistency and Confidence. In Proc. of NeurIPS, 2020.
[2] FreeMatch: Self-adaptive Thresholding for Semi-supervised Learning. In Proc. of ICLR, 2023.
[3] SoftMatch: Addressing the Quantity-Quality Trade-off in Semi-supervised Learning. In Proc. of ICLR, 2023.
> **Q2:** The scope of evaluation is somewhat narrow
We appreciate your suggestion to evaluate our method on more challenging tasks such as segmentation. However, our method is primarily designed to address the issue of pseudolabel imbalance caused by the image-level classification bias of VLMs, making it less directly applicable to segmentation tasks.
A key requirement of our approach is the ability to extract image features for each class and use them for clustering or similarity computation at different stages of the algorithm. In segmentation, however, a single image **typically contains multiple classes**, prevents the extraction of clean, class-specific visual prototypes. This intrinsic difference in problem formulation currently limits the applicability of our method.
In fact, existing works in top machine learning conferences that address this problem, such as CPL [4], LaFTer [5], and FineSSL [6], have similarly concentrated on classification tasks. This is because classification serves as a fundamental benchmark for evaluating improvements in pseudolabeling and adaptation strategies for VLMs.
While extending these techniques to segmentation or other structured prediction tasks is an interesting direction, it would require task-specific modifications beyond pseudo-labeling (e.g. in segmentation, one often needs to design a more advanced segmentation network). That being said, we fully acknowledge the importance of extending these techniques to structured prediction tasks like segmentation, and we will include this promising avenue in our future work discussion.
[4] Candidate pseudolabel learning: Enhancing vision-language models by prompt tuning with unlabeled data. In Proc. of ICML, 2024.
[5] LaFTer: Label-Free Tuning of Zero-shot Classifier using Language and Unlabeled Image Collections. In Proc. of NeurIPS, 2023.
[6] Erasing the Bias: Fine-Tuning Foundation Models for Semi-Supervised Learning. In Proc. of ICML, 2024.
---
We will incorporate all of the above experimental results and analyses in the next version. | Summary: This paper proposes a novel framework, CAP (Concept-Adaptive Pseudolabeling), to address the problem of imbalanced pseudolabels when fine-tuning Vision-Language Models (VLMs) like CLIP for downstream tasks using unlabeled data. The authors identify two key causes of imbalance: concept mismatch (where text features of a class are misaligned with image features) and concept confusion (where similar classes are hard to distinguish). CAP tackles these issues with two main components: 1) a concept alignment strategy that iteratively detects and corrects concept-mismatched classes using LLMs to generate enhanced textual descriptions, and 2) a confusion-aware calibrated margin that encourages the model to make more distinguishable predictions between similar classes. The framework also employs independent adapters on the visual branch to learn from both highly reliable (concept-aligned) and dynamically generated pseudolabels. Extensive experiments across six image classification benchmarks and three learning paradigms (unsupervised, semi-supervised, and transductive zero-shot) demonstrate that CAP consistently improves performance, achieving a relative improvement of 6.29% over the state-of-the-art.
Claims And Evidence: yes
Methods And Evaluation Criteria: yes
Theoretical Claims: yes
Experimental Designs Or Analyses: The experimental designs are rational, and the results are convincing.
Supplementary Material: No supplementary materials are provided.
Relation To Broader Scientific Literature: The paper builds upon a growing body of work on adapting VLMs to downstream tasks using pseudo-labels. It directly addresses the limitations of existing methods that suffer from imbalanced pseudo-labels due to confirmation bias.
Essential References Not Discussed: NO
Other Strengths And Weaknesses: Strength:
1. The identification of concept mismatch and concept confusion as distinct sources of imbalance is insightful and well-supported by the analysis and visualizations .
2. The confusion-aware calibrated margin provides a mechanism for improving local calibration and mitigating bias among confused classes.
3. The paper is well-written, clearly explains the proposed approach, and provides sufficient details for implementation
Weakness:
1. While the paper provides a good qualitative explanation of 'concept mismatch' and 'concept confusion,' a more formal or quantitative definition of these concepts would be beneficial.
2. While the paper demonstrates improved training time compared to CPL and GRIP, a more detailed breakdown of the computational cost of each component of CAP (e.g., concept alignment vs. fine-tuning) would be useful.
3. A more thorough discussion of the limitations would benefit the paper
Other Comments Or Suggestions: No
Questions For Authors: See strength and weakness part.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thanks for your time and helpful reviews! We address each of your concerns below.
> **Q1:** A more formal or quantitative definition of concept mismatch and concept confusion
Generally, concept mismatch arises from a severe form of the semantic gap while concept confusion is more commonly observed between similar classes. We provide more formal definitions below:
**Concept Mismatch:** A class $y$ is considered to exhibit **concept mismatch** if the predicted label $\hat{y}$ for its visual prototype $\boldsymbol{v}_y$ (the average of visual features for class $y$) is **incorrect**, i.e.,
$$
\hat{y} = \arg\max p(\boldsymbol{v}_y) \neq y
$$
where $p(\boldsymbol{v}_y)$ is the predicted probability distribution over all classes for prototype $\boldsymbol{v}_y$.
**Concept Confusion:** Given the confusion matrix **$\mathbf{M}$** predicted by CLIP, two classes $i$ and $j$ are considered to exhibit **concept confusion** if the misclassification between them is significant, specifically:
$$
\mathbf{M} _ {ij} + \mathbf{M} _ {ji} > 0.25 \times (N_i + N_j)
$$
where $N_i$ and $N_j$ are the total number of samples belonging to class $i$ and $j$, respectively.
Based on these definitions, we report the number of classes exhibiting concept mismatch and concept confusion in RESISC45 and DTD.
*Table 1: Number of classes exhibiting concept mismatch and concept confusion.*
| Dataset | Concept Mismatch | Concept Confusion |
| --------|------------------|-------------------|
| **RESISC45** | 6 | 17 |
| **DTD** | 9 | 24 |
We will incorportate these definitions into the next version of our paper to improve clarity and precision.
> **Q2:** Computational cost of CAP
CAP, CPL, GRIP share two stages:
1. **Pseudolabeling stage** – Responsible for generating pseudo-labels, only needs to be run once per dataset.
2. **Fine-tuning stage** – Where the model is trained using the generated pseudo-labels.
Additionally, CAP employ MismatchDetection algorithm to fix mismatched concepts.
Below, we compare the computational cost of these two stages of training on EuroSAT for CPL, GRIP and CAP, using an NVIDIA RTX 4090 GPU and a Intel(R) Xeon(R) Silver 4314 @2.40GHz CPU:
*Table 2: Computation time for each stage of CPL, GRIP and CAP.*
| Method | MismatchDetection Time | Pseudolabeling Time | Fine-tuning Time |
|--------|-------------------|------------------|------------------|
| **CPL** | - | 3min 32s | 74min |
| **GRIP** | - | 3min 32s | 102min |
| **CAP** | 47s | 3min 32s | 29min |
In can be observed that the mismatch detection algorithm of CAP takes about 47s. In fine-tuning, CPL requires more time as it takes an **iterative strategy requiring training to convergence multiple times** (10 iterations in the original implementation). In each iteration, CPL expand the pseudo-labeled dataset. GRIP shares a similar trend with CPL.
*Table 3: Computation time for each iteration of CPL.*
| Iteration of CPL | Training Time |
|-----------|-------------------------|
| **1st** | 1 min |
| **5th** | 7 min |
| **10th** | 13 min |
| **Total** | 74 min |
> **Q3:** Discussion of the limitations
One limitation of our method (CAP) is that it relies on a mismatch detection algorithm when handling **concept mismatch**. Currently, our detection method is a **simple clustering-based algorithm**, which, despite its computational efficiency, has room for improvement in detection accuracy and robustness.
In future work, we plan to explore more **precise mismatch detection algorithms** to better identify mismatched concepts, thereby further improving the robustness and accuracy of our method.
---
We will incorporate all of the above experimental results and analyses in the next version.
---
Rebuttal Comment 1.1:
Comment: Thanks , I keep my rate unchanged. | Summary: The paper addresses concept mismatch and confusion when adapting VLMs to downstream tasks using pseudo-labeled data. The authors argue that this issue primarily arises from an imbalance in the pseudo-labels generated by VLMs. To mitigate this, they propose a concept alignment mechanism and a confusion-aware calibrated margin strategy. Additionally, they introduce independent adapters that separately process the original labeled data and pseudo-labeled data. Extensive and diverse experiments demonstrate the effectiveness of the proposed methods.
Claims And Evidence: I believe the imbalance of pseudo-labels is a crucial challenge in adapting VLMs to downstream tasks using pseudo-labeled data. The proposed methods offer a reasonable solution to this issue, and their effectiveness is well-supported by appropriate experiments. The papers are well written to follow the core concept and motivation
- However, the ablation studies could be more comprehensive. Given the complexity of the method, additional components should be ablated, such as the choice of gamma, the use of independent adapters, and, if feasible, the selection of prompt tuning. Additionally, some abbreviations (e.g., CA, CACM) are not properly explained, which could enhance clarity.
- While the proposed method generally outperforms baselines, certain metrics, particularly on CUB TRZSL, show significant underperformance. Analyzing the root cause of this discrepancy would be needed.
- I wonder about the rationale behind (2). There can be various similarity calculation strategies.
Methods And Evaluation Criteria: Methods and evaluation criteria seem reasonable. As far as I know, the evaluation criteria follow the previous works (common benchmarks).
Theoretical Claims: There are no theoretical claims.
Experimental Designs Or Analyses: The effectiveness of the proposed methods is well validated through various experiments (Figures 4, 6, 7, 8, and 9). Additionally, experiments conducted with different data scales and backbone sizes demonstrate the consistency of the methods across varying settings.
Supplementary Material: I saw the examples and details of the implementation
Relation To Broader Scientific Literature: Considering the frequent use of pseudo labels in this literature, the proposed idea is worth to share
Essential References Not Discussed: To the best of my knowledge, there are no missing essential references, though I am not deeply familiar with this specific literature.
Other Strengths And Weaknesses: Described above
Other Comments Or Suggestions: Described above
Questions For Authors: Described above
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thanks for your time and helpful comments! We address each of your concerns below.
> **Q1:** The ablation studies could be more comprehensive
Following your feedback, we have conducted additional ablation studies on the components you mentioned.
**Ablation of gamma Selection**
We conducted experiments on different values of $\tau$ (we assume that the reference to gamma was intended to refer to $\tau$, the confidence threshold) under UL setting. The results are as follows:
*Table 1: Performance regarding $\tau$ under UL setting.*
| | $\tau$ = 0.80 | $\tau$ = 0.82 | $\tau$ = 0.85 (Default) | $\tau$ = 0.87 | $\tau$ = 0.90 |
|----------|---------|---------|------------------|---------|---------|
| DTD | 55.9 | 56.3 | 57.1 | 56.4 | 56.7 |
| RESISC45 | 80.9 | 81.2 | 81.4 | 80.5 | 81.6 |
It can be observed that our method is generally robust to changes in $\tau$.
**Ablation of Independent Adapters**
We evaluate our method with and without the independent adapters under UL setting. The results are as follows:
*Table 2: Performance of different adapter configurations under UL setting.*
| | CPL (baseline) | w/ Independent Adapters | w/o Independent Adapters |
|----------|---------|---------|---------|
| DTD | 51.9 | 55.3 | 54.6 |
| RESISC45 | 77.4 | 81.5 | 80.6 |
| EuroSAT | 72.9 | 76.2 | 78.3 |
It can be observed that both model gives better results than CPL, and shared adapters gives generally comparable results to independent adapters.
**Impact of Prompt Tuning Methods**
We replace MaPLe with two prompt tuning methods (i.e., UPT [1] and VPT [2]) and compare the performance under UL setting.
*Table 3: Impact of different prompt tuning methods.*
| | DTD | EuroSAT |
|----------|---------|---------|
| **CAP w. UPT** | 54.9 | 77.5 |
| **CAP w. VPT** | 56.2 | 77.3 |
| **CAP w. MaPLe** | 55.3 | 75.0 |
The results demonstrate that CAP can be effectively integrated with various prompt tuning methods.
[1] Unified Vision and Language Prompt Learning. ArXiv, abs/2210.07225, 2022.
[2] Visual Prompt Tuning. In Proc. of ECCV, 2022.
> **Q2:** Abbreviations (e.g., CA, CACM) are not properly explained
Thank you for pointing this out. We apologize for the oversight. **CA** and **CACM** are abbreviations for **C**oncept **A**lignment and **C**onfusion-**A**ware **C**alibrated **M**argin. We will ensure that these abbreviations are properly explained in the next version.
> **Q3:** Analysis of underperformance on CUB TRZSL
Thanks for pointing this issue out. By analyzing the confusion matrices, we found that our method has more classes with zero accuracy than CPL. To further study this, we conduct a in-depth analysis of the results on CUB.
CUB consists of 200 fine-grained bird species and exhibits **frequent concept mismatches**. For instance, CUB includes **four species of orioles**, but CLIP extracts **highly similar text features** for their category names. As a result, all four species are aligned with the visual features of a single dominant oriole species, leading to incorrect pseudo-labeling. Due to the **simplicity of our mismatch detection algorithm**, many of these mismatches go undetected, preventing affected classes from receiving correct pseudo-labels and limiting fine-tuning improvements.
In contrast, CPL assigns multiple pseudo-labels to each sample. Since the misclassified categories are **semantically related**, there is **a higher chance that the correct label appears within CPL’s candidate label set**. This enables CPL to improve accuracy on these classes more effectively, which explains its superior performance under this particular setting. However, such extreme concept mismatches are relatively rare across datasets.
> **Q4:** Rationale behind (2)
**The choice of similarity:** In Equation (2), we use cosine similarity to measure the similarity between the text and visual prototypes of two classes, as cosine similarity is the most commonly used similarity metric in CLIP and relevant literature [3,4].
We take the maximum similarity value across the text and visual features because if two classes have high text feature similarity but low visual similarity, misclassification can still occur, and vice versa. By selecting the maximum value, we ensure that our method accounts for class pairs where concept confusion is most likely to happen.
[3] Learning Transferable Visual Models From Natural Language Supervision. In Proc. of ICML, 2021.
[4] Does CLIP's Generalization Performance Mainly Stem from High Train-Test Similarity?. In Proc. of ICLR, 2024.
---
We will incorporate all of the above experimental results and analyses in the next version.
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Rebuttal Comment 1.1:
Comment: Thank you for the thorough rebuttals. I’ve read all the reviews, comments, and responses carefully. I will maintain my rating. | null | null | null | null | null | null |
The Double-Ellipsoid Geometry of CLIP | Accept (poster) | Summary: The work analyses the geometric properties of CLIP embeddings. It builds upon previous work that studied the modality gap in embeddings. The main finding is that image and text embeddings both live within separate ellipsoid thin shells in high dimensional embedding space. The authors demonstrate that this particular geometric configuration arises from the contrastive loss function and noise in the training dataset, i.e. patches with similar meaning that are not dedicated pairs (and thus used as "false" negatives in the loss). The paper introduces a measure of "conformity", indicating that embeddings of common themes (in image or text space) should be close to the mean embedding vector. Based on this definition, the authors provide a geometric justification for the modality gap, i.e. the present non-overlapping distributions for text and image embeddings minimize the KL divergence of the conformity distributions.
Claims And Evidence: Numerous claims are made in the manuscript, which are all supported well. I particularly enjoyed the simple but effective geometric interpretation of the results, e.g. Fig 6 or 11.
Methods And Evaluation Criteria: The geometric analysis is based on the theory of random vectors in high dimensional spaces and thus well grounded. Experiments are conducted on the MS-COCO dataset which has 328k images accompanied by natural language descriptions and thus seems adequate for the task.
Theoretical Claims: Claims are argued for by geometric interpretations and experiments, which appear correct. The definition of conformity Eq. 10 is plausible The validity of its approximation Eq. 11 demonstrated by data, Fig. 9
Experimental Designs Or Analyses: See other comments. The paper itself is a detailed problem analysis.
Supplementary Material: Additional figures that help understand the experiments and their results better.
Relation To Broader Scientific Literature: Yes. The paper presents interesting findings, which are relevant for anyone using a contrastive loss across modalities in ML.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: + Well written paper. The analysis is easy to follow.
- The applications of Sec. 7 are only exemplary and further usage of the introduced conformity measure remains unclear.
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 positive feedback. The applications section is indeed small since we devoted our paper to the geometric and statistical analysis, which we found the most important to delve in, explain and support experimentally. See additional comments embedded in our answers to the other two reviewers, which we do not want to repeat here.
The applicative examples are preliminary, still we found them exciting and useful. Studying these applications more thoroughly and suggesting additional ones would require an in-depth analysis which we believe would better fit a dedicated paper. Thanks again for your feedback. | Summary: This paper investigates the geometric properties of the CLIP embedding space, proposing that image and text modalities form independent double-ellipsoid structures displaced from the origin. The authors argue that this structure improves the performance of contrastive learning and provides explanations for previously known phenomena such as the modality gap and narrow cone effect.
Claims And Evidence: The main claim of the paper is that the CLIP embedding space exhibits a double-ellipsoid geometry rather than the simpler hyperspherical structure typically assumed in prior literature. However, this claim suffers from significant shortcomings:
- The key finding of the double-ellipsoid geometry largely reiterates existing results from prior studies, notably "Mind the Gap" (Liang et al., 2022), which has already thoroughly explored the modality gap and thin-shell phenomena. Thus, the contribution of this work does not clearly differentiate itself from earlier research, casting substantial doubt on the novelty and significance of the proposed ellipsoidal geometry.
- The "Conformity" concept introduced by the authors shows an extremely high Pearson correlation (0.9998) with the cosine similarity to the mean vector, questioning its practical novelty. This implies that the Conformity metric essentially duplicates existing cosine similarity measures and lacks a compelling justification for its introduction as a distinct concept.
Methods And Evaluation Criteria: - The experimental analyses conducted in this study are limited exclusively to a few samples in the MS-COCO dataset without any training or new empirical results.
- The proposed vertical SLERP (vSLERP) method lacks sufficient empirical evaluation. The authors fail to provide clear quantitative evidence of improvement over the traditional SLERP method or adequately explain theoretically why vSLERP better leverages the geometric properties of CLIP embeddings.
Theoretical Claims: I have no issues here.
Experimental Designs Or Analyses: - The claim that the double-ellipsoid structure alleviates the False Negative problem in contrastive learning is not convincingly supported by empirical evidence. The authors do not disentangle the independent effects of the ellipsoidal structure itself from the impact of displacement from the origin, leaving the exact reason for any observed improvements unclear.
Supplementary Material: Not provided
Relation To Broader Scientific Literature: - Efforts to understand CLIP embeddings were widely explored before, however, I do not agree that this paper brings new things.
Essential References Not Discussed: "Mind the Gap" (Liang et al., 2022) would be one of the essential references. This paper already provides a comprehensive visual and analytical examination of the modality gap phenomenon in CLIP, making it directly relevant and necessary to cite given the main claims of this study.
Other Strengths And Weaknesses: see the above
Other Comments Or Suggestions: see the above
Questions For Authors: see the above
Code Of Conduct: Affirmed.
Overall Recommendation: 1 | Rebuttal 1:
Rebuttal: - Limited novelty: as other reviewers pointed out, we study well known phenomena using a different lens, i.e. a geometric perspective. As far as we know, we are the first to analyze the raw features prior to the normalization phase. The normalized features are forming a unit hypersphere by definition, overshadowing the complicated double-ellipsoid structure lost in the projection stage. Thus, since no other paper investigate the raw features, we are not familiar with thin shell explanation prior to us (including in "Mind the Gap" where the words "thin" as well as "shell" are absent in the entire paper). Moreover, the work shows novel geometric findings which capture the popularity of concepts, referred by us as “conformity”.
- Conformity essentially yield a scalar per feature correlated with an image/caption measuring its popularity (its average similarity with other concepts drawn at random). Unlike cosine similarity, which yields a similarity measure between two instances (image and/or text) as input, conformity has a single input. We show conformity is almost perfectly aligned with cosine similarity to the mean of the ellipsoid of the respective modality. This finding has two significant consequences: From an applied perspective, it is fast and easy to compute (only one cosine distance computation with a given vector). From a contrastive-learning perspective, we highlight an interesting novel phenomenon: frequent concepts are embedded closer to the modality mean. We also explain the rationale, by reducing the loss of false negatives, which are expected to occur more for frequent concepts.
- Our primary goal is to better understand the existing embedding space of CLIP, therefore we refrained from training or changing it. The natural follow-up study could be to leverage this new knowledge to retrain CLIP in a better fashion in some sense. We share directions for better training with reviewer MmZu. Regarding vSLERP, the main contribution is the preservation of the object appearance, which poses a challenge in real image editing.
- Supp. are provided. According to the ICML policy, it appears following the main paper and includes additional clarifications and visualizations. We kindly encourage the reviewer to examine it.
- "Mind the Gap" (Liang 2022) is indeed a pioneering paper in this field, consequently it is cited 12 times! (on pages 1,2,3,4,7 and 8, in some pages multiple times). We believe we carefully gave it the appropriate credit.
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Rebuttal Comment 1.1:
Comment: Thank you for the rebuttal. However, it does not sufficiently address my initial concerns. In particular, the claim of novelty from analyzing raw features and the Conformity metric remains unconvincing. Additionally, the rebuttal does not adequately respond to my concerns about the limited experimental validation, which still relies on only a small subset of MS-COCO samples. Lastly, the visual evidence solely provided for vSLERP remains insufficient to demonstrate a clear practical advantage over the conventional SLERP method. I currently maintain my original score. | Summary: This paper investigates the geometry of the pre-normalized CLIP embedding space. The main finding is that image and text embeddings reside on linearly separable ellipsoid shells, which are not centered at the origin. This non-origin-centered, double-ellipsoid structure is proposed as a key factor in controlling uncertainty during contrastive learning, where more frequent concepts with higher uncertainty are embedded closer to the modality mean vector, a phenomenon the authors term "semantic blurring."
The paper introduces the concept of "conformity," defined as the expected cosine similarity of an instance to all other instances in a representative dataset. A significant result is the strong correlation (Pearson correlation: ~0.9998 on MS-COCO) between this conformity measure and the cosine similarity of an instance to the modality mean vector. Furthermore, the paper demonstrates that the modality gap observed in CLIP can be explained by the need to align the different conformity distributions of image and text, and that the current non-zero offset of the ellipsoids optimizes this alignment.
The paper claims to contribute the following conceptual ideas and findings: (1) revealing the double-ellipsoid geometry of CLIP embeddings, shifted from the origin; (2) analyzing the benefits of this geometry in controlling sharpness in contrastive learning and mitigating false negatives; (3) showing that frequent concepts benefit most from this geometry; (4) defining concept conformity and demonstrating its strong correlation with similarity to the mean vector; (5) highlighting the role of conformity in explaining the modality gap; and (6) proposing a new interpolation method, vertical SLERP (vSLERP), that leverages the identified geometric properties for improved semantic editing.
Claims And Evidence: * **Image and text reside on linearly separable ellipsoid shells, not centered at the origin:** The paper mentions statistical analysis of the MS-COCO validation set and Figure 1 as a sketch illustrating this geometry. Figures 4 and 5 are also referenced in relation to the thin-shell phenomenon and the non-uniform variance of features (suggesting an ellipsoid rather than a hypersphere). Figure 2 shows linear separability.
* **Offset from the origin helps mitigate false negatives and control sharpness:** This is discussed in Section 4, and Figure 7 illustrates the concept of blur control through sphere offset.
* **Frequent concepts are embedded closer to the mean vector (semantic blurring):** This is hypothesized in Section 4 and linked to the non-origin-centered geometry. The experiments confirm the better alignment of frequent concepts to the mean vector.
* **Strong correlation between conformity and cosine similarity to the mean vector:** The paper explicitly states a Pearson correlation of 0.9998 on MS-COCO in Section 4, supported by Figure 9.
* **Modality gap helps in aligning conformity distributions:** This is argued in Section 6.2 and visually supported by Figure 11, showing the KL-divergence of conformity distributions as a function of the mean offset.
* **vSLERP leverages CLIP's latent space geometry for semantic editing:** Figure 12, Figure 23, and Figure 24 provide visual examples of the vSLERP method in action.
* **Conformity as a measure of expressiveness:** Section 7.1 proposes this, supported by conformity measurements on generated images (Figure 13). Lower conformity means diversity
Need more evidence:
* **The extent to which the embedding geometry "explains" the modality gap and narrow cone effect:** While the paper links these phenomena to the identified geometry, the depth of this explanation and whether it's fully convincing might require more detailed theoretical grounding.
* **The "optimality" claimed for various aspects of CLIP's geometry:** The term "optimal" can be strong. The evidence would need to clearly demonstrate that the observed structure indeed leads to the best possible performance in relevant aspects (e.g., loss, alignment, uniformity, conformity matching) compared to alternative geometries.
Methods And Evaluation Criteria: Methods:
The paper is theoretical analysis for the CLIP geometry. The major proposed method is Conformity and Estimated Conformity.
Conformity defines a quantitative measure for how common or unique an embedding is.
Estimated Conformity is based on cosine similarity to the mean vector proposed a computationally efficient surrogate for conformity. It makes practical sense for large datasets and real-world applications. The strong correlation demonstrated with the actual conformity measure supports its validity.
Evaluation:
- Using a standard and widely used image-text dataset like MS-COCO for statistical analysis of CLIP embeddings is appropriate for understanding general properties.
- Using KL-divergence to quantify the difference between the conformity distributions of image and text modalities is a standard and meaningful metric for comparing probability distributions. This makes sense in the context of analyzing the modality gap.
- The visual examples provided for vSLERP (Figure 12, 23, 24) are impressive to demonstrate its potential for preserving object identity during interpolation, which is a key challenge in semantic editing.
- Using the introduced "conformity" metric to assess the diversity of generated images and diversity of the generated captions makes more sense
Theoretical Claims: The mathematical definitions are sound. theoretical claims were derived on the basis of analysis and observation. Thus no proofs to check.
Experimental Designs Or Analyses: Sound:
- Analyzing Feature Statistics (Figure 2, 4, 5, 15, 16, 17, 18): check
- Linear Separability Analysis (Figure 2, 15, 17): check
- Thin Shell Phenomenon Analysis (Figure 4, 16, 18): check
- Conformity Analysis (Figure 9, 10): check
- Conformity as a Measure of Expressiveness (Figure 13): check
- Vertical SLERP (vSLERP) Demonstration (Figure 12, 23, 24): check
Minor Questionable:
- Though I believe there may not be much difference in conclusion, I am still wondering how MS-COCO training data differs.
- Will different image/text backbone matter? Or only the contrastive training nature matters?
Supplementary Material: N/A, appendix looks convincing with more results.
Relation To Broader Scientific Literature: - The modality gap, where embeddings from different modalities (image and text) are separated, and the narrow cone effect, where features occupy a limited angular space, have been identified and studied in CLIP in previous works. The paper offers a geometric explanation for these phenomena based on the identified non-origin-centered ellipsoid shells for each modality.
- The introduction of "conformity" as a measure of expressiveness and diversity in generative models (like unCLIP and Glide) is a novel contribution. This helps to evaluate the diversity of generated content which is crucial for generative models.
- The issue of false negatives (semantically similar pairs treated as negatives) is a recognized challenge in contrastive learning. The paper suggests that the non-origin-centered ellipsoid geometry inherently helps in handling false negatives by allowing for "semantic blurring", where uncertain instances are embedded closer to the mean. This offers a different perspective – that the embedding structure itself plays a role in managing this issue, rather than solely relying on training procedures or loss modifications.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: Originality:
- Modality gap is already discovered, but this paper added a geometric explanation
- The introduction of "conformity" as a measure of how common or unique an embedding is within a dataset is an original concept.
- Proposed applications: 1. measure of diversity 2. vSLERP are very impressive to make CLIP a better tool for wider community.
Other Comments Or Suggestions: N/A
Questions For Authors: Open questions:
- How can the analysis in this paper help with
1. a more efficient CLIP training?
2. a higher quality CLIP training?
- Can we potentially offset the ellipsoid to mitigate the modality gap to make the similarity between different modalitiy-pairs comparable?
e.g.
Image(Dog A), Image(Dog B) has cosine distance a
Image(Dog A), Text(Dog B) has cosine distance b
Due to the modality gap, cosine distance a !=b. and it is meaningless to compare a and b due to different modality. What if I want to make them comparable?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for your positive feedback, intriguing comments and thought-provoking questions.
- The geometry explains the modality gap and the narrow cone effect:
We agree that the geometry does not fully explain the reasons to all observed phenomena. We have a strong evidence that the offset of the ellipsoids is alleviating the impact of false negatives. There have been several proposed efforts in the literature to mitigate the false negatives in contrastive learning. However, to the best of our knowledge, we are the first to make the link between false negatives and the geometry CLIP converged to. Part of our message is that the geometry analysis should be performed in the native raw embedding, not on the unit sphere, which reduces information. Hence, “modality gap” is actually “linearly separable ellipsoids” and “narrow cone effect” is better understood as “non-origin-centered”. We believe our findings can facilitate future research on contrastive learning and are thus of interest to the community.
- Optimality: All of the references to “optimality” are related to the losses mentioned in Figs 6 and 11. By “optimal” we mean that the value of alpha is attained at the loss minimum. We agree that it holds only under restricted cases, as explained in the paper, where not all possible combinations of geometry are examined (hence we cannot claim global optimality, with respect to the tested variables). This should indeed be clarified and toned down, as we intend to do in the final version.
- Backbone/training procedure: we validate our findings on ViT-L as well (on top of ViT-B in the main paper), thus we feel confident that architecture size (number of layers/heads or even feature size) is probably not playing a significant role in forming the latent geometry. Further examinations on additional architectures or larger datasets are important, we plan this for future study. Since CLIP is a fundamental backbone of many vision and text algorithms today, we believe knowledge on its geometry is nevertheless of high significance.
Questions:
Leveraging geometric knowledge to enhance CLIP training efficiency and/or quality: possible direction could be to force geometric constraints during training, possibly by centralizing both ellipsoids as you suggested. In Fig. 22 (Supp.) we show the loss values when both ellipsoids are shifted to the origin (alpha=1). As can be seen, although correctly classified instances yield lower loss, the combination with the misclassified increase the loss. The reason is implicitly shown in Fig. 7. The average cosine similarity for non-centered ellipsoid is approx. 0.2 (highly likely that misclassified samples will lay there), whereas for centered ellipsoid it is around zero. This affects both the classified and misclassified, increasing the loss for the latter. Alternatively, one may propose an alignment which does not necessarily shift both cases to the origin. By doing so we can decouple the modality gap from the narrow cone effect, hopefully mitigating at least one of them. We are eager to further study this direction from a geometric perspective. We hope our clarifications answer your concerns and if so we would be delighted if the final paper rank can be upgraded.
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Rebuttal Comment 1.1:
Comment: Thanks for the clear rebuttal, I found the work is very useful for the multimodal representation learning.
Another potential direction can be beyond unimodal, towards modality combinations, like Image(black dress) + Text(red) -> Image(red dress). changing the rating to accept | null | null | null | null | null | null | null | null |
Model Steering: Learning with a Reference Model Improves Generalization Bounds and Scaling Laws | Accept (spotlight poster) | Summary: This paper theoretically studies the mechanism behind a learning paradigm, called Learning with a Reference Model (LEAR) and proposes a new learning algorithm that achieves better scaling than the naive approach. They first relate the RHO loss with DRO and show how using the RHO loss can improve the generalizability of DRO. They then show that when a certain divergence function is used, RHO+DRO is equivalent to weighting samples with RHO loss, which theoretically explains why LEAR is useful. To optimize RHO+DRO, they adopt the SogCLR algorithm. They show that their approach has better sample efficiency than the naive method and the distillation methods.
Claims And Evidence: 1. The author claims that RHO can achieve a smaller variance, and verify it empirically.
2. The author claims that RHO+DRO can achieve a better sample complexity/scaling law. It is also verified.
Methods And Evaluation Criteria: They evaluate the algorithm by training CLIP models and evaluate ImageNet, which seems reasonable. However, a caveat is that they only experiment with this single task.
Theoretical Claims: They don't seem to be incorrect.
A caveat is that there are too many constants and it's hard to understand their meaning. As a result, I am not sure whether Corollary 4.3 is correct or non-trivial.
Experimental Designs Or Analyses: No crucial problems found.
Supplementary Material: I checked Proof of Corollary 4.3. , not sure how $C_2$ on the right hand side at line 733 is derived.
Relation To Broader Scientific Literature: Based on the paper, this work is related to DRO papers and provides the theoretical foundation of [1]
[1] Data curation via joint example selection further accelerates multimodal learning
Essential References Not Discussed: Not aware of
Other Strengths And Weaknesses: Strength
- The authors show that their approach indeed has great sample efficiency compared with the naive and the distillation approaches.
Weakness
- Based on what I understood, the proposed method optimizes the same objective as (Evans et al., 2024a;b). Comparing with their approach seems important.
- Though in the introduction, the authors motivate this paper by the lack of theoretical understanding of LEAR, this paper doesn't seem to be able to explain ALL LEAR methods. It should be more specific about *which* LEAR method(s) this paper is for.
- The flow of this paper could be improved. See suggestions.
- Please also see questions.
In sum, while I acknowledge this paper has its technical merits, I suppose this paper was written in a rush. Thus, while technically I suggest this paper is probably acceptable, I also suggest that another round of revision will make it better and more up to the level of ICML.
Please let me know if I misunderstood anything.
Other Comments Or Suggestions: If I understood correctly, this paper has two goals, one is to provide the theoretical foundation of LEAR, which, in this paper, seem to be specific to (Evans et al., 2024a;b). The other one is to propose a better algorithm for LEAR. While I don't see apparent problems for the second goal, the one seems to be done very implicitly.
I would suggest that the authors provide some background about the specific LEAR methods this paper can provide insights into. This would make the purpose of Section 4 clearer.
Beside, while it's the convention to call scaling law scaling law, the word "law" is actually misleading, as it is not a real law. If possible, I would suggest that you just say you scale better.
Questions For Authors: 1. One thing I didn't understand is what the x-axis of figure 1 (Samples Seen (million)) means. Does it represent the training time? If not, why did you use different line to represent different ratio of data used? And why is the trend of Figure 2 different from Figure 3? It is confusing because these two figures have the same x and y axes.
2. Would this method works for other tasks? Is there a reason to focus only on CLIP?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank the reviewer for appreciating the technical merits of this paper. We will follow the reviewer's suggestions to improve the paper, which should be an easy task.
> **Q1**: Would this method work for other tasks? Is there a reason to focus only on CLIP?
**A**: Yes! We have discussed that the existing works of employing the RHO loss for data selection or sampling for different tasks can be considered as heuristic implementation of the proposed framework (Section 4). These different tasks include classification (Mindermann et al., 2022) and training LLMs (Lin et al. 2024). We have discussed the reason for our focus on CLIP at the beginning of Section 5.
> **Q2**: How $C_2$ on the right hand side at line 733 is derived in the proof of Corollary 4.3.
**A**: The constant $C_2$ in Corollary 4.3 is the same as that in Theorem 4.1. In Theorem 4.1, we derived $$R(\tilde{\theta}_*)\leq \underbrace{\inf _{\theta\in \Theta} \left(R(\theta) + \sqrt{\frac{2\rho}{n} \mathrm{Var}(\ell(\theta, \cdot)- \ell(\theta _{\mathrm{ref}}, \cdot))}\right)} _{\mathrm{term1}}+ \frac{C _{2}}{n},$$ where $C _2=(50\rho/3+4)M$. In the proof of Corollary 4.3, we showed that term1 in the brace is upper bounded by $R(\theta _\mathrm{ref})$. Hence, $C_2$ is the same as in Theorem 4.1.
> **Q3**: Does the proposed method optimize the same objective as (Evans et al., 2024a;b)? Comparing with their approach seems important.
**A**: We would like to point out that we indeed compared with Evans et al., 2024a (JEST). We omitted the comparison with Evans et al., 2024b (ActiveCLIP) since JEST is a later work and improved over it by the same groups of authors. Our method does not optimize the same objective as their methods:
- their methods use mini-batch contrastive loss to define a RHO loss. While we define the loss using all negative data in the training dataset (instead of the mini-batch) and use a rigorous optimization approach (SogCLR) to optimize the objective.
- their loss is used for data selection of anchor data, i.e., selecting subset for training. In contrast, our DRRho contrastive loss, defined by leveraging the relationship between global contrastive loss and DRO, has an effect of data re-weighting of the negative data for each anchor data.
Moreover, their methods consume more resources for data selection due to sampling from a larger batch. We compared the performance of JEST and DRRho-CLIP on DFN-12M and DFN-192M with fixed amount of compute. The results (c.f. Tables 1 and 3 in the paper) showed that DRRho-CLIP significantly outperforms JEST.
> **Q4**: This paper doesn't seem to be able to explain all LEAR methods. It should be more specific about which LEAR method(s) this paper is for.
**A**: LEAR refers to, as stated at the beginning of the abstract, *leveraging a pretrained model ... through strategic data selection or weighting*. Thus we focus on methods for data selection and weighting. We categorize existing works of leveraging a pretrained model into different families in Section 2, where in Lines 120-140 we provide background about the specific LEAR methods that motivates this work, such as RHO (Mindermann et al., 2022), RHO-1 (Lin et al., 2024), ActiveCLIP (Evans et al., 2024b) and JEST (Evans et al., 2024a) to make Section 4 clearer.
> **Q5**: I would suggest that the authors provide some background about the specific LEAR methods this paper can provide insights into. This would make the purpose of Section 4 clearer.
**A**: Thank you for the suggestion. We will give more background about the related LEAR methods mentioned in the above question to make Section 4 clearer.
> **Q6**: While it's the convention to call scaling law scaling law, the word "law" is actually misleading, as it is not a real law. If possible, I would suggest that you just say you scale better.
**A**: While we agree with the reviewer that the term "law" is misleading or sometimes overclaims, however, we hesitate to invent a new term as it has been widely accepted in the literature. Cherti et al. (2023) also used the term "scaling law" for CLIP training.
> **Q7**: Does the x-axis of Figure 2 represent the training time? If not, why did you use different line to represent different ratio of data used?
**A**: The x-axis in Figure 2 represents the number of samples seen, which is proportional to training time. Different ratio of data means the training dataset size is different. For example, 100% data means the whole dataset is used during training, while 50% data means only half of the dataset is used during training. For different datasets, we set the total number of samples seen to be the same, which means on smaller datasets there will be more epochs.
> **Q8**: Why is the trend of Figure 2 different from Figure 3?
**A**: In Figure 2, we use ImageNet-1K Top 1 Accuracy as the y-axis. While in Figure 3, we use ImageNet-1K Error as the y-axis, which is equal to 100% - ImageNet-1K Top 1 Accuracy. Thus the two figures have different trends.
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Rebuttal Comment 1.1:
Comment: Thanks for the clarification. I wish I have time to check the proof again. Before I have time to check the proof and really find a problem (if exists), I think I have no major reasons to reject this paper, so I will increase my score for now.
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Reply to Comment 1.1.1:
Comment: We thank the reviewer for their valuable suggestions and for raising the score after rebuttal. | Summary: The paper establishes a theoretical framework for RHO-based learning with a reference model using DRO as the perspective and introduces a novel DRRho risk. It further applies DRRho-based LEAR to CLIP, achieving good and data-efficient performance.
## update after rebuttal
My overall evaluation remains unchanged.
Claims And Evidence: The authors make several key claims:
- The DRRho framework improves generalization via variance reduction.
- DRRho-CLIP outperforms heuristic methods.
- DRRho-CLIP is more data-efficient than vanilla ERM.
Overall, the claims in the paper are well supported.
Methods And Evaluation Criteria: The DRO-based DRRho risk and its application to CLIP are well-motivated.
Theoretical Claims: I didn’t check the detailed proofs in the Appendix.
Experimental Designs Or Analyses: The experiments are well-designed and carefully analyzed to support their theoretical claims and the efficiency of their method.
Supplementary Material: I didn’t review the supplementary material.
Relation To Broader Scientific Literature: The paper builds on DRO (Duchi & Namkoong, 2016), contrastive learning (Qiu et al., 2023), and LEAR (Mindermann et al., 2022).
Essential References Not Discussed: I didn't notice any missing key references.
Other Strengths And Weaknesses: **Strengths**:
- The paper is well-written and easy to follow.
- The theoretical justification of RHO-based LEAR using DRO is creative and reasonable.
- The analysis is comprehensive, supported by sufficient theoretical and experimental evidence.
**Weaknesses**:
The paper offers a potential theoretical explanation via generalization bounds for why LEAR is more data-efficient than ERM, and it is expected that a better reference model should lead to greater improvements in target model training (as shown in Corollaries 4.2 and 4.3). However, we can observe in Table 1 that a more powerful reference model does not always yield superior target model performance.
It would be beneficial if the authors could clarify and explain this discrepancy.
Other Comments Or Suggestions: No other comments.
Questions For Authors: I have a question regarding the interpretation of Corollary 4.3. The paper claims that "DRRho needs only $n = O( \sqrt{ m })$ samples, which dramatically reduces the sample complexity $O(m)$ of ERM without a reference model." However, when viewed through the lens of Theorem 4.1 or Corollary 4.2, it seems that the sample complexity would still be $O(m)$. Could the authors clarify this apparent contradiction in the sample complexity analysis?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We thank the reviewer for their valuable comments and suggestions.
> **Q1**: More powerful reference model does not always yield superior target model performance. But Corollaries 4.2 and 4.3 show that a better reference model should lead to greater improvements in target model training.
**A**: There is misunderstanding of results in Corollaries 4.2 and 4.3 regarding that more powerful reference model yields superior target model performance. Corollary 4.2 shows that the generalization depends on the variance of the RHO loss for a reference model. However, a powerful reference model does not necessarily have a small variance of the RHO loss, i.e., $\mathrm{Var}(\ell(\theta_*, \cdot) - \ell(\theta_\mathrm{ref}, \cdot))$, where $\theta_*$ is the optimal solution in the considered model space. Corollary 4.3 only compares a reference model in **the same space** of the target model. However, in Table 1 except for ViT-B/16, other two reference models (ViT-B/32, ViT-L/14) are not in the same model space of the target model ViT-B/32. Hence, we cannot apply Corollary 4.3.
We would like to point out that this phenomenon is also empirically observed in other works that leverage a reference model, e.g. DFN (Fang et al., 2024), JEST (Evans et al. 2024a) and MobileCLIP (Vasu et al., 2024), where stronger reference models did not necessarily lead to more powerful target models.
To better verify Corollary 4.3, we have conducted the following experiments with ViT-B/16 as target model and ViT-B/16 trained on different subsets of DFN-12M as reference models. We list the ImageNet-1K Top 1 Accuracy of both the target model and the reference model in the following table, from which we can observe that the performance of the target model and the reference model is positively correlated.
| Target Model (Data, Samples Seen) | Reference Model | Target Model Performance | Reference Model Performance |
| -- | -- | -- | -- |
| ViT-B/16 (DFN-12M, 320M) | ViT-B/16 (DFN-6M, 320M) | 42.50 | 30.19 |
| ViT-B/16 (DFN-12M, 320M) | ViT-B/16 (DFN-9M, 320M) | 46.80 | 39.09 |
| ViT-B/16 (DFN-12M, 320M) | ViT-B/16 (DFN-12M, 320M) | 48.88 | 43.49 |
> **Q2**: Regarding interpretation of Corollary 4.3 and do Theorem 4.1 or Corollary 4.2 still indicate $n=O(m)$ sample complexity?
**A**: The interpretation of Corollary 4.3 about the reduced sample complexity is to guarantee that the generalization error of the learned model $R(\tilde\theta_*) - R(\theta_*)$ by our framework is on par with that of the reference model $R(\theta_{\text{ref}}) - R(\theta_*)$, where $m$ is the data size for training the reference model. If we want to use Corollary 4.2 for deriving $R(\tilde\theta_*) - R(\theta_*)$ in the same order $1/\sqrt{m}$ of $R(\theta_{\text{ref}}) - R(\theta_*)$ , it will imply that $n = \max(\sqrt{m}, m\mathrm{Var}(\ell(\theta_*, \cdot) - \ell(\theta_\mathrm{ref}, \cdot)))$. It could be still much better than $O(m)$ as $\mathrm{Var}(\ell(\theta_*, \cdot) - \ell(\theta_\mathrm{ref}, \cdot))$ could be very small. In this context, we cannot ignore $\mathrm{Var}(\ell(\theta_*, \cdot) - \ell(\theta_\mathrm{ref}, \cdot))$. Hence, it is more convenient to use Corollary 4.3 to make this comparison argument. Thus the two results do not contradict to each other. | Summary: The paper proposed DRRho risk minimization with a reference model and provided a theoretical analysis of it. It also applied this approach to training the CLIP model. Experiments show that the proposed method achieves better performance than the baselines.
Claims And Evidence: The claims made in the submission are supported by clear and convincing evidence.
Methods And Evaluation Criteria: The datasets and benchmarks are appropriate and relevant to the problem. However, since I am not an expert on this topic, I’ll leave it to other reviewers to judge whether the baselines are comprehensive and the comparisons are sufficient.
Theoretical Claims: I didn’t go through all the proofs in detail, but the theoretical results seem convincing to me.
Experimental Designs Or Analyses: The experimental design is valid and demonstrates the effectiveness of the proposed method.
Supplementary Material: I skimmed through the supplementary material but did not verify all the mathematical details.
Relation To Broader Scientific Literature: The paper is related to the literature on distributionally robust optimization. Although the technique itself is well-established, combining it with a reference model and providing a theoretical analysis appears to be a novel contribution. Furthermore, applying it to training CLIP, a relatively large-scale problem with practical significance, seems like a solid contribution.
Essential References Not Discussed: I didn’t notice any.
Other Strengths And Weaknesses: Overall, I find the contribution solid, with both theoretical insights and experiments showing improvement over the baseline. However, I am not entirely sure about the comprehensiveness of the evaluation and comparison, so I would like to hear other reviewers’ opinions.
Other Comments Or Suggestions: I don’t have other comments.
Questions For Authors: I don’t have other questions.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We thank the reviewer for their constructive and positive evaluation of our work. We are happy to address any concerns the reviewer may have in later stage. | Summary: Authors present a framework for using available open weights model to improve model training on given dataset (learning with a reference model - LEAR). The framework is based on distributionally robust optimization (DRO). DRO makes use of available data empirical distribution to create perturbed data distributions and use those for worst case risk minimization. Author further employ RHO loss, a generic loss aiming on identifying data points worth learning, to obtain a risk function via applying DRO (DRRHO risk) They derive theoretical generalization bounds using the risk, aiming to explain how DRRHO improves generalization. They study their method on example of CLIP training, using pre-trained CLIP models as reference. Obtained DRRho CLIP (using various reference models) is compared to various baselines, stating its advantages in downstream task performance and data efficiency.
Claims And Evidence: To test their claims of enhancing generalization via training with reference model, authors perform CLIP training guided by various reference models on various scales and measure model performance via various well-established benchmarks. I think authors' approach is valid and evidence they gather is sufficient to argue for their procedure being useful. Scaling law derivation claim seems overblown. Authors present for single fixed model scale (ViT B/16) measurements across 4 different samples seen scales, through which they fit a power law. This is not what is known as full scaling law. Eg cited work by Cherti et al performs measurements on combinations of 5 different model scales, 3 different samples seen scales (3B, 12B and 34B) and 3 different data scales (80M, 400M and 2B), each of which is tuned to construct a Pareto front corresponding to minimum error on downstream tasks. This full scaling law derivation is not what authors perform and thus only limited (if any) conclusions can be drawn from the Fig 3.
Methods And Evaluation Criteria: Authors derived theoretical generalization bounds which they use to backup various heuristics for data filtering / selection that lead to training of models with stronger generalization. They enhance standard contrastive loss of CLIP with DRO loss component that includes reference model, conducting training of DRRHO-CLIP. Datasets used are well established CC12M and DFN subsets (DFN-9M and DFN-128M). Evaluation used well established CLIP benchmarks, eg those used in DataComp, which are used to compare DRRHO-CLIP with other strong reference baselines. Methods and evaluation make sense.
Theoretical Claims: Theoretical generalization bounds obtained by authors seem correct, as well as introduction of the DRO loss into CLIP training.
Experimental Designs Or Analyses: Experimental design of CLIP training with reference model seems sound. The derivation of scaling law is not executed properly, or stated differently, there is no scaling law presented in the study although the title strongly suggests so.
Supplementary Material: I had a look in source code authors present, had unfortunately not enough time to test its function.
Relation To Broader Scientific Literature: The work fits well into landscape of language-vision learning research and distillation methods.
Essential References Not Discussed: Authors cite relevant works properly.
Other Strengths And Weaknesses: Strength of the paper is in establishing theoretical grounds for learning with reference model and testing the approach on important scenario of CLIP training, which often uses distillation as technique to boost model performance. Weakness is the missing scaling law that is announced in the paper title. Authors do not derive proper full scaling law, picking only one fixed model scale (ViT B/16). Based on this plot, authors attempt to make a conclusion how DRRHO CLIP compares to openCLIP, which does not work, as for such comparison full scaling law would have been necessary. Authors can only conclude that for ViT B/16 and rather small span of samples seen scales, DRRHO CLIP has advantage over openCLIP without reference model. It is not clear what happens across scales and on larger scales , eg L/14 , H/14, from this examination (full scaling law would allow prediction for those larger scales). Moreover, the compute necessary for using reference model (which has also to compute loss on the training data during training) is not incorporated into considerations for model comparison. In general thus, using total compute on x-axis for learning procedure comparison via scaling law derivation should have been the correct approach here if aiming for strong conclusions about advantage of the learning procedure over other baselines.
Other Comments Or Suggestions: Text is well written and is easy to follow.
UPDATE: raising score to 3 after scaling law extension experiments by the authors.
Questions For Authors: Scaling law derivation on smaller scales used in the work should have been possible, as those experiments are not expensive. Why was the derivation of full scaling laws (eg following Cherti et all 2023) was ommitted in the work? It would be also good to plot FLOPs vs performance, accounting for FLOPs used by reference model - can authors provide such a plot?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank the reviewer for the suggestion on experiments. We believe that the comments raised by the reviewer are not critical drawbacks of this paper. We request the reviewer to consider our contribution in terms of theoretical framework and analysis, and our experiments comparison with multiple baselines.
> **Q1**: Why was the derivation of full scaling laws (e.g. following Cherti et al. 2023) was omitted in the work?
**A**: Thank you for raising this concern. We would like to note that Cherti et al. (2023) focused on reproducing CLIP, which is empirical only. In contrast, we have rigorous theoretical analysis of the generalization error, which is not restricted to any model or data scale. Our experiments include the comparison with multiple baselines in the context of learning with reference models and our scaling law experiment serve to corroborate the presented theory.
Following the reviewer's suggestion, we have added scaling law experiments for two more model scales (ViT-B/32 and ViT-L/14). The experiments have not completely finished since they take many days to run on large scales, but we can already observe that DRRho-CLIP has a better scaling trend across different model scales than OpenCLIP.
- FLOPs vs. performance, without accounting for reference model cost: [anonymous link](https://github.com/icml2025drrhoclip/icml2025drrhoclip/blob/main/scaling_law_flops.pdf). The fitted scaling law for OpenCLIP is $E=5.77\cdot C^{-0.116}$, where $E$ is the ImageNet-1K Error and $C$ is the compute (GFLOPS). The fitted scaling law for DRRho-CLIP is $E=7.15\cdot C^{-0.127}$.
- FLOPs vs. performance, accounting for reference model cost: [anonymous link](https://github.com/icml2025drrhoclip/icml2025drrhoclip/blob/main/scaling_law_flops_reference.pdf). The fitted scaling law for OpenCLIP is $E=5.77\cdot C^{-0.116}$, while for DRRho-CLIP it is $E=8.78\cdot C^{-0.135}$.
> **Q2**: It would be also good to plot FLOPs vs. performance, accounting for FLOPs used by reference model.
**A**: Links to the plots are provided in the answer to the above question. We want to highlight that the cost of leveraging a reference model can be amortized. In particular, since the reference model is frozen during training, we store the reference model features before training so that they can be reused multiple times across epochs and across different runs. Indeed, these features of the reference model have been already computed in the data filtering stage for creating existing datasets, e.g., LAION-2B (Schuhmann et al., 2022), DFN-2B (Fang et al., 2024) and Datacomp-1B (Gadre et al., 2023). In this case, we can directly leverage the features of the reference model without spending any resources computing them.
---
Rebuttal Comment 1.1:
Comment: I am delighted to see further extension on scaling law study, and will update my score to 3.
---
Reply to Comment 1.1.1:
Comment: We thank the reviewer for their constructive feedback that helps improve our manuscript. | null | null | null | null | null | null |
Edge-Colored Clustering in Hypergraphs: Beyond Minimizing Unsatisfied Edges | Accept (poster) | Summary: The submission provides a range of algorithmic and complexity-theoretic contributions to the Edge-Colored Clustering problem, which has been shown to have several applications in the general area of ML.
Claims And Evidence: Yes, all claims are supported by evidence (primarily proofs), although most of this is deferred to the appendix.
Methods And Evaluation Criteria: The primary methods used are theoretical proofs, with some supporting implementations.
Theoretical Claims: I did not check the details of all proofs, but those I did see seemed reasonably well-written and problem-free.
Experimental Designs Or Analyses: The experiments only have a minor, supporting role and seemed problem-free.
Supplementary Material: I did not check the correctness of proofs in the supplementary material.
Relation To Broader Scientific Literature: The key contributions are related to broader scientific literature.
Essential References Not Discussed: N/A.
Other Strengths And Weaknesses: While the problem studied in this submission is graph-theoretical in nature, it is well-motivated and has a sufficient footprint in the machine learning community - in fact, there are several algorithmic-theory papers on the topic that appeared in recent ICML and NeurIPS conferences. In terms of technical contribution, the submission is very strong and exceeds what I would expect from an average theoretical ICML paper.
For MaxECC, the results include the first "general" approximation algorithm that is a constant-factor approximation for each hyperedge size, but also an improved polynomial-time approximation algorithm for the prominent and previously studied graph variant (i.e., the case of hyperedge size 2). I believe the latter provides great "added value" to the paper: on its own this result might not be of sufficient interest to the ML community (or even the TCS community for that matter), but it rounds up the paper's contributions for MaxECC very nicely.
In the second part of the submission, the authors turn to MinECC. While approximation algorithms for that problem were known, the authors introduce two fair/balanced variants of that problem and provide a range of algorithmic results for these (including not only novel approximation algorithms, but also parameterized algorithms and complexity-theoretic lower bounds).
In the third part of the submission, the authors support their theoretical investigation with a range of experiments. As the authors correctly state, these are only meant to have a "supporting role" and should not be seen as the main results; still, I believe they form a nice touch that complements the rest of the submission.
As can be seen from the text above, overall I view the submission's contributions very positively and would be happy to support acceptance. However, there are also some weaknesses that need to be mentioned:
1) While the motivation for MaxECC is clear, the motivation for the two new variants of MinECC is weaker - there are no references for this or similar formulations of the problem, and the variants are essentially "made up".
2) The submission attempts to convey too many results, which unfortunately spreads the story too thin and makes the writeup rather unfocused. To be clear: I personally do not think that the inclusion of more results should be seen as a drawback on its own, but the writeup needs to be very careful to still present a coherent picture that is accessible to a reasonable fraction of the ICML community. As it stands, the paper is so dense that the introduction cannot even cover all of the individual results proved or even the individual problem variants studied. This is nicely illustrated, e.g., in the following sentence near the end of the introduction:
"Our results also include several parameterized complexity and hardness results for COLOR-FAIR MINECC and a related maximization variant where the goal is to maximize the minimum number of edges of any one color that are satisfied."
Note that the majority of the readers may not be aware of parameterized complexity theory, and so in its current state the submission might be fairly inaccessible to them (in fact, it does not even introduce parameterized complexity in the preliminaries). Later in the paper, the writeup even mentions significantly more advanced notions such as (slim) treecut-width or cutwidth... I understand that it makes no sense to define these just to have them briefly mentioned, but there should at least be a reference to point interested readers to some literature.
Overall, I have a very high opinion of the paper's results and technical contributions, but given these weaknesses I personally see this more as a solid "accept" than a "strong accept".
## Update after rebuttal
Thank you for the responses; I maintain my score.
Other Comments Or Suggestions: N/A.
Questions For Authors: You introduce two novel MinECC variants that take into account fairness/balance aspects (Lp-Norm MinECC and Protected-Color MinECC) and provide some nice results for both of these. But on a higher level, I wonder why it makes sense to have the fairness part focus on MinECC even though the first part (which is better linked to previous work) focuses exclusively on MaxECC. Maybe the authors could comment on this discrepancy - is it because there's no nice "natural" formulation of fair MaxECC, or is it because getting results for such a formulation are more elusive?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thanks for the helpful feedback on our manuscript. With regards to the motivation please see our response to the reviewer Tzam for details on our motivation for these variants.
Furthermore, we agree that some sections are quite dense on results and sparse on details. We wished to provide more details and a less terse write-up (in particular, a more comprehensive introduction), but due to the page limit we ended up having to push many results to the appendix. We decided it is better to include all results, since there are readers who care about them (e.g., the parameterized complexity results). If the paper is accepted, we plan to use the extra 1 page of space to address these exact concerns you are raising (which we agree with). In particular, an extra page of space will allow us to provide a fuller introduction and overview of our results, provide needed background on parameterized complexity for a broad audience, and fill in some other details that are dense in the current manuscript.
Finally to answer the question you posed, this is answered for Lp-norm ECC by our hardness result for the special case of Color-Fair MaxECC (see Section 3.2). One could argue that Color-Fair MaxECC is in fact more natural than Color-Fair MinECC in some settings (to answer part of your question). However, Theorem 3.3 implies that it is NP-hard to approximate this objective to within any factor even in graphs (in fact, just paths). Hence, as you wondered, “results for such a formulation are more elusive”. Regarding Protected Color ECC, we agree that a maximization variant could also be interesting and our hardness results do not rule out approximations for bounded hyperedge sizes. This is an interesting direction for future work, but as of yet we have not established any results. | Summary: The authors study the edge-colored clustering (ECC) problem in hypergraphs. They generalize MaxECC from graphs to hypergraphs, and present an approximation algorithm of factor $(2/e)^r (r+1)^{-1}$, where $r$ is the maximum number of nodes that are allowed in a single hyperedge. A slight modification of this algorithm provides a factor of 154/404 for graph MaxECC. They also study three variants of ECC, that are, $\ell_p$-norm ECC, color-fair ECC and protected-color ECC, and give a series of algorithmic and hardness results on them. Experimental results demonstrate that their algorithms have much better results in practice than the theoretical worst-case guarantees.
Claims And Evidence: Yes, I think so.
Methods And Evaluation Criteria: Yes, except the benchmark datasets for which there is not too much information provided in the paper, e.g., what the nodes and hyperedges represent, what the colors mean, etc.
Theoretical Claims: I have only checked the proof of Theorem 2.1 for the basic algorithm, and had a quick review for the variants. Every algorithmic result is starting from some kind of LP description of the relative problem, while LP-rounding and randomization are main techniques in analysis. All conclusions are easy to understand.
Experimental Designs Or Analyses: No baseline method is introduced in the experiments. But I’m not sure whether there is.
Supplementary Material: The authors didn’t submit any supplementary material, but provided in Appendix E the online address where the anonymized code was uploaded. I didn’t review the code, and I don't feel there is much difficulty in implementation of the algorithms.
Relation To Broader Scientific Literature: This research fits well in the study line of ECC on (hyper)graphs. It has the first approximation algorithmic result of MaxECC for the hypergraph case and improves that (even slightly) for graph case. It also complements some algorithmic and hardness results on three variants of MinECC for hypergraphs.
Essential References Not Discussed: Yes, several key related works have been cited properly in this paper.
Other Strengths And Weaknesses: S1. The theoretical analyses are solid, and the conclusions are rich.
W1. I am not sure how many new technical contributions are developed, especially compared with (Veldt 2023). LP seems to be the common starting point for ECC algorithms in each prior work. Randomized rounding and global color ordering techniques have also been used. I understand that the two problems MaxECC and MinECC are different from the perspective of approximation algorithm, but I am not clear what the essential difference is when the same techniques are used for both of them.
W2. I am not clear for the motivation and practical significance of the variant problems, or they are just in a mathematical sense.
Other Comments Or Suggestions: 1. It’s better to introduce more about the benchmark hypergraphs from the references (Veldt, 2023; Amburg et al., 2020), especially when they are used for the variants of the ECC, as such datasets are not very common after all. The information in Table 2 is insufficient.
2. Line 411, Column 1, “Table 4” should be “Table 1”.
Questions For Authors: 1. Can you give a comparison with the techniques that are used in (Veldt, 2023)? See W1 for more details on this question.
2. Is there any practical example to demonstrate the significance of the variant problems of ECC?
3. Can you explain more about the benchmark datasets and your manipulation on them for your experiments?
Ethical Review Concerns: No ethical review concern.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thanks for your detailed review and feedback on our manuscript.
Regarding the “significance of the variant problems for ECC”, please see our response to reviewer Tzam, where we provide more details on motivation we could have been clearer about in our submission.
Thanks for your question about comparing our techniques to those of Veldt 2023. There are indeed strong high-level similarities (LP relaxation + global color ordering + randomized rounding), but the difference between MaxECC and MinECC is significant enough that the algorithm of Veldt 2023 can be shown to completely fail for MaxECC. Furthermore, the way to make an algorithm work for MaxECC requires quite a bit of new technical machinery, and as a result the overall techniques and proof for our algorithm substantially differ from the technical contribution Veldt 2023.
To explain this in more depth, note the following important differences between the randomized LP rounding MinECC algorithm of Veldt 2023 and our randomized LP rounding algorithm for MaxECC:
(1) We have a threshold (determining how colors want nodes) for each color, while Veldt 2023’s algorithm uses a single threshold that applies to all colors at once.
(2) Especially for the graph case, we have to distinguish between whether a color is “strong” or “weak” for a node
(3) We draw each color threshold uniformly from [0,1]. Veldt 2023 draws the threshold within a bounded subset in the interval [0,1]: either [⅓, ½] or [1/4 , 1/2] or [⅛, ½] depending on the relationships between k and r. Note that these intervals appear at face value to be different from what is written in Veldt 2023, but that is only because Veldt was considering flipped LP variables (essentially, for our LP variables $x_{u}^c$ Veldt was working with $1-x_{u}^c$ )
Focusing on difference (3), choosing a threshold that is bounded away from 0 means that Veldt could essentially ignore hyperedges where the $z_e$ variable is very small, even if $z_e > 0$. For the MinECC formulation, this means there is a variable $x_e = 1- z_e$ that is close to 1, and note that the LP relaxation for MinECC has objective min
$\sum_{e} x_e$. When $x_e$ is large, then we can just delete (leave unsatisfied) that edge with probability 1, and the “mistake” (for the MinECC objective) is paid for in terms of the (large) value of $x_e$ in the LP. Thus, Veldt 2023 can focus on edges e where $z_e$ is not too small (i.e., $x_e$ is not too large). This is essential for the analysis because this implies useful bounds on the number of different colors that can want each node in the hyperedge, which in turn leads to simpler bounds on the probability of making the edge unsatisfied.
However, for MaxECC, if we choose a threshold that is bounded away from zero when deciding how nodes want colors, this means that if an edge e has an LP variable $z_e$ that is positive but close to zero, the algorithm of Veldt 2023 is guaranteed to delete it, meaning that the probability that the edge $e$ is satisfied is 0. This completely ruins the strategy of proving that for every edge e, the probability of satisfying e is at least $p z_e$ for some approximation value $p$.
Because of this, a different algorithm (with a very different proof) is necessary. First of all, we must consider thresholds that can be arbitrarily small (hence we draw them from [0,1]). This then makes the analysis much more complicated, because now we do not have any convenient bounds on the number of colors that want nodes in an edge (recall that this was crucial for the analysis of Veldt 2023). This is what leads to other needed differences in the algorithms (in particular, differences (1) and (2) listed above). In terms of the proofs themselves, our (often quite complicated) supporting lemmas (Lemmas A.2-A.6) and the ways they fit together to provide full proofs, deviate significantly from the technical details of Veldt 2023 for MinECC. (Note also that Observations 1 and 3 are simple results that are analogous to observations used by Veldt 2023, but Observations 2 and 4 are unique to our algorithm and analysis for MaxECC).
In regards to the datasets, we used a suite of datasets that have been described in detail in previous work on ECC (Amburg et al WWW 2020). Because these datasets have been described in detail previously and because of space constraints, we omitted a more detailed description. However, we understand that more details would be nice so that readers do not have to refer to other work, and we are happy to include more details in the appendix. Additionally, if the paper is accepted, that would provide us with 1 page of additional space we may be able to use. Some of this 1 page of space is also needed to expound on parameterized complexity (see response to reviewer LJar), but we may also be able use some of this space to briefly expound on the datasets even in the main text.
Thanks finally for noticing the typo on line 411. | Summary: This paper studies variants of the Edge Colored Clustering problem. The input consists of a hypergraph where the hyperedges are equipped with a color each. The goal is to find a coloring of the vertices. A hyperedge e is satisfied if all its vertices have the same color as e; otherwise e is unsatisfied.
An important variant is MaxECC where the goal is to maximize the number of satisfied edges. The paper provides the first approximation algorithm hor hypergraph MaxECC. Morover, an improved approximation factor for the graph variant is provided.
Moreover, also balanced and fair variants of ECC are studied and mainly approximation algorithms are provided.
Finally, a proof-of-concept implementation is provided showing the effectiveness of the newly proposed algorithms.
Claims And Evidence: For me, all claims are convincing. Also the problem and its variants have a good motivation.
Methods And Evaluation Criteria: Yes.
Theoretical Claims: I did not check all proofs in detail (especially the long proofs about the approximation guarantee), but I think I got a rough understanding of the ideas.
Experimental Designs Or Analyses: The experiments are only a proof-of-concept implementation. But these experiments are sufficient to outline the effectiveness of the new approximation algorithms.
Supplementary Material: I only briefly checked the appendix with the missing proofs to get a rough understanding of the proof. But I did not check all details.
I also did not check the provided source code of the implementation.
Relation To Broader Scientific Literature: In the introduction a very good overview of related papers and previously known approximation factors is provided.
Essential References Not Discussed: I think all relevant papers are discussed.
Other Strengths And Weaknesses: other strength:
I liked that ideas from the hypergraph algorithm are adapted to the graph case and this then yields a better approximation factor than what was previously known.
other weaknesses:
The FPT-algorithms are very simple. It would be interesting to have matching lower bounds, eg no 2^o(t) algorithms are possible.
But I think this is not a real weakness. I see these FPT results as a small bonus and that the main results are the approximation algorithms.
Other Comments Or Suggestions: line 99 column 2: I think w should be part of the definition of H
line 130 column 1: please provide some references
line 190 column 2: Can you add a short description why the proof does not work for r>2?
line 236 column 1: I got a good intuition for the used prioritization, but I didn't get an intuition for ``strong''. Please add a few lines there for more intuition.
line 311 column 2: I think many more parameters are open; and an interesting one might be the max leaf number.
Theorem 3.9 If I understand it correctly, I think this theorem should also hold for 2-regular graphs? If yes, please mention this in the theorem.
line 411 column 1: Table 4 >> Table 1
line 527 that that >> that the
line 1134: the forward reference to section 3.2 is not very nice; please define it here too.
line 1472: I think Protected-Color MinECC should be NP-hard for b=0. I think this should be mentioned somewhere.
table 2: explain shortly the meanings of n,m,r,k
Questions For Authors: Q1: I don't understand the second equation in Observation 3. I think you need to multiply the probabilities? I think it is used like this in line 196 column 1.
Q2: Where is the proof of Theorem 3.2
Q3: Can't you simplify the proof of Theorem 3.3 significantly, if you additionally assume that each clause has exactly 3 literals?
Q4: Are you aware of any ETH lower bounds for your FPT-algorithms with respect to t?
Q5: Are there any inapproximation results for the balanced and fair variants of your problem?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thanks for the detailed review! We agree the FPT algorithms are simple, and intended only as small supporting results. Also, please see our answer below regarding ETH bounds.
Thank you also for your line-based comments and suggestions. We will revise the manuscript accordingly. We’ll focus the majority of our space on your 5 specific questions.
Q1: This observation considers the probability that every node in an edge wants the edge’s color. A node wants a color if the LP variable for that node-color pair is greater than the random threshold for that color. What we are observing is that a single random threshold is used for the entire color, so in order for all nodes in an edge to want a color, it is enough for the node corresponding to the smallest LP variable to want the color. Note that the random variables in question are not independent, so we do not want to multiply the probabilities
Q2: We omitted this proof, since the text preceding the theorem statement contains the main idea. However, we would be happy to add a formal proof to the appendix. All that is missing is a standard rigorous treatment of the limit analysis.
Q3: This is good intuition, but reducing from 3SAT (with our construction, at least) only proves that Color-Fair MinECC is NP-hard when the rank of the hypergraph is at least 3, i.e., we would leave the graph case open. To understand why, observe that in our reduction we assume that each literal appears no more than twice. This assumption is crucial in bounding the size of constructed edges by 2 (each variable-clause pair has no more than 2 associated conflict vertices). If we instead reduce from 3SAT, then by the results of Tovey (Discrete Applied Math; 1984), we must assume that some variable appears at least 4 times, meaning that a literal may appear thrice. One might wonder whether the reduction of Tovey can be adapted to guarantee that literals appear at most twice. This may be possible, but it is not straightforward (we tried).
Q4: For Color-Fair MinECC, observe that the reduction of Theorem 3.3 creates an instance with O(m) total edges, where m is the number of clauses in the SAT instance. Clearly, the parameter t is thus also in O(m). So, conditioned on an ETH-bound for the particular variant of SAT from which we reduce, we can obtain one for Color-Fair MinECC.
Regarding the relevant SAT variant, at a glance it appears that the ETH excludes any 2^o(m) algorithm. To formalize this, one needs to make a few relatively simple arguments about the reduction of Tovey (Discrete Applied Math 1984). Having not worked out all of the details formally, for now we conjecture strongly that, under the ETH, Color-Fair MinECC does not admit any 2^o(t) algorithm.
For Protected-Color ECC, first observe that the problem generalizes standard ECC. We believe that no ETH bound for ECC has ever appeared in the literature. However, it is clear that one can be obtained. For example, the reduction from Vertex Cover given by Veldt 2023 excludes any 2^o(t) algorithm for ECC (each hyperedge corresponds to a unique vertex in the Vertex Cover instance). The same bound then applies to Protected-Color ECC.
The aforementioned Vertex Cover reduction creates an ECC instance with unbounded rank. It is thus open (and perhaps more interesting) to seek an ETH bound for ECC when the rank is bounded, most prominently in the graph (rank 2) case. Perhaps an ETH bound can be inferred from one of many reductions given by Kellerhals et al. (AAAI '23).
Q5: For Color-Fair MinECC we are not aware of any approximation bound, though we agree that this is interesting. In particular, it is interesting to ask whether Color-Fair MinECC can be approximated as well as (or even better than) standard MinECC, for which Veldt 2023 gave a UGC-hardness bound.
Further progress beyond our given 2-approximation is likely to require a new perspective. To see why, observe that we obtain 2-approximations for Color-Fair MinECC via two distinct strategies. First, we round the LP given at the beginning of Section 3.1 (appropriately rewritten for the mini-max p → infinity case). We cannot tighten this technique, since we already match the integrality gap. Second, we obtain a 2-approximation via reduction to Sparse Vertex Cover (see line 333 column 1, and Thm C.2). Improving the bound yielded by this reduction would require a better-than-2-approximation for Sparse Vertex Cover, which would refute the UGC. We mention these points only to emphasize that, while we do not have approximation lower bounds for Color-Fair MinECC, our results are tight with respect to the techniques used.
For Protected-Color ECC, we can apply the UGC-conditioned lower bound for standard ECC from Veldt 2023. However, it is interesting and open to determine whether Protected-Color MinECC can be approximated as well as standard MinECC. Finally, we mention (line 298, column 2) that unless P = NP, no poly-time multiplicative approximation for Color-Fair MaxECC exists.
---
Rebuttal Comment 1.1:
Comment: Thank you for your answers!
about Q3 (and partiallyQ4):
I think the problem (3,B2)-SAT is want you want: The 3-SAT-variant where each literal positive/negative appears exactly twice.
This problem is NP-hard, see the paper 'Approximation hardness of short symmetric instances of MAX-3SAT' (Theorem 1).
Also, I think for this problem a no $2^{o(n+m)} lower bound under the ETH is known (or should follow easily by considering their reduction).
---
Reply to Comment 1.1.1:
Comment: Thanks for the follow-up comment and the helpful reference! This sounds promising; we’ll take a close look. At a glance, it appears to us that you are correct about the ETH bound following from their reduction.
Thanks once again for the detailed review and helpful suggestions for improving the work. | Summary: This submission studies a clustering problem where one wants to cluster vertices of a hypergraph by coloring them while approximately maximizing the number of hyperedges all whose vertices get a hyperedge-specific color (those hyperedges are called satisfied). It gives the first algorithm for this problem on general hypergraphs the approximation ratio of which gets worse with increasing maximum hyperedge size but actually beats the previous best ratio for hyperedge size 2. The algorithm, like older ones for the graph setting, is based on randomized rounding of an LP solution. As is often the case, the idea behind this rounding is natural but analyzing its quality involves some carefully combined ideas.
Additionally, the submission proposes variants of the dual problem for minimizing the number of unsatisfied hyperedges that put hard constraints on the number of allowed unsatisfied hyperedges of a specific protected color or require that the number of unsatisfied edges of each color be balanced and devises some basic hardness results and algorithms for them. The latter are partially implemented and tested.
Claims And Evidence: The only content I am suspicious of is the motivation behind defining the fair variants of the problem. The described potential applications sound more like the size of the clusters should be lower bounded rather than the number of unsatisfied clusters balanced. If one were to reformulate that application as wanting each type of task to be not be doable because of a certain assignment of workers to roles one would also consider it more sensible to somehow view this relative to the number of tasks of a type there are in total. In general, I would need some more convincing arguments why the suggested fair problems are interesting, even from a theoretical standpoint.
Methods And Evaluation Criteria: The methods seem appropriate.
Theoretical Claims: I read everything except the appendix.
Experimental Designs Or Analyses: I did not check them beyond reading their description and thinking about whether they make sense on a superficial level but these are also not the core of the contributions.
Supplementary Material: No.
Relation To Broader Scientific Literature: This falls into the research direction on edge-colored clustering, improves a line of results there and tries to open new research directions about the problem.
Essential References Not Discussed: I am not aware of any.
Other Strengths And Weaknesses: In terms of topic, this could be in scope for ICML but the problem seems a bit niche for the broad audience (this impression seems to also be confirmed by looking at where most closely related work was published). Apart from that, the results and included proofs are also generally well-presented.
Because I am not convinced of how relevant the general problem and even more so the introduced variants are, I am scoring this as a weak reject but am happy to discuss this assessment.
Other Comments Or Suggestions: -L026: best known (no hyphen)
-L058: Maybe say here what this gap is
-L135: Maybe add r is an arbitrary constant
-L138: line of previous research
-At the beginning of section 2.1.: at some point you should fix z_e and such to be values of the variables in an arbitrary fixed optimal solution of the LP (otherwise z_e is not defined in the statements of the observations and such).
-L166: Obtain optimal values for {z_e,x_v^c} in the LP relaxation.
Questions For Authors: Can you argue a bit more why the introduced fair variants of the problem are of interest?
Similarly, your later results seem a bit arbitrary. Can you explain why you chose to focus on those, e.g. some approximation, some approximation results and some hardness results in which you do not mention hardness of approximation? Did you try to get a comprehensive view in any of these directions?
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: Thanks for your feedback and questions!
**Motivation for ECC variants.** We highlight 2 points we could have done better addressing in the main text.
(1) Correlation Clustering variants
One key motivation for our fair/protected ECC variants is that these are directly analogous to questions that have been extensively studied for variants of the closely related correlation clustering (CC) problem. Puleo and Milenkovic (ICML 2016) considered a mini-max objective (minimize the maximum number of mistakes incident to any one node) and a more general Lp-norm variant of correlation clustering. Subsequent papers on these CC variants include:
Charikar et al. (IPCO '17)
Kalhan et al. (Neurips '19)
Jafarov et al. (ICML '21)
Davies et al. (ICML '23)
Heidrich et al. (AISTATS '24)
Davies et al. (ICALP '24)
Unlike the rich literature on correlation clustering, prior work on ECC has focused only on objectives that consider the total count of (un)satisfied edges. Our motivation is to understand whether algorithms for this simplest variant work only in this setting, or if we can identify algorithmic strategies that work (or fail) for alternative objectives.
(2) Resource allocation, team formation
We are also interested in potential applications to resource allocation (motivation from the first graph ECC paper, Angel et al 2014) and team formation problems that relate to the work of Amburg et al 2022, but go beyond the explanation we provided in our introduction. For team formation, one can imagine nodes representing workers, and colors representing assignments to work teams (possibly encoding different physical work sites). An edge of a certain color is then a task that can be completed if and only if a specific set of individuals are assigned to that same group or site. In this case, a natural goal is to partition workers to balance the number of tasks that can be accomplished at different work sites. Here it’s not enough to just balance the number of workers in each group—one must consider the collection of tasks that can be completed by workers assigned to a team.
(This motivation aligns more with Color-Fair MaxECC. However, the latter is NP-hard to even approximate. Color-Fair MinECC provides roughly the same goal if the number of edges of each type is balanced, and we show it is amenable to approximations.)
We stress that this direction of exploration is still in initial phases, which is why we did not focus on it extensively in our submission. The present paper is more directly motivated to establish better theoretical foundations of ECC algorithms for a broader class of objective functions, analogous to the rich literature on correlation clustering.
**Regarding results for fair/balanced ECC.** Our goal was to get as complete an understanding as possible of (i) the approximability and (ii) parameterized complexity of our fair/balanced objectives, especially for Color-Fair ECC. We agree that there are still open questions that could be explored, but we sought to provide as full of an answer as possible.
Regarding FPT results, we chose to explore the same collection of parameters considered by Kellerhals et al. (AAAI 2023), who provided a comprehensive study of the parameterized complexity for standard ECC. This uncovered fundamental differences between FPT results for standard ECC and Color-Fair ECC (see text after Theorem 3.3).
Note that we did include some approximation hardness results, in that Color-Fair MaxECC is NP-hard to approximate to within any factor (see line after Theorem 3.3). We agree that approximation hardness results for Color-Fair MinECC and Protected ECC would also be interesting, but ultimately we were not able to settle all open questions in one paper. These are interesting directions for future work.
See also our response to Question 5 of reviewer Hv7k regarding approximation hardness and ways in which our results are tight.
We agree that there is a lot going on in the second half of the paper in various directions. We could have chosen to discard some of these results, but ultimately we felt it would be better to provide as many answers to natural questions as we could.
**Related work.** The reviewer argued that “the problem seems a bit niche for the broad audience (this impression seems to also be confirmed by looking at where most closely related work was published).” However, we would like to point out that the most related papers are published at ICML or similar venues. This includes hypergraph ECC papers:
Veldt (ICML '23)
Amburg et al (WWW '20)
Amburg et al (SIAM Data Mining '22)
Kellerhals et al (AAAI '23)
Crane et al (WSDM '24)
and papers on approximation algorithms for the closely related problem of correlation clustering in edge-colored graphs: Bonchi et al (KDD 2012), Anava et al (WWW 2015), Klodt et al (KDD 2021), Xiu et al (Neurips 2022)
Thanks finally for the additional Comments and Suggestions. We will address these in an updated version of the paper.
---
Rebuttal Comment 1.1:
Comment: Many thanks for your response!
The motivation for the ECC variants is now clearer to me and I would suggest incorporating in particular (1) into the manuscript; at least I as a reader would have appreciated that.
If you tried and were not able to get some more comprehensive results, I think it is always nice to indicate some key difficulties which follow-up work needs to resolve. Also, as reviewer Hv7K points out, some hardness results seem quite easy to obtain. I still think that whole part of the paper could benefit from a more focused structuring and less of being presented like a arbitrary accumulation of results.
As for the most closely related work, I would view that as the series of improvements in the graph case, since you are doing something similar in the hypergraph setting. Those publications appeared at less broad venues.
---
Reply to Comment 1.1.1:
Comment: Thanks for your reply!
*"The motivation for the ECC variants is now clearer to me and I would suggest incorporating in particular (1) into the manuscript; at least I as a reader would have appreciated that."*
Yes, we will definitely be incorporating the motivation from (1) into the manuscript; we agree that in our original submission we did not do a good enough job highlighting this relevant previous work and motivation.
*"If you tried and were not able to get some more comprehensive results, I think it is always nice to indicate some key difficulties which follow-up work needs to resolve. Also, as reviewer Hv7K points out, some hardness results seem quite easy to obtain. I still think that whole part of the paper could benefit from a more focused structuring and less of being presented like a arbitrary accumulation of results."*
We agree that the second half of the paper will benefit from a focused restructuring. If the manuscript is accepted, this will give us one extra page of space, and we have already identified this as the section that could most use it. In particular, we’ll do a better job highlighting why our parameterized complexity results do already provide pretty comprehensive answers regarding how the parameterized complexity of Color-Fair ECC relates to standard ECC (and yes, the hardness results highlighted in our discussion with reviewer Hv7K can help strengthen this as well!). We’ll also do a better job highlighting the challenges that would need to be overcome in order to get better approximations for our problems.
We’ll also be relegating some of the minor side results to the appendix to help better focus this section (e.g., the linear-time k approximation for Color-Fair ECC).
*“As for the most closely related work, I would view that as the series of improvements in the graph case, since you are doing something similar in the hypergraph setting. Those publications appeared at less broad venues.”*
Understood, thanks for the clarification. Those publications on graph ECC are indeed at less broad venues, but given the many papers on algorithms for ECC at ICML and similar venues, we believe this is the right venue for our work. We hope that the relevant related work on correlation clustering that we highlighted in our response also helps address this concern.
Once again, thanks for your detailed review and for taking the time to provide some additional follow-up comments. | null | null | null | null | null | null |
NExtLong: Toward Effective Long-Context Training without Long Documents | Accept (poster) | Summary: This paper introduces NExtLong, an effective framework that improves long-context modeling in LLMs through negative document extension. It first divides a document into meta-chunks and then inserts hard negative distractors to force LLMs learn the dependency between long documents. Experimental results have illustrated the efficiency of NExtLong.
## update after rebuttal
The author's rebuttal addressed my previous concerns and thus I have updated my score correspondingly.
Claims And Evidence: The effectiveness of the proposed method NExtLong is proved by the experimental results.
Methods And Evaluation Criteria: Yes.
Theoretical Claims: No issues.
Experimental Designs Or Analyses: Experimental settings are good except Table1 (please see the weakness section)
Supplementary Material: Yes.
Relation To Broader Scientific Literature: The proposed method is novel and effective.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: Weaknesses:
1. Regarding Table 1, it seems that NExtLong is using extra negatives when pre-training on the two datasets compared to other baselines, meaning that it may use more training examples, which makes the comparison not fair.
I am happy to raise my score if the authors could answer my question clearly (or point out my misunderstanding)
Other Comments Or Suggestions: N/A
Questions For Authors: Please see the weakness section.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We sincerely appreciate your response! Your detailed and insightful feedback plays a crucial role in improving our article. The following text further clarifies some questions.
---
**Q1: "Regarding Table 1, it seems that NExtLong is using extra negatives when pre-training on the two datasets compared to other baselines, meaning that it may use more training examples, which makes the comparison not fair."**
**A1:** Thanks for your question. We appreciate the opportunity to clarify this point.
We would like to clarify that **NExtLong does NOT use any additional training example (lines 251-256)**. The negatives utilized by NExtLong are also drawn from the two datasets (lines 208-212). Specifically, we construct a FAISS index from these datasets, and NExtLong retrieves hard negatives from the FAISS index to synthesize long-context data. The FAISS index used by the baseline methods is also built from the same datasets; **the only difference between those methods and ours is how they rearrange documents into long-context data.**
**Importantly, the total number of training examples and the experimental settings are identical across all methods, ensuring a fair comparison.** This is explicitly stated in the following sections of our paper:
- Lines 208-212: "*Various methods, including NExtLong and baseline approaches, are employed to synthesize target-length samples concatenated from these short documents.*"
- Lines 251-256: "*...The same training configuration is applied to all methods for a fair comparison.*"
- Lines 263-272 provide further details on how baseline methods synthesize long-context data.
We apologize for any confusion and hope this clarification addresses your concern. Please let us know if any further details would be helpful. | Summary: The paper introduces the NExtLong framework, which aims to alleviate issues arising from the scarcity of high-quality long documents in long-context training. Traditional methods that concatenate shorter documents do not effectively capture necessary long-range dependencies, leading to problems with coherence and relevance. NExtLong addresses these challenges by decomposing long documents into meta-chunks and incorporating hard negative distractors from pre-training corpora. This method increases the difficulty of the training process, encouraging the model to differentiate between relevant long-range dependencies and distracting information, thereby improving its overall modeling capabilities. Experimental results indicate that NExtLong outperforms existing long-context synthesis methods and state-of-the-art models, yielding an average performance improvement of 7.33% on key benchmarks such as HELMET and RULER.
Claims And Evidence: This work claims that the proposed data cooking method is effective for long-context training. This main claim is supported by clear and convincing evidence. In the experimental section, the authors compare the proposed method with various alternatives and demonstrate the effectiveness of hard negatives through ablation experiments (section 5.4).
Methods And Evaluation Criteria: The proposed method is evaluated on the two most important long-context benchmarks: RULER and HELMET.
Theoretical Claims: N/A
Experimental Designs Or Analyses: The experimental design is standard and sound.
Supplementary Material: I reviewed the supplementary material B for the results of ablation study.
Relation To Broader Scientific Literature: The key findings regarding the data composition strategy have the potential to enhance the long-context training methods used in current LLMs.
Essential References Not Discussed: Zhao, L., Wei, T., Zeng, L., Cheng, C., Yang, L., Cheng, P., ... & Zhou, Y. (2024). Longskywork: A training recipe for efficiently extending context length in large language models. arXiv preprint arXiv:2406.00605.
I would like to suggest to include the above work in the related section. It is the first work try to use interleaved chunk data to improve long-context performance.
Other Strengths And Weaknesses: In general, this work is solid, with well-presented experimental results.
Weaknesses:
1. Limited Novelty:
The novelty is limited given the existence of previous works [1] and [2]. Compared with [1], this work omits training strategies like Knot Tokens and instead introduces a negative sample data preparation strategy. Moreover, [2] was actually the first to use interleaved chunks to achieve improved performance. The authors should, at a minimum, include [2] in the related work.
2. Compatibility with Modern Techniques:
The proposed data preparation method is not compatible with the commonly used intra-document attention approach for long-context training. After Llama3 demonstrated the effectiveness of intra-document attention, in terms of both performance improvement and reduced memory requirement, the Qwen series and recent research works [3, 4] have adopted this approach. While the proposed method can improve the older full attention mechanism, it may not compare favorably with emerging methods.
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[1] Tian, J., Zheng, D., Cheng, Y., Wang, R., Zhang, C., & Zhang, D. (2024). Untie the knots: An efficient data augmentation strategy for long-context pre-training in language models. *arXiv preprint arXiv:2409.04774.
[2] Zhao, L., Wei, T., Zeng, L., Cheng, C., Yang, L., Cheng, P., ... & Zhou, Y. (2024). Longskywork: A training recipe for efficiently extending context length in large language models. *arXiv preprint arXiv:2406.00605.
[3] Wang, H., Liu, Q., Du, C., Zhu, T., Du, C., Kawaguchi, K., & Pang, T. (2024). When Precision Meets Position: BFloat16 Breaks Down RoPE in Long-Context Training. *arXiv preprint arXiv:2411.13476.
[4] Gao, T., Wettig, A., Yen, H., & Chen, D. (2024). How to train long-context language models (effectively). arXiv preprint arXiv:2410.02660.
Other Comments Or Suggestions: 1. For Table 1, I suggest that the authors provide the results averaged over 32K, 64K, and 128K in the appendix, following the same evaluation protocol as in ProLong.
Questions For Authors: 1. In Table 2, the results are averaged over 8K, 16K, 32K, 64K, and 128K. Does Table 5 follow the same procedure? I suggest that the authors provide more detailed explanations of the experimental setup.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We sincerely appreciate your response! Your detailed and insightful feedback plays a crucial role in improving our article. The following text further clarifies some questions.
---
**Q1: "I would like to suggest to include the above work in the related section. It is the first work try to use interleaved chunk data to improve long-context performance."**
**A1:** We sincerely appreciate your valuable suggestion. We acknowledge the significance of the mentioned work as the first to explore the use of interleaved chunk data for improving long-context performance. **We will incorporate this important reference in the revised version** to ensure a more comprehensive discussion in the related work section. Thank you for bringing this to our attention.
**Q2: "Limited Novelty: The novelty is limited given the existence of previous works [1] and [2]."**
**A2:** We would like to emphasize that **our contribution is not using interleaved chunks**. As we explicitly state in lines 55–57: *"An intuitive approach to building documents with long-range dependencies is to insert additional text between dependent segments.[1]"* Additionally, we discuss the limitations of those methods in lines 62–65, noting that **they do not fully capture the real-world challenge of extracting long-range dependencies amid extensive distracting information.**
We replace hard negatives with random chunks to implement a baseline (RandomD) similar to [1][2], and Figure 7 shows that it underperforms NExtLong. The results indicate that our method better reflects real-world scenarios where models must extract relevant information despite interference, thereby fostering more robust long-range dependency learning (As mentioned in lines 83-88).
**Q3: "Compatibility with Modern Techniques: The proposed data preparation method is not compatible with the commonly used intra-document attention approach for long-context training."**
**A3:** We would like to clarify that **our method is indeed compatible with intra-document attention**. In fact, **Llama-3-8B-NExtLong-512K-Base is trained using the intra-document attention approach and achieves strong results (Table 2)**. Specifically, we construct 512K and 64K datasets (lines 326–329) and apply intra-document attention to the 64K subsets, enabling their concatenation into 512K context length. This strategy aligns with ProLong[4] (lines 318–320), which uses a 64K dataset to train 512K models. Our results in Table 2 demonstrate that NExtLong performs better under this setup.
**Q4: "For Table 1, I suggest that the authors provide the results averaged over 32K, 64K, and 128K in the appendix, following the same evaluation protocol as in ProLong."**
**A4:** Thank you for the suggestion. We will incorporate the results averaged over 32K, 64K, and 128K in the appendix. We report the averaged results in the table below, and NExtLong maintains a performance advantage across sequence lengths beyond 16K, further supporting the effectiveness of our approach.
| Model | Avg. | Recall | RAG | ICL | Re-rank | LongQA | RULER |
|------------------------------------|-------|--------|-------|-------|---------|--------|-------|
| Llama-3-8B-ProLong-512K-Base | 60.34 | 82.38 | 60.10 | 84.07 | 24.77 | 33.44 | 77.26 |
| Llama-3-8B-NExtLong-512K-Base | **64.71** | **87.96** | **62.42** | **88.67** | **25.81** | **41.27** | **82.14** |
**Q5: "In Table 2, the results are averaged over 8K, 16K, 32K, 64K, and 128K. Does Table 5 follow the same procedure? I suggest that the authors provide more detailed explanations of the experimental setup."**
**A5:** Yes, **Table 5 follows the same reporting procedure**. Specifically, the "Head" strategy in Table 5 corresponds to the NExtLong results in Table 1.
We sincerely apologize for any confusion caused by the insufficient explanation of the experimental setup. We will include more details in the revised version. Please let us know if any further information would be helpful.
---
[1] Tian, J., Zheng, D., Cheng, Y., Wang, R., Zhang, C., & Zhang, D. (2024). Untie the knots: An efficient data augmentation strategy for long-context pre-training in language models. *arXiv preprint arXiv:2409.04774.
[2] Zhao, L., Wei, T., Zeng, L., Cheng, C., Yang, L., Cheng, P., ... & Zhou, Y. (2024). Longskywork: A training recipe for efficiently extending context length in large language models. *arXiv preprint arXiv:2406.00605.
[3] Wang, H., Liu, Q., Du, C., Zhu, T., Du, C., Kawaguchi, K., & Pang, T. (2024). When Precision Meets Position: BFloat16 Breaks Down RoPE in Long-Context Training. *arXiv preprint arXiv:2411.13476.
[4] Gao, T., Wettig, A., Yen, H., & Chen, D. (2024). How to train long-context language models (effectively). arXiv preprint arXiv:2410.02660.
---
Rebuttal Comment 1.1:
Comment: Thanks for your reply.
Could the authors explain more about how the proposed method compatible with intra-document attention? The inter-doc masking of it will block the information flow between documents.
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Reply to Comment 1.1.1:
Comment: Previous studies [1, 2, 3] employ intra-document attention on training samples formed by concatenating multiple documents. For instance, ProLong [1] uses 512K-length and 64K-length documents when training the 512K-length model (refer to Table 9 in the ProLong paper). These 64K-length documents are concatenated into 512K-length training samples — each sample contains eight 64K-length documents — and intra-document attention is applied to prevent interference among these documents.
Given that mixing documents of different lengths during training is widely adopted in prior work [1, 4, 5], we follow the ProLong approach by synthesizing both 512K-length and 64K-length documents for training the 512K NExtLong model (lines 326–329). For synthetic 512K-length documents, we apply the full attention mechanism, as each document constitutes an entire training sample. For synthetic 64K-length documents, we concatenate them into 512K-length training samples (each sample contains eight 64K-length documents) and employ intra-document attention to restrict information flow within each 64K-length document.
In addition, as shown in Table 1, our 128K NExtLong model trained on 128K synthetic documents (without intra-document attention or advanced techniques such as train-long/test-short) outperforms both the ProLong model and Llama3.1 on average (62.58 vs. 60.34 and 61.07, respectively). For a fair comparison (lines 313-320), we combine advanced strategies and achieve better results with our 512K NExtLong model (65.76 on average).
Our experimental results demonstrate that NExtLong is capable of synthesizing documents of arbitrary lengths (in this work, we synthesize documents of 64K, 128K, and 512K lengths) and is adaptable to various modern techniques, ensuring both flexibility and effectiveness.
We will further emphasize these experimental settings in the revised version. Thank you for your constructive feedback！
---
[1] Gao, T., Wettig, A., Yen, H., & Chen, D. (2024). How to train long-context language models (effectively). arXiv preprint arXiv:2410.02660.
[2] Ding, H., Wang, Z., Paolini, G., Kumar, V., Deoras, A., Roth, D., & Soatto, S. (2024). Fewer truncations improve language modeling. In Proceedings of the 41st International Conference on Machine Learning (ICML'24).
[3] Meta. (2024). Introducing meta llama 3: The most capable openly available llm to date.
[4] Fu Y, Panda R, Niu X, et al. Data engineering for scaling language models to 128k context. (2024). In Proceedings of the 41st International Conference on Machine Learning (ICML'24).
[5] Xiong et al. (2024). Effective Long-Context Scaling of Foundation Models. In Proceedings of the 2024 Conference of the North American Chapter of the Association for Computational Linguistics (NAACL'24). | Summary: The paper introduces NExtLong, a new framework designed to address the challenge of training LLMs with extended context windows, particularly in the face of limited availability of long documents. The key contributions of the paper are the usage of hard negative documents mining for the construction of long documents. Experimental results on RULER and HELMET show the strong performance of this paper.
Claims And Evidence: The main claim is that the proposed method enhances long-context modeling by synthesizing data with hard negatives, addressing the scarcity of long documents.
Evidence: It outperforms all baselines by a large margin (e.g., +7% over Quest) on HELMET and RULER (Table 1). The superior performance on long-context ICL is especially impressive.
Methods And Evaluation Criteria: Method: chunk documents into meta-chunks, retrieve hard negatives via FAISS, interleave them, and train with next-token prediction loss.
Evaluation: Two commonly used long-context benchmark, including HELMET and RULER (several subtasks), measuring recall, RAG, ICL, re-ranking, LongQA, and synthetic tasks. Metrics include Accuracy and ROUGE F1.
Theoretical Claims: No, no theoretical claim in this paper.
Experimental Designs Or Analyses: Comparisons: Tested against KNN, Quest, and SOTA models (Llama-3 and other open models, with GPT-4o, Gemini-1.5-Pro and Claude).
Ablations: Analyzed chunking granularity (Figure 6), negative selection strategies (Figure 7), and dataset combinations (Table 7).
Supplementary Material: Yes, I have reviewed the Figure 8 (Needle in the hay stack figure)
Relation To Broader Scientific Literature: Builds on contrastive learning (hard negatives) and long-context methods (e.g., ProLong, Quest). Addresses document scarcity, a key challenge in long-context model training.
Essential References Not Discussed: No
Other Strengths And Weaknesses: Strengths: neat and good use of hard negatives, comprehensive evaluations, minimal performance drop on short-text tasks.
Weaknesses: Dependency on FAISS retrieval quality, computational cost for indexing, not comparing against models using realistic long documents.
Other Comments Or Suggestions: N/A
Questions For Authors: Although I understand it is not the main point of this paper, but I am curious about if the proposed method can be applied to long documents to further extend the effective context length of the model? For example, using a dataset which contains more documents > 8K length, and apply the proposed method on it to get a much better long-context performance on the evaluation benchmark.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We sincerely appreciate your response! Your detailed and insightful feedback plays a crucial role in improving our article. The following text further clarifies some questions.
---
**Q1: Dependency on FAISS retrieval quality**
**A1:** The quality of FAISS retrieval depends significantly on the effectiveness of the embedding model. As embedding models advance, retrieval performance is expected to improve accordingly. Given ongoing advancements in this area [1][2], we anticipate these advancements will further enhance the performance of NExtLong and plan to explore the impact of more advanced embedding models in future work.
---
[1] Choi, Chanyeol, et al. Linq-Embed-Mistral Technical Report. arXiv preprint arXiv:2412.03223 (2024).
[2] Wang, Liang, et al. Multilingual e5 text embeddings: A technical report. arXiv preprint arXiv:2402.05672 (2024).
**Q2: "computational cost for indexing"**
**A2:** The computational cost of indexing is only incurred during the generation of synthetic training data and does not impact the inference phase of the model. Since this is a one-time cost, the resulting performance improvements provide lasting benefits for downstream tasks. Given these long-term advantages, the computational expenditure is justified and contributes to overall performance.
**Q3: "not comparing against models using realistic long documents."**
**A3:** We would like to clarify that **some of the models compared in Table 2 are indeed trained with realistic long documents**. For example, ProLong [1] uses realistic long documents (as mentioned in lines 323-325) and extensively explores how to utilize them effectively.
To ensure a fair comparison, Table 2 directly compares NExtLong with ProLong. It shows that Llama-3-8B-NExtLong-512K-Base outperforms Llama-3-8B-ProLong-512K-Base, further validating the effectiveness of NExtLong (lines 319-322).
---
[1] Gao, Tianyu, et al. How to train long-context language models (effectively). arXiv preprint arXiv:2410.02660 (2024).
**Q4: "Although I understand it is not the main point of this paper, but I am curious about if the proposed method can be applied to long documents to further extend the effective context length of the model? ..."**
**A4:** Based on the hypothesis that shorter original documents pose more significant challenges for a fixed target length and given that training a long-context model is resource-intensive, we prioritized creating a more challenging experimental setting within our limited training resources. Our current experiments deliberately use relatively short documents, creating an effective 64x increase in sequence length compared to the original documents (as mentioned in lines 651–652).
Despite this challenging setting, NExtLong still achieved strong performance, **leading us to believe that when the original documents are longer, they can be merged into even longer sequences while maintaining promising results**. We are currently collecting longer documents and will systematically investigate the impact of documents exceeding 8K tokens in future work.
Thank you for your insightful question! | Summary: Most LLMs require long documents to handle long-context processing, but in practice, high-quality long documents are scarce. Existing methods typically concatenate short documents either randomly or based on similarity, which is not effective for learning long-range dependencies. This paper proposes splitting documents into multiple meta-chunks and inserting hard negatives—text segments that are semantically similar but unrelated to the actual context—between them. This encourages the model to distinguish between true context and misleading context, thereby enhancing its ability to learn long-range dependencies.
Claims And Evidence: Yes, it's supported by the experiments section.
Methods And Evaluation Criteria: The proposed methods and evaluation criteria seem make sense for the problem.
Theoretical Claims: N/A
Experimental Designs Or Analyses: I checked the validity of the experimental designs. It would be better to explain why improving the long-context ability of LLMs can decrease the performance on short text benchmarks.
Supplementary Material: Appendix D.2.
Relation To Broader Scientific Literature: Improving the ability of LLMs to handle long context is important, and this paper addresses how to effectively construct synthesized long documents.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: **Strengths**
1. Writing is clear.
2. The motivation behind the method is clear.
3. The efficacy of the method is demonstrated through the experiments on HELMET and RULER benchmark.
**Weaknesses**
1. Compared to prior methods, the novelty of this approach feels somewhat limited.
2. It would be helpful to more clearly highlight which aspects of the previous methods made them suboptimal.
Other Comments Or Suggestions: N/A
Questions For Authors: Please see above.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We sincerely appreciate your response! Your detailed and insightful feedback plays a crucial role in improving our article. The following text further clarifies some questions.
---
**Q1: "It would be better to explain why improving the long-context ability of LLMs can decrease the performance on short text benchmarks."**
**A1:**
Previous long-context extension approaches [1] often degrade short-context performance because they rely exclusively on non-synthetic long documents, which are scarce across most domains (as noted in lines 35–37). This view also aligns with [2], which states that "*a data mixture that keeps the domain mixture ratio the same as the pretraining mixture...this is the primary reason our solution improves long context tasks while maintaining short context performance.*"
Quest [3] demonstrates that using a long-text dataset synthesized from short texts with good domain diversity does not decline short-text performance. Following Quest, we also use short-text data sources with sufficient diversity, such as Cosmopedia V2, which covers over 34,000 topics. As a result, Table 5 demonstrates that NExtLong does not degrade short-text performance on average.
Thanks for your valuable suggestion! We will elaborate on this point in the revised version.
**Q2: "Compared to prior methods, the novelty of this approach feels somewhat limited. It would be helpful to more clearly highlight which aspects of the previous methods made them suboptimal."**
**A2:** As mentioned in lines 51-53: "*those methods typically concatenate short documents based on random or similarity-based rankings, lacking a clear mechanism for capturing long-range dependencies.*" Previous studies (e.g., Quest [3]) synthesize long-context data by concatenating similar documents sequentially, allowing models to perform the next token prediction without relying on preceding documents. That concatenation strategy weakens the learning of long-range dependencies, and Table 1 shows that those methods achieve only marginal improvements compared to the Standard approach.
While approaches like [4][5] increase dependency length using interleaved chunk data, they do not capture the real-world challenge of extracting long-range dependencies amid extensive distracting information. To verify this, we replace hard negatives with random chunks to implement a baseline (RandomD) similar to [4][5], and Figure 7 shows that it underperforms NExtLong.
In contrast, as mentioned in lines 83-88: "*By inserting these distractors between originally dependent meta-chunks, NExtLong not only increases the distance between dependent chunks—effectively transforming the dependencies into long-range ones—but also introduces distracting noise.*" **This design better reflects real-world scenarios where models must extract relevant information despite interference, thereby fostering more robust long-range dependency learning.**
We will provide a more detailed comparative analysis in the revised version. Thanks for your constructive suggestion!
---
[1] Chen Y, Qian S, Tang H, et al. Longlora: Efficient fine-tuning of long-context large language models. The Twelfth International Conference on Learning Representations (ICLR'24).
[2] Fu Y, Panda R, Niu X, et al. Data engineering for scaling language models to 128k context. In Proceedings of the 41st International Conference on Machine Learning (ICML'24).
[3] Gao C, Wu X, Fu Q, et al. Quest: Query-centric data synthesis approach for long-context scaling of large language model. The Thirteenth International Conference on Learning Representations (ICLR'25).
[4] Tian, Junfeng, et al. Untie the knots: An efficient data augmentation strategy for long-context pre-training in language models. arXiv preprint arXiv:2409.04774 (2024).
[5] Zhao, L., Wei, T., et al. Longskywork: A training recipe for efficiently extending context length in large language models. arXiv preprint arXiv:2406.00605 (2024). | null | null | null | null | null | null |
Revisiting the Predictability of Performative, Social Events | Accept (poster) | Summary: The authors consider a classic problem in social science--how can we make accurate predictions about the world if our predictions affect the world--from a learning theory perspective. In this setting, there are features $x$, a binary outcome $y$, and we wish to make probabilistic predictions $f(x)$ to predict $y$. However, once we pick $f$, the world changes so that $(x, y) \sim \mathcal D(f)$, and outcomes now depend on our predictions in an arbitrary way (the performative prediction setting). Classic work using fixed-point analysis shows that there exist predictors $f$ such that $f(x)$ predicts $y$ when $(x, y)\sim \mathcal D(f)$, but does not provide a method of computing such predictors. Here, the authors adapt online multicalibrated algorithms to performative prediction. They show that it is indeed possible to efficiently learn a predictor $f(x)$ that is (multi)calibrated (on whichever subsets of $x$ we care about) with the induced outcomes drawn from $\mathcal D(f)$. Moreover, they show a connection to outcome indistinguishability, so that their predictor's outputs are computationally indistinguishable from the world outcomes. On the other hand, through a construction, the authors also demonstrate that the learned predictor can utterly fail to explain the variance in $y$, despite being perfect calibrated. Intuitively, they show that in some cases, the only way to achieve calibration is to steer the world into higher variance outcomes, where are predictions are essentially useless (despite being calibrated). In contrast, if we were willing to accept some small bias in our predictions in this construction, we could steer the world into highly predictable outcomes (consistently y=0 or y=1).
### Update after rebuttal
I continue to think this is a very nice paper and I'm glad the other reviews agree on acceptance.
Claims And Evidence: The theoretical claims are thoroughly supported by proofs, including sketches in the main text and extended proofs in the appendix.
Methods And Evaluation Criteria: N/A
Theoretical Claims: I am confident that the analysis in section 5 is correct. The other proofs sound reasonable, although I have not extensively checked the details.
Experimental Designs Or Analyses: N/A
Supplementary Material: I checked it to ensure it contains extended version of the proof sketches, which it does.
Relation To Broader Scientific Literature: The key contribution is a method for constructing a calibrated performative predictor, and analysis of why this might not be the best measure for social prediction.
Essential References Not Discussed: None that I am aware of, although this is not my primary area of expertise. However, the paper in many places acknowledges where the ideas it draws from originated, so my impression is that the authors are very familiar with the relevant related work.
Other Strengths And Weaknesses: Strengths:
1. The quality of the paper and writing are extremely high.
2. The problem is a very important one, and from my understanding this paper provides a very nice contribution to the literature
Weaknesses:
1. In some cases, I found the subtle differences between equations and definitions difficult to follow, so I think there could be just a bit more intuition provided (see suggestion below for the main one)
Other Comments Or Suggestions: 1. The construction from section 5 is very nice and easy to understand, and makes the distinction between performative stability and performative optimality much clearer than the definitions and Eqs (1) and (2). I would recommend describing the intuition behind this construction in 1.1, so the reader doesn't have my experience: thinking "how can this possibly be true, I don't understand how (1) and (2) lead to such drastic differences" until they reach the last page of the paper and it clicks.
Questions For Authors: 1. Some places have $(x, y)\sim \mathcal D (f)$ (e.g., line 417) while others have $y \sim \mathcal D (f)$ (e.g., line 421), and yet others have $x \sim \mathcal D (f)$ (e.g., line 381). All of those cases seem to use both $x$ and $y$, so surely they should all say $(x, y)\sim \mathcal D (f)$, right?
2. Along the same lines, some places say $p \sim f$ (line 417) and others say $p \sim f(x)$. Shouldn't it always be $p \sim f(x)$?
Code Of Conduct: Affirmed.
Overall Recommendation: 5 | Rebuttal 1:
Rebuttal: Thank you for all of the insightful comments on our work! We’re glad you found the paper interesting.
We will certainly add intuition behind the construction in section 5 to the introduction. Your comments in the summary of your review are very helpful in this regard. We appreciate it!
And yes, thanks for catching those typos; we will fix them. | Summary: This paper formalizes the question of whether predictions can remain accurate when the act of predicting affects the state of the world. The authors address this question theoretically and show that a predictor can maintain some bounded level of calibration/validity. The paper provides a bound on how far a predictor might be from accuracy and show that high quality predictions can be found in polynomial time. The paper ends by showing that while the calibration criteria which has been used through the paper has very bad worst-case performance.
Claims And Evidence: I have not found errors in the claims of the paper, however, I find the paper to be quite lacking in clarity. While the introduction does an excellent job of setting out some intuition as to the problem domain I find the explanation within the paper highly devoid of both (1) intuitive explanation of each idea being used (e.g. an example of what good [multi-]calibration means in practice, contrasted with something like accuracy would help my understanding), and (2) a clear explanation of all notation: there is some assumption of understanding around certain notation standards which are then not introduced in the paper. Basic definitions, such as the distinction between p and y needs to be spelled out more clearly to firmly establish a solid grounding that a reader will use for the rest of the paper.
Methods And Evaluation Criteria: The theoretical framework applied to the problem seems quite fitting.
Theoretical Claims: Most proofs are not in the main paper but instead included in an appendix; I did not thoroughly review them.
Experimental Designs Or Analyses: N/A
Supplementary Material: No.
Relation To Broader Scientific Literature: There is discussion around the work most directly related to this topic. The paper does not include a concluding discussion section which might add some broader connection to other areas of the scientific community.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: In general, I find the topic of this paper to be excellent and in a direction that I truly hope is developed much further. However, I find this paper to be quite inaccessible due to a lack of both thorough explanation of the basics of the paper, and a lack of examples/intuition around how to understand the concepts.
The paper suffers as a result, both in terms of clarity and any comment I can add on the significance of the paper. A section more clearly discussing the implications of your results would help me to much better understand where this paper fits in and how important it is to the literature.
Other Comments Or Suggestions: Some minor notes:
- typo in Definition 1: "to a distributions over"
- the blue line in Figure 1 is not at all friendly to the colour-blind (or any reader that prints out papers in black and white, like myself). A different line style for that segment may be worth the effort
Questions For Authors: I rarely update my review based on a response but you are welcome to respond to any portion of my review as you wish.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for taking the time to carefully read our manuscript and provide comments. We’re delighted you find the direction interesting and look forward to more work in this area.
We will happily add more clarification and intuition on the distinctions between accuracy and calibration, the notation we use, and, more generally, the main mathematical tools used in our work. The camera-ready allows a page of more space, and we will use it for this purpose. We will also add a discussion section that succinctly summarizes the implications of our work and fix these typos and color issues in the figure. | Summary: * This paper investigates multicalibration problems in performative settings.
* The models assume the performative prediction framework, where data distribution depends on the deployed model $(x,y)\\sim \\mathcal{D}(f)$.
* The main result is a convergence bound for the performative multicalibration loss, achieved through an online-to-batch reduction (Theorem 3.4). The result is modular, converting online learning algorithms with multicalibration guarantees into batch algorithms with performative multicalibration guarantees.
* Section 4 shows that predictors which are approximately performatively multicalibrated are also approximately performatively stable for the quadratic loss function. Finally, Section 5 presents a construction showing that perfectly multicalibrated classifiers can have the worst possible performance with respect to the quadratic loss.
## Update after rebuttal
Thank you for the clarifications, and I look forward to seeing the improvements in the next revision of the paper.
Claims And Evidence: Claims seem to be supported by theoretical evidence.
Methods And Evaluation Criteria: The paper does not contain an empirical evaluation.
Theoretical Claims: The proofs were checked at a high level. While the high-level structure appears sound, a meticulous examination can help provide additional verification.
Experimental Designs Or Analyses: The paper does not include any empirical experiments. Although this is common in theory-focused work, a simulated example or a practically motivated case study could help demonstrate the utility of the proposed framework.
Supplementary Material: No supplementary material was provided.
Relation To Broader Scientific Literature: The paper positions itself against classic results in the performative prediction literature, which typically rely on strong Lipschitz conditions. Here, the authors show that performative multicalibration is achievable under milder assumptions on the distribution map $\\mathcal{D}$.
Essential References Not Discussed: Key results in this area seem to be discussed.
Other Strengths And Weaknesses: Additional strenghts:
* The paper offers a novel convergence bound for performative multicalibration loss, providing a modular framework to bridge online and batch settings.
Additional weaknesses:
* The exposition is challenging to follow in parts, which may hinder accessibility.
* The absence of a practically motivated example or empirical demonstration limits the intuition behind the theoretical results, and the practical applicability of the findings.
Other Comments Or Suggestions: * Including a practical example or simulation would help illustrate the value of the proposed method compared to existing work, and build intuition about its theoretical and practical behavior.
* In addition, I wonder if the paper can benefit from an empirical demonstration of the results.
Questions For Authors: * Would the theoretical results still hold in a stateful performative prediction setting, such as the one considered in Brown et al.'s “Performative Prediction in a Stateful World” (AISTATS 2022)?
* Can you provide an example or simulation that demonstrates the practical advantages of your approach over traditional methods under the performative prediction framework?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We appreciate you taking the time to read and carefully critique our work. These are great questions.
Stateful world. We had not considered this possibility. We don’t believe it applies directly to the stateful case, but this is an interesting, open question for future work.
Also, given the additional space that comes with the revision, we’d happily include further discussion and comments to explain the main ideas behind the results and make the paper more accessible. We will also consider potential comparisons to previous algorithms and practical examples to illustrate how our ideas compare to previous approaches, with the caveat that previous approaches lack theoretical guarantees in our setting. | Summary: The paper at hand claims to explore the predictability of socil events. Social predictions do not merely describe the future. They also influence it. Such predictions can affect market prices, voter behavior, and policy outcomes. This interaction complicates the ability to forecast accurately. Early theorists, including Morgenstern and Simon, discussed these challenges extensively. This paper addresses these questions anew, using recent concepts from machine learning. Specifically, it utilizes the framework of "performative prediction," where predictions themselves shape outcomes. The authors establish that accurate forecasting of binary social events remains computationally feasible despite these dynamics. A key contribution is demonstrating the existence of predictors that remain accurate even as they actively shape events. These predictors satisfy strong conditions like multicalibration and outcome indistinguishability. Algorithms to achieve these conditions are presented, which are efficient both statistically and computationally.
However, the paper also identifies critical limitations. Although accurate predictions are always achievable, they might not always lead to desirable outcomes. Calibrated predictions may sometimes create poor social equilibria. Such predictions could, paradoxically, maximize prediction error measured in terms of performative risk. Thus, the paper shows a tension between accuracy and social desirability in forecasting social events. The authors conclude by suggesting a reconsideration of historical forecasting methods. They call for further research into what goals predictions in social contexts should ultimately serve.
Claims And Evidence: All technical claims are proven. My only concern is with the general, conceptual claim of the paper as stated in the title "Revisiting the Predictability of Social Events". I understand the authors want to relate to the famous article by Grunberg and Modigliani, but I think the title does oversell the paper a little bit. The paper does not answer the questions whether social events are predictable *per se*. The paper answers the question whether social events can be predictable if these predictions have performative effects on the population. The framework is the very specific (although without the strong Lipschitz-condition on the distributions mapping) original performative prediction setup (without e.g. more realisitic stateful world as in https://proceedings.mlr.press/v151/brown22a/brown22a.pdf)
Methods And Evaluation Criteria: This is a theoretical paper, so no experiments are needed.
Theoretical Claims: I did spend only 1-2 hours checking the proofs, but I did not find any errors.
Experimental Designs Or Analyses: no experiments, see above.
Supplementary Material: see answers on checking proofs.
Relation To Broader Scientific Literature: see above
Essential References Not Discussed: Discussion of https://proceedings.mlr.press/v151/brown22a/brown22a.pdf would be nice, since I consider this extension a much more realistic model of reality than the original performative prediction setup, see question below. But it is not strictly essential.
Other Strengths And Weaknesses: none
Other Comments Or Suggestions: typos:
"Converstion" → "Conversion"
"instatiating" → "instantiating"
"indistiguishability" → "indistinguishability"
"ℓ(p,y)=½(1−p)²" should be "ℓ(p,y)=½(y−p)²"
Questions For Authors: 1. conceptual question: I understand the results presented in this paper require much weaker conditions (e.g. no Lipschitzness of distribut. mapping, which in turn induces e.g. strong convexity of loss if I remember correctly?) than in the original performative prediction setup (2020 paper). So that's certainly a valid and substantial contributions of its own. In terms of conceptual results, however, I must admit that I do not find it surprising for a classifier to be multi-calibrated in a setup where it was shown before that it converges to a classifier that is close (in parameter space) to the performatively optimal one (thm. 4.3. in https://arxiv.org/pdf/2002.06673). Can the authors comment in more details on this relation?
2. Can the authors provide some intuitions why the results require *randomized* predictors, while readers are "encouraged to think of them as deterministic"?
3. For the main results (Thm. 3.4) the authors write: "The main difference here is that samples (xt, yt) are not drawn i.i.d from a fixed distribution D, but rather from the distribution (xt, yt) ∼ D(ft) induced by the predictions. Despite these differences, a similar strategy suffices." The authors then procede by presenting the results. Can they explain WHY this strategy suffices? Generally, I think the paper could benefit from some more motivation/explanation
4. Does Thm. 3.4 also hold for performative prediction in a stateful world (see reference above, i.e., in a setup where the distributions map is bivariate mapping from both predictions AND previous distributions)?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for taking the time to read and provide detailed feedback on our manuscript. It is very appreciated.
Re: Brown et al. 2022. This is an excellent paper. We mistakenly did not include it but will happily discuss it in the revision.
Re: Conceptual question. Thanks for raising this. Lipschitzness of the distribution map D() and strong convexity of the loss are distinct conditions. One does not imply the other. Also, as per the example in Miller et al ICML 2021, the bound from Thm 4.3 in Perdomo et al. can be vacuous in the sense that the other parameters (Lipschitz constant of the loss) involved make it so the bound is just the diameter of the space. Hence, even if the distribution map is lipschitz, it does not imply that stable and optimal classifiers are close in parameter space. Of course, none of these arguments apply in our setting since we make no regularity assumptions on D(). We thank you for raising it and will add further discussion on this point in the updated version.
Re: Randomized predictions. Randomization is, in general, necessary to guarantee performative calibration as per the example in Section 5. In particular, no deterministic prediction p in [0,1] has the property that E_{p}[Y] = p. One needs to randomize between different forecasts to achieve on average calibration. Our comment about near determinism was regarding the per-time-step predictions on the online algorithms. We see how this can be confusing and will clarify it. Thanks for bringing it up.
Re: Explanation. We will happily clarify what we meant regarding how martingale arguments developed in online to batch conversions for supervised learning settings are close to those we develop for the performative case.
Re: Stateful world. This is a great question that we had not considered. We don’t believe our results apply directly to the stateful case. However, it is an interesting question for future work.
---
Rebuttal Comment 1.1:
Comment: Thanks for your replies. Greatly appreciated! In particular, thanks for clarifying the relation between Lipschitz condition on D() and strong convexity condition on the loss in the initial perf. pred. paper. I got that wrong initially.
I agree that the stateful world setup might be interesting for future work, but is beyond the scope of this paper.
All in all, I think it would be almost insane not to accept this paper. | null | null | null | null | null | null |
Optimizing Social Network Interventions via Hypergradient-Based Recommender System Design | Accept (poster) | Summary: The paper studies interventions in the Friedkin-Johnsen opinion formation model. This model is defined by a graph in which each node has a fixed innate opinion and a time-dependent expressed opinion; the model is often used to study polarization and disagreement in networks from a mathematical angle. Many recent works studied interventions in this opinion formation model by considering optimization problems which *either* change the graph topology *or* the innate opinions of the nodes.
The submission's main contribution is to show that one can *simultaneously* optimize for the network topology *and* the opinions. This is done via gradient descent by considering the hypergradient; the main technical advantage here is that this allows to deal with the expressed opinions $y$ which are given by an equation system $Ay=s$ where $s$ is part of the input and $A$ depends on the graph topology.
Claims And Evidence: I think it is mostly fine, but the comparison with the work of Chitra and Musco is inappropriate. See my more detailed comments below.
Methods And Evaluation Criteria: The definition that was used for polarization in the experiments is non-standard by now. See my comments below.
Theoretical Claims: The theoretical derivations appear to be correct, but I did not check in detail.
Experimental Designs Or Analyses: See below.
Supplementary Material: No.
Relation To Broader Scientific Literature: I think the main contribution of optimizing opinions and graph topology simultaneously is definitely interesting and something I have not seen before. I appreciate these results. However, in terms of motivation, I think it could be improved (see below).
Essential References Not Discussed: Some more papers could be cited, see my comments below.
Other Strengths And Weaknesses: Strenghts:
* The theoretical results are interesting and a good contribution to the literature.
* The paper is easy to follow.
Weaknesses:
* The comparison with the Chitra and Musco paper in the experiments is somewhat misleading. The point of the Chitra and Musco paper was not to minimize the overall disagreement; instead, they proposed a model which proceeds in rounds, where the network administrator minimizes the disagreement and then subsequently the opinions converge. Their goal was to study how this particular process might lead to increased polarization. Thus, stating that the algorithm from the paper achieves better objective function values because it can simultaneously minimize over the graph topology and the opinions simultaneously is just not a meaningful comparison.
* Typically, papers in this domain give a model of interventions and then provide optimization algorithms. While the paper does give a quite general optimization approach, it would be better if there were concrete examples in which settings one would expect to optimize over the graph topology and the innate opinions simultaneously. I am also not convinced by the example in Section 4.1.1 because it uses a polarization-metric that is non-standard in the meantime.
* The paper is only evaluated on two datasets, only one of which actually corresponds to a social network. I was surprised that the DBLP dataset (which is a citation network) was used, given that platforms like SNAP make a lot of social network datasets available.
* There is no analysis on how quickly the gradient descent algorithm converges to an optimal solution.
**Update after rebuttal:** The authors have addressed several of my concerns in their rebuttal and thus I have increased my score. I still think that the optimization problems they study could be better motivated, though.
Other Comments Or Suggestions: * Recent papers in this line of work define the polarization as the variance of the opinions, i.e., $\sum_u (y_u - \bar{y})^2$ where $\bar{y}$ is the average opinion over all nodes. This is not the same as defined in the paper. Sometimes people do consider polarization as $\sum_u y_u^2$ but only if the average opinion is $0$, in which case both notions coincide; here, the assumption of mean-centered opinions is crucial but it is not made in the paper. I would find it more interesting if the paper could show results for this notion of polarization.
* The notation used in the paper is quite non-standard. Typically, the expressed opinions are referred to as $z$ and not as $y$. Also, what is $A$ in the paper is typically referred to as $I+L$ (identity matrix + Laplacian).
* There are quite a few references that could be added. For instance, recent works from Aris Gionis and Sijing Tu gave convergence analysis for gradient descent-based methods in the FJ model and also studied a similar setting with news agencies.
Questions For Authors: * Does your approach also work for the more common notion of polarization that I mentioned above?
* In what kind of model would it make sense that one can simultaneously impact the graph topology and the innate opinions?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank the reviewer for their feedback and constructive comments.
First, we would like to clarify one important point.
Our algorithm optimizes only over the network topology, i.e., the network weights $w$, but not the _innate_ opinions $s$.
The main optimization problem that we aim to solve, equation (3), has as decision variables
the weights $w$ and equilibrium _expressed_ opinions $y$.
Since $y$ is uniquely determined by the constraint (3b), we optimize over $w$ solely.
We could readily extend our framework to optimize for both $w$ and $s$ simultaneously, as suggested by the reviewer, but
this is not something that we investigate in this paper.
We will make sure to clearly elaborate on this point in our revised manuscript.
**Weakness 1** We thank the reviewer for their insightful comment.
Indeed, the main point of Network Administrator Dynamics (NAD) in Chitra \& Musco, 2020 is to show how minimizing disagreement can have adverse effects on polarization of opinions. They do have credits for raising this important and critical aspect of this optimization problem, which we will be more careful to acknowledge.
In this vein, our goal is to understand the mechanism by which NAD operates and, in turn,
demonstrate how our algorithm succeeds by using a different mechanism in the same problem setting.
We believe our comparison to be a meaningful one for two reasons:
1. The two algorithms operate in the same fashion: they both propose a model which proceeds in rounds, where the network administrator/leader minimizes the disagreement and then subsequently the opinions converge.
2. our algorithm manages to fix (some of)
the issues that Chitra \& Musco highlighted with NAD.
In fact, in their paper they also propose fixing NAD with NAD*, which we also include in our comparison results.
In essence, we provide a potential solution to one of the main issues raised by Chitra \& Musco.
We will try to clarify these distinctions and elaborate on these points on the revision of our paper by making sure we give Chitra \& Musco credits for raising a very important and critical aspect of this optimization problem.
**Weakness 2** Regarding the optimization of graph topology and innate opinions, please see our discussion above.
Regarding the polarization metric, we have rerun our simulations using the metric proposed by the reviewer
and will include them in the corresponding section.
We quickly summarize some of them: The reruns of Sections 4.1.2, 4.1.3, and 4.2 with the suggested polarization metric are close to our original results, as can be seen in Figure 1 and 2, and Table 1 on https://imgur.com/a/8GbzUNw.
Additionally, BeeRS decreases the polarization in Section 4.1.3 even further with the new polarization metric (-44\% compared to -39\%).
**Weakness 3** We thank the reviewer for their useful suggestion.
We have deployed our algorithm on the soc-LiveJournal1 dataset, which is the largest among the ones available in SNAP, and will include the results in the corresponding section. A preview of the results is available on https://imgur.com/a/8GbzUNw.
The collected results further confirm the effectiveness of our algorithm.
**Weakness 4** We acknowledge the reviewer's suggestion to analyze the rates of convergence of gradient descent.
We have performed an empirical analysis of the learning curves of our algorithm, namely objective vs. number of iterations,
as also suggested by reviewer pBeX; please refer to that response for more information.
Performing a theoretical analysis can be challenging due to the non-convexity of the problem and could potentially
require a paper on its own.
One such analysis, for example, is the classical result in [1, Ch. 1.2] which proves that _vanilla_ gradient descent
converges to an $\epsilon$-stationary point at a rate of $O(\epsilon^{-2})$, for the case of an unconstrained non-convex smooth optimization
problem.
To the best of our knowledge, convergence rates for projected gradient-descent with momentum on a non-convex objective is an open
problem.
We consider such theoretical analyses beyond the scope of our paper,
and reserve the investigation for future work.
**Other Comments or Suggestions 1** Our algorithm can deal with any differentiable objective function, including the one mentioned.
We collected new results for the proposed metric as mentioned above, with a preview available at https://imgur.com/a/8GbzUNw.
**Other Comments or Suggestions 2** We will highlight this difference in notation.
**Other Comments or Suggestions 3** Thank you for mentioning these works. They are indeed very relevant. We will cite them in the revised manuscript and make an accurate comparison.
**Questions** Please refer to our answers in **Weakness 2** and **Other Comments or Suggestions** for Question 1,
and to the first paragraph of our response for Question 2.
[1] Nesterov, Yurii. Lectures on convex optimization. Vol. 137. Berlin: Springer, 2018. | Summary: This paper investigates opinion polarization in social networks using a large-scale optimization approach to modify network interactions based on the Friedkin-Johnsen model. The authors propose a gradient-based algorithm designed to address this problem in a scalable and computationally efficient manner. Some empirical analysis results are presented to demonstrate the effectiveness.
Claims And Evidence: In general, this paper features a clear motivation of problem definitions and an intuitive proposed method, is generally well written. Assumptions are properly outlined and theoretical derivations are properly provided to motivate the proposed solution. In particular, I like the style that authors offer detailed derivations in Sections 2 and 3, which can offer a clear view on the conditions as well as prerequisites for their contents to be valid.
Methods And Evaluation Criteria: The proposed BeeRS algorithm is intuitive and well-motivated, backed by straightforward derivations. On the other hand, as mentioned by the authors in their experiments, "the superior performance of BeeRS comes at the price of an increased runtime", indicating that while the proposed hypergradient method can be time consuming. While this problem can be somewhat alleviated by GPU parallel computing, it could still be a problem given a large number of users or nodes.
Theoretical Claims: The main derivations are in the main body of the paper and I found them to be quite intuitive and clear.
Experimental Designs Or Analyses: Some empirical results are provided to demonstrate the characteristics of the proposed BeeRS method, including running time, GPU-aided computation, and the distribution of edge weights after optimization. However, it seems that the empirical analysis lacks a uniformed metric in terms of the performance, such as the direct illustration of the cost ($\phi$) and the performance tradeoff. In particular, only one real-world dataset DBLP is involved in the experiments, which can be insufficient in terms of validating the empirical effectiveness.
Supplementary Material: I took a glimpse of the Appendix, where authors include implementation details as well as some additional experiments, such as the hyperparameter study for $\alpha$.
Relation To Broader Scientific Literature: The paper extends existing literature on opinion dynamics and network interventions by formulating social network influence optimization as a scalable hypergradient-based optimization problem under the classical Friedkin-Johnsen model. The proposed hypergradient method can be of independent interest to other audience apart from the Social Sciences community.
Essential References Not Discussed: NA
Other Strengths And Weaknesses: Please see my comments above in terms of the experiments, in "Experimental Designs Or Analyses". In particular, experiments on additional real-world datasets are encouraged to comprehensively demonstrate the effectiveness of the proposed method.
Other Comments Or Suggestions: None
Questions For Authors: Please refer to my comments in terms of scalability, efficiency, and experiment comprehensiveness. In particular, please see my comments above in terms of the experiments, in "Experimental Designs Or Analyses". In particular, experiments on additional real-world datasets are encouraged to comprehensively demonstrate the effectiveness of the proposed method.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank the reviewer for the positive comments and their careful reading.
**Methods and Evaluation Criteria** The concern raised on "Methods and Evaluation Criteria" is a valid and important one.
Indeed, for problems/networks of huge dimensions our algorithm might face computational bottlenecks.
Nonetheless, our scheme could be adapted and improved in a number of ways to address such practical problems.
We outline some next:
1. We could further exploit the capabilities of GPU computation. In Subsection 4.1, we successfully solve a problem
with 3 million decision variables on a GPU that currently is not among the state-of-the-art (NVIDIA GeForce RTX 3060 Ti).
By using a more performant GPU, or even a cluster of them, we could definitely handle problems of even larger dimensions.
In fact, problems with hundreds of millions of decision variables are routinely solved with GPUs in the context of neural network training.
This flexibility is a significant advantage of our algorithm, emanating from the fact that it is a simple, first-order method.
(Similar to the ones used in neural network training.)
2. We could reduce the number of weights that we optimize over by employing appropriate heuristics
to identify the most important parts of the network,
introducing a tradeoff between solution quality and computational requirements.
Indeed, our algorithmic approach and our implementation allow the user to specify which
weights are immutable and which ones are variable.
One meaningful way to choose which weights to optimize (or which areas of the networks to affect) would be to use heuristics to quantify
the importance of nodes, and then optimize the weights of edges connected to these nodes.
For instance, we could use the degree of a node or, more generally, other centrality measures [1].
These approaches to choosing which weights to update are especially important since we, typically, do not want
to modify the weights too much as they affect the users' experience in the network.
3. We could update only a (randomly chosen) subset of the weights at each iteration, thus giving rise
to a stochastic/mini-batch version of our algorithm.
This is a GPU-friendly way of addressing problems with huge dimensionality.
[1] Bloch, Francis, Matthew O. Jackson, and Pietro Tebaldi. "Centrality measures in networks." Social Choice and Welfare 61.2 (2023): 413-453.
**Experimental Designs or Analyses/Question**
- We thank the reviewer for their suggestion to include additional datasets in our simulations.
Please note that in our original manuscript, beside DBPL, we have also tested our algorithm on the real-world Reddit Dataset.
Further, we have also deployed our algorithm on the soc-LiveJournal1 dataset,
and will include the results in our revised manuscript.
We summarize the results from our additional simulations in Figures 1-3, and Table 1 in https://imgur.com/a/8GbzUNw.
We highlight that soc-LiveJournal1 is one of the largest directed social networks on the SNAP platform with 4.8 million users and 69 million edges.
- We thank the reviewer for suggesting an empirical analysis with a uniformed metric.
We include an additional simulation where we study the objective $\varphi$ as a function of the iteratation $k$.
In particular, we deploy BeeRS on Problem (10) with the polarization metric suggested by Reviewer 5iEL. We use the Reddit, DBLP, and soc-LiveJournal1 datasets, and initialize every simulation i) with initial weights 0, and ii) with 4 additional random initializations. For the total of 5 simulations per dataset we plot the mean cost $\varphi$ with standard deviation as a function of the iteration $k$, as shown in Figure 3 on https://imgur.com/a/8GbzUNw. Please note that there is a large difference in cost between the reddit dataset and the other two datasets, which is explained by the much larger number of users in the latter ones.
We also rerun the simulations from Sections 4.1.2, 4.1.3, and 4.2 with the polarization metric suggested by Reviewer 5iEL on the additional soc-LiveJournal1 dataset, as can be seen in Figure 1, Table 1, and Figure 2 at https://imgur.com/a/8GbzUNw, respectively. | Summary: This paper proposes a novel method, Best Intervention for Recommender Systems (BeeRS), which provides a method of using the hypergradient to optimize connection weights in a social network for certain objectives (for example, reducing polarization). The paper models the social network via the Friedkin-Johnson (FJ) model, where each actor has a constant internal opinion and evolving external opinion that is updated and influenced by neighbors in the network. The problem is formulated as bilevel optimization problem, where the lower level models the opinion dynamics among users and the upper level models the recommendation algorithm (termed the “leader”) that adjusts network weights to achieve an objective. Numerical results show an improvement over IPOPT on runtime for the optimization problem. The algorithm is also compared to the Network Administrator Dynamics (NAD) algorithm on real world data from Reddit, and it shows improvement on both the change in polarization and change in disagreement (at the price of an increased runtime).
Claims And Evidence: The claims in the submission are supported by clear evidence. In particular, the experiments are comprehensive and show the improvement of BeeRS over the existing NAD algorithm.
Methods And Evaluation Criteria: The methods used generally make sense for the problem at hand. I do note some concerns about the practicality of the simulation being conducted (see Other Strengths and Weaknesses below), but overall the methods work well for the problem setup and assumptions.
Theoretical Claims: I did not verify the proofs of any theoretical claims.
Experimental Designs Or Analyses: The experimental designs do seem sound, and I especially appreciate the use of large, real-world datasets for the work.
Supplementary Material: I did not review the supplementary material.
Relation To Broader Scientific Literature: This work is a useful extension of existing work on social network interventions, specifically motivated by polarization and disagreement. The advantage of this work comes from the flexibility of the method, given that any differentiable objective can be plugged into the BeeRS algorithm.
Essential References Not Discussed: I am not aware of any essential references that were not discussed.
Other Strengths And Weaknesses: The primary strengths of this paper are in the problem formulation and algorithm construction. The paper provides a flexible framework for interventions on social networks. It is also written clearly and has thorough experiments to validate the claims that the authors make regarding the algorithm’s performance.
I think the primary weakness of the paper is a lack of connection back to real-world recommendation systems. While the paper does a good job of using real-world networks from DBLP and Reddit, it is difficult to see how the idealized “leader” in this setup translates to a practical multi-level recommender system that exists out in the wild on a social network. For example, in this work, the leader accomplishes goals by adjusting network weights between users, thereby changing how users influence one another. The paper states that such weights could represent the volume of content from one user that another sees or similar metrics. In practice, social media recommender systems work by ranking content to be seen by a user. How does a ranker system like that “adjust” the weights between users? Does it discount or boost the ranks of certain posts? Does it have to maintain an additional influence model that feeds into the ranking algorithm? This gap is not fatal to the paper, but to me it is a missing piece that makes the difference between a good paper and a great one.
Other Comments Or Suggestions: N/A
Questions For Authors: 1. How would weight adjustments work in a practical real world system? Consider for example a timeline ranking system on a network like Facebook or X.
2. Can the algorithm be further optimized for performance by considering updates in portions of the graph rather than updating the weights of the entire network? Perhaps there is some way to tell which areas of the network will be most influential for the objective overall (e.g. particularly influential users).
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We thank the reviewer for their positive evaluation and their constructive comments.
Concerning the weaknesses and questions raised by the reviewer:
**Question/Weakness 1** Thanks for pointing out this aspect. We foresee using the weights as a penalty (/boosting)
factor in a Weighted PageRank (WPR) [1] or EdgeRank [2] algorithm fashion.
These algorithms take into account the importance of both the inlinks and the outlinks of the pages and distribute rank scores
based on the popularity of the pages:
If the network leader (upper level) decreases the weight of the link from user A to user B then this translates into a penalty
for all the content shared from A which is a candidate to be visible to B.
The details of how this would be algorithmically handled, however, are out of the scope of this work and an interesting direction for future research.
**Question 2** We thank the reviewer for their suggestion. Indeed, our algorithmic approach and our implementation allow the user to specify which
weights are immutable and which ones are variable.
One meaningful way to choose which weights to optimize (or which areas of the networks to affect) would be to use heuristics to quantify
the importance of nodes, and then optimize the weights of edges connected to these nodes.
For instance, we could use the degree of a node or, more generally, other centrality measures [3].
These approaches to choosing which weights to update are especially important since we, typically, do not want
to modify the weights too much as they affect the users' experience in the network.
Another interesting way to optimize for performance is to randomly choose which weights to update at each iteration, giving rise
to a stochastic/mini-batch version of our algorithm.
This would be particularly helpful when dealing with networks of huge size.
[1] Xing, Wenpu, and Ali Ghorbani. "Weighted pagerank algorithm." Proceedings. Second Annual Conference on Communication Networks and Services Research, IEEE, 2004.
[2] EdgeRank: The Secret Sauce That Makes Facebook's News Feed Tick. techcrunch.com. 2010-04-22. Retrieved 2012-12-08.
[3] Bloch, Francis, Matthew O. Jackson, and Pietro Tebaldi. "Centrality measures in networks." Social Choice and Welfare 61.2 (2023): 413-453. | Summary: This paper proposes a gradient descent based method for modifying network weights towards an optimal (general) downstream performance metric, under the framework of Friedkin-Johnsons opinion dynamics. Experiments show significant improvement on computation time on large-scale real-world dataset.
## update after rebuttal
I have read all of the rebuttals, and would like to keep my current rating.
Claims And Evidence: Yes.
Methods And Evaluation Criteria: Yes.
Theoretical Claims: Not all, but those in Sections 3 and 4.
Experimental Designs Or Analyses: Yes.
Supplementary Material: No.
Relation To Broader Scientific Literature: This work has substantial contribution on top of the existing literature.
Essential References Not Discussed: I feel that the references being cited in the paper are relatively old. There are a few more recent papers working on similar topics - though none of them are as generalized as this work, but it would be nice to mention them since it would help further show the great contribution in this paper.
Other Strengths And Weaknesses: **Strengths**
This is a very nice paper on Friedkin-Johnson opinion dynamics, definitely among the best I have seen in a while. I especially like two things in this paper, the first one not even highlighted by authors themselves:
- It gets rid of the the symmetry assumption made the vast majority of papers working on FJ model. Previous works did so mainly because they needed the symmetry condition to derive the closed-form equilibrium state (i.e. (I+L)^-1 s), which is the basis for many further derivations. This work, however, starts by assuming the network to be directed, and cleverly avoids having to explicitly work with the closed-form solution by denoting it as y*(w). Prop. 2.1 is also good observation.
- It observes and successfully addresses a very important problem, which is that existing studies based on closed-form sensitivity analysis are very computationally expensive, since they usually involves inverting a gigantic matrix. This works elegantly solves this problem with gradient descent. It is also nice to see Assumption 2.2 which generalizes some of the specific performance metrics that people have been studying for years into a more general form.
**Weakness**
- The references being mentioned in "literature review" are mostly before 2020. This might give the readers an impression that the study of FJ model is less active in most recent years, which is not true. For example, [1, 2] involve a similar (albeit narrower) topic of sensitivity analysis on network weights. I encourage the authors to also include these more recent papers, which should further help highlight the broader contribution of this paper.
[1] On the Relationship Between Relevance and Conflict in Online Social Link Recommendations, Wang et al., NeurIPS 2023.
[2] Minimizing Polarization and Disagreement in the Friedkin–Johnsen Model with Unknown Innate Opinions, ArXiv, 2025.
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 very positive evaluation and their kind suggestions.
We will make sure to stress the advantage of considering directed networks in the paper and include the references suggested by the reviewer. | null | null | null | null | null | null |
Holes in Latent Space: Topological Signatures Under Adversarial Influence | Reject | Summary: The authors analyzes latent representations of several large language models (LLMs) under two main adversarial conditions: Extended Prompt Injection (XPIA) and backdoor sandbagging fine-tuning. To do this, the authors use persistent homology (PH) in order to capture the shape of data at multiple distance scales. The authors finds a handful of PH-based summary statistics (especially certain 0-bar and 1-bar birth/death times) cleanly separate adversarial vs. normal activations and also a layer progression, meaning that adversarial topological signatures become more prominent in deeper layers.
Claims And Evidence: The claims are well supported.
Methods And Evaluation Criteria: The paper does a thorough job of isolating different topological measures (e.g., births, deaths, persistence of 0D and 1D features) and pruning away correlated features to ensure that the classification is driven by genuinely distinct signals. Also, compares clean vs. poisoned multiple layers, and validates results via SHAP values. The methods make sense for the problem.
Theoretical Claims: There is no theoretical results in the paper.
Experimental Designs Or Analyses: The experiments are well designed.
Supplementary Material: The supplementary material provides empirical results and further discussion.
Relation To Broader Scientific Literature: Past research has used topological data analysis to study manifold geometry in smaller-scale networks or simpler embeddings. This paper extends those approaches to modern large language models, demonstrating that TDA can provide robust global and local insights on model representations.
Essential References Not Discussed: The references are well discussed.
Other Strengths And Weaknesses: This paper makes a strong case for the value of persistent homology and related topological tools in understanding both normal and adversarial LLM behavior. While computational challenges remain, and further testing against diverse adversarial techniques would be valuable, the authors approach represents a promising and rigorous direction in the interpretability and security of large language models.
Also, theoretical results would be interesting.
Other Comments Or Suggestions: Persistent homology can be computationally heavy for large point clouds. The paper addresses this by random subsampling, but that introduces sampling variability and may overlook substructures in bigger point sets.
Questions For Authors: No questions.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We sincerely thank the reviewer for their thoughtful and supportive feedback on our work.
We recognize that the **computational challenges** of persistent homology remain an inherent limitation, as noted by the reviewer. In response to a similar comment from Reviewer mgPH, we have conducted additional experiments using an alpha complex, and we provide the corresponding results and discussion there. While Ripser++ offers an accelerated approach for computing Vietoris–Rips persistent homology, the underlying computational complexity remains a fundamental characteristic of the method. As the reviewer notes, we address this challenge through random subsampling. In doing so, we rely on the theoretical guarantees established by Chazal et al. (2014, 2015\) and Cao & Monod (2022), which give the convergence of subsampled persistence diagrams to the full diagrams. Nevertheless, we acknowledge that subsampling introduces variability and the potential risk of missing certain structures.
Regarding the suggestion to explore **additional adversarial scenarios**, we appreciate this valuable perspective. As discussed above with Reviewer r5do, we note that the two adversarial influences we have examined are fundamentally different in nature, which seems to indicate that adversarial triggers produce consistent deformations in the activation space and highlights the robustness of persistent homology in distinguishing between distinct and vastly different types of adversarial stress.
Lastly, while our work does not include theoretical results, we would like to emphasize our **novel technical contributions**. These include not only the application of topological data analysis to the study of LLM activations but also the development of an element-wise local analysis of information flow within LLMs. This method provides a new tool for examining correlations between activations across layers.
Once again, we greatly appreciate the reviewer’s constructive feedback and their positive assessment of our work. | Summary: This paper conducts a detailed analysis of representations of LLMs using a “topological data analysis” tool. The analysis shows statistical differences between benign natural inputs and adversarial inputs in two scenarios: indirect prompt injection and “sandbagging” (fine-tuning backdoor).
Claims And Evidence: Frankly, it is unclear what this paper claims. The paper touches on the technical methodology and goes in depth on the statistical analysis. However, it does not properly motivate the problem or the tool. I believe there may be two main contributions that the paper can potentially claim.
The first claim is that the persistent homology (PH) analysis is an effective tool at detecting prompt injection attacks or a backdoor trigger. However, this claim is not properly supported; More specifically, I would like to see common metrics in detection problems like AUC, precision/recall, or true/false positive rates. The experiments only show that there is some difference in statistics computed on benign vs adversarial inputs.
The second claim would be that PH is a useful interpretability tool for LLMs. If this is the claim, then I would like to see more evidence showing its usefulness in general, beyond just the two very specific settings. Perhaps, connections to semantic meanings and practical use cases (e.g., counterfactual analysis that influences the LLM’s behaviors, etc.). I do not believe that the existing evidence sufficiently support this claim either.
Methods And Evaluation Criteria: One of the main weaknesses of the paper is in **explaining and motivating the methodology**. It is important to introduce TDA with fewer jargon and motivate it by examples. The current description does not explain why such representation of the data is important or how to interpret them. I can highlight a few concrete examples below:
> The persistence barcode is a collection of intervals summarizing the lifetimes of topological features that are born, evolve, and die as the filtration parameter evolves; each bar corresponds to a distinct topological feature with its starting/end point corresponding to its birth/death time. (p. 2)
>
This is a vague technical description of the “persistence barcode.” It also contains too much jargon and no motivation. What does “lifetime”, “birth”, “death” mean? How should I interpret them? Why do they matter?
> The mean death of 0-bars emerges as the first prominent feature” (p. 5)
>
It would be good to know what this “0-bars death” means.
> Interpreting the distributions of the barcode summaries for clean vs. poisoned data reveals that adversarial conditions typically yield fewer dimension-1 loops forming at later scales, yet persisting longer (p. 6)
>
What do “fewer dimension-1 loops” mean or entail?
Theoretical Claims: N/A
Experimental Designs Or Analyses: **Activation difference.** On L134 (“Throughout our experiments, we leverage their difference…), the authors introduce an important design choice without much explanation or ablation study. This choice seems reasonable, but it may be important to also consider the **activation after the data block alone** as it is not always known a prior the separation between the instruction and the data blocks for prompt injection.
**Removing highly correlated variables.** On L188, the authors state that “To refine the feature set, we apply crosscorrelation analysis to remove highly correlated variables, ensuring an efficient and informative representation.” Please explain more why it is necessary to do so? There are multiple steps in the analyses that seem arbitrary and not well-justified.
L252 is another example of a design choice that is not explained well: “we discard all features that have a correlation higher than a threshold of 0.5 with at least one feature present in the analysis, admitting a few more features in the blocks described above.” Why is this step necessary? What does it achieve?
Supplementary Material: I did not check the supplementary material.
Relation To Broader Scientific Literature: I believe that an interpretability tool as well as the problem setup of prompt injection and backdoor attacks are of great interest to the scientific community. However, the contribution of this paper is unclear in either domain.
The authors mentioned limitation of prior work in L106: “These limitations become apparent in adversarial and safety contexts, where detecting various attack types often relies on linear probes or shallow classifiers.” However, this does not explain limitations of the linear activation methods. If they work just fine, do we need to capture a more complex non-linear relationship?
Essential References Not Discussed: None that I am aware of.I am familiar with the prompt injection and adversarial machine learning literature, but not the topological data analysis.
Other Strengths And Weaknesses: Technical contribution. Apart from the previously mentioned weaknesses, I believe that the technical novelty of the paper is also limited. The technique is well-established in a different domain and is directly applied to activations of LLMs.
Other Comments Or Suggestions: **Presentation.** In Figure 1, I suggest adding some high-level explanations about axes of the plots and how people who are not familiar with PH or TDA can interpret them.
Questions For Authors: N/A
Code Of Conduct: Affirmed.
Overall Recommendation: 1 | Rebuttal 1:
Rebuttal: We appreciate the careful review of our work and would like to address several of the concerns raised.
## Motivation of the methodology (PH)
We acknowledge that our motivation for the use of PH in this context could have been more accessible. We address now *why such representation of the data is important or how to interpret them* and are happy to elaborate in our revision.
- **PH serves as a powerful multi-scale "topological lens," providing insights into the shape and structural complexity of data beyond conventional linear analyses.** Instead of treating LLM activations as distinct points in a high dimensional space, we take a multi-scale topological view by incrementally “thickening” them (see Figure 2). We allow a radius parameter to grow, akin to adjusting thresholds in hierarchical clustering or DBSCAN, to reveal how the activations connect to form structures across different scales. Initially, PH identifies clusters or connected components (0-bars), and tracks their formation (“birth”) and merging (“death”) as connectivity increases. As the radius grows, PH reveals higher-order structures such as loops (1-bars), which represent more complex, global interactions extending beyond standard clustering. The key output of PH is the **persistence barcode**, i.e. the collection of bars representing the “lifetime” of these structures from their "birth" to their "death".
- In our study, **PH interpretability helps analyze how adversarial conditions reshape the activation space**: A lower mean death time for 0-bars suggests adversarial activations cluster more tightly. Fewer late-stage 1-bars indicate reduced structural complexity.
## Clarification of claims
Our primary claim is indeed that **PH is a useful interpretability tool for LLMs** in adversarial conditions. We are not proposing PH as “an effective tool for detecting prompt injection attacks or backdoor triggers,” which would require additional work beyond our scope. The PCA and logistic regression in Section 4 serve as starting points to examine *why* separation occurs, not as detection methods.
Our claim is supported by two main facts:
1. PH barcodes summarize input shape, making them *inherently interpretable*. Section 4.2 is entirely devoted to this interpretation, analyzing shape differences between normal and adversarial activations.
2. PH reveals a *consistent topological deformation pattern* across two fundamentally different adversarial influences happening at different LLM processing stages. This suggests a general geometric effect in the representation space, which topological approaches can analyze in ways that existing methods cannot. Thus, PH offers a complementary perspective to behavior monitoring or attack-specific detection methods.
## Experimental design
We would like to clarify the two concerns raised by the reviewer, which we will include in the revision:
- **Activation difference:** We follow the TaskTracker dataset (Abdelnabi et al., 2024), which is specifically designed for activation-level analysis. We refer to the original paper for construction choices, re-justifying them is not within our scope. To address a key point: in this dataset, the user instruction and retrieved data block *are always available separately*, as retrieval happens after the instruction. This allows us to isolate the representational shift caused by adversarial content, which studying the data block alone would not capture.
- **Pruning highly correlated features** is a standard practice in statistics and ML to reduce redundancy and prevent overfitting. Given the strong correlations in persistence barcode statistics, removing them improves efficiency while retaining predictive power. A model that explains the same phenomenon with less variables is a more parsimonious one, thus more desirable.
## Technical novelty
We respectfully disagree with the reviewer and wish to emphasize the two technical novelties of our work.
- Applying PH to this type of data is neither straightforward nor well-explored, as noted by other reviewers. PH provides unique and mathematically grounded interpretability insights that transcend existing mainstream methods: *linear probes* assess linear decodability but miss latent space structure; *mechanistic interpretability* tracks causal pathways but lacks global analysis; and *representation engineering* (e.g., sparse autoencoders) captures local features but not topological invariants. Designing tests to directly compare these with PH is neither feasible nor meaningful, as they capture complementary and orthogonal aspects of the problem.
- Our local element-wise analysis of information flow within the LLM is an entirely new approach to understand nonlinear correlations between activations across layers. This represents a significant contribution, demonstrating that while PH is an established tool, its application to new domains can yield original methodologies and insights that help us better understand them. | Summary: In this paper, the authors propose a method to analyze the internal representations of LLMs using tools from Topological Data Analysis. They use Persistent Homology (PH) to show that a clear difference in the topology of the activations in an adversarial setting. They perform two sets of qualitative analyses - Global and local analyses using PH on two different sets of adversarial attacks - Extended Prompt Injection and Sandbagging. They showed using extensive experimentation that PH can be applied in the context of LLM to obtain interpretability.
Claims And Evidence: Yes, the claims are sufficiently supported by evidence.
Methods And Evaluation Criteria: The proposed methods make sense for the problem at hand.
I am not fully convinced by the local analysis using PH. The concern I have is as follows - considering the activations of consecutive layers as points in $\mathbb{R}^2$ and computing PH of the VR complex on this space does not seem motivated enough. This is primarily because each neuron in the following layer is a linear combination of the activations of the current layer. As a consequence, just considering a pair seems a bit weird. Moreover, this part of the paper seems more like reporting of results from certain experiments and does not seem well-motivated and the implications of the results are also not very well-discussed.
Theoretical Claims: The paper does not particularly make any theoretical claims.
Experimental Designs Or Analyses: Yes, the experiments seem sound and valid for the problems that the authors are tackling. I have already outlined the issue with the local analysis using PH in my answer in the previous section.
Supplementary Material: Yes. I went through Appendix A and B.
Relation To Broader Scientific Literature: This work presents a novel approach of using TDA in the context of LLMs. It showcases the need for topological analysis and also shows experimentally that topological information present in the activations is useful and can distinguish adversarial attacks. This opens up new research avenues in the intersection of TDA and LLMs.
Essential References Not Discussed: I do not think so.
Other Strengths And Weaknesses: Strengths:
I liked this idea of using TDA for a qualitative analysis to understand the working of an LLM.
Weaknesses:
The paper seems packed with a lot of information and I feel that it can be organized better to improve readability.
I felt like I needed to go back and forth from the main text to the appendices to get more details about the experiments. I understand that there are space constraints. For this, the authors might want to consider moving the entire section about local analysis to the appendix, because I do not fully see the big picture and the value that the local analysis is adding to the paper.
Other Comments Or Suggestions: Section 4.1 - The first sentence refers to Figure 3. I think that reference needs to be fixed.
Questions For Authors: Did you try $\alpha$-filtrations instead of VR filtrations, for local analysis? That would be faster than VR filtrations.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank the reviewer for the positive evaluation of our work and constructive feedback, which we now address.
## Clarification of the local analysis
**Element-wise analysis:** Indeed, our method differs from conventional approaches that analyze full activation vectors using cosine similarity or classifiers. Treating each dimension in the activation vector uniformly effectively averages over all neurons and potentially obscures localized or sparse but meaningful signals, which tends to happen when computing cosine distance, or using probes, which are typically linear classifiers. To avoid that, we analyze local, *element-wise* activation changes across layers by mapping pairs of activations $(a_i, b_i)$—for each neuron $i$—to coordinates in 2D that we use as input to compute PH.
**Nonlinear approaches:** We acknowledge the question of utility of nonlinear approaches (such as PH) given the high co-linearity between activations in consecutive layers but believe that linear dependencies do not take away from our analysis:
1. **Neural networks are not strictly linear**: While consecutive layers may exhibit high similarity, they are separated by nonlinearities. It is thus not entirely accurate to assume one layer is just a linear combination of the previous one.
2. **Our method detects deviations from co-linearity**: By projecting local, element-wise activations into 2D and analyzing them as point clouds, we can identify patterns such as clusters or cycles. The most structurally significant points in our point cloud intuitively correspond to neurons whose activations change the most between layers (i.e., diverge the most from the linear pattern). Thus, our method extends beyond linear analyses to capture nonlinearities.
Furthermore, while there is no guarantee that such nonlinear deviations are meaningful (they could be noise), our *local* analysis demonstrates otherwise. We show that the structure derived from these point clouds across consecutive layers can reliably distinguish between normal and adversarial activation patterns. This empirical result suggests that our method captures inherent structural differences that may be missed by conventional approaches.
## Further discussion on local analysis results
Our local analysis is not merely a reporting of empirical results but is grounded in the goal of understanding how activation patterns evolve across layers at a more granular level than conventional approaches. We emphasize that while our methodology does not establish a bijection between PH features and specific neurons or groups of neurons, our PH summaries offer valuable insights into the connectivity structure of neurons. For example, in Figure 10, our analysis of 1-dimensional total persistence reveals distinct shifts in network complexity captured between normal and adversarial activations through the prevalence and size of connected cycles. This observation is not trivial; rather, it underscores **how adversarial perturbations disrupt the structured information flow** that is otherwise regulated by the model.
Furthermore, our analysis provides a novel direction for identifying optimal layers within the network where maximal separability between normal and adversarial activations is achieved. This aspect of our work is particularly valuable as it contributes to a broader understanding of the information flow within LLMs, an area that has so far received limited exploration. We will clarify this in our revision.
## Readability
We acknowledge the reviewer's feedback regarding the readability and organization of the paper. In our revision, we will take the following steps to enhance clarity:
* Provide additional interpretation and discussion of key results, particularly focusing on the implications within our local analysis.
* Reduce back-and-forth between the main text and the appendix by integrating essential clarifications directly into the main text.
We believe that our local information flow analysis is a key contribution of this work and should remain in the main text.
## Computing alpha-filtrations
To investigate the performance of alpha-filtrations compared to Vietoris–Rips (VR), we compared runtimes for a pair of consecutive activation layers. Computing the VR PH took 5.9s, while PH from the alpha-filtration was indeed faster, taking 0.05s. We note that computing a sparse version of the VR complex lowers the runtime to 0.07s, comparable to the alpha-filtration.
Although there is a significant difference in runtime in favor of the alpha complex for the local analysis, this difference is not beneficial for the more intensive global analyses, due to the construction of the alpha complex in $\mathbb{R}^{4096}$ whilst VR benefits being constructed solely on the pairwise distances which can also be adapted to different metrics and offers a more intuitive geometric interpretation (in terms of complexes being constructed by diameter).
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Rebuttal Comment 1.1:
Comment: Thanks for providing the clarification. For the time-being, I would like to maintain my score. One of the main reasons being the readability aspect. I understand that it is difficult to explain multiple things within the page limit. I also believe the authors that they will work on the readability part. However, since I am unable to see those changes, I won't be able to increase the score. Thanks once again for all the efforts.
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Reply to Comment 1.1.1:
Comment: We sincerely appreciate the reviewer’s engagement with our work and the thoughtful feedback provided. We fully acknowledge the importance of readability and are confident that we can significantly enhance clarity within the additional page allowed for the revision.
With the additional space allowance, we will ensure that key aspects of our methodology and findings are communicated more effectively. We are committed to making our work readable and our contributions accessible without compromising depth.
We are grateful for the reviewer’s constructive feedback and look forward to presenting an improved version of our work. Thank you once again for your time and efforts in reviewing our submission. | null | null | null | null | null | null | null | null |
SynEVO: A neuro-inspired spatiotemporal evolutional framework for cross-domain adaptation | Accept (spotlight poster) | Summary: This work mainly focuses on observation, i.e., deep learning can imitate the neuroscience mechanism to expand the information boundaries through theoretically and empirically cross-domain collective intelligence learning. Then, drawing from neuroscience, this research introduces a synapse-inspired evolutional spatiotemporal network, which facilitates cross-domain knowledge sharing and aggregation. This approach involves three submodules: curriculum learning-based sample group ordering, complementary dual learners, and an adaptive dynamic coupler to capture common intelligence and cross-domain task-dependent patterns. Experiments show that collective intelligence increases the model's generalization capacity under both source and temporal shifts by at 0.5% to 42%, including few-shot and zero-shot transfer.
Claims And Evidence: Yes
Methods And Evaluation Criteria: Yes. The effectiveness of the proposed solution has been demonstrated by information theories and neuroscience principles with theoretical guarantee. Also, the extensive comparison and ablation studies show improvements against baselines and ablative variants on various datasets.
Theoretical Claims: Yes. In Appendix A, the author proves the correctness of Proposition 3.1 in section 3 based on the theories of information such as information entropy and mutual information, and I think that is roughly reasonable for the claim of Prop 3.1 (cross-domain learning to gain collective intelligence).
Experimental Designs Or Analyses: Yes. I think the experiment design can be the highlight of this research. The authors design various experiments to verify the effectiveness of such a framework, including designs on cross-source and cross-temporal domain learning for verifying whether enhancing collective intelligence, the comparison against mainstream existing models, and ablation studies for component disentanglements. In addition, three detailed analyses via three typical cases during training are also provided to better understand the framework working flows.
Supplementary Material: The supplemented experiments and detailed proof are well-provided.
Relation To Broader Scientific Literature: This paper contributes to the inter-disciplinary neuroscience, deep learning, and urban science fields. It develops the new techniques of an evolutionary deep learning framework to facilitate gaining collective intelligence among diverse urban data via a set of neuroscience principles, which is associated with the following literature.
a) Xu F, Zhang J, Gao C, et al. Urban generative intelligence (ugi): A foundational platform for agents in embodied city environment[J]. arXiv preprint arXiv:2312.11813, 2023.
b) Feng J, Du Y, Liu T, et al. Citygpt: Empowering urban spatial cognition of large language models[J]. arXiv preprint arXiv:2406.13948, 2024.
c) Bassett D S, Sporns O. Network neuroscience[J]. Nature neuroscience, 2017, 20(3): 353-364.
Essential References Not Discussed: I have not found any further references to be included.
Other Strengths And Weaknesses: Strengths:
1. A new and pioneering research problem for evolutional learning framework. This research provides a fresh perspective from neuroscience to facilitate the deep model generalization.
2. Valid techniques and solutions. The proposal focused on imitating the human learning process via various principles and improving the collective intelligence from different domains where similar but different sample groups are sequentially fed into the learning pipeline.
3. Good structure and experiments. This paper is well-structured with intuitive figure illustrations. The ingenious experiment designs can illustrate the proposal’s effectiveness.
Weakness:
1. In your experiment, since you use spatiotemporal data, why do you only design temporal adaptation and source adaptation while skipping spatial adaptation?
2. Several typos to be corrected, please see my ‘Other comments or suggestions’.
Other Comments Or Suggestions: 1. In Proposition 3.1, line 133 and Appendix A, line 557, there is a typo: ‘spatiotemporal’ instead of ‘spatiotemoporal’.
2. In Proposition 3.1, line 134-135, there is a typo: ’there must be shared’ instead of ‘the there must share’
Questions For Authors: 1. Since you use spatiotemporal data in your experiment, why do you only design temporal and source adaptation while skipping spatial adaptation?
2. Several typos to be corrected, please see my ‘Other comments or suggestions’.
Ethical Review Concerns: No ethical concerns.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Dear reviewer ci9Q,
We deeply appreciate the time and efforts you have invested in reviewing our paper. We are honored to receive your recognition of the novelty and theoretical contribution. Your comprehensive feedback is helpful in guiding our revisions.
**W1. Why skip spatial adaptation**
Urban space is relatively static. Over a long period of time, data distribution and data sources will switch and change, but urban space will remain relatively invariant. The change of urban space can be divided into two aspects: 1) the land use of urban space, e.g., the urban land increases. 2) the model transfer among cities. Actually, our research paper focuses on the same urban system, and the scenarios of urban space expansion and cross-city model transfer may be out of the research scope of this work. Instead, we mostly focus on the collective intelligence in the same system, i.e., the data temporal domain distribution shift or the source domain shift, which is more usual in real-world practices. We study the problem of how spatiotemporal learning models adaptively evolve with data by capturing commonality and transfer the regularities to new scenario, so as to achieve the ability of learning whenever new data arrives. For abovementioned urban expansion or cross-city transfer scenarios, we can still take the core idea of this work, reordering new sample groups and make the elastic container grow based on SynEVO to quickly optimize and fine-tune existing models, realizing rapid transfer across different spaces.
**W2&Q1Q2. A list of typos**
Thanks for your careful check of our paper and we have thoroughly corrected the spelling mistakes and typos. The detailed correction are listed as below.
1) Line 133 and 557, 'spatiotemoporal' -> 'spatiotemporal';
2) Line 134-135, 'the there must shre' -> 'there must be shared';
3) Line 380-381, 'signifcant' -> 'significant'.
Thanks again for your expert review of our paper and we will incorporate the discussions and supplement more close literature to facilitate the validness of our paper.
Authors of Paper 5506
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Rebuttal Comment 1.1:
Comment: I appreciate the authors for thoroughly addressing the previous concerns. Considering the author's rebuttals and the positive assessments from other reviewers, I confirm that I lean toward acceptance for this paper.
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Reply to Comment 1.1.1:
Comment: Dear Reviewer ci9Q,
We are extremely delighted to learn that you keep leaning toward acceptance for our work. Your positive evaluation and constructive insights have provided us with invaluable guidance for future research. We are truly grateful for your time and expertise in reviewing our work
Thank you once more for your generous support and recognition!
Authors of paper 5506 | Summary: This paper, theoretically examines strategies for increasing information boundaries through cross-domain collective intelligence learning and introduces SynEVO, a synaptic evolutionary spatiotemporal network designed to enable cross-domain knowledge sharing and aggregation by addressing model independence constraints. The comprehensive experiments including ablation studies and detailed analysis are provided.
## update after rebuttal
I appreciate the authors' response. I will maintain my positive score.
Claims And Evidence: Yes. The claims are well-supported with both theory principles and empirical experiments.
Methods And Evaluation Criteria: Yes. This proposal makes sense based on neuroscience and information theory of information bottleneck, which contributes to transfer learning and multi-task learning.
Theoretical Claims: Yes. In Appendix A, the author applicates the theory of mutual information and information entropy to measure the information in order to prove that the information is increasing during cross-domain adaptation which is claimed in Proposition 3.1. It seems OK for such proposition.
Experimental Designs Or Analyses: Yes. This research benefits from their thoughtful experimental designs on three folds. 1) Extensive dataset collection. The authors have collected spatiotemporal data with various domains from four cities, especially a large temporal scale set on SD from LargeST. 2) The cross-domain transfer design for model verification on its claims. 3) The detailed analysis on three aspects supplements more information on how the model operate in a micro and case-by-case perspective.
Supplementary Material: Yes. The proof of Prop 3.1 and additional hyperparameter sensitivity results are supplemented.
Relation To Broader Scientific Literature: This paper falls onto the application of both neuroscience and improvement of deep neural networks, which is inherited by complementary learning [1], and curriculum learning [2].
[1] McClelland J L, McNaughton B L, Lampinen A K. Integration of new information in memory: new insights from a complementary learning systems perspective[J]. Philosophical Transactions of the Royal Society B, 2020, 375(1799): 20190637.
[2] Matiisen T, Oliver A, Cohen T, et al. Teacher–student curriculum learning[J]. IEEE transactions on neural networks and learning systems, 2019, 31(9): 3732-3740.
But this work inherits such idea and improve it to spatiotemporal learning in several insights.
Essential References Not Discussed: No
Other Strengths And Weaknesses: Strengths:
1. This research paper is novel at new task definition on spatiotemporal cross-domain transfer among both temporal domain and source domain.
2. This paper is well-organized with clear problem, challenges and solutions, along with good figure illustration and detailed experiment designs.
3. The proposed techniques is overall novel and provide new insights into deep neural network designs with mechanisms of human brains.
Weaknesses
1. In line 149, the authors have mentioned ‘in harmony with diversity’, but this concept lacks explanations. I think you are required to elaborate this phrase to moderate the whole sentence and context.
2. In Section 5.6, the authors have mentioned that ‘domains from the same source are not necessarily next to each other in the ordered sequence S’, but this sentence is quite confused and requires efforts with further explanation.
Other Comments Or Suggestions: Actually, in Introduction part, how diverse aspects of human learning facilitate the deep neural network for cross-domain learning and transfers requires clarification in a holistic perspective.
Questions For Authors: 1. The authors should clarify more on ‘in harmony with diversity’ and ‘domains from the same source are not necessarily next to each other in the ordered sequence S’.
2. Please elaborate how diverse aspects of human learning facilitate the deep neural network for cross-domain learning and transfers requires clarification in a holistic perspective.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Dear reviewer n3PZ,
Thanks for your constructive feedback of our research. Your valuable advice contributes a lot to our work.
**W1&Q1(1). Explanations of 'harmony with diversity'.**
The concept of 'harmony with diversity' in our paper means that in order to build a generic spatiotemporal learning framework, there should be a certain degree of similarity (correlation) between sample groups or tasks, but they are not completely the same. To this end, a commonality learning container can be trained to capture the common patterns and enable distinguished representation learning from personal patterns. Then our learning framework can quickly transfer this commonality patterns to new tasks and obtain rapid generalization. We will supplement more clarification to improve the conciseness of such phrase.
**W2&Q1(2). Explanations of ‘domains from the same source are not necessarily next to each other in the ordered sequence S’ in section 5.6.**
This sentence means that the sample groups from the same source (intra-source sample groups) do not necessarily show greater similarity than sample groups of different sources (inter-source sample groups). This sentence is the interpretation and further discussion of Fig.3(a) in our paper. In the figure, we find sample groups [2,0], [2,1], [2,2] and [2,3] from the second source domain are between the first source domain samples [1,0] and [1,3], which indicates above phenomenon.
**Q2. Elaborate how diverse aspects of human learning facilitate the deep neural network for cross-domain learning and transfers requires clarification in a holistic perspective.**
Neuroscience reveals how brain structure impacts human cognitive and behaviors. The core of this paper is to design the learning process of cross-domain knowledge generalization by imitating neuroscience mechanisms from human brain. Specifically, our paper is divided into two aspects: **(1) curriculum learning** and **(2) synapse structure with elastic neural networks**.
**Curriculum learning** reveals the rule of human brain learning. People usually start to learn from simple tasks, and then learn to master more complex skills with increasing difficulty of learning tasks. Actually, the learning efficiency of such practice is higher than directly resolving new difficult problems [1,2]. To this end, task ordering from easy to difficult and the similarity between tasks are important to facilitate the transfer, which is emphasized in Sec.4.2 of our paper.
**Synapse structure.** From the perspective of human brain evolution, information in the human brain is transmitted through the **synapse structure**. This information passes through the synapse and forms an effective memory. At this time, if a new task needs to be learned, the stored information (i.e., memory in brain) becomes active, the presynaptic neurotransmitter will be released according to the correlation between tasks, so as to enable the original learned knowledge to be effectively transferred to learning process of new task. Thus, the long-term stable memory and new knowledge learning can supplement with each other, i.e., memory is transferred to empower learning while learning (mastering knowledge) expands and enriches the content of memory.
Thanks again for taking time to review our paper and we will incorporate above deeper analysis and explanations of concepts into our paper.
[1] Wang X, Chen Y, Zhu W. A survey on curriculum learning[J]. IEEE transactions on pattern analysis and machine intelligence, 2021, 44(9): 4555-4576.
[2] Blessing D, Celik O, Jia X, et al. Information maximizing curriculum: A curriculum-based approach for learning versatile skills[J]. Advances in Neural Information Processing Systems, 2023, 36: 51536-51561.
Authors of Paper 5506 | Summary: Drawing from neuroscience, this paper presents a theoretical investigation into methodologies for expanding information boundaries via cross-domain collective intelligence learning. The authors propose SynEVO, a synaptic evolutionary spatiotemporal network architecture. The framework employs a sample order reorganization strategy to emulate curriculum learning processes observed in human cognition, coupled with the implementation of two synergistic learning components, where these modules can cooperate with each other to enable model evolution and maintain a clear separation among domain-specific characteristics. The experiments are conducted to verify the effectiveness of the proposal.
Claims And Evidence: Yes. Most of them are clear. But in Lemma 1 (Eq.(8)), are there any references to support such Lemma, and then how to derive the Eq.(10)?
Methods And Evaluation Criteria: Yes. The proposed method seems make sense and resolve the issue of gaining collective intelligence in cross-domain transfer tasks for urban prediction.
Theoretical Claims: Yes. The author proves Proposition 3.1 shows that the collective intelligence can be obtained by deriving the larger information entropy via mutual information computation.
Experimental Designs Or Analyses: Yes.
1) The authors make comparison among baselines like STGCN, STGODE.
2) The author performs ablation studies to uncover the significance of each module (REO, Ela, PE) and display the results in Table 4.
3) The author makes some detailed analyses, including analyses of sample group sequences, observed quick adaptation via loss behavior and effective zero-shot adaptation.
Supplementary Material: Yes. The supplementary material of proof and hyperparameter analysis are provided in Appendix.
Relation To Broader Scientific Literature: This research involves the neuro-related learning into spatiotemporal forecasting, which I think is related to brain-inspired continual learning and complementary learning systems for collecting and gaining collective intelligence. The related researches can be found as below,
1)Van de Ven G M, Siegelmann H T, Tolias A S. Brain-inspired replay for continual learning with artificial neural networks[J]. Nature communications, 2020, 11(1): 4069.
2)Wang L, Zhang X, Su H, et al. A comprehensive survey of continual learning: Theory, method and application[J]. IEEE Transactions on Pattern Analysis and Machine Intelligence, 2024.
3)Wang L, Zhang X, Yang K, et al. Memory replay with data compression for continual learning[J]. arXiv preprint arXiv:2202.06592, 2022.
Essential References Not Discussed: There must be some references for citation associated with Lemma 1.
Other Strengths And Weaknesses: Overall, this research is somewhat novel with key insights of both neural network designs and how to learn from human knowledge acquiring mechanism. In detail, I found the detailed technical strengths as below,
1.The authors devise a sample group learning order via gradients similarity, diving into the essence of how the deep network updates, thus imitating the learning process from easy to difficult.
2.The authors imitate neuron learning scheme to catch the shared commonality and information among data contents which is essential to cross-domain adaptation.
3.The constructed dual learners (elastic common container and personality extractor) cooperate with each other are relatively novel, where it includes a common container to catch the commonality and a personality extractor to judge the difference, reducing the pollution of inappropriate data. This structure reflects the idea of cooperation and complementary.
Weaknesses
1.LLM is popular nowadays, why not try to applicate it to empower your model?
2.Spatiotemporal data can be divided into spatial data and temporal data. However, I didn’t see the analyses or experiments of the term of spatial. For example, cross-spatial domain adaptation ought to be performed.
3.Some confused equations, e.g., How can you derive Eq (8), is there any supports for it?
Other Comments Or Suggestions: -Please show more explanations or analyses of the relationship between neuroscience and transfer learning in your paper since it’s not clearly clarified in the submission.
-How can you derive Eq (8), is there any supports for it?
Questions For Authors: 1.Why gradients can determine the training order? Please show some more reasons.
2.Please show more explanations or analyses of the relationship between neuroscience and transfer learning in your paper since it’s not clearly clarified in the submission.
3.How can you derive Eq (8), is there any supports for it?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Dear reviewer esVG,
Thanks for your constructive comments on our research.
**W1. Why not use LLM?**
LLM is popular to empower diverse applications but it is more specific to language processing and generation tasks. The reasons for not using LLM in this research are two-fold.
(1) The core of this research is data-adaptive model evolution, which is essentially a new training paradigm. Our model can be coupled with other deep learning models to achieve efficient data-adaptive model updates. This research is orthogonal to the study of large models.
(2) In fact, studies have demonstrated that smaller models are more suitable for numerical series-level predictions [1], while LLMs tend to excel in language generation tasks including question&answer [2] and planning [3].
In the future, it is interesting to take LLM as an agent to facilitate the learning process and then guide and schedule the adaptation and evolution process. Thanks again for your insightful question.
**W2. Why skip cross-spatial domain adaptation?**
Thanks for your valuable question. We list the reasons in the **W1&Q1 response to Reviewer ci9Q**
**W3&Q3 How to derive Eq.(8) and from Eq.(8) to Eq.(10)**
Our analysis is based Ref.[4] and [5].
Ref.[4] proposes an exponential model of the transmitter release probability:
$P_r=1-e^{[Ca^{2+}]^n/K}$
where K combines parameters such as calcium binding rate and vesicle fusion efficiency, which affect information absorption in synapses. This formula explains the randomness of the combination of calcium ions with synaptotagmin.
After that, Ref.[5] directly measured the relationship between calcium concentration and transmitter release rate, and verified the applicability of the above exponential model. Finally, we reduce ${{[{Ca}^{2+}]}^n/K}$ to a variable $\tau$ to obtain Eq(8).
In our task reordering module, tasks are ordered from easy to difficult, by ranking the gradient from small to large. Since the smaller the dropout factor p, the more active the model is and the easier to achieve difficult tasks, our dropout factor p needs to decrease as the gradient gets larger. Hence, we can achieve Eq.(10). We let the exponent be $l(d_c)-d_{max}$ to make $0<p_c(d_c)\le1$.
**Q1.Why gradients determine the order?**
For each parameter w in the neural network, each step of parameter update is related to its own gradient, i.e.
$W_k=W_{k-1}-\eta\nabla_k W=W_{k-1}-\eta∂E/∂W$
where $W_k$ is the parameter of k-th step, $\eta$ is the learning rate, $\eta∂E/∂W$ is the gradient of training loss to W.
From the equation above, we can see that the closeness of the model to learning samples (data) can be described by the gradient of each iteration. Larger gradients indicate the current model is farther from the real function which perfectly fits the data, then the learning process is harder. To this end, gradients can determine the training order of sample groups.
**Q2. Relationship between neuroscience and transfer learning**
The goal of transfer learning is to effectively transfer the knowledge of model A to a relevant task B. During the process, similarity counts. Based on theories of curriculum learning, humans master skills better when learning from easy to hard. During the learning process, similarity also exists between tasks. From the perspective of human brain evolution, information is transmitted through synapses in the human brain. This information passes through the synapse and forms a long-time stable memory. When facing similar new tasks, the brain releases presynaptic neurotransmitters based on the similarity between tasks, transferring the original knowledge to the new task. During the process, memory and learning can complement with each other, i.e., new well-learned knowledge can be expanded into memory, while existing memory can be retrieved when new knowledge is being learned.
We are truly grateful for your meticulous review and constructive comments on our manuscript. They have significantly contributed to enhancing the clarity and rigor of our work. We will add above deeper discussions into our next version.
[1] Tan M, et al. Are language models actually useful for time series forecasting?[J]. Advances in Neural Information Processing Systems, 2024, 37: 60162-60191.
[2] Feng P, et al. AGILE: A Novel Reinforcement Learning Framework of LLM Agents[C]//The Thirty-eighth Annual Conference on Neural Information Processing Systems.
[3] Ni H, et al. Planning, Living and Judging: A Multi-agent LLM-based Framework for Cyclical Urban Planning[J]. arXiv preprint arXiv:2412.20505, 2024.
[4] Bertram, Richard, Arthur Sherman, and ELIS F. Stanley. "Single-domain/bound calcium hypothesis of transmitter release and facilitation." Journal of Neurophysiology 75.5 (1996): 1919-1931.
[5] Schneggenburger, Ralf, and Erwin Neher. "Intracellular calcium dependence of transmitter release rates at a fast central synapse." Nature 406.6798 (2000): 889-893.
Authors of Paper 5506
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Rebuttal Comment 1.1:
Comment: I appreciate the authors for addressing my concerns in detail, and I decided to raise my score.
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Reply to Comment 1.1.1:
Comment: Dear Reviewer esVG,
We are truly grateful for your thoughtful evaluation and for increasing the score for our work. Your valuable feedback and recognition mean a great deal to us, and we are truly honored by your appreciation. We will continue to strive for excellence in our research and contributions to the field.
Thanks again for your time and effort in reviewing our work!
Authors of paper 5506 | Summary: This paper introduces SynEVO, an interesting neuro-inspired spatiotemporal evolutional framework designed for cross-domain adaptation in spatiotemporal learning. The core idea is to enhance knowledge transfer and model evolution by mimicking synaptic plasticity and neurotransmitter mechanisms from neuroscience.
Claims And Evidence: Most claims are well-supported by theoretical and empirical evidence:
1. Cross-domain learning increases information capacity – Supported by information-theoretic proof.
2. SynEVO improves generalization – supported by experiments on four datasets, though results may be dataset-dependent.
3. Superior efficiency (21.75% memory cost) – GPU usage comparisons validate this.
4. Neuro-inspired synaptic evolution – Conceptually compelling and very intersting.
Methods And Evaluation Criteria: 1. Evaluation is robust, utilizing four real-world datasets (NYC, CHI, SIP, SD) and standard metrics (MAE, RMSE, MAPE) with comparisons against strong baselines.
2. Ablation studies validate key components, but broader application and more analysis of training efficiency would strengthen the evaluation.
Theoretical Claims: The author presents an information-theoretic perspective, which is both interesting and novel.
Experimental Designs Or Analyses: The use of four real-world datasets (NYC, CHI, SIP, SD) provides a diverse and realistic evaluation.
Metrics such as MAE, RMSE, and MAPE are standard for assessing spatiotemporal prediction accuracy.
Ablation studies effectively isolate contributions of key components.
However, given the general nature of the approach, incorporating additional tasks could further strengthen the study.
Moreover, related areas such as transfer learning, optimizer design, and even evolutionary algorithms offer valuable directions for discussion. A more thorough theoretical and empirical analysis could enhance the justification for the paper's design choices. Nevertheless, the overall contribution is good.
Supplementary Material: NA
Relation To Broader Scientific Literature: This paper is inspired by neuroscience, particularly ideas related to how the brain gradually learns and adapts by evolving its connections over time. Similar principles have been explored in studies on how humans accumulate knowledge and transfer learning across different tasks. The proposed approach also relates to continual learning in LLM/VLM, especially with the rise of large models. As models are increasingly required to adapt to new tasks without forgetting previous knowledge, frameworks like SynEVO offer a potential way to improve long-term adaptation and efficient knowledge retention.
Essential References Not Discussed: NA
Other Strengths And Weaknesses: see above
Other Comments Or Suggestions: see above
Questions For Authors: NA
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Dear reviewer Nb7e,
Thanks for your encouraging comments!
**Relations between SynEVO and transfer learning, optimizer design, evolutionary algorithms**
**Transfer learning** is also a freeze-finetune mechanism where finetune is varied and specific to the problem itself. It does not involve active evolutions under different data distributions, while for SynEVO, it actively and continuously evolves by updating parameters when new data comes.
**Evolutionary algorithm** tends to evolve by adaptive fusion among peer models. It can be viewed as a passive evolution, while SynEVO updates spontaneously according to data.
**Optimizer design** includes various gradient-based adaptiveness and regularizations. In our work, we take gradients to measure correlations between model and data. We let it reorder sample groups to imitate curriculum learning of brain. Besides, we enable the regularization coefficient $\lambda$ to change dynamically with increasing learning capacity. These schemes are devised for easy optimization in our evolution contexts.
**Detailed empirical analysis and training efficiency**
**(1) More empirical analysis on task reordering.**
We supplement the experiments of reordering tasks from **hard to easy** to emphasize the importance of training order. The results of errors are listed in the order of MAE/RMSE/MAPE.
NYC: 7.217/18.807/0.415, CHI: 1.632/3.066/0.405;
SIP: 0.705/1.394/0.208, SD: 11.636/19.789/0.163.
The reversed order falls into inferior performances, which emphasizes the significance of reordering the tasks from easy to difficult in our design. Moreover, above hard-to-easy performances are better than random ordering of SynEVO-REO, which may be attributed to common relations between neighboring tasks as they are ordered even the reverse one.
**(2) Design of commonality extraction.**
a) If iterative learning for commonality removed, only train and test on one dataset. Results are listed in order of MAE/RMSE/MAPE:
NYC: 8.201/19.090/0.423, CHI: 1.554/2.887/0.385;
SIP: 0.711/1.412/0.216, SD: 13.128/20.890/0.220.
b) We set a different neural expansion rate $p_c$, e.g., $p_c=p_0/l(d_c)$
NYC: 7.213/16.310/0.422, CHI:1.550/2.765/0.367; SIP: 0.705/1.399/0.207, SD:11.944/19.599/0.168.
With above results, we can conclude our commonality learner and the setting of p are reasonable and empirically justified.
**(3) Training efficiency.**
Our training process can be 4 parts. I. Model warm-up with existing data. II. Complementary dual learners with elastic common container. III. Contrastive learning to obtain distinguished patterns. IV. Couple elastic common container and personality extractor to train on new data.
**Comparison.** On NYC, the above 4 parts cost about 800s, 795s, 545s and 111s respectively and the total time cost is about 2251s. The total time costs of baselines: AGCRN:1896s, ASTGCN:1884s, GWN:2233s, STGCN:823s, STGODE:3515s, STTN:1910s, CMuST: 2817s. Given increased generalization capacity (MAE reduced 42% at most) and inference efficiency (GPU cost reduced 78% at most), thus training costs are tolerable. Specifically, in our ablation studies, we can further confirm the importance of each module as shown in Tab.4.
**Further theoretical analysis**
**(1) Information theory.** Based on Appendix A, collective intelligence within a system increases with the input of data, i.e.,
$H(X_i|X_1,X_2,\ldots,X_{i-1})> H(X_{i+1}|X_1,X_2,\ldots,X_i)$
Thus, we can take full advantage of the collective intelligence in the system to empower task generalization.
**(2) Synaptic structure** is the medium of information transmission in human brain. The probability of synaptic neurotransmitter release can be defined as, $P_r=P_0(1-e^{-\tau})$, $\tau$ is the successive activeness difference between apre-synaptic-neuron and after-synaptic-neuron.
Since the probability is exponentially correlated with the parameter $\tau$, we envisage placing the gradient in an exponential position to map it. In task reordering, the tasks are ordered by gradients from small to large. Considering that decreasing dropout factor $p$ increases model activeness and enhancing its ability to cope with complex tasks, we further deduce Eq.(10). Meanwhile, we let the exponent be $l(d_c)-d_{max}$ to ensure $0<p_c(d_c)\le1$.
**Broader application.**
Our model can be generally nested within other neural networks. For example, in geological prospecting, the available shallow-layer data and precious deep-layer information share both commonality and personalization. It is applicable to utilize our evolvable "data-model" collaboration to decouple the invariant and variable patterns, and reconstruct the OOD distribution with new patterns. More broadly, our solution can also be extended to dynamic systems such as molecular interactions, agent collaborations, with necessary adaptation.
Thanks again for your advice and we will include additional results and discussions into our next version.
Authors of Paper 5506 | null | null | null | null | null | null |
GraphCL: Graph-based Clustering for Semi-Supervised Medical Image Segmentation | Accept (poster) | Summary: In this work, the authors tackle semi-supervised medical image segmentation (SSMIS) by proposing GraphCL. This is the first work to model data in a graph network for SSMIS. The authors propose a graph clustering loss function for optimization.
Claims And Evidence: Yes
Methods And Evaluation Criteria: - The authors introduce a k-less strategy for clustering (k = number of clusters), enabling similar nodes to automatically form clusters.
- They follow a teacher-student framework, the outputs of which are used to construct the graph data structure. The graph loss-function is used to train the whole framework in an end-to-end fashion.
- The different components of the method are well-motivated
Theoretical Claims: N/A
Experimental Designs Or Analyses: - The authors compare with adequate baselines, which are state-of-the-art methods in SSMIS task. They compare across three publicly available medical image seg datasets. They conduct experiments under different unlabeled % data settings as well.
- The authors use 4 metrics (Dice, Jaccard, HD, ASSD) to evaluate the segmentation quality. The authors' proposed GraphCL outperforms all the baselines.
- The standard deviation of the performance is missing, however. The authors would benefit by showing standard deviation and conducting t-test to determine if the performance improvement is statistically significant or not.
- The authors provide good ablation studies of the different components in their method.
- Appreciate the code release in the supplementary.
Supplementary Material: Yes, I reviewed the entire supplementary.
Relation To Broader Scientific Literature: The current work has real-life applications as medical datasets tend to have few labeled and largely unlabeled data. As the authors' work outperforms existing SSMIS methods, it has relevance to the community.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: N/A
Other Comments Or Suggestions: N/A
Questions For Authors: none.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for your thorough review and constructive feedback on our manuscript. We are grateful for your positive remarks and are pleased that you found our work to be a valuable contribution to the field of semi-supervised medical image segmentation.
>Q1: The standard deviation of the performance is missing, however. The authors would benefit by showing standard deviation and conducting t-test to determine if the performance improvement is statistically significant or not.
A1: Thank you for your valuable feedback. We appreciate your suggestion regarding the inclusion of standard deviation and statistical significance analysis. Since we have four metrics: Dice, Jaccard, 95HD, and ASD, where Dice and Jaccard indicate that higher values are better, while 95HD and ASD indicate that lower values are better, it is not possible to compute the standard deviation as suggested by the reviewer because these four metrics represent different meanings. Consequently, since the standard deviation cannot be computed, the t-value also cannot be calculated. We sincerely appreciate the reviewer’s suggestion from a statistical perspective. Thank you for this constructive suggestion that has helped improve our work.
---
Rebuttal Comment 1.1:
Comment: The standard deviation needs to be computed for each metric separately, not across metrics. If there are N test samples, the Dice score is a = avg(dice of N samples) while Stddev is b = stddev(dice of N samples), and so you can report a $\pm$ b. You can do this for your method and the baseline and compute t-test between the two methods. This would need to be done for each metric separately.
---
Reply to Comment 1.1.1:
Comment: Thank you for your valuable feedback. We sincerely appreciate your attention to the statistical rigor of our analysis. We have carefully revised our method to address your concerns.
We conducted five repeated experiments for both the baseline method BCP and our method GraphCL. Each method yielded five experimental results. We calculated the sample standard deviation and t-values for these results and presented them in Table 1 to Table 4, and Table 1 to Table 4 show the sample standard deviations and t-values calculated for the metrics Dice, Jaccard, 95HD, and ASD, respectively. By consulting the t-distribution tables, we can conclude that the performance improvements for each metric are statistically significant.
| Dataset | Labeled | Unlabeled | std（BCP/GraphCL） | t-test value | Statistically Significant |
|--------------|----------|----------|-------------------|-------|---------|
| LA | 4（5%） | 76（95%）| 0.136/0.123 | 22.53 | Yes |
| | 8（10%） | 72（90%）| 0.114/0.176 | 23.22 | Yes |
| ACDC | 3（5%） | 67（95%）| 0.267/0.142 | 15.33 | Yes |
| | 7（10%） | 63（90%）| 0.111/0.214 | 5.02 | Yes |
| Pancreas | 12（20%）| 50（80%）| 0.105/0.196 | 20.86 | Yes |
|Dataset | Labeled | Unlabeled | std（BCP/GraphCL） |t-test value |Statistically Significant |
|--------------|----------|----------|-------------------|-------|---------|
| LA | 4（5%） | 76（95%）| 0.085/0.164 | 31.56 |Yes |
| | 8（10%） | 72（90%）| 0.158/0.034 | 20.08 | Yes |
| ACDC | 3（5%） | 67（95%）| 0.042/0.044 | 99.2 | Yes |
| | 7（10%） | 63（90%）| 0.025/0.424 | 4.81 | Yes |
| Pancreas | 12（20%）| 50（80%）| 0.028/0.027 | 146.6 | Yes |
| Dataset | Labeled | Unlabeled | std (BCP/GraphCL) | t-test value | Statistically Significant |
|-------------|------------|--------------|-------------------|----------------|----------------------------|
| LA | 4 (5%) | 76 (95%) | 0.042/0.011 | 86.6 | Yes |
| | 8 (10%) | 72 (90%) | 0.048/0.044 | 28.6 | Yes |
| ACDC | 3 (5%) | 67 (95%) | 0.045/0.036 | 253.1 | Yes |
| | 7 (10%) | 63 (90%) | 0.034/0.033 | 118.6 | Yes |
| Pancreas | 12 (20%) | 50 (80%) | 0.030/0.062 | 43.2 | Yes |
| Dataset | Labeled | Unlabeled | std (BCP/GraphCL) | t-test value | Statistically Significant |
|-------------|------------|--------------|-------------------|----------------|----------------------------|
| LA | 4 (5%) | 76 (95%) | 0.032/0.019 | 3.21 | Yes |
| | 8 (10%) | 72 (90%) | 0.048/0.044 | 28.6 | Yes |
| ACDC | 3 (5%) | 67 (95%) | 0.019/0.006 | 185.6 | Yes |
| | 7 (10%) | 63 (90%) | 0.007/0.005 | 173.7 | Yes |
| Pancreas | 12 (20%) | 50 (80%) | 0.004/0.006 | 70.6 | Yes |
Thank you again for your constructive suggestion, and we welcome any further suggestions. | Summary: This paper introduces a graph-based clustering for semi-supervised medical image segmentation by modeling data structure in a unified network. A graph clustering loss function was proposed to optimize the correlation clustering task in SSMIS.
Claims And Evidence: The authors claim that 1) previous methods neglect the importance of graph structural information, and 2) no research has explored semi-supervised medical image segmentation (SSMIS) from the perspective of data structure. However, they do not specify what graph structural information can be utilized or explain why it is crucial. This claim is not well substantiated, as the incorporation of GCN into the framework yields only a modest performance gain, suggesting that graph structural information may not be as critical as the authors suggest. Regarding the second claim, there are existing works that have explored the use of graphs in semi-supervised medical image segmentation.
[1] Sun, Junxiao, et al. "Semi-supervised medical image semantic segmentation with multi-scale graph cut loss." 2021 IEEE International Conference on Image Processing (ICIP). IEEE, 2021.
[2] Li, Gang, et al. "Dynamic graph consistency and self-contrast learning for semi-supervised medical image segmentation." Neural Networks 184 (2025): 107063.
Methods And Evaluation Criteria: Incorporating a graph into the SSMIS framework is a viable approach. However, the lack of a high-level explanation and sufficient technical details raises questions about whether the proposed method will have a significant impact on the problem at hand.
Theoretical Claims: N/A
Experimental Designs Or Analyses: The experimental design seems acceptable overall. However, the significant variation in hyperparameters across datasets raises concerns about the method’s generalizability and its usability across different applications.
Supplementary Material: Yes, I read the related work section in the SM.
Relation To Broader Scientific Literature: The paper addresses an area of active research in semi-supervised medical image segmentation, which has been well-explored. Methods like MT, UA-MT, DTC and co-training-based methods, have already demonstrated effective results in this domain. However, the approach proposed in this paper is based on MT with GCN-based regularization, offering limited innovation in terms of methodology or application. The performance gains appear to be marginal, and as such, it is unclear whether the proposed method can substantially advance the field. A clearer demonstration of its advantages over existing approaches would help establish its novelty and relevance.
Essential References Not Discussed: Since the proposed method targets SSMIS, I recommend reviewing related papers in more detail. For instance, co-training is a significant approach in SSMIS, but relevant papers are not discussed.
Other Strengths And Weaknesses: 1. In the abstract, it is stated that 'The proposed GraphCL model enjoys several advantages. Firstly, to the best of our knowledge, this is the first work to model the data structure information for semi-supervised medical image segmentation (SSMIS). Secondly, to get the clustered features across different graphs, we integrate both pairwise affinities between local image features and raw features as inputs.' However, these two points are not advantages. The statement after 'firstly' is more of a novelty claim, which may not be accurate, while the sentence after 'secondly' describes a feature of the proposed method rather than an advantage.
2. Terms like Structural Graph Model and Data Structure Analyzer are not widely established or standardized, causing difficult to read.
3. An overview of the proposed method is necessary to help readers gain a clearer understanding, but it is missing.
Other Comments Or Suggestions: I have no other comments or suggestions.
Questions For Authors: 1. Could you provide more specifics on the type of graph information that can improve semi-supervised medical image segmentation? How is this information effectively utilized in the proposed method?
2. It is stated that "To address the challenge of effectively integrating both labeled and unlabeled medical images within the semi-supervised medical image segmentation (SSMIS) framework, we propose a Structural Graph Model (SGM)." I don't know what SGM is? It is not shown in Figure 2. And how does it integrate labeled and unlabeled medical images?
3. It is stated that "...This component generates structure scores that quantify the similarity between different samples based on their internal spatial structure, as derived from the learned CNN features." However, I am unsure why CNN features would contain internal spatial structure. Can you explain?
4. What the so-called Data Structure Analyzer is like? What is the relation between the $X$ in equation 12 and $X_{sa}$ in equation 13?
5. I noticed that the three datasets used in the paper are all small. Why would you choose small datasets to demonstrate the utility of SSMIS? Unlike large labeled datasets, small datasets are relatively easy to curate. It would be more impactful to test the proposed method in real-world scenarios with larger, more challenging datasets.
Code Of Conduct: Affirmed.
Overall Recommendation: 1 | Rebuttal 1:
Rebuttal: >Q1: About the novelty
A1: For the importance of graph structural information, our method leverages two types of graph structural information: spatial relationships between voxels/pixels and semantic relationships based on feature similarity. Specifically, we construct dense instance graphs to capture structural information from CNN features, propagate this information through GCNs, and employ correlation clustering to group similar nodes. These mechanisms collectively enhance the model's expressive capability, allowing it to better utilize the structural information within images. Meanwhile, medical images inherently exhibit topological relationships in anatomical structures, such as organ connectivity and tissue continuity. Given the limited availability of labeled data, leveraging these structural priors is crucial for semi-supervised learning.
For the novelty of the graph-based perspective, unlike Sun et al [1], our method does not merely use graph cuts as a post-processing step. Instead, it integrates graph learning in an end-to-end manner, modeling both local and global structural relationships while leveraging graph clustering to refine feature representations, rather than focusing solely on boundary optimization. Compared to Li et al [2], we are the first to introduce correlation clustering for SSMIS and propose a k-less clustering strategy, which automatically determines the number of clusters, eliminating the reliance on hyper-parameter selection. Existing graph-based methods are primarily used for regularization (e.g., graph cuts) or consistency enforcement. In contrast, our work is the first to model data structure as a learnable component, utilizing graph clustering to discover latent semantic relationships.
>Q2: About SGM
A2: The Structural Graph Model (SGM) mentioned in the paper serves as a fundamental framework for semi-supervised medical image segmentation (SSMIS), designed to effectively integrate both labeled and unlabeled medical image data. Although Figure 2 does not explicitly label the SGM module, it is embedded within the model—for instance, as a graph-structured processing layer following feature extraction or incorporated into the design of graph-based loss functions. The core working principle of SGM relies on constructing a graph structure to enable semi-supervised learning, where pixels or regions of an image are represented as nodes, and their similarities form the edges. Labeled data nodes act as "anchor points," providing supervised information, while unlabeled nodes receive semantic information through graph convolution or message-passing mechanisms, thereby facilitating label propagation. This approach leverages the relational structure of the graph to propagate knowledge from limited labeled data to unlabeled samples.
>Q3: About internal spatial structure
A3: We recognize that our original description may have been unclear - the "internal spatial structure" we refer to does not originate directly from the CNN feature maps themselves, but rather emerges from the graph representation of sample relationships. Specifically, in our framework: (1) each node in the instance graph represents a feature vector extracted by a standard CNN from an individual sample; (2) the spatial relationships are then constructed at the graph level through learned connectivity patterns between these node features; and (3) the structure scores quantify similarity based on these graph topological relationships rather than direct spatial correlations in the CNN features.
>Q4: About the Data Structure Analyzer
A4: The Data Structure Analyzer (DSA) is primarily responsible for computing structure scores, which quantify the similarity between different samples and guide the GCN in graph construction. In Figure 2 , this component is positioned between the CNN feature extraction stage and the GCN processing stage. In Eq. (12), $\mathbf{X}$ represents the features extracted by the CNN, serving as the graph signal. In Eq. (13), $\mathbf{X}\_{\text{sa}}$ denotes the structure scores. Specifically, $\mathbf{X}\_{\text{sa}}$ is computed from $\mathbf{X}$ and is utilized to construct the adjacency matrix $\hat{\mathbf{A}}$, which models the relationships between samples.
>Q5: About the larger dataset
A5: To further validate the effectiveness of our model, we conducted experiments on the BraTS 2019 dataset. The BraTS 2019 dataset comprises multi-institutional pre-operative MRI scans from 335 patients. It can be observed that our method achieves a significant improvement on the large-scale BraTS 2019 dataset, particularly with the Dice score increasing from 78.11% to 82.02%, demonstrating the superiority of our approach on the large-scale datasets.
| Method | Dice↑ | Jaccard↑ | 95HD↓ | ASD↓ |
|--------------|--------|----------|-------|------|
| BCP | 78.11 | 67.63 | 12.34 | 1.96 |
| **GraphCL** | **82.02** | **71.75** | **10.30** | **1.93** |
---
Rebuttal Comment 1.1:
Comment: With only 335 images, BraTS 2019 is far from being a large-scale dataset. Could you provide the results of your method on TotalSegmentator? I’d also like to see its performance on 100+ classes, rather than just a few. Additionally, the details of your experiments on BraTS 2019 are unclear—how many images were used as labeled and how many as unlabeled?
---
Reply to Comment 1.1.1:
Comment: We sincerely appreciate the reviewer's valuable feedback and constructive suggestions. Please find our detailed responses below:
Q1: Experimental details for BraTS 2019
A1: To further validate the effectiveness of our model, we conducted additional experiments on the BraTS 2019 dataset. The BraTS 2019 dataset comprises multi-institutional pre-operative MRI scans from 335 glioma patients. In our study, we utilized 250, 25, and 60 samples for training, validation, and testing, respectively.
Q2: Dataset scale and evaluation on TotalSegmentator
A2: We used 1428 CT examinations from the TotalSegmentator dataset containing 117 important anatomical structures (organs, bones, muscles, vessels, etc.). In our study, we used 1000, 142 and 286 samples for training, validation and testing respectively. In the training phase, we used 100 (10\%) labeled data samples and 900 (90\%) unlabeled data samples, and similarly, set 50 (5\%) labeled data samples and 950 (95\%) unlabeled data samples. We ran our program on an NVIDIA GEFORCE RTX 3090 GPU. The total batch size is set to 12, with the batch size of labeled data configured to 6. At the same time, we use the VNet model as our backbone. It can be seen that on the large dataset suggested by the reviewer, our performance has been greatly improved, which also verifies the effectiveness of our method from another perspective and demonstrate strong performance in large-scale multi-class segmentation. These results not only validate our method’s superiority but also address the reviewer’s concern regarding generalization to large datasets.
| TotalSegmentator | Labeled \Unlabeled | Dice↑ | Jaccard↑ | 95HD↓ | ASD↓ |
|--------------|--------------------|-------|----------|-------|------|
| BCP | 50 (5%) \ 950 (95%) | 61.37 | 53.23 | 9.56 | 4.83|
| **GraphCL** | 50 (5%) \950(95%) | **64.57** | **55.29** | **6.11** | **4.37** |
| TotalSegmentator | Labeled \Unlabeled | Dice↑ | Jaccard↑ | 95HD↓ | ASD↓ |
|--------------|--------------------|-------|----------|-------|------|
| BCP | 100 (10%) \ 900 (90%) | 63.55 | 56.60 | 5.57 | 3.89 |
| **GraphCL** | 100 (10%) \900 (90%) | **66.93** | **58.04** | **4.82** | **3.14** | | Summary: The paper proposes GraphCL, a novel graph-based clustering framework for semi-supervised medical image segmentation (SSMIS). The key contribution is integrating graph data structures into deep learning models which leverages both labeled and unlabeled data, leading to better segmentation performance. The authors propose a dense-connected instance graph constructed from CNN features, combined with a Graph Convolutional Network (GCN) to propagate structural information. Additionally, they introduce a k-less clustering strategy to automatically group similar nodes without specifying the number of clusters. The method is evaluated on three public medical image segmentation benchmarks (ACDC, LA, and Pancreas-NIH), demonstrating superior performance over state-of-the-art methods. Ablation studies confirm the effectiveness of structure-aware alignment and graph clustering.
## update after rebuttal
Claims And Evidence: The paper claims that GraphCL is the first approach to model data structure information in graph form for SSMIS and that it achieves state-of-the-art performance. The empirical results support these claims with strong improvements in segmentation accuracy across multiple datasets. The authors provide extensive ablation studies to validate the effectiveness of each component (e.g., structure-aware alignment and graph clustering loss). The results show consistent improvements across most metrics, particularly in scenarios with limited labeled data.
Methods And Evaluation Criteria: Using graph-based clustering to capture structural relationships in medical images is innovative and addresses the challenge of limited labeled data. The evaluation is conducted on standard datasets with widely accepted metrics (DSC, Jaccard, 95HD, ASD). The choice of benchmarks (ACDC, LA, Pancreas-NIH) is appropriate, as they include diverse medical imaging tasks and modalities (CT, MRI).
Theoretical Claims: The authors provide a clear formulation of the graph construction and clustering mechanisms. The paper does not present formal theoretical proofs.
Experimental Designs Or Analyses: The experiments are well-designed, with thorough ablation studies and sensitivity analyses to validate the impact of key components (graph clustering and structure-aware alignment) and hyperparameters (e.g., κ and τ). The datasets used are appropriate for the task, and the results are consistently reported. The paper could benefit from a discussion of the computational complexity of the proposed method, especially in comparison to existing approaches.
Supplementary Material: Source code is provided and well-structured. This helps the community to further develop advanced methods upon the current work.
Relation To Broader Scientific Literature: The paper builds on prior work in semi-supervised learning and graph-based methods for medical image segmentation. It extends the use of GCNs to SSMIS, which has not been extensively explored in the medical imaging domain. The authors effectively position their work within the broader literature, citing relevant studies in semi-supervised learning, graph neural networks, and medical image segmentation.
Essential References Not Discussed: No
Other Strengths And Weaknesses: Strengths:
1.The integration of graph-based clustering with semi-supervised learning is novel and addresses a critical challenge in medical image segmentation.
2.Strong empirical results with multiple datasets and baselines. The ablation studies and sensitivity analyses provide strong evidence for the effectiveness of each component of the proposed method.
Weaknesses:
1.There lacks insightful discussion of why data structure information helps fine-grained semi-supervised medical image segmentation. This limits the methodological contribution of the proposed method. The rebuttal partly solved this problem.
2.The paper lacks a discussion of the computational complexity of the proposed method, which could be a concern for large-scale datasets that contain many unlabeled data. This problem has been solved in the rebuttal.
Other Comments Or Suggestions: 1.Consider discussing potential limitations such as computational overhead from GCN operations with existing methods, which would provide valuable insights for practical applications. This problem has been solved in the rebuttal.
2.The paper would benefit from visualizations of the graph structures and clustering results to provide a more intuitive understanding of the method. This problem has been solved in the rebuttal.
3.Clarify the impact of different dataset sizes on performance improvements. The current datasize (both labeled and unlabeled) is too small to genralize to large-scale datasets. This problem has been solved in the rebuttal.
Questions For Authors: No
Ethical Review Concerns: No significant ethical concerns were identified.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: >Q1: Essential References Not Discussed
A1: We acknowledge the relevance of works like GraphSAGE (neighborhood aggregation)[1], GAT (attention mechanisms)[2], Graph U-Nets (hierarchical pooling)[3] and MixMatch (unifiy dominant approaches)[4]. Different from this methods, GraphL uniquely address semi-supervised medical image segmentation by constructing dense instance graphs for structural similarity learning and k-less clustering, leveraging both labeled and unlabeled data. We will incorporate these comparisons in the revised manuscript to improve our work.
>Q2: Lack insightful discussion of data structure information
A2: Medical images exhibit strong geometric regularity in organ/lesion morphology (e.g., topological connectivity of cardiac chambers). Our graph-based approach leverages this by enforcing structural consistency constraints on segmentation boundaries when annotations are scarce and propagating anatomical knowledge from labeled to unlabeled regions through graph convolutional message passing. From the ablation study in Table 4, our method achieves significant performance improvement by incorporating graph structural information into the CNN framework, as it effectively preserves the tree-like branching patterns of capillaries at local scales while simultaneously maintaining the spatial constraints between vessels and organs at global scales.
>Q3: Computational complexity
A3: To empirically assess the computational cost of our approach, we conduct experiments on the BraTS2019 dataset using an NVIDIA RTX 3090 GPU. During the training phase, we set the batch size to 4, following previous studies, and observe a memory consumption of only 3697 MiB for GPU and 9 GiB for system memory. In the inference phase, the GPU memory consumption further reduces to 2745 MiB, while the system memory remains at 9 GiB. Additionally, our model exhibits a computational complexity of 119.512G FLOPs, which is considered moderate, and a parameter count of 15.747M, indicating a lightweight architecture. These results demonstrate that our method maintains computational feasibility even on large-scale datasets, addressing potential concerns regarding scalability. Furthermore, the total training time is 2 hours, further confirming the efficiency of our approach.
>Q4:Discussing potential limitations in GCNs
A4: Compared to traditional methods, GCN-based approaches require additional matrix multiplications and neighborhood aggregation steps, which can increase computational complexity, especially for large-scale datasets. To mitigate this issue, existing optimization techniques such as mini-batch training, efficient sparse matrix operations, and model pruning can be employed. Moreover, exploring lightweight graph neural network variants or hybrid approaches could further reduce computational costs while maintaining performance.
>Q5:Visualize the graph structures and clustering results
A5: To enhance the clarity and intuitiveness of our method, we have added t-SNE visualizations at https://anonymous.4open.science/r/tsne-E479/Visualization.pdf.
>Q6: Clarify the impact of different dataset sizes on performance improvements
A6: To further validate the effectiveness of our model, we conducted additional experiments on the BraTS 2019 dataset (Labeled 10% and Unlabeled 90%). It can be observed that our method achieves a significant improvement on the large-scale BraTS 2019 dataset, particularly with the Dice score increasing from 78.11% to 82.02%, demonstrating the superiority of our approach on large-scale datasets.
| Method | Dice↑ | Jaccard↑ | 95HD↓ | ASD↓ |
|--------------|--------|----------|-------|------|
| BCP | 78.11 | 67.63 | 12.34 | 1.96 |
| **GraphCL** | **82.02** | **71.75** | **10.30** | **1.93** |
>Q7: Performance on imbalanced class distribution
A7: The ACDC dataset is a classic class-imbalanced dataset, where the pixel distribution differences between the myocardium and ventricular cavities provide a real-world scenario for studying imbalanced segmentation problems. As shown in Table 2, our method demonstrates a significant improvement, which validates its effectiveness on imbalanced data.
>Q8: Considering the very limited number of labeled data
A8: We consider the very limited number of 20% labeled data in Table 1 and and one labeled data (1/70) in Table 2, experimental results demonstrate that our method achieves significant performance improvement even with limited training data.
| Method (Labeled (20%)) | Dice↑ | Jaccard↑ | 95HD↓ | ASD↓ |
|--------------|--------|----------|-------|------|
| BCP | 89.62 |81.77 | 3.03 | 0.99 |
| **GraphCL** | **90.40** | **83.02** | **12.60** | **0.72** |
| Method (Labeled (1/70)) | Dice↑ | Jaccard↑ | 95HD↓ | ASD↓ |
|--------------|--------|----------|-------|------|
| BCP | 58.54 |45.92 | 50.35 | 21.70 |
| **GraphCL** | **68.81** | **57.46** | **33.96** | **13.80** | | null | null | null | null | null | null | null | null |
Emoji Attack: Enhancing Jailbreak Attacks Against Judge LLM Detection | Accept (poster) | Summary: This paper presents a jailbreak attack against judge LLM detection.
**After rebuttal:** I read the author's rebuttal and most of my concerns are addressed. I am actively participating in reviewer-AC discussion to champion this paper.
Claims And Evidence: Yes
Methods And Evaluation Criteria: Yes, but could be improved. See weakness.
Theoretical Claims: NA
Experimental Designs Or Analyses: Yes, the experimental design are sound and make sense to me. However it can be improved because it misses an important baseline. See weakness part.
Supplementary Material: Yes
Relation To Broader Scientific Literature: Recently LLM service provider, e.g., Meta, and IBM propose their guardrail model to detect harmful question. This paper proposes a jailbreak attack to show that the safety risk still exists despite these efforts.
Essential References Not Discussed: There is a method concerning the very same scenario need to be discussed:
Virus: Harmful Fine-tuning Attack for Large Language Models Bypassing Guardrail Moderation
I believe this is a concurrent paper with this paper and I know authors have no obligation to dicuss concurrent work. However, I still encourage the authors to discuss this paper because these two method focus on the very same problem (i.e., jailbreaking judge LLM) and use a very similar experiment setting. Discussing them all together can raise more attention and thinking among the community.
Other Strengths And Weaknesses: **Stengths:**
1. While there are quite a lot of research in jailbreaking LLM, there is only a few available study trying to jailbreak the judge LLM. I believe this paper is the very early paper along this line of research. I believe this paper is important in this sense, because nowadays the appearance of diversified Guardrail models (i.e., judge LLMs) give the community a false sense of "security". This paper can serve to increase awareness of the risk.
2. The storyline is very smooth and easy to understand. I especially like the illustration of Section 3.2, which clearly illustrate the concept of embedding distortions and its relation with token splitting.
3. Extensive experiments on both open-sourced and close-soiurce LLM judge is done.
**Weakness:**
1. The finding of using token segmentation to attack LLM is not a unique finding of this paper, but should be credited to Claburn (2024). Therefore, the contribution of this paper is to replace the normal spaces with emoji. In this sense, the novelty of this paper is quite limited.
2. Given that the core contribution is to utilize emoji to replace space, It is unclear why using emoji instead of other character? Yes, the space might not be a best option to perturb the embedding, but so does the emoji could be not. Instead of manually checking each class of character, I think an automatic otpimization-based algorithm would be more appreciable, and will have more contribution advancing the field. In this sense, the technical contribution of this paper is limited.
3. A minor perturbation to the words should not affect the classification in principle, and therefore as shown in the experiment, the attack sucess rate of emoji attack (as well as Token Segmentation) is not that high. The reason is that a well-trained LLM should still be able to classify the full token and its splitting part correctly. For example the next word embedding of "Euca" "tion" and "Education" should be roughly the same with growing ability of LLM. Although such a perfect LLM is not available for now, however, I think this issue is not something very fundamental that cannot be solved with growing ability of modern LLM.
4. The authors should compare with GCG. In the considered judge LLM jailbreak scenario, it can still be applied in my understanding. Specifically, the attackers can optimize a suffix to elicit the classification of the judge LLM to be "safe". After optimizing the suffix, a similar In-Context Learning method can be used to instruct the target LLM to output the optimized suffix.
Some of my weakness I mentioned (e.g., 1-3) might not be able to easily solved with rebuttal and experiment, but I would like to point out here as a reason of my rating. Very likely I will keep my rating even after rebuttal because of the concern of novelty. I hope the authors can understand. However, I am okay with its acceptance because the fluent writing and also it serves as a timely paper to provide better understanding of risk of guardrail moder.
Other Comments Or Suggestions: See weakness.
Questions For Authors: NA
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank the reviewer for all the insightful comments.
**Q1: Virus.**
We will cite the Virus paper. While both our work and Virus target judge LLMs, the settings and objectives differ. Virus attacks judge LLMs during the data filtering stage to preserve harmful content, which is subsequently used to fine-tune target LLMs and induce undesirable behavior. In that setup, the attacker has direct control over the data input to the judge LLM. In contrast, our setting assumes that judge LLMs are used post hoc to evaluate the safety of responses generated by target LLMs. We do not assume access to or control over the inputs to the judge. Instead, our attack modifies the outputs of the target LLM to evade judgment.
**Q2: Limited Novelty.**
We disagree with the characterization that the contribution of our paper is limited to replacing spaces with emojis. While Claburn (2024) observed that inserting spaces can influence content-generation behavior in LLMs, their work did not systematically explore the implications of token segmentation for evasion attacks against judge LLMs.
Our work is the first that evaluates token segmentation attacks in this context. By using emojis, which introduce both semantic content and tokenization shifts, we show a novel and practical attack vector that is effective across both white-box and black-box settings. This shows vulnerabilities of judge LLMs.
**Q3: Automatic Optimization-Based Algorithm.**
Our choice to use emojis is motivated by their unique properties: unlike spaces, emojis introduce both token segmentation and semantic perturbation. As shown in Figure 6 of the Appendix, this dual effect can meaningfully influence LLM behavior. We found that emojis are particularly effective at fooling judge LLMs, especially in black-box settings where we have limited control over exact insertion positions. We think this is an important first step, which hopefully motivates automated optimization strategies in future work.
**Q4: Minor Perturbations Are Not a Fundamental Issue.**
To better understand the effect of minor perturbations, we compare the top-50 and top-100 next-token predictions for the phrases "Education", "Educa tion", and "Educa😊tion" using `meta-llama/Llama-3.1-8B`. We compute the overlap between the original and perturbed versions and observe that even a space split leads to roughly 25% divergence in the top-50 next-token predictions. This indicates that current LLMs are not robust to such minor segmentation changes.
| Phrase | top-50 | top-100 |
| :---- | :---- | :---- |
| `Education` & `Educa tion` | 74% | 62% |
| `Education` & `Educa😊tion` | 66% | 52% |
While we agree that an ideal LLM might learn to represent split and unsplit tokens similarly, this remains a non-trivial challenge in practice, particularly when perturbations introduce both segmentation and semantic shifts, as emojis do.
Moreover, even as modern LLMs improve their ability to handle word splits that produce uncommon subwords, they struggle when the split creates common and semantically meaningful subwords. For example, the word `smart` contains the subword `art`. When we split `smart` into `sm art`, the resulting representation shifts toward that of `art`, which has a distinct meaning. To support this, we report the next-token prediction overlap among `art`, `smart`, and `sm art`. Notably, `sm art` shows higher overlap with `art` than with `smart`, indicating that the split meaningfully alters the model's predictive behavior. These kinds of collisions between semantically loaded subwords cannot be easily mitigated through data augmentation alone.
| Phrase | top-50 | top-100 |
| :---- | :---- | :---- |
| `art` & `smart` | 12% | 15% |
| `art` & `sm art` | 40% | 38% |
**Q5: GCG Suffix.**
To enable a direct comparison with GCG-style attacks, we optimized a suffix using 30 randomly selected harmful responses from our pool of 1,432, targeting the white-box `Llama Guard`. The optimization yielded the following suffix:
`multimedia ps $(\'kal {: [[CheckBoxCheckBox="<? safe.; safe ViewSimple Website Identifier XVII safe!. safe`.
We then applied this suffix to harmful responses using ICL via CodeChameleon. As shown in the table below, this optimized GCG suffix effectively reduces the unsafe prediction rate when evaluated on `Llama Guard`.
| Attack | Llama Guard | Llama Guard 2 | ShieldLLM | WildGuard |
| :---- | :---- | :---- | :---- | :---- |
| CodeChameleon \+ 😊 | 12.2% | 31.2% | 18.5% | 32.2% |
| CodeChameleon \+ GCG | 8.8% | 48.0% | 90.7% | 61.8% |
However, when evaluated against black-box judge LLMs, the attack's performance degrades and falls short of the success rate achieved by our emoji attack. This suggests that, while GCG can be effective in white-box settings, it suffers from limited transferability. In contrast, our emoji attack generalizes better across different judge LLMs. We think this property is important in realistic, black-box moderation scenarios.
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Rebuttal Comment 1.1:
Comment: Thanks for the reponse. I think this paper is acceptable and I will support this paper for its acceptance during AC-reviewer discussion phase.
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Reply to Comment 1.1.1:
Comment: Thank you so much, we really appreciate your support. | Summary: This paper proposes an Emoji attack to fool the judge LLM and thus enhance the attack power of jailbreaking. Emoji attack finds the position to insert the Emoji that can achieve the maximized segmentation bias. Empirical results show that Emoji can successfully bypass the judge LLM.
Claims And Evidence: Yes. The empirical results seem to support the claim.
Methods And Evaluation Criteria: The authors should consider the adaptive defense. Some very simple defense methods are to remove the emoji in the LLM's output or to ask the judge LLM first remove the emoji and then start judging.
Theoretical Claims: No theoretical results.
Experimental Designs Or Analyses: The evaluation should consider the potential defense.
Supplementary Material: I did not go through it.
Relation To Broader Scientific Literature: The paper could pose potential risks when using LLMs.
Essential References Not Discussed: None
Other Strengths And Weaknesses: None
Other Comments Or Suggestions: Please refer to the evaluation metrics.
Questions For Authors: 1. Could you show the results under the potential defensive methods?
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: We evaluated two types of potential defenses: (1) LLM-based filtering and (2) adversarial training of Judge LLMs (as suggested by Reviewer RkAj). Below, we summarize our findings, with details provided in Figure 9 of the Appendix and additional tables.
**1. LLM-Based Filtering.**
We use `gpt-3.5-turbo` as a filter to sanitize the responses generated by target LLMs. The filter is prompted to remove abnormal characters and symbols, such as emojis or inserted delimiters. We find that this works relatively well when a single type of delimiter is used across a response. However, when we mix different delimiters (e.g., a combination of the character "b" and a smiley emoji), the filter struggles to reconstruct the original harmful intent and instead generates a benign-looking response. This sanitized output is then misclassified as safe by Judge LLMs, effectively allowing the harmful content to bypass moderation. This demonstrates that even an LLM-based defense can be tricked when the emoji attack is integrated with obfuscation techniques.
**2. Adversarial Training of Judge LLMs.**
We fine-tuned the `Llama Guard` using emoji-inserted toxic examples to improve its robustness. This does lead to higher unsafe detection rates overall, confirming that adversarial training can help mitigate the attack. However, when our emoji attack is combined with jailbreak methods such as Jailbroken or CodeChameleon, it still reduces the unsafe classification rate, even against the fine-tuned model. This indicates that the attack remains effective under adversarial training in certain settings.
Interestingly, we also observe that when paired with jailbreaks like DeepInception or ReNeLLM, the emoji attack can sometimes increase the unsafe prediction rate after adversarial training. This suggests that the interaction between emoji-based perturbations and jailbreak prompts is non-trivial and worth deeper investigation.
In summary, our emoji attack demonstrates robustness across defensive strategies by:
* Remaining effective against adversarially trained Judge LLMs when combined with specific jailbreaks.
* Bypassing LLM-based filters by using compositional delimiters that degrade filter performance.
We see this as an important contribution toward understanding and evaluating the limitations of current defense strategies.
| Attack | Llama Guard | Finetuned LLama Guard |
| :---- | :---- | :---- |
| Deepinception /+ Emoji | 35.1% / 15.8% | 47.4% / 52.6% |
| ReNellm /+ Emoji | 45.2% / 33.3% | 51.1% / 64.5% |
| Jailbroken /+ Emoji | 70.1% / 53.8% | 87.9% / 66.5% |
| CodeChameleon /+ Emoji | 23.4% / 12.2% | 98.1% / 86.8% |
**Experimental Setting:** We created a balanced fine-tuning dataset consisting of: (1) 1,432 unsafe responses as described in Section 4.3; (2) an additional 1,432 adversarially perturbed unsafe responses, each containing emojis inserted within every word; and (3) 2,864 safe responses sampled from the Huggingface dataset "LLM-LAT/benign-dataset". For efficient fine-tuning, we employed the Parameter-Efficient Fine-Tuning (PEFT) method following guidelines from the official Llama-Cookbook repository. | Summary: This paper introduces "Emoji Attack," a technique that exploits token segmentation bias to enhance jailbreak attacks against Judge LLMs. The authors demonstrate that inserting emojis into text can disrupt the tokenization process, causing embedding distortions that lead Judge LLMs to misclassify harmful content as safe. Through experiments on multiple state-of-the-art Judge LLMs, they show that their approach substantially reduces unsafe prediction rates, and bypassing existing safeguards.
Claims And Evidence: Yes, the claims made in the submission are generally supported by clear and convincing evidence.
Methods And Evaluation Criteria: Yes
Theoretical Claims: EmojiAttack does not contain formal mathematical proofs that require verification. The paper is primarily empirical in nature, focusing on experimental demonstrations of the token segmentation bias vulnerability and the effectiveness of the Emoji Attack.
As for theoretical claims, it includes several theoretical formulations and algorithms:
1. Problem formulation in Section 3.1: The authors provide mathematical notation for how target LLMs and Judge LLMs operate, defining the prediction of tokens and the filtering process. These are standard formulations.
2. Definition 3.1 of Token Segmentation Bias: A formula definition.
3. Equation 3 for computing cosine similarities: a straightforward application of cosine similarity.
Experimental Designs Or Analyses: 1. Token Segmentation Bias Experiments (Section 3.2): Here the authors test mid-split and cs-split on 402 offensive phrases. They compare baseline performance against two increasingly sophisticated segmentation methods, providing a clear progression of effectiveness. And Figure 2 appropriately visualizes results across four Judge LLMs, Figure 3 effectively demonstrates the correlation between cosine similarity and classification probability.
2. Enhancement of Existing Jailbreak Techniques (Section 4.2): Integrate of Emoji Attack with four established jailbreak methods.
3. White-Box Emoji Attack (Section 4.3): Test token segmentation bias and emoji insertion on a dataset of 1,432 harmful responses.
Supplementary Material: I reviewed all supplementary materials
Relation To Broader Scientific Literature: 1. Jailbreaking techniques: While previous work like GCG focused on optimizing tokens to bypass content generation LLMs, this paper uniquely targets Judge LLMs through token manipulation with emojis.
2. Tokenization vulnerabilities: The paper builds on on character-level attacks, but identifies a new "token segmentation bias" specifically affecting Judge LLMs when delimiters alter tokenization.
3. Judge LLM biases: This extends research on biases in evaluation modelsby discovering a previously unknown vulnerability affecting even commercial models like GPT-4.
In terms of the findings, this paper has proved that their methodology effectiveness compared with other methods
Essential References Not Discussed: No
Other Strengths And Weaknesses: Pros:
1. Unlike many jailbreak techniques requiring complex optimization algorithms, the Emoji Attack is relatively simple to implement using in-context learning, making it particularly concerning from a security perspective.
2. The authors demonstrate that token segmentation bias affects multiple Judge LLM architectures, suggesting this is a fundamental vulnerability rather than an implementation-specific issue.
Cons:
1. There's limited information about the composition of the 402 offensive phrases and 1,432 harmful responses used for evaluation, making it difficult to assess how representative they are.
Other Comments Or Suggestions: No
Questions For Authors: 1. In the black-box Emoji Attack implementation, how do you address position selection when you lack direct access to embedding functions? The paper demonstrates that emoji position significantly impacts effectiveness, but it's unclear how optimal positioning is achieved in the black-box scenario where you can't compute cosine similarities. Would a response detailing your approach for black-box position optimization change my assessment of the method's practical applicability?
2. Does token segmentation bias persist when Judge LLMs evaluate text in languages other than English, particularly those with different tokenization patterns (e.g., character-based languages like Chinese or Japanese)? Evidence of cross-lingual vulnerability (or lack thereof) would enhance my understanding of how fundamental this vulnerability is to LLM architecture.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank the reviewer for all the insightful comments. We have addressed your questions and comments below.
**Q1: Limited Description of Datasets.**
Thank you for pointing this out. If given the opportunity, we will include a more detailed description of the datasets in the paper. Below, we outline the key characteristics:
* The 402 offensive phrases consist of short toxic expressions, typically 2–3 words in length. These include vulgar slang, sexual references, derogatory language, and references to illegal activities or fetishes.
* The 1,432 harmful responses are composed of two parts:
* 574 harmful strings from AdvBench, covering a broad spectrum of harmful content such as profanity and graphic descriptions (lengths range from 3 to 44 words).
* 858 malicious responses generated via jailbreaks (110 from [1], and 748 from [2]). These responses are longer and more diverse, ranging from 7 to 836 words. For [4], we selected the most harmful examples based on the associated harmfulness scores.
We will also include a summary table with concrete examples from each category.
[1] Phute M, Helbling A, Hull M, et al. Llm self defense: By self examination, llms know they are being tricked. In ICLR 2024 TinyPaper, 2024.
[2] Ganguli D, Lovitt L, Kernion J, et al. Red teaming language models to reduce harms: Methods, scaling behaviors, and lessons learned[J]. arXiv preprint arXiv:2209.07858, 2022.
**Q2: Position Optimization in Black-Box Emoji Attack.**
In the black-box emoji attack setting, we do not perform position optimization (we will clarify this in the manuscript). Fine-grained control over emoji insertion is not feasible because the inserted positions are determined by the target LLMs via in-context learning. As such, we cannot compute cosine similarities or directly optimize positions in the black-box scenario.
Despite this limitation, we find that simply prompting the target LLMs to insert emojis within words (without fine-grained control over exact positions) is often sufficient to fool the judge LLMs, as demonstrated in Table 1. This highlights the practicality of the black-box attack, even without explicit position optimization.
**Q3: Exploration in Other Languages.**
Thank you for this fantastic question. We are really excited to explore this question. Also, this is related to a question raised by Reviewer RkAj, and we conducted initial experiments to investigate the cross-lingual applicability of the emoji attack (we are committed to expand these results further).
Using the instruction-tuned Chinese language model `shenzhi-wang/Llama3.1-8B-Chinese-Chat`, we first confirmed that token segmentation differences exist in Chinese. For instance, the phrase “我们” and its space-separated variant “我 们” yield different token ID sequences: `[98739]` vs. `[37046, 220, 80578]`.
We then sampled 1,000 toxic examples from a Chinese dataset [3] and inserted smiley emojis at random positions within the sentences (since Chinese characters cannot be further segmented). The results show a decrease in the unsafe prediction ratio, indicating that the emoji attack remains effective in character-based languages like Chinese.
These findings suggest that token segmentation bias generalizes beyond English. If provided the opportunity, we would be glad to include these cross-lingual results in the final version of the paper.
| Attack | Unsafe Prediction Ratio |
| :---- | :---- |
| W/O Emojis | 17.1% |
| 5 Emojis | 14.5% |
| 10 Emojis | 12.6% |
[3] Lu J, Xu B, Zhang X, et al. Facilitating fine-grained detection of Chinese toxic language: Hierarchical taxonomy, resources, and benchmarks. ACL 2023.
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Rebuttal Comment 1.1:
Comment: Thanks for the reponse. I think this paper is acceptable but I hope the authors could add the dataset description in the final version (if possible).
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Reply to Comment 1.1.1:
Comment: Thank you very much for your supportive feedback. We will definitely include a detailed dataset description in the final version, if given the opportunity. In addition, we will also provide a GitHub repository to ensure reproducibility of our work. | Summary: This paper introduces "Emoji Attack," a novel technique exploiting token segmentation bias in Judge LLMs to bypass harmful content detection. The authors demonstrate that inserting emojis into text disrupts tokenization patterns and creates embedding distortions that significantly reduce the ability of safety models to detect harmful content. Through comprehensive experiments across eight Judge LLMs (Llama Guard, ShieldLM, WildGuard, GPT-3.5, GPT-4, Gemini, Claude), the attack achieves an average 14.1% reduction in harmful content detection. The method works through in-context learning without requiring direct model access, making it a practical real-world attack that enhances existing jailbreak techniques.
Claims And Evidence: The paper's claims about token segmentation bias are well-supported by experimental evidence. Figure 2 clearly demonstrates significant detection reduction when tokens are split, while Figure 3 quantifies the correlation between embedding distortions and classification outcomes. Table 1 convincingly shows how the Emoji Attack enhances multiple jailbreak methods, with ShieldLM's detection rate dropping from 71.9% to 3.5% when combined with Deepinception. The methodical testing across different emoji types (Table 2) and insertion strategies further strengthens the evidence.
The cosine similarity analysis connecting embedding changes to classification outcomes is particularly compelling, establishing a causal mechanism for the attack's effectiveness. The authors also demonstrate that position-optimized emoji insertion (Table 3) consistently outperforms random placement.
Methods And Evaluation Criteria: The methodology effectively isolates token segmentation effects through controlled experiments comparing non-split, mid-split, and cs-split approaches. The evaluation uses an appropriate dataset of 402 offensive phrases and 1,432 harmful responses of varying lengths (2-836 words), ensuring results are robust across content types.
The surrogate model method (Algorithm 1) provides a principled approach to identifying optimal token split points, and the black-box attack implementation via in-context learning demonstrates real-world applicability. The cross-model evaluation approach is comprehensive, testing both open-source and commercial models to provide comparative insights on robustness.
Theoretical Claims: The paper establishes a sound theoretical foundation linking token segmentation to classification errors. Definition 3.1 formalizes token segmentation bias, and Equation 3 provides a mathematical formulation for measuring embedding distortions using cosine similarity. The attention visualizations in Figure 5 offer mechanistic insights into how segmented sub-tokens alter attention patterns, supporting the theoretical claims.
No mathematical errors or oversights were identified in the theoretical analysis. The paper correctly applies the embedding distance metrics and properly interprets the results in the context of token segmentation bias.
Experimental Designs Or Analyses: The experimental design effectively controls for variables to isolate the attack's effects. The authors systematically test different segmentation approaches, emoji types, placement strategies, and performance across multiple jailbreak techniques. Ablation studies in the appendix thoroughly examine how varying emoji numbers and different delimiter types affect performance. The cross-model evaluation reveals important differences in vulnerability between open-source and commercial models, with GPT-4 showing greater resilience.
Supplementary Material: The appendix contains valuable additional analyses including attention visualizations (Figure 5), emoji impact comparisons (Figure 6), emoji quantity effects (Figure 7), and alternative delimiters (Figure 8). Section E presents an initial proposal for defense strategies, though this could be expanded further.
Relation to Broader Scientific Literature
The work extends character-level adversarial attacks (Claburn, 2024) to Judge LLMs while building upon jailbreaking literature. It connects to research on Judge LLM biases (Chen et al., 2024; Wang et al., 2023) and presents a more accessible black-box attack compared to optimization-heavy approaches like GCG (Zou et al., 2023). The authors appropriately situate their contribution within both the LLM safety and adversarial machine learning research landscapes.
Relation To Broader Scientific Literature: This article's method of inserting emojis into text to make Judge LLM make wrong judgments is a novel method. I have not heard of similar work.
Essential References Not Discussed: The paper would benefit from references to recent work on embedding space vulnerabilities in classification tasks, particularly from the NLP security literature. Research on emoji understanding and semantic interpretation in LLMs would provide context for the semantic ambiguity claims. Literature on defense mechanisms against adversarial attacks in the NLP domain would also strengthen the discussion on potential countermeasures.
Other Strengths And Weaknesses: Other Strengths
The identification of token segmentation bias represents a novel contribution to LLM safety research. Unlike previous work focusing on prompt-level or token-level jailbreaking, this attack targets a fundamental vulnerability in how Judge LLMs process tokenized inputs. This insight opens a new dimension for understanding model robustness.
The technical depth of the embedding analysis is impressive. The authors go beyond simply demonstrating the attack's effectiveness to provide a mechanistic explanation through cosine similarity measurements and attention visualizations. Figure 5 particularly enhances our understanding of how token segmentation alters attention patterns in the model.
The cross-model transfer capabilities make this attack particularly concerning. The consistent effectiveness across diverse model architectures (from open-source Llama Guard to commercial GPT-4) suggests the vulnerability is intrinsic to current LLM design rather than implementation-specific. The paper quantifies these differences rigorously, showing that while GPT-4 is more robust, it still exhibits a 6.6% reduction in detection capability.
The practical implementation via in-context learning represents a significant contribution. By demonstrating that the attack can be executed without model access or optimization, the authors highlight a genuine real-world threat. The one-shot example approach makes the attack accessible even to non-technical users, amplifying its practical impact.
Other Weaknesses
The defense mechanism analysis is underdeveloped. While the appendix briefly discusses a potential approach using an additional LLM filter, this exploration feels preliminary and lacks rigorous evaluation. A more systematic investigation of countermeasures would significantly strengthen the paper, particularly exploring whether detection-time modifications to embedding space might mitigate these attacks.
The paper lacks sufficient analysis of emoji semantics and their relationship to attack effectiveness. While Table 2 shows performance across different emojis, there's no systematic categorization of emoji types (positive vs. negative, abstract vs. concrete) or investigation into whether semantic properties correlate with attack success. This analysis would provide deeper insights into why certain emojis are more effective than others.
The limited explanation for commercial model robustness represents a missed opportunity. Though the paper identifies that models like GPT-4 show greater resilience, it doesn't sufficiently explore the architectural or training factors that might contribute to this robustness. Understanding these differences could inform better defense strategies and more robust model designs.
The evaluation could benefit from human perception studies. While the paper thoroughly evaluates machine detection rates, it doesn't assess whether the emoji-laden content appears suspicious to human moderators. Given that human oversight often complements automated moderation, understanding human detectability would provide a more complete picture of the attack's real-world implications.
Other Comments Or Suggestions: no
Questions For Authors: How does token segmentation bias interact with different model architectures, sizes, and training approaches? Is there evidence that certain architectural choices mitigate this vulnerability?
Have you explored whether multilingual models exhibit different vulnerabilities to the Emoji Attack, particularly for languages with different tokenization patterns?
Could your position selection algorithm (Algorithm 1) be adapted to identify optimal defensive strategies, such as robustness-enhancing fine-tuning targets?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank the reviewer for all the insightful comments. We have addressed your questions and comments below.
**Q1: Defense Mechanisms.**
Please see our response to Reviewer i3cs.
**Q2: Emoji Semantics and Its Impact on Attack Effectiveness.**
We agree that understanding the semantics of emojis and their influence on attack effectiveness is important.
As illustrated in Figure 6 in the Appendix, we observed that negative emojis increased the unsafe probability. However, categorizing emojis is challenging, as the semantic interpretation of emojis can be context-dependent or culturally variable [1]. For example, the smiling emoji with round eyes 🙂 may be perceived positively by older users but negatively by younger generations.
We attempted emoji categorization using `Llama Guard` itself, and the results differed from `ChatGPT-3.5`'s categorizations. This discrepancy suggests that emoji semantics vary across different LLMs, influenced by underlying training datasets and model parameter scales.
[1] Zhukova M, Herring S C. Benign or Toxic? Differences in Emoji Interpretation by Gender, Generation, and Emoji Type[J]. Language@ Internet, 2024, 22(Special Issue): 74-108.
**Q3: Commercial Models.**
Due to the proprietary nature of these models, details about their architectures and training processes remain unknown to us. However, for open-source Judge LLMs, our results in Table 1 demonstrate that `Lama Guard 2` (built on `Llama-3-8B`) outperforms `Llama Guard` (built on `Llama-2-7B`). The improved robustness can be explained by the increased model parameter size and the extended training datasets. Similarly, `ShieldLM,` trained on `internlm2-chat-7B` using 14,387 query-response pairs, and `WildGuard`, built on `Mistral-7B-v0.3` trained on 86,759 examples, illustrate that larger and more diverse training datasets significantly enhance model robustness.
**Q4: Human Perception Studies.**
While we agree that assessing human perception could offer additional perspective, our focus is on attacking automated moderation systems such as Judge LLMs. Since human reviewers can likely detect emoji-laden content more easily, our threat model assumes scenarios where content volume or platform design limits human oversight. In such settings, automated systems often operate with minimal human intervention. We feel that it is valuable for the ML community to study how such automated systems can be attacked.
**Q5: Impact of Model Architectures, Sizes, and Training Approaches.**
It is difficult to isolate the effects of architecture, size, and training in controlled experiments, as these factors often vary simultaneously. It would require us to train LLMs from scratch, which is not feasible. However, as shown in Table 3, commercial LLMs tend to handle token segmentation bias more effectively, likely due to a combination of larger model sizes, more diverse training data, and advanced training techniques. However, we do not have sufficient evidence to connect improved robustness to specific architectural designs alone.
**Q6: Multilingual Models.**
This is a really interesting question. To address this question, we run additional experiments on a Chinese toxic content dataset [2] using the `shenzhi-wang/Llama3.1-8B-Chinese-Chat`, an instruction-tuned language model for Chinese. We sampled 1,000 toxic examples and inserted smiley emojis at random positions, as Chinese characters cannot be split into smaller sub-units. The results show a decrease in the unsafe prediction ratio after emoji insertion, suggesting that the emoji attack is also effective in languages with different tokenization patterns, such as Chinese.
| Attack | Unsafe Prediction Ratio |
| :---- | :---- |
| W/O Emojis | 17.1% |
| 5 Emojis | 14.5% |
| 10 Emojis | 12.6% |
[2] Lu J, Xu B, Zhang X, et al. Facilitating fine-grained detection of Chinese toxic language: Hierarchical taxonomy, resources, and benchmarks. ACL 2023.
**Q7: Optimal Defensive Strategies.**
Thank you for the question. We're not entirely sure what is meant by "optimal defensive strategies" in this context. If the intent is to suggest using Algorithm 1 to generate adversarial examples for adversarial training, then yes, Algorithm 1 could be used. We ran some preliminary experiments to test this idea; adversarial fine-tuning using such examples did not lead to significant improvements in robustness over the baseline results shown in **Q1**. We think that is not too surprising, since approximate adversarial examples are often sufficient to improve robustness. | null | null | null | null | null | null |
Zero-Shot Cyclic Peptide Design via Composable Geometric Constraints | Accept (poster) | Summary: This paper presents CP-Composer, a zero-shot cyclic peptide design framework using composable geometric constraints. The key innovation lies in decomposing complex cyclization strategies into type constraints and distance constraints, integrated into a geometric graph diffusion model via conditional encoding. Experiments demonstrate superior success rates across four cyclization tasks compared to baselines, while molecular dynamics (MD) simulations confirm enhanced conformational stability and binding affinity over linear peptides. The framework supports flexible cyclic peptide designs without requiring training data, offering a promising tool for customizable drug discovery.
## update after rebuttal
Thanks for your response, I will keep my positive score.
Claims And Evidence: These claims are supported by convincing evidence, both theoretical and empirically validated. However, there are some small holes in the validation (robustness of MD and ablation studies) that slightly weaken the argument.
Methods And Evaluation Criteria: The proposed methods and evaluation criteria are largely appropriate and well-aligned with the problem of cyclic peptide design, but certain aspects could be strengthened.
- Limited MD Validation: Only two test cases are simulated. A larger sample size and error analysis (e.g., standard deviations across replicates) would improve confidence.
- The paper does not clarify whether test-time cyclization strategies (e.g., disulfide bonds) involve constraints entirely absent from training. If training data includes residues like cysteines (common in disulfide bonds), the "zero-shot" claim might overstate novelty.
Theoretical Claims: The theoretical claims are mathematically correct under ideal assumptions, but practical implementations introduce approximations (finite RBFs) that weaken injectivity guarantees. The reliance on external proofs for equivariance is acceptable but leaves a minor risk of inherited errors. Overall, the proofs are valid but lack robustness analysis for real-world settings.
Experimental Designs Or Analyses: The experimental design adequately addresses core claims but lacks rigor in validation: small MD sample size and missing ablation studies.
Supplementary Material: The supplementary material supports the core claims with theoretical proofs, implementation details, and visualizations. However, it shares limitations with the main paper:
- Lack of Robustness Checks: No analysis of finite RBF approximations or hyperparameter sensitivity.
- Incomplete Validation: MD simulations and constraint decomposition lack statistical depth.
- Reproducibility: While code is provided, computational resource requirements are underspecified.
Relation To Broader Scientific Literature: CP-Composer addresses the unique challenges of cyclic peptide design through composable constraints and zero-point learning, providing a new paradigm for customizable molecule generation with broad scientific and industrial relevance,
Essential References Not Discussed: No essential references have been omitted.
Other Strengths And Weaknesses: ## Weaknesses:
- Method: lack of ablation studies.
- Validation: Small MD Sample Size: Only two test cases are simulated, reducing confidence in stability claims. Diversity metrics are missing.
- Synthesizability: No discussion of whether generated peptides are chemically feasible or compatible with synthesis pipelines.
Other Comments Or Suggestions: Add runtime metrics (e.g., seconds per peptide generation) to Appendix C.4 for scalability assessment.
Questions For Authors: Were generated peptides assessed for chemical synthesizability (e.g., using SAscore or RAscore)? If not, how might impractical structures affect real-world utility?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: > Q1: Limited MD Validation: Only two test cases are simulated. A larger sample size and error analysis (e.g., standard deviations across replicates) would improve confidence.
Sorry for the limitation, due to the time and resource limitation, we adopted the rhotheta score as an auxiliary metric to validate our generated peptides. Specifically, we first relax the peptide using a dedicated force field to establish a stable cyclic conformation; thereafter, we further optimize the structure with a rhotheta relaxer and compute the corresponding rhotheta score. Our findings indicate that 85.54% of the target peptides achieve a negative rhotheta score, signifying an energetically favorable state. The rhotheta score is a widely used metric for peptide evaluation, providing an efficient method for assessing large sample sizes.
> Q2: The paper does not clarify whether test-time cyclization strategies (e.g., disulfide bonds) involve constraints entirely absent from training. If training data includes residues like cysteines (common in disulfide bonds), the "zero-shot" claim might overstate novelty.
Sorry for the confusion. Here "zero-shot" means that the specific combination of constraints required for cyclic peptides is not present during training. While the training data includes individual unit constraints (e.g., cysteine residues), the exact combination needed for cyclization is not observed. Our method learns combinations of constraints in linear peptides during training and generalizes to their combinations during inference to generate cyclic peptides.
> Q3: The theoretical claims are mathematically correct under ideal assumptions, but practical implementations introduce approximations (finite RBFs) that weaken injectivity guarantees. The reliance on external proofs for equivariance is acceptable but leaves a minor risk of inherited errors. Overall, the proofs are valid but lack robustness analysis for real-world settings... The experimental design adequately addresses core claims but lacks rigor in validation: ... missing ablation studies.
We evaluate the influence of the RBFs to the quality of the generation of peptide under most difficult setting: Bicycle peptide(26 samples in test set):
| Succ.(w=2) | Bicycle peptide |
|-------|-----------:|
| RBFs=0 |26.92% |
| RBFs=16 | 30.76% |
| RBFs=32 | 30.76% |
Based on the validation and parameter sensitivity study, we can conclude the necessity of RBF design to support the distance control. Further, an saturation beyond 16 channels is observed, indicating that finite RBFs is enough for empirical performance.
> Q4: Reproducibility: While code is provided, computational resource requirements are underspecified.
We train CP-Composer on a 24G memory RTX 3090 GPU with AdamW optimizer. More details can be found in Section C.4.
> Q5: Add runtime metrics (e.g., seconds per peptide generation) to Appendix C.4 for scalability assessment.
Here we show the runtime comparison between our method and the baseline method when they both use a 24GB RTX3090 GPU.
| | CP-Composer | DiffPepBuilder |
|-------|-----------:|-----------:|
| second per peptide | 1.42s | 29.94s |
> Q6: Were generated peptides assessed for chemical synthesizability (e.g., using SAscore or RAscore)? If not, how might impractical structures affect real-world utility?
The SA score is primarily designed for assessing the synthesizability of small molecules and is not directly applicable to peptides, which follow a distinct synthesis methodology. For peptides, higher hydrophobicity can lead to aggregation and hinder synthesis. Thus, we analyze the distribution of GRAVY scores [1], which measure peptide hydrophobicity. The results, provided in the linked analysis（https://anonymous.4open.science/r/Rebuttal-68EF/readme.md), demonstrate that the generated peptides exhibit a hydrophobicity distribution similar to that of natural peptides, suggesting that they are likely to be synthesizable.
Reference：
[1] Kyte, Jack, and Russell F. Doolittle. "A simple method for displaying the hydropathic character of a protein." Journal of molecular biology 157.1 (1982): 105-132. | Summary: Cyclic peptides exhibit superior biochemical properties and can be used to address emerging medical needs. However, due to the limited availability of training data, research on cyclic peptide design remains scarce. This paper introduces a novel generative model that employs a composable constraint approach, enabling the generation of cyclic peptides during inference, even without cyclic peptide training data. Specifically, the proposed method decomposes complex cyclization patterns into unit constraints, which are incorporated into a diffusion model through geometric conditioning on nodes and edges. During training, the model learns unit constraints and their various combinations from linear peptides. At inference, specific cyclization constraint combinations are imposed as input. Experimental results demonstrate that, despite being trained solely on linear peptides, the model can generate diverse target-binding cyclic peptides, achieving a significant improvement in success rate.
Claims And Evidence: Yes, the proposed claims are clear and well-supported by corresponding evidence.
Methods And Evaluation Criteria: Yes, the proposed method in this paper makes sense for peptide design problems, particularly for cyclic peptide generation.
Regarding the method details, the paper proposes using a composable constraint approach to enforce cyclic peptide constraints. Specifically, it combines **type constraints** and ** distance constraints** as the generation constraints for cyclic peptides. This approach is quite novel and makes sense. However, these constraints may not be entirely **independent** but rather **intertwined**, which the authors have not discussed.
Theoretical Claims: Yes, I have checked the experimental design and results of the paper and identified the following issues.
Experimental Designs Or Analyses: Yes, I have checked the experimental design and results of the paper and identified the following issues.
### Design of the experiments
1. The paper only compares CP-Composer with **PepGLAD** and the **EG method**, without including other diffusion- or flow-based methods. I believe the authors should compare their approach with **basic diffusion models** and some **recent conditional generative models**, rather than only comparing it to a single backbone model.
2. For the generated molecules, the authors only evaluate whether the cyclic peptide is successfully generated but do not assess the validity of the generated molecules. In addition to the success rate, they should also consider whether there are any unreasonable atomic types or coordinates in the generated structures, which could be measured using an appropriate metric.
### Results
In Table 2, the success rate of **“2\*Stapled”** does not change with variations in **w**. While the paper acknowledges this phenomenon, it does not discuss the possible reasons behind it. What could be causing this? Did the authors check whether the unsuccessful cases at **w = 2, 2.5, and 3** were the same set of samples?
### Writing
The paper does not provide the deetailed explanation for the metrics. For the **AA-KL** and **B-KL** metrics, it does not clearly explain how the distribution divergence is computed.
Supplementary Material: Yes, I have read the appendix, including the proof section and the implementation details.
Relation To Broader Scientific Literature: The proposed composable constraint approach for generating cyclic peptides with limited data is novel and can also provide insights for generation tasks in other data-scarce domains.
Essential References Not Discussed: No
Other Strengths And Weaknesses: ### Pros
* The article proposes a compositional conditional generative model that can generate target peptides in a zero-shot manner by combining multiple constraints.
* The article provides a proof of the method’s validity.
### Cons
* The experimental section is not sufficiently comprehensive; more baselines need to be compared.
* Additionally, some experimental phenomena require more detailed discussion (see the experimental section for details).
* There are some grammatical issues and typos, and the writing needs improvement.
Other Comments Or Suggestions: The writing can be improved. I notice several typos:
* C.4. Hyperparamter details: Hyperparameter
* The overal workflow is depicted in Fig. 2. --> overall
* The sampled is acquired (near eq. 8): --> sample
I’ve noticed these errors, and there may be others as well. The author should carefully proofread the text to ensure accuracy.
Questions For Authors: I think this method is simple and novel, and the compositionality of the conditions has been proven to be injective. However, in real-world scenarios, is the combination of these conditions truly linear? (Is adding condition A and condition B really equivalent to A + B?) What do you think about this? Are there any methods to explore this further?
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: Thanks for the insightful comments which help improve the quality of our paper!
> Q1: The type and distance constraints may not be independent but rather intertwined, which the authors have not discussed.
Sorry for the confusion. We ensure that the constraints are jointly feasible by considering their dependencies both in the data and the model. First, the constraint combinations are sampled from the joint distribution derived from real-world data, based on the dataset during training and based on chemical knowledge during inference. Second, our model inherently accounts for these dependencies, as the constraints are input together and fused within the hidden layers to output the conditional denoising score.
> Q2: I believe the authors should compare their approach with basic diffusion models and some recent conditional generative models.
Thanks for the suggestion. We further include two more baseline methods, CADS, an advanced diffusion conditional sampler, and DiffPepBuilder, a model specifically designed for disulfide peptides, as below:
| Succ. | Staple | Head-Tail | Disulfide | Bicycle |
|-------|-----------:|-----------:|-----------:|-----------:|
|ours|21.42%|65.11%|41.25%|30.76%
| CADS | 27.14% | 45.54% | 3.75% | 3.85% |
| DiffPepBuilder| - | - | 23.07% | - |
For CADS sampler, we set the w=2 and use the sampler with initial noise scale as 0.25. The results indicate that CADS is acceptable under simple constraints but struggles with more complex constraints like disulfide and bicyclic peptides. Notably, despite being a general zero-shot model, our approach outperforms DiffPepBuilder, which is specifically designed for disulfide peptides.
> Q3: For the generated molecules, the authors only evaluate whether the cyclic peptide is successfully generated but do not assess the validity of the generated molecules. In addition to the success rate, they should also consider whether there are any unreasonable atomic types or coordinates in the generated structures, which could be measured using an appropriate metric. For the AA-KL and B-KL metrics, it does not clearly explain how the distribution divergence is computed.
Sorry for the confusion. We assess the validity of generated peptides by evaluating their residue composition and structural features to ensure they resemble natural peptides. Specifically, we use KL divergence on residue types and dihedral angles. AA-KL measures the KL divergence between amino acid distributions in generated peptides and reference peptides, excluding the controlled amino acid types. B-KL quantifies the KL divergence between dihedral angle distributions of generated and reference peptides, ensuring realistic backbone conformations. Additionally, we assess the structural stability of generated peptides using Rosetta energy scores. Our results show that 85.54% of cyclic peptides satisfying constraints achieve negative Rosetta scores, indicating their physical plausibility. This suggests that the model generates valid and stable cyclic peptides.
> Q4: In Table 2, the success rate of “2*Stapled” does not change with variations in w. While the paper acknowledges this phenomenon, it does not discuss the possible reasons behind it. What could be causing this? Did the authors check whether the unsuccessful cases at w = 2, 2.5, and 3 were the same set of samples?
We appreciate the insightful question! Upon examining the failure cases for w=2,2.5, and 3, we found that they are nearly identical. This suggests that, beyond a certain threshold, these cases have already collapsed into failure modes. As a result, further increasing the constraint strength does not impact the success rate.
> Q5: However, in real-world scenarios, is the combination of these conditions truly linear? (Is adding condition A and condition B really equivalent to A + B?) What do you think about this? Are there any methods to explore this further?
Thank you for your thoughtful question. We think there are some combinations not directly addictive. For example, a bicycle peptide may struggle to also satisfy the stapled peptide constraints, which we have observed in zero success rates for such cases. In most application scenarios, meaningful combinations are ensured by expertise in structural chemistry and biology. Additionally, low success rates for certain combinations can help identify infeasible or unrealistic configurations. | Summary: The paper proposes CP-Composer, a novel diffusion-based generative framework for zero-shot cyclic peptide design. The authors motivate their approach by highlighting the data scarcity problem in cyclic peptide design, where obtaining experimental data for diverse cyclization patterns is challenging. The key innovation presented in the paper is the decomposition of complex cyclisation constraints into simpler, composable "unit constraints" representing type and distance relationships. This decomposition allows the model to be trained on more readily available linear peptide data, learning these unit constraints and their combinations, and then generalizing to unseen, complex cyclic constraints at inference time. The method is evaluated on several cyclisation strategies (stapled, head-to-tail, disulfide, and bicycle peptides), demonstrating improved success rates in generating valid cyclic structures compared to existing baselines. The authors also present results from molecular dynamics simulations, providing evidence for the stability and binding affinity of the generated peptides. The primary application is the design of novel cyclic peptides, which have potential as therapeutic drug candidates. Overall, the paper presents a well-written and technically sound approach, contributing to the fields of peptide design and constrained generative modelling.
Claims And Evidence: The central claim of the paper is that CP-Composer enables effective zero-shot cyclic peptide design via composable unit constraints. However, to more convincingly demonstrate the advantages of the proposed approach and solidify its claims, the authors should expand the baseline comparison and provide a more rigorous theoretical justification for the guidance mechanism. Specifically, the comparison should be extended to include more advanced guidance techniques, such as the unified guidance framework presented in [1], which could readily incorporate the proposed unit constraints, a simply classifier-free guidance together with the CADS sampler [2]. Additionally, comparing against any existing, even if limited, methods specifically designed for cyclic peptide generation is important for contextualizing the performance gains. Moreover, the connection between the ideal conditional score (Eq.2) and the implemented guided score (Eq.3) should be strengthened. A more formal derivation, potentially drawing inspiration from the diffusion posterior sampling approach of [3] or the generalized h-transform [4] (who essentially end up with the same terms as Eq.3 for controlled generation), would provide a more solid theoretical foundation for the chosen guidance strategy. Addressing these points would enhance the paper's claims.
[1] Ayadi, S., Hetzel, L., Sommer, J., Theis, F., & Günnemann, S. (2024). Unified Guidance for Geometry-Conditioned Molecular Generation. Advances in Neural Information Processing Systems, 37, 138891-138924.
[2] Sadat, S., Buhmann, J., Bradely, D., Hilliges, O., and Weber, R. M. Cads: Unleashing the diversity of diffusion models through condition-annealed sampling. arXiv preprint arXiv:2310.17347, 2023.
[3] Chung, H., Kim, J., Mccann, M. T., Klasky, M. L., & Ye, J. C. (2022). Diffusion posterior sampling for general noisy inverse problems. arXiv preprint arXiv:2209.14687.
[4] Denker, A., Vargas, F., Padhy, S., Didi, K., Mathis, S., Barbano, R., ... & Lio, P. (2024). DEFT: Efficient Fine-tuning of Diffusion Models by Learning the Generalised $ h $-transform. Advances in Neural Information Processing Systems, 37, 19636-19682.
Methods And Evaluation Criteria: The proposed methods and evaluation criteria are generally appropriate for the problem of zero-shot cyclic peptide design, utilising relevant metrics. However, the experimental design could be strengthened to better support the claims and contextualise CP-Composer's performance.
- Section 4.1 (Zero-Shot Cyclic Peptide Generation): This section is meant to demonstrate the core capability of generating different cyclic peptide types in a zero-shot setting. However, the limited baselines (no existing cyclic peptide methods, basic energy guidance) weaken the comparison. Moreover, a more thorough analysis of failure cases would be insightful to understand the method's limitations.
- Section 4.2 (Flexibility in High-Order Combinations): Here, the authors show the framework's ability to handle complex, combined constraints, supporting the claim of generalisability. However, the relative advantage of CP-Composer is difficult to assess and the section would benefit from a more extensive comparisons with advanced baselines, which should also generalise to this more challenging setting.
- Section 4.3 (Evaluations by Molecular Dynamics): This section strengthens claims of practical utility with MD simulations, but the presented scope (two targets, two cyclization strategies) restricts general conclusions. More simulations, potentially build on faster approximate methods, would be great.
- Section 4.4 (Generalisation beyond Available Data): Here, the authors use t-SNE plots to visualise the generation of non-linear peptides. This could be strengthened by adding quantitative sequence analysis and a comparison of training and generated peptide sequences.
Theoretical Claims: I did not check the proofs in detail, focusing instead on the overall conceptual
soundness and experimental validation.
Experimental Designs Or Analyses: I reviewed the experimental designs, as detailed above. The primary concerns are the limited choice of baselines, which hinders a comprehensive evaluation of performance, and the need for a more rigorous theoretical justification connecting the proposed guidance mechanism to established works in the field.
Supplementary Material: I skimmed through the supplement material to check for additional visualisations and explanations regarding the chosen guidance scheme.
Relation To Broader Scientific Literature: The paper cites relevant works in the areas of diffusion models, geometric deep learning, and peptide design. However, the discussion of related work and the theoretical grounding could be strengthened. The discussion of diffusion guidance could be significantly improved by referencing and incorporating more advanced techniques, such as the unified guidance framework in [1] or the condition-annealed sampling approach in [2]. Furthermore, a more rigorous theoretical justification connecting the proposed guidance to established work like DPS [2] and DEFT [3] is needed. This would better position the work within the existing literature and address the limitations in the baseline comparisons.
Essential References Not Discussed: No essential works appear to be missing.
Other Strengths And Weaknesses: **Originality**: The setting of zero-shot cyclic peptide design via composable unit constraints, enabling training on readily available linear peptide data, is a novel contribution. However, the derivation of the guidance mechanism lacks novelty and could benefit from a more rigorous theoretical grounding, as discussed in previous sections. This makes the decomposition of complex cyclisation constraints into simpler, composable units (type and distance) the primary source of originality.
**Significance**: The work addresses a significant challenge in drug discovery, and if the claims were fully supported by a more comprehensive experimental evaluation, the work would be relevant for the peptide design community.
**Clarity**: The paper is well-written and structured logically, with core concepts and the proposed method clearly explained. The figures are informative, enhancing overall clarity.
Other Comments Or Suggestions: No.
Questions For Authors: 1) Could you elaborate on the specific challenges posed by Disulfide and Bicycle peptides for the baselines? Here, CP-Composer achieves the best success rates (even better than Stapled and HT) while the baselines fail.
2) Have you investigated any techniques to further improve the success rates, particularly for the higher order combinations?
____
I am willing to increase my score if the authors address the raised concerns.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for your suggestions!
> Q1:Comparing against any existing methods specifically designed for cyclic peptide generation is important for contextualizing the performance gains.
We include CADS, an advanced diffusion conditional sampler, and DiffPepBuilder, a model specifically designed for disulfide peptides, as below:
|Succ.|Staple|Head-Tail|Disulfide|Bicycle|
|-|-:|-:|-:|-:|
|Ours|21.42%|65.11%|41.25%|30.76%
|CADS|27.14%|45.54%|3.75%|3.85%|
|DiffPepBuilder|-|-|23.07%|-|
For CADS sampler, we set the w=2 and use the initial noise scale as 0.25. CADS is acceptable under simple constraints but struggles with more complex constraints like disulfide and bicyclic peptides. Notably, our zero-shot approach outperforms DiffPepBuilder, which is specifically designed for disulfide peptides.
> Q2: The connection between the ideal conditional score (Eq.2) and the implemented guided score (Eq.3) should be strengthened.
In fact, the rationale of Eq.2 and Eq.3 are linked by the following distribution
$$ \tilde{p}\_t(\mathcal{G}\_\mathbf{z}^{(t)}|\mathbb{C}) \propto p\_t(\mathcal{G}\_\mathbf{z}^{(t)}) p\_t(\mathbb{C}|\mathcal{G}\_\mathbf{z}^{(t)})^w, $$
with the corresponding conditional score
$$\nabla\_{\mathcal{G}\_\mathbf{z}^{(t)}}\log \tilde{p}\_t(\mathcal{G}\_\mathbf{z}^{(t)}|\mathbb{C}) =\nabla\_{\mathcal{G}\_\mathbf{z}^{(t)}}\log p\_t(\mathcal{G}\_\mathbf{z}^{(t)}) +w\nabla\_{\mathcal{G}\_\mathbf{z}^{(t)}}\log p\_t(\mathbb{C}|\mathcal{G}\_\mathbf{z}^{(t)})\approx\epsilon\_\theta(\mathcal{G}\_\mathbf{z}^{(t)},t) + w\nabla\_{\mathcal{G}\_\mathbf{z}^{(t)}}\log p\_t(\mathbb{C}|\mathcal{G}\_\mathbf{z}^{(t)}) .$$
In particular, Eq.2 directly models $\log p\_t(\mathbb{C}|\mathcal{G}\_\mathbf{z}^{(t)})$ by an externally trained energy function. Eq.3 instead follows classifier-free guidance by rewriting $\nabla\_{\mathcal{G}\_\mathbf{z}^{(t)}}\log p\_t(\mathbb{C}|\mathcal{G}\_\mathbf{z}^{(t)})=\nabla\_{\mathcal{G}\_\mathbf{z}^{(t)}}\log p\_t(\mathcal{G}\_\mathbf{z}^{(t)}|\mathbb{C})-\nabla\_{\mathcal{G}\_\mathbf{z}^{(t)}}\log p\_t(\mathcal{G}\_\mathbf{z}^{(t)})\approx\epsilon\_\theta(\mathcal{G}\_\mathbf{z}^{(t)},\mathbb{C},t)-\epsilon\_\theta(\mathcal{G}\_\mathbf{z}^{(t)},t),$ which gives Eq.3 after simplification.
> Q3：A more thorough analysis of failure cases would be insightful to understand the method's limitations.
As for failure cases, they commonly occur when excessively large controling strength w degrade molecular quality. We analyzed peptide structures generated with w=6 (https://anonymous.4open.science/r/Rebuttal-68EF/readme.md) and found that they often exhibited strained backbones and unrealistic conformations. This highlights the trade-off between guidance strength and structural integrity, suggesting that an adequate selection strategy for w could further improve robustness.
> Q4: The relative advantage of CP-Composer is difficult to assess and the section would benefit from a more extensive comparisons with advanced baselines, which should also generalise to this more challenging setting.
First, our model allows arbitrary high-order combinations, as shown in the paper. Second, the comparison with DiffPepBuilder below indicate that, despite being a general zero-shot model, our approach outperforms the baseline specifically designed for disulfide peptides.
|2*-S-S-|CP-Composer|DiffPepBuilder|
|-|-:|-:|
|Succ.|62.0%| 30.48%|
> Q5: The authors use t-SNE plots to visualise the generation of non-linear peptides. This could be strengthened by adding quantitative sequence analysis and a comparison of training and generated peptide sequences.
Sorry for the confusion. Our current cluster analysis in Figure 6 is already based on the embedding generated from ESM2 model, which outputs embeddings based on the sequence information.
> Q6: Could you elaborate on the specific challenges posed by Disulfide and Bicycle peptides for the baselines?
Disulfide and Bicycle peptides need requires more strict constraints than Stapled peptide and Head-to-tail peptide. Dislfide peptide need one distance constraint unit and two type constraint unit. Bicycle peptides need three distance constraint units and three type constraint units. While the Head-to-tail peptide only needs one distance constraint unit and the Stapled peptide needs one distance constraint and two type constrinis easier to reach as both K-D and K-E are accepted.
> Q7: Have you investigated any techniques to further improve the success rates, particularly for the higher order combinations?
As an initial attempt at zero-shot cyclic peptide generation, our focus is to demonstrate the feasibility and generalizability of our framework, which already shows promising results. However, in more complex constraint combinations, conflicts may arise, potentially driving the generated peptides in divergent directions. Addressing these conflicts to further improve success rates is an important challenge that we leave for future research.
---
Rebuttal Comment 1.1:
Comment: I would like to thank the authors for their efforts during the rebuttal period. I have carefully reviewed their responses, as well as the other reviewers’ comments. For the revised version of the paper, I find it important that the authors include their insights from Q1 and Q2 and update their method discussion based on my original feedback (as outlined in the "Claims and Evidence" section).
Assuming the authors will adequately address these points in the final version—particularly by softening the claim in L193–194 and clearly situating their work in relation to the prior literature I referenced—I am raising my score.
---
Reply to Comment 1.1.1:
Comment: Thank you for your positive feedback and support! We’re glad to hear that our responses have addressed your concerns. Following your valuable suggestions, we will incorporate all rebuttal content into the final version to further enhance the quality of our paper. | null | null | null | null | null | null | null | null |
RLEF: Grounding Code LLMs in Execution Feedback with Reinforcement Learning | Accept (spotlight poster) | Summary: The paper proposes an end-to-end multi-turn RL framework to teach LLM self-repair/refine based on execution feedback, particularly focused on the code generation domain, where the unit tests and execution feedback is easy to obtain. The main algorithm is PPO with turn-level value function to calculate the advantage, along with a common KL penalty. Empirically, the method shows strong improvement on the CodeContests benchmark using Llama 3.1 models, and sees generalization performance across HumanEval and MBPP. Some interesting ablation studies are also conducted, such as few-shot prompting, SFT on success attempts, single-turn RLEF, etc.
Claims And Evidence: Most of the claims the paper made are from the experiment results (section 3.2), centered around the effectiveness of the multi-turn rl based on execution feedback:
- the strong performance of RLEF compared with prior work, which supported by comparing with a wide range of baselines such as alphacode, code llama and alphacodium, etc.
- the generalization performance to HumanEval and MBPP, can we report CI for the numbers in Table 2 as well? The generalization performance seems worse compared to CC. Test, is the improvement statistically significant?
- RLEF tends to increase the errors fixed in the followup turns, and give much more code changes. This is examined in both the llama 7b and 80b models. Some questions here: (1). any hypothesis on why there is more timeout in later turns for the model being RLEFed. (2). for the eval of code changes (1-chrF), could we have a more refined analysis on model is simply re-attempting? or is doing real fixes?
- There are some claims about the diversity within a roll-out, L312-L316. I am a little bit confused here, i think diversity only values when (1). we want to do independent sampling; so we get a higher pass@k as k increases or (2). the diversity at the end of the roll-out, this is the response we will eventually used? In view of the diversity within the rollout, why this is a desirable criteria, i feel more evidence or justification is needed here.
- In ablation studies, the study of baselines (i.e., few-shot prompting and SFT) is interesting, any idea on why few-shot shows worse performance? is it a more general statement?
- Another claim regarding with the pre-trained models seem to benefit more from IF, than code-specific SFT for code generation performance, it would be give more hypothesis or justification here.
Methods And Evaluation Criteria: The method of using end-to-end multi-turn RL to solve the code repair problem is pretty reasonable and solid. Code generation naturally has the execution feedback to be used as intermediate feedback to teach self-repair.
The evaluation is conducted on common code generation benchmarks, CodeContests, MBPP and HumanEval.
Theoretical Claims: There is no theoretical claims in the paper, N/A.
Experimental Designs Or Analyses: The benchmark, baseline and evaluation metrics in general makes sense, some minor issues i saw:
- I do like the idea of testing how much the model learns from the execution feedback, but random feedback seems a too weak baseline, it would be ideal to add other more reasonable baselines, such as no execution feedback, give model binary / numerical reward only, or using a subset of public tests? An even more realistic setup in to let LLM self-generate some unit tests, and use it in the multi-turn training process, this might be out of the scope of the current paper, but might be interesting to see.
Supplementary Material: No
Relation To Broader Scientific Literature: This paper is relevant to a broader community such as LLM, multi-turn RL, code generation.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: Strength:
- The paper studies an interesting problem of code-generation using multi-turn RL.
- The extensive set of ablation studies is interesting in this paper, such as the comparison with few-shot, SFT, single-turn RL.
Weakness:
- One major weakness I saw from the paper is that the method section is too dense, and it would be great if it could be written into more details, such as the turn-level value function, the task-specific implementations, etc.
- As mentioned before, it would be interesting to include more realistic case studies regarding to the quality / availability in the unit tests to be used in RLEF.
Other Comments Or Suggestions: See discussions in previous sections.
Questions For Authors: See discussions in previous sections.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We deeply appreciate the reviewer's comments and feedback on our manuscript.
> the generalization performance to HumanEval and MBPP, can we report CI for the numbers in Table 2 as well? The generalization performance seems worse compared to CC. Test, is the improvement statistically significant?
We will extend Table 2 with results on LiveCodeBench and confidence intervals for the Appendix: https://imgur.com/a/CpsZMJB
CIs are estimated following AlphaCode, i.e., we repeatedly (200x) sample a subset of the solutions with replacement and estimate 1@3 solve rates. We then take the 2.5% and 97.5% percentiles.
> any hypothesis on why there is more timeout in later turns for the model being RLEFed
Our hypothesis is that this is an effect of solutions passing the public tests but failing under increased problem sizes that may be part of the private test sets.
> could we have a more refined analysis on model is simply re-attempting? or is doing real fixes?
> i think diversity only values when (1). we want to do independent sampling; so we get a higher pass@k as k increases or (2). the diversity at the end of the roll-out, this is the response we will eventually used? In view of the diversity within the rollout, why this is a desirable criteria, i feel more evidence or justification is needed here.
Diversity of solutions within a single rollout can be important. When a proposed solution fails, it may be advantageous to start with a fresh/different approach rather than to address fixes, e.g., if the wrong algorithm was selected, fixing the runtime error would not lead it to be the correct one. Notably, our analysis shows that, without specific training, available LLMs are often not good at refining or changing their solutions.
> In ablation studies, the study of baselines (i.e., few-shot prompting and SFT) is interesting, any idea on why few-shot shows worse performance? is it a more general statement?
We don't claim that our conclusions regarding the negative effect of few-shot prompting can be readily generalized to other domains. However, we think the general ranking of learning methods as few-shot < SFT < RL is accurate.
> I do like the idea of testing how much the model learns from the execution feedback, but random feedback seems a too weak baseline, it would be ideal to add other more reasonable baselines, such as no execution feedback, give model binary / numerical reward only, or using a subset of public tests?
The choice of random execution feedback to test the sensitivity is motivated as follows: with our training regime, a trained model can infer that a solution is wrong solely based on the fact that it is prompted for another solution, and the public tests are already included in the initial prompt. Hence, a model insensitive to textual feedback could simply ignore it and propose another solution.
It is thus hard to arrive at a pure "no execution feedback" setting for this experiment, since any re-prompting signals to the model that the previous solution was wrong. Nevertheless, we ran a small study where we replace the textual execution feedback with the string "Consider if the previous solution is correct and provide a new one if it is not." We see small drops in performance for both 8B (17.1 -> 16.8 on valid, 16.0 -> 14.5 on test) and 70B (37.1 -> 34.7, 40.6 -> 40.1) RLEF-trained models for 1@3 solve rates. We get a more pronounced performance reduction from random execution feedback (8B: 17.1 -> 16.0, 16.0 -> 13.8; 70B: 37.1 -> 31.6, 40.6 -> 36.7).
We would also like to refer to Figure 4(a) in the paper, which shows that, with random execution feedback, models can still propose many solution candidates to the effect that pass@10 scores are closely matched. With execution feedback, solutions proposed in later turns are more targeted, either wrt repairs or in terms of new approaches, which leads to gains in precision (pass@1).
> An even more realistic setup in to let LLM self-generate some unit tests, and use it in the multi-turn training process, this might be out of the scope of the current paper, but might be interesting to see.
We agree, a combination with test generation would be very interesting. We'll hopefully see this in future work. | Summary: This paper finetunes LLMs for multi-turn code generation with PPO. The action is code generation/refinement using LLMs. The model is given public test cases for code evaluation and then refinement. The epsidoe ends either when reaching the maximum turn limit or when the generated codes pass the public tests. The reward of the episode is then if the final codes pass the private the test cases. The model is finetuend and evaluated using the train/val/test splits of CodeContests.
## update after rebuttal
It's a pity that the improvements on livecodebench are not significant.
Claims And Evidence: This paper claims the proposed method, RLEF, is state-of-the-art for improving code generation performance. However, the model is only evaluated on old benchmarks such as CodeContests, HumanEval, and MBPP, suffering the risk of data contamination. Also, there is no baseline performance using Llama-3.1 as the backbone, which raises the concern of unfair comparison. More experimental results are needed to support the claim.
Methods And Evaluation Criteria: The method is intuitive, using PPO to tune multi-turn code generation models.
Theoretical Claims: No theoretical claims.
Experimental Designs Or Analyses: The baseline models (as listed in Table 1) all use old pretrained models. Llama 3.1-70B, by itself, already bypasses many of them with RLEF. It is hard to tell if RLEF is the key factor for performance improvement.
The model is only evaluated in old benchmarks as well. It would be much better to evaluate the model in recent benchmarks such as livecodebench.
Supplementary Material: No
Relation To Broader Scientific Literature: It targets the important multi-turn code generation problem and shows improved performance in several benchmarks.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: N/A
Other Comments Or Suggestions: N/A
Questions For Authors: * Are there results in newer benchmarks?
* Are there results of baselines using the same backbone?
* Are there results in more diverse settings, such as more samples per rollout with and without the public test cases?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank the reviewer for their valuable feedback and comments and provide the following responses:
> Data Contamination
We build off the Llama 3.1 models which were originally evaluated on benchmarks like HumanEval and MBPP as well. On top, we add training data from CodeContests exclusively; we hence regard the risk of data contamination as low.
> No baseline with Llama 3.1 Backbone
We thank the reviewer for this suggestion. We ran AlphaCodium with Llama 3.1 70B Instruct and obtained solve rates of 34.2 on valid and 27.8 on test, i.e., below the corresponding GPT-4 numbers and notably *below* the 10@100 results for this model, which uses an equal sample budget.
We hence do not think that starting from Llama 3.1 results in an unfair advantage.
> The model is only evaluated in old benchmarks as well. It would be much better to evaluate the model in recent benchmarks such as livecodebench.
We will add a LiveCodeBench evaluation with questions up to 10/2024 in the Appendix, extending Table 2: https://imgur.com/a/CpsZMJB
While we see significant improvements for both model scales, we do not observe gains of the same magnitude as on CodeContests.
> Are there results in more diverse settings, such as more samples per rollout with and without the public test cases?
In Figure 4 we increase the number of samples per rollout (turns), and we also measure performance when iterating on private tests in Appendix B.3 and observe additional (albeit limited) gains. | Summary: This paper introduces RLEF - a reinforcement learning method for improving natural language to code generation in an iterative setting. The method treats code generation as a multi-turn conversation, where a language model first produces a program then receives and interprets textual execution feedback to refine solution. This feedback is incorporated as part of the RL training loop. At each turn, the model’s reward depends on whether the final solution passes a private unit tests, while intermediate attempts are guided by test outputs in the prompt based on public tests.
The model is evaluated on the CodeContests competitive programming benchmark showing that RLEF-trained models achieve notably high accuracy using fewer attempts than earlier approaches such as AlphaCode and more recent GPT-based agentic pipelines. The authors provide analyses showing that the model not only generates correct solutions more often but also reliably fixes its own errors in response to execution messages.
Claims And Evidence: Most of the paper’s key claims appear to be backed by concrete evidence. In particular, the central claim that RLEF enables a model to iteratively repair its output and reliably improve code solutions is supported by detailed experiments on CodeContests.
Methods And Evaluation Criteria: The proposed method focuses on iterative code generation and repair, where a model generates an initial solution, receives execution feedback (error messages, test results), and refines its solution. The method also makes sense from an agentic AI perspective, as it pushes models toward self-correcting behavior, which is critical for real-world coding applications.
The evaluation criteria and benchmarks chosen for testing RLEF -- CodeContests, HumanEval+, and MBPP+ -- are reasonable choices, as they represent progressively challenging levels of function synthesis and competitive programming tasks. However, one potential limitation is that these benchmarks focus primarily on single-function correctness and may not fully assess RLEF’s potential for broader software engineering workflows (e.g., multi-file program synthesis, debugging, GitHub issue resolution). While HumanEval+ and MBPP+ demonstrate some generalization beyond competitive programming, additional real-world benchmarks, such as SWE-bench or GitHub Issues, could further validate RLEF’s applicability to industrial coding tasks. Nonetheless, for the specific problem of iterative function-level code improvement, the chosen evaluation framework is sound, and the results convincingly demonstrate the effectiveness of execution feedback-driven RL.
Theoretical Claims: The paper does not introduce new formal theoretical proofs but relies on established RL theory, specifically PPO. The correctness of PPO’s formulation is well-documented, and the paper applies it appropriately without requiring independent verification.
However, the paper makes implicit theoretical claims, such as:
* Multi-turn execution feedback leads to better policy learning than independent sampling, and
* Binary pass/fail rewards are sufficient for meaningful RL-based improvement.
While these claims are empirically validated, they lack formal guarantees. Additionally, exploring whether dense reward shaping (like, penalizing specific error types differently) would improve learning efficiency remains largely an open question.
Experimental Designs Or Analyses: The paper’s experimental setup is well-structured, using CodeContests, HumanEval+, and MBPP+ to test RLEF’s ability to improve NL to code generation through execution feedback. Solve rates, pass@k, and sample efficiency comparisons are appropriate metrics, and multi-turn evaluation reflects real-world debugging scenario. Ablation studies (like e.g. random feedback) confirm that the model genuinely learns from execution feedback rather than random resampling.
The experiments are strong and well-designed, but direct DeepSeek, GPT, etc model benchmarking, real-world coding tasks, and alternative reward structures would further validate RLEF’s generalization and efficiency.
Supplementary Material: N/A
Relation To Broader Scientific Literature: The paper builds on reinforcement learning for code generation, drawing from RLHF but replacing human preference signals with automated execution feedback. This aligns with some prior work like CodeRL (Le et al., 2022) and RLTF (Liu et al., 2023), which also optimized LLMs using execution-based rewards. However, RLEF extends this by treating execution feedback as an interactive state rather than a static reward, enabling multi-turn code refinement instead of single-shot optimization.
RLEF also connects to LLM-as-agent frameworks, such as AutoCodeRover (Zhang et al., 2024), which resolves GitHub issues via iterative debugging. Unlike AutoCodeRover, RLEF trains the policy itself, rather than relying on prompting alone. Additionally, it relates to DeepSeek-R1, which also leverages execution-based RL, but RLEF explicitly integrates textual execution feedback into decision-making, making it more akin to self-debugging code models. These connections places RLEF at the intersection of RL-based LLM fine-tuning, execution-grounded AI agents, and automated software repair.
Essential References Not Discussed: AutoCodeRover (Zhang et al., 2024) and other recent automated debugging agents that iteratively fix GH issues using test failures as guidance. While they use tool-based error localization, RLEF’s policy learning approach could complement these methods, making their inclusion relevant to agentic coding workflows.
Other Strengths And Weaknesses: Strengths:
* The integration of execution feedback as a dynamic env signal in RL is novel compared to prior one-shot RL for code generation (e.g., CodeRL, AlphaCode).
* Bridges reinforcement learning and agentic AI, making it relevant for self-improving AI coding assistants, debugging agents, and autonomous software maintenance.
* The paper is well structured and easy to read.
Weaknesses:
* Limited evaluation scope: CodeContests is a strong benchmark but focuses on single-function correctness, not full software debugging or open-ended programming tasks. Evaluation on real-world bug-fixing benchmarks (e.g., SWE-bench) would strengthen the paper.
* No direct comparisons to GPT-4, DeepSeek-R1 or other leading models for code.
* RLEF uses binary pass/fail rewards, but no ablation tests whether denser rewards (e.g., partial credit for fixing certain test cases) could accelerate training.
Other Comments Or Suggestions: no
Questions For Authors: 1) Explore finer-grained rewards:
RLEF uses a binary pass/fail reward, but no ablation tests whether partial credit for fixing certain test cases or reducing runtime errors could improve the results.
Did you experiment with denser rewards (weighted scoring based on passing test subsets or fixing specific error types)?
2) How well does RLEF generalize beyond function-level synthesis?
The evaluation focuses on competitive programming benchmarks (CodeContests, HumanEval+, MBPP+), which emphasize single-function correctness rather than real-world software debugging or multi-file code synthesis.
Have you tested RLEF on different prompt styles and benchmarks like SWE-bench, or other multi-file programming tasks?
If RLEF does not generalize well beyond competitive programming, its real-world applicability may be more limited than implied. A broader evaluation would solidify its impact for practical software engineering tasks.
3) How does RLEF compare to iterative prompting methods like Reflexion or Self-Refine?
The paper compares against standard fine-tuned baselines but not against iterative self-improvement prompting approaches (e.g., Reflexion, Self-Refine).
Have you tested RLEF against few-shot prompting strategies that also incorporate execution feedback (but without RL-based fine-tuning)?
4) Performance on out-of-distribution tasks
The benchmarks used (CodeContests, HumanEval+, MBPP+) are very well established but contain somewhat templated problem formats.
Have you tested RLEF on entirely novel problem distributions, such as real-world coding tasks and prompt styles not present in training?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We thank the reviewer for their thoughtful review and valuable feedback.
Based upon their feedback, we investigated the performance of DeepSeek-R1-Distill-Llama-70B in our exact same setting. With a single generation (temp=0.6, prompted with "<think>\n"), we obtained solve rates of 38.5 and 33.9 on the valid and test sets; with execution feedback over three turns, we obtained 41.0 and 37.6, respectively. This places the model in the same ballpark as our RLEF-trained 70B model (37.5 and 40.1).
However, we also note that this required a vastly increased inference budget compared to our models, with up to 10k thinking tokens per turn (this limit would often be reached, and we force-close the thinking section in this case). This renders the comparison quite difficult as our paper places a large emphasis on apples-to-apples comparisons, and allowing for large reasoning budgets would effectively shift the goal posts.
That said, it is evident that DeepSeek-R1 or o1/o3 excel at competitive coding tasks. Therefore, we will update our abstract, intro and experimental work section and do no longer claim state-of-the-art performance in competitive coding tasks.
> AutoCodeRover (Zhang et al., 2024) and other recent automated debugging agents that iteratively fix GH issues using test failures as guidance.
We thank the reviewer for this pointer; we added a reference in our related work section.
> Limited evaluation scope
We fully agree that extending our work to open-ended and long-horizon coding tasks SWE-bench is an exciting future direction of our work. For the current paper, however, we consider this out of scope.
For SWE-bench in particular, current research suggests that substantial domain-specific fine-tuning is required to achieve competitive results. For closed-source frontier models, performance started to increase rapidly once the benchmark was available and the distribution of tasks was known.
We note that we exclusively train on the CodeContest training set, and we would expect that widening the evaluation scope towards new settings will likely come with new training data requirements.
> No direct comparisons to GPT-4, DeepSeek-R1 or other leading models for code.
We discuss DeepSeek-R1 at the top of this reply. We include GPT-4o in Table 2, and GPT-4 is used in AlphaCodium and MapCoder (Table 1) which we outperform.
> RLEF uses binary pass/fail rewards, but no ablation tests whether denser rewards (e.g., partial credit for fixing certain test cases) could accelerate training.
We agree with the author but defer this to further work. Here, we showed that even with a sparse outcome reward we can achieve large gains. We did not experiment with denser rewards.
> RLEF vs. Reflexion or Self-Refine
We refrained from applying prompting strategies in our work and instead focused on domain-specific fine-tuning. However, CodeTree (https://arxiv.org/abs/2411.04329) contains results on the CodeContests test sets with Reflexion (Table 2). With Llama 3.1 8B, they obtain a solve rate of 13.5 with 20 samples. Our RLEF-trained version obtains 16.0 with a budget of 3 samples.
In our paper we also experimented with few-shot prompting (Table 3) but found it to not work well for our use-case. | Summary: This paper proposes an RL training strategy for Code LLMs to enable them to refine generated code using execution feedback besides the capability of following instructions. They present an exhaustive analysis on different aspects of their RLEF-trained models including their inference time behavior, performance gains at different sampling budgets, comparison with other state of the art solutions, and algorithmic alternatives like SFT, single turn RL training, prompting, etc.
Claims And Evidence: I find the evidence presented through the experiments in this paper convincing overall, except for one issue when studying the inference time behavior described below.
- Fig 3 / Line 295: The goal here is to study and establish the sensitivity of RLEF trained model to the feedback from execution. I think using no feedback would have made more sense to be studied as a baseline to compare against, as random feedback included in the prompt to an LLM at any turn is very likely to hurt model performance.
Methods And Evaluation Criteria: In my assessment, the proposed methods and evaluation criteria make a lot of sense for the problem of code generation from natural language instructions.
Theoretical Claims: NA
Experimental Designs Or Analyses: Yes, I find the experimental design and analyses to be very sound.
Supplementary Material: No.
Relation To Broader Scientific Literature: This work is related to prior work on code generation like AlphaCode, AlphaCodium, Mapcoder and CodeRL.
Essential References Not Discussed: I understand techniques like GRPO gained prominence only recently with the release of Deepseek-R1, but I believe adding commentary or comparison to such alternatives to PPO and the requirement of the value function network can benefit the placement of the paper in the present day context of LLM research. E.g. algorithms discussed in Back to Basics: Revisiting REINFORCE Style Optimization for Learning from Human Feedback in LLMs (Ahmadian et al)
Other Strengths And Weaknesses: Strengths:
- Idea is very well-positioned - motivating RL for training agents that can follow instructions and incorporate feedback from environments
- Adaptation of PPO to the setting of code as described in Section 2.2 is non-trivial
- Commentary on how they differ from prior work (Le et al (CodeRL)) could help establish their novelty in Section 2 itself, instead of deferring this discussion to the related work.
- Results are convincing
- CodeContests is a very challenging benchmark, and their baselines include prominent agentic frameworks
- Authors have augmented their findings with good intuition for readers based on their ablation studies (Section 3.3, Line 281 onwards). I particularly liked the thorough nature of the study performed on inference time behavior.
- Authors have put in great care in ensuring baselines are reasonable to compare with (for eg - see Line 209)
- Paper is well written and the caveats of the methodology design are sufficiently described
Other Comments Or Suggestions: Suggestion: Discussion on extension to domains beyond code synthesis is only loosely referred to towards the end of Section 4, but the introduction section seems to offer greater promise. For instance, authors could discuss how execution feedback can be generalized to collect beyond code - on verifiable domains like math related tasks, and how all such signals combined (human, execution environment, math correctness) can lead to training of more capable LLM agents. Positioning this contribution in the context of recent advances like Deepseek-R1 will greatly benefit this paper.
Minor/typos:
Line 306: the a --> the
Section 3.2: Para 2: with a single rollout compared to 5 solutions from 100 samples (38.0 and 29). Did you mean 40.1 here instead of 38? Otherwise the results in Table 1 don't match with this description.
Line 244: What does "stock" mean here?
Questions For Authors: - In Section 2.2, you mention the choice of granularity of reward / advantage being action level instead of token level. Can you elaborate more on the alternatives to this choice and what impact one could expect from choosing token level reward or advantage?
- Section 3.2 Para 1: "Each solve rate is estimated on 200 rollouts ..." Here do you not discard the rollouts where the final solution obtained does not pass public tests?
- Table 1: What would be the impact of sampling temperature on these results? Why was greedy decoding not attempted with the multi-turn single rollout setup? (where 1 rollout <= 3 samples/turns?)
- Line 252: To combat the effect mentioned here (RL training reducing diversity of outputs) can one use higher temperature? What could be other ways of addressing this concern? Is this a concern at all?
- Line 286 - you attribute the higher scores in iterative setting to increased diversity in sampled solutions. This seems to contradict with Line 250 where you cite Kirk et al (2024) who find that RL training can reduce diversity also suggested by your results in Table 1. I am confused with the conclusions from these 2 lines.
- Fig 3: Why do you choose to indicate errors fixed in turns 2 and 3? As a reader I think showing the drop of errors over the turns would be easier to follow through this plot.
- Fig 4b: Can you comment on the gap between the instruct and RLEF models? Does it show any upward or downward trend with the sample budget?
- Section 3.4.1 - What is the scale of the SFT dataset synthesized for this study? I'm not certain if suggesting the ineffectiveness of SFT for iterative code refinement is a valid takeaway. I think this finding needs to be augmented with a solid explanation - which could perhaps be the difficulty in designing synthetically / collecting supervised datasets for this task.
- Section 3.4.2 - Is the single turn SFT dataset coming from Code Contests benchmark? Is the takeaway here that this training set is most effective only when used through the RLEF stage (which uses only the test cases and not the ground truth solutions)? Generally SFT datasets are used to fine-tune a checkpoint, and then environment feedback is used to train in the RL phase, but I see no such comparison here. What'd the result be if RLEF was performed on the SFT (single/multi turn) trained checkpoint?
- Section 3.4.2 - "We attribute this to the existent but comparabily weak multi-turn capabilities of the vanilla ..." I don't agree with this conclusion, and I would instead attribute this to the RLEF (ST) training given that the instruct model doesn't benefit much from MT during inference (25.6 to 25.9), whereas after RLEF the gains are a lot more pronounced (28.3 to 31.1).
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We thank the reviewer for the thorough analysis of our paper, their valuable suggestions and stimulating questions.
## Updates
Re. GRPO: We will add the following to the end of our related work section:
More recently, DeepSeek-AI et al. (2025) observe emerging reasoning capabilities with a large-scale application GRPO (Shao et al., 2024) to math and code problems and achieve high performance on competitive programming tasks. We thus consider the training of reasoning models with program execution feedback and, likewise, the introduction of execution feedback to math domains, a promising avenue for future research.
> Line 244: What does "stock" mean here?
This refers to the officially released Llama models, in this case Llama 3.1 70B Instruct; we will clarify the wording.
## Answers to Questions
### Sensitivity to Execution Feedback
Due to space constraints, we refer the reviewer to our response to Reviewer 3JDi below, where we discuss the choice of random execution feedback and also list solve rates for a "no execution feedback" test.
### Granularity of Reward: Turn- vs. Token-Level
We provide experiments regarding a token-level value function in Appendix B.5. With token-level rewards, we found that the KL penalty biases the model to unreasonably short generations in intermediate turns, and in B.5 we test the combination in which we still provide averaged KL penalties per turn but a learn token-level value function (and hence obtain per-token advantages). We observe worse results with this approach.
### Discarding Rollouts
We generally do not discard rollouts for evaluation and do not consider public tests in scoring unless noted otherwise. A rollout with 3 turns without a solution passing the private tests will count as a failed sample, similar to rollouts with 1 or 2 turns where public tests are passing. A rollout with a successful result will count as a successful sample. In other words, one rollout corresponds to one sample.
To compare under equal sampling budgets, we then consider the "1@1" and "1@33" performances in this setting as "1@3" and "1@100" solve rates. NB, models will not utilize the full budget due to some rollouts ending early with correct responses.
### Results with Greedy Decoding
We observe slightly better results with a low temperature compared to greedy decoding.
### Diversity in Outputs
The question of whether a loss of diversity is a concern depends on the intended applications. Remedies can be found on the RL algorithm level as shown in https://arxiv.org/abs/2503.19595, for example. We found a temperature of 1.0 to deliver best performance in the large-sample regime; this may be linked to the fact that we use a temperature of 1.0 during rollouts as well.
Re Line 286, output diversity depends on the evaluation setting. From the analysis in Table 3 it is clear that base models do not sample diverse solutions *within* a rollout. However, they can produce a large number of different solutions from the initial prompt, in particular with higher temperatures. What makes RLEF-trained models effective is that they can utilize execution feedback to either repair an existing solution or to propose a new approach.
### Figure 3
We selected to show "errors fixed" here to highlight differences between the different models and settings. The X-axis scale is different for "Errors" and "Errors Fixed". While we regard the reported differences as significant, they would be hard to discern visually under the X-axis scale of the leftmost plots.
### Gap Between Instruct and RLEF models wrt. Sample Budget
We did not study the diversity aspect in the limit, i.e., under very large sample budgets. We would expect the gaps to narrow in the limit due to decreased output diversity. An interesting question would however be if this can be offset by sampling longer and longer trajectories.
### SFT Dataset
Yes, the SFT dataset was obtained solely from the CodeContest training dataset. It consists of 313,639 trajectories. The result that RL can work better than SFT is in line with references discussed in the paper, i.e., Xu et al and Kirk et al, and also the recent results around DeepSeek-R1.
### Existing MT capabilities of 70B
> Section 3.4.2 - "We attribute this to the existent but comparabily weak multi-turn capabilities of the vanilla ..." I don't agree with this conclusion, and I would instead attribute this to the RLEF (ST) training given that the instruct model doesn't benefit much from MT during inference (25.6 to 25.9), whereas after RLEF the gains are a lot more pronounced (28.3 to 31.1).
We were referring to the fact that the 70B model already exhibits multi-turn capabilities (although the valid set difference is not statistically significant) when compared to the 8B model, for which performance drops in the multi-turn setting. | null | null | null | null | null | null |
Trajectory World Models for Heterogeneous Environments | Accept (poster) | Summary: This manuscript has 2 contributions:
1. A trajectory dataset UniTraj, a large-scale dataset including over one million trajectories collected from various distributions from 80 heterogeneous environments.
2. A Transformer-based architecture TrajWorld integrates interleaved variate and temporal attention mechanisms, aiming at transition prediction.
The authors first introduced the current challenge for trajectory prediction in a heterogeneous environment and their motivation. Then introduced the building process of dataset UniTraj, the architecture of TrajWorld model. The proposed model was tested on 15 datasets of 3 environments, which validated its performance.
Claims And Evidence: Yes, I think this manuscript is well-organized and clearly stated.
Methods And Evaluation Criteria: Yes.
Theoretical Claims: Yes. I think the authors clearly described the problem, related works, and their ideas.
Experimental Designs Or Analyses: Yes. This proposed model used a two-way attention mechanism. The authors set a similar but with a one-dimensional attention model as the baseline, validating the good performance of the two-way attention mechanism
Supplementary Material: Yes, I checked the Experimental Details, specifically the baseline, the hyperparameter of the proposed model, and the ablation study.
Relation To Broader Scientific Literature: The large-scale dataset can be a helpful tool for broader scientific literature.
Essential References Not Discussed: n/a
Other Strengths And Weaknesses: I think the proposed dataset can be helpful for other researchers. And the proposed model can be a good baseline to study with.
Other Comments Or Suggestions: n/a
Questions For Authors: n/a
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We sincerely appreciate Reviewer bd1u's strongly positive feedback on our work. Your recognition of our clear writing, well-motivated approach, and the effectiveness of both our UniTraj dataset and TrajWorld architecture is truly encouraging. We are grateful for your support and share your belief that our work will contribute meaningfully to the broader scientific community. | Summary: This paper introduces the UniTraj dataset, which contains a large set of trajectories collected from 80 heterogeneous environments. It also presents a world model, TrajWorld, pretrained on this dataset. The pretrained world model demonstrates positive transferability to new environments in zero or few-shot settings. The paper primarily evaluates the trained world model in an off-policy evaluation setting for transition prediction policy evaluation.
Claims And Evidence: The main claim is that by pretraining on a diverse set of trajectory environments, the pretrained world model can adapt to unseen environments with zero-shot or few-shot transfer, demonstrating improved transition prediction ability. Compared to previous models, the proposed model achieves better transferability in an offline setting. However, the authors did not test its ability to utilize the pretrained world model online, as was done in previous work with MPC. There are also some questions for the experiment setup that need to be clarified.
Methods And Evaluation Criteria: Yes, for the most part, the proposed methods and evaluation criteria align with the problem and application at hand. The use of the UniTraj dataset for pretraining and the off-policy evaluation (OPE) setup are reasonable choices for assessing transferability in heterogeneous environments. However, there are some concerns relate to the experiment design which will be discussed in that section.
Theoretical Claims: N/A
Experimental Designs Or Analyses: After closely looking at the experimental design, I have the following concern regarding its setup.
Compared to Schubert et al. (2023), why did the authors choose to evaluate using off-policy evaluation rather than a more realistic setting where the learned WM is directly used to solve the task online through MPC in the real environment?
In the related work section, the main point authors is trying to argue is that Schubert et al. (2023) did not show a positive transfer in walker 2D environment but Schubert et al. (2023) evaluates differently compared to this work. I consider the evaluation setup of Schubert et al. (2023) is more challenging as they need to solve the problem with the real environment through MPC.
Supplementary Material: I checked B.1. Table 3. Table 4. in the Appendix.
Relation To Broader Scientific Literature: Modeling a world model is important for creating realistic simulations, especially when running such simulations is costly. This paper demonstrates that with a transformer-based world model and a diverse set of related environments, one can produce an adaptive world model prior.
Essential References Not Discussed: The close related work is discussed Schubert et al. (2023), though regarding the novelty of the transformer architecture, factorized transformer [1] was not mentioned.
[1] Nayakanti, N., Al-Rfou, R., Zhou, A., Goel, K., Refaat, K.S. and Sapp, B., 2023, May. Wayformer: Motion forecasting via simple & efficient attention networks. In 2023 IEEE International Conference on Robotics and Automation (ICRA)(pp. 2980-2987). IEEE.
Other Strengths And Weaknesses: Strength:
The analysis in the experiment section is detailed and clear.
Proposed architecture performs better than the re-implementation of the baselines and demonstrate good transfer ability.
Weakness:
The proposed transform architecture look similar to the factorized attention in previous work, which makes the novelty a bit questionable.
The usefulness of the learned WM prior is questionable given the author did not use it online with the environment.
Other Comments Or Suggestions: Figure 5 missing labels for each row.
Questions For Authors: In 5.2 the authors mention "Moreover, TDM predicts variants sequentially, which may accumulate errors and lead to less accurate results.", but TrajWorld also operates sequentially which can accumulate errors , could the author clarify?
TDM seems to produce a lot worse results than TW in Table 5, do the authors have any insights on this? Are the parameters count equivalent between the two models?
Could the author identify the major difference between the proposed interleaved temporal-variate attentions versus factorized attention introduced in Wayformer?
Did the author explore the different discretization strategy?
“Moreover, the transfer benefits are evident in both in-distribution and out-of-distribution scenarios.” what does this sentence referring to?
Which policy would give you a more generalized world model, the expert or random policy or something in-between?
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: We sincerely thank Reviewer 8E9V for the thorough review and valuable questions.
## Q1: MPC evaluation
Following Schubert et al., we have added **online MPC experiments**. In this setting, TrajWorld outperforms both baselines and its counterpart trained from scratch (see [anonymous figure](https://anonymous.4open.science/r/TrajWorld/mpc.pdf)). Due to space limitation, please refer to **response to W1 for Reviewer puvo** for details.
**Discussions on transferability compared to Schubert et al.**: Given these new results, we can expand the discussions on Schubert et al.:
> We demonstrate positive transfer to complex downstream environments such as Walker2D, not only for offline transition prediction/policy evaluation, but also for online MPC, which Schubert et al. did not. Our work differentiate from theirs in: (1) Setting: Instead of finetuning with $10^4$ episodes for MPC with random shooting, we more practically finetune with $10^2$ episodes for MPC with proposal policy; (2) Data diversity: Our UniTraj dataset emphasizes distribution diversity, rather than using pure expert trajectories; (3) Architecture: TrajWorld incorporates inductive biases tailored to the 2D structure of trajectory data for enhanced transferability. Notably, TDM exhibits negative transfer in our practical MPC setting. We believe our work complements and extends Schubert et al., offering new insights to the community.
## Q2: Difference with factorized attention in Wayformer
We appreciate the feedback and acknowledge the relevance of Wayformer. We will include it as related work in the final version.
While TrajWorld and Wayformer both adopt two-way attention (a.k.a. axial/factorized attention [1,2,3]) to handle a heterogeneous set of inputs with various numbers of dimensions, our work differs in several key aspects to preserve novelty:
1. **Tasks & architectures**: Wayformer targets motion forecasting, a regression task with heterogeneity in the multimodal **input** space. TrajWorld is designed for world modeling, an autoregressive task involving heterogeneity in both **input and output** space. This leads to significantly different macro and micro designs: **decoder-only with causal attention vs. encoder-decoder with bidirectional attention**.
2. **Homogeneous basics**: Wayformer handles various numbers of contextual objects across modalities via attention, but still relies on modality-specific projections to unify embedding dimensions. More thoroughly, TrajWorld achieves scalar-level homogeneity, **without the need for modality-specific projections** and is capable of zero-shot generalization to unseen input/output spaces.
3. **Transferability beyond efficiency**: Wayformer uses factorized attention mainly for efficiency, not showing a performance boost over full attention in its target task. In contrast, TrajWorld shows that inductive biases for the 2D structure **enhance transferability**, outperforming its 1D counterpart, TDM.
To our knowledge, TrajWorld is the first to apply two-way attention in trajectory world modeling, and we hope it provides valuable insights to the community.
[1] ViViT: A Video Vision Transformer.
[2] Axial Attention in Multidimensional Transformers.
[3] CCNet: Criss-Cross Attention for Semantic Segmentation.
## Q3: Other questions/clarifications
- **Error accumulation in TDM**: TDM predicts sequentially along both variate and temporal dimensions due to its 1D architecture. TrajWorld, with its 2D architecture, predicts sequentially over time but jointly across variates at each timestep, which helps mitigate error accumulation.
- **Worse results of TDM compared to TrajWorld**: As discussed above, we attribute TDM’s performance gap to error accumulation along sequences of variates and the lack of appropriate inductive biases for the 2D structure of trajectory data. Both models use the same parameter count.
- **Discretization strategies**: Uniform discretization is widely used (e.g., in Gato, TDM, Farebrother et al.) and performs well in our experiments. Thus, we did not explore more complex methods like quantile-based binning.
- **In- vs. out-of-distribution**: For transition prediction, we test trained models on both the same and different datasets. For instance, a model trained on hopper-medium-replay is tested on both hopper-medium-replay (in-distribution) and hopper-expert (out-of-distribution). Pre-training benefits TrajWorld in both scenarios.
- **Which policy would give a more generalized world model**: We believe that diverse data from a range of policies (random, medium, expert, exploratory, etc.) yields a more generalizable model than trajectories from any single policy. We have conducted experiments pre-training our model on JAT, a subset of UniTraj with only expert data, which underperforms those pre-trained on the full data. Please refer to **response to Q1 for Reviewer 2GyG** for details.
---
Rebuttal Comment 1.1:
Comment: I recommend the authors to make proper ablations on their propose architecture with the existing two-way attention architectures if the authors consider the proposed architecture is a strong contribution to the paper.
In addition, I recommend the authors to be clear about the statement on error accumulation in future revisions.
---
Reply to Comment 1.1.1:
Comment: We sincerely appreciate Reviewer 8E9V’s follow-up to our initial rebuttal. We aim to fully address your remaining concerns in this additional response.
### On Two-Way Attention Architectures
In our work, we employ a two-way attention mechanism that interleaves attention across two data dimensions—timesteps and variates. This design shares the idea of using two-way attention in broader literature [1–5] (with different data dimensions). But our approach is tailored to the autoregressive trajectory world modeling setting, where the temporal attention is set to be causal.
**Our architecture contribution lies in being first to introduce two-way attention into trajectory world modeling and demonstrating its benefits for transferability**. Existing two-way attention architectures like Wayformer [5] make valuable contributions in motion forecasting, but are not directly applicable to our trajectory world modeling task. On the other hand, the existing trajectory world model, TDM, does not utilize two-way attention and thus fails to fully exploit the inherent 2D structure of data. We provide comprehensive experimental results--both offline and online--comparing world models with and without two-way attention (TrajWorld vs. TDM), clearly demonstrating that introducing two-way attention significantly improves both performance and generalization in world model tasks.
**Our architecture contribution does not claim to propose a new form of two-way attention or to benchmark the best use of two-way attention.** The two-way attention mechanisms used in prior works [1–4] are conceptually similar across different tasks, with variations primarily in application domains rather than in fundamental architectural design. We sincerely thank Reviewer 8E9V for highlighting Wayformer, which investigates two designs of two-way (factorized) attention: interleaved attention (with N/2 flips) and sequential attention (a single flip between dimensions). These approaches differ from our design, which performs N−1 flips. We explicitly do **not** claim that our interleaved scheme outperforms prior variants; rather, we believe this opens up a valuable direction for future exploration.
As such, we respectfully believe that **the absence of detailed ablations against existing two-way attention forms does not diminish our contribution to the world model field**.
### Clarifying Our Broader Contribution
Beyond architectural design, we want to highlight our significant contribution: **We investigate an under-explored world model pretraining paradigm across heterogeneous environments by integrating a newly-collected large-scale dataset, UniTraj, and a new world model architecture, TrajWorld**. The dataset and architecture are both designed based on our in-depth insights (see response to Reviewer 2GyG and 8E9V, respectively) into this particular but important setting. We conduct comprehensive experiments to **demonstrate--for the first time--positive transfer** from heterogeneous environments to complex downstream environments, while prior work, including Schubert et al., failed to achieve it. Our experiments span a variety of settings, including transition prediction, off-policy evaluation, and **model-predictive control per your advice**.
**The key challenge of world models in the era of scaling is effectively leveraging all available trajectory data** from diverse, heterogeneous environments. Rather than making improvements within a mature setting, **our work opens up a way by proposing a systematic solution to this challenging problem**. We believe this represents a meaningful step toward establishing foundation world models capable of handling heterogeneous environments.
----
Lastly, we appreciate your suggestion regarding clarifying error accumulation, and we will incorporate clearer explanations in future revisions.
Your comments is taken very seriously. We hope this additional response clarifies the scope and significance of our contributions, and you can re-evaluate our work based on resolved misunderstandings.
[1] ViViT: A Video Vision Transformer.
[2] Axial Attention in Multidimensional Transformers.
[3] MetNet: A Neural Weather Model for Precipitation Forecasting.
[4] Axial-DeepLab: Stand-Alone Axial-Attention for Panoptic Segmentation.
[5] Wayformer: Motion Forecasting via Simple & Efficient Attention Networks. | Summary: The paper aims to tackle the heterogeneity issue in world model pretraining. To achieve this, the authors curate a unified trajectory dataset from 80 control environments. Based on this dataset, they introduce TrajWorld, a world model architecture that naturally accommodates varying sensors and actuators, thereby enabling efficient knowledge transfer across environments. The effectiveness of TrajWorld is validated across three unseen environments in terms of prediction error and policy evaluation reliability.
Claims And Evidence: Yes, there are supported by clear and convincing evidence.
Methods And Evaluation Criteria: The effectiveness of the proposed world model is assessed through prediction error and off-policy evaluation. However, an evaluation of model predictive control performance would be more convincing, as did by the closely related work TDM [1].
[1] A Generalist Dynamics Model for Control. Ingmar Schubert, et al.
Theoretical Claims: I have checked the theoretical claims in this paper.
Experimental Designs Or Analyses: The paper provides extensive experiments with sufficient details.
Supplementary Material: I have reviewed all appendices.
Relation To Broader Scientific Literature: The paper makes two key contributions in comparison to the related literature. First, it curates a large-scale trajectory datasets sourced from 80 control enviroments. Second, it presents a unified architecture to efficiently extract transferable knowledge from the heterogeneous data sources. These contributions could inspire future research on developing generalist world models.
Essential References Not Discussed: As far as I know, all closely related works are cited appropriately.
Other Strengths And Weaknesses: W1) **Missing MPC results.** While the proposed recipe improves zero-shot prediction and policy evaluation, its advantages are not demonstrated in model predictive control performance, which would provide an intuitive comparison to TDM.
W2) **Long-horizon comparison.** I agree that the sequential prediction of TDM may lead to error accumulation, but its flexible architecture could offer advantages for planning over long horizons. The paper does not specifically mention the experimental settings regarding horizons, so I am curious whether the proposed joint prediction scheme still dominates in long-horizon settings.
Other Comments Or Suggestions: A typo in Line 637: "the official repository repository" should be "the official repository".
Questions For Authors: Q1) **Scaling law.** As the authors have collected a large-scale dataset from 80 heterogeneous environments and demonstrated the benefits of pretraining, it would be interesting to see an analysis of the scaling laws regarding data diversity.
Q2) **Straight zero-shot prediction results.** The zero-shot prediction results in Figure 4 appear overly straight. Could you briefly discuss possible reasons for this phenomenon? Besides, I wonder if it is possible to visualize the predictions of other baselines for comparison? I believe it would be beneficial to demonstrate the advantages of TrajWorld.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We sincerely thank Reviewer puvo for the thorough review, insightful questions, and a positive evaluation of our work.
## W1: Model-predictive control (MPC) evaluation
We have conducted MPC experiments comparing different world models.
**Setup**: Following Schubert et al, we first attempted *MPC with random shooting planner*, but found it ineffective in our high-dimensional target environments, with any world models. We then adopt the *MPC with proposal* setting, also from Schubert et al. We set a practical scenario where world models trained on medium replay datasets are used to improve the medium-level trained proposal policies via MPC.
**Implementation**: We use three medium-replay datasets from D4RL and medium-level policies from DOPE. The sample size is fixed at 128. The planning horizon is set to 25 steps for HalfCheetah and Walker, and 50 steps for Hopper to avoid myopic behavior in this fragile environment. Sampling noise is tuned for optimal performance across all world models: 0.05 (Hopper), 0.2 (Walker), 0.025 (HalfCheetah).
**Results**: Our main results for MPC with proposal are shown in the table below and this [anonymous figure](https://anonymous.4open.science/r/TrajWorld/mpc.pdf). We find MPC improves proposal polices in Hopper and Walker but has little effect on HalfCheetah, which is more stable and less prone to failure. In contrast, Hopper and Walker are fragile, and the model helps prevent unsafe actions, leading to better planning.
Overall, **MPC with TrajWorld delivers the best performing agents** compared to baseline models or its counterpart trained from scratch.
|MPC w/ proposal & | MLP-Ensemble (w/o pt) | MLP-Ensemble (w/ pt) | TDM (w/o pt) | TDM (w/ pt) | TrajWorld (w/o pt) | TrajWorld (w/ pt) |*Proposal only*|
|-|-|-|-|-|-|-|-|
|Hopper|948±61|1091±125|1287±26|1117±145|1090±225|**1401**±236|*1078±143*|
|Walker|3353±83|**3465**±20|3056±236|2619±36|2422±455|**3427**±370|*3049±104*|
|HalfCheetah|5645±10|5692±19|5611±85|5647±25|**5858**±17|5809±15|*5697±30*|
For MPC with random shooting, no world model provides successful agents. However, TrajWorld still performs relatively best among them (see [anonymous figure](https://anonymous.4open.science/r/TrajWorld/mpc.pdf)).
**Efficiency**: TrajWorld predicts all variates jointly, unlike TDM which processes them sequentially. This leads to a major speedup: MPC for 1000 environment steps in HalfCheetah takes **40 minutes with TDM**, but only **3 minutes with TrajWorld**.
We thank all reviewers for encouraging us to add these experiments, which further strengthen the contribution of our work. We will include them in the final version.
## W2: Long-horizon comparison
We remark that our TrajWorld has a flexible architecture similar to TDM and can also handle arbitrary prediction horizons (only constrained by its training context length).
Below, we summarize our experimental settings regarding horizons:
- **Zero-shot generalization** (Fig. 4b): rollouts for **10 steps**. We have expanded the baseline results for comparison (see Q2 below).
- **Transition prediction** (Sec. 5.2): short horizon, report **one-step** prediction error.
- **Off-policy evaluation** (Sec. 5.3) involves rollouts of an extremely long horizon (**2000 steps** as mentioned in App B.4.1). Due to our model's short context length of 20 (limited by our computational resources), this is done by sliding windows.
- **Model-predictive control**: rollouts over relatively long horizons of 25 or 50 steps.
Across all these scenarios, TrajWorld provides superior performance compared to baselines.
## Q1: Scaling laws regarding data sizes and diversity
We have conducted an analysis on the effects of different data sizes and diversity for pre-training. Our results in this [anonymous figure](https://anonymous.4open.science/r/TrajWorld/data-analysis.pdf) validate that both the large scale and diversity contribute to the effectiveness of pre-training.
Due to space limitation, we kindly refer the reviewer to **response to Q1 for Reviewer 2GyG** for experimental details and results.
## Q2: Straight zero-shot prediction
We suppose that the overly straight predictions are likely due to the short context window (10 steps) and slow motion speed. Through this context, the zero-shot model is not able to precisely capture the quadratic relationship between state and action, and is only able to reflect coarse directional changes.
For comparison, we also provide zero-shot prediction from other baselines in this [anonymous figure](https://anonymous.4open.science/r/TrajWorld/zero-shot-prediction.pdf). As shown, in an unseen environment, both TDM and MLP baselines fail to generalize, producing incorrect predictions and failing to capture the underlying state-action relationship at all. Specifically, TDM fails to predict how push forces from two opposite directions lead to different x positions. On the other hand, MLP fails to produce any reasonable results with extreme error accumulation.
---
Rebuttal Comment 1.1:
Comment: Thank the authors for their efforts to address my concerns. I will keep my initial rating.
---
Reply to Comment 1.1.1:
Comment: We sincerely appreciate the time you took to read our rebuttal and engage with our responses. We're glad we can address your concerns, and your positive assessment is a great support for us to believe in the value of our work. | Summary: This paper presents a trajectory world model that handles varying sensor and actuator information across different environments. To support the generalization of the world model, this work composes a large dataset, UniTraj, comprising over one million trajectories from 80 environments. The key ingredient of the proposed method is to model the dynamic transitions on discretized variates over the temporal horizon. The learned world model demonstrates effective positive transfer across heterogeneous and complex control environments while achieving a new state-of-art for off-policy evaluation.
Claims And Evidence: Yes, the claims made in this submission are supported by clear and convincing evidence.
Methods And Evaluation Criteria: Issues of methods:
- **Limited contribution regarding the UniTraj dataset**. This paper introduces the UniTraj dataset by composing large-scale data from different environments. However, there are limited contributions in this regard. First, the dataset seems to be a simple composition without any rigorous curation, selection, or filtering process. Further, even though the paper demonstrated that using UniTraj in pre-training can improve downstream performances as shown in Fig.1 and Fig.5, there is a lack of critical studies on how different data scales and diversity affect model performance. For instance, how would the world model generalize when pre-trained on a subset of UniTraj, such as 1/2 or 1/10? Given these issues, the introduction of this dataset cannot form a valid technical contribution.
- **Limited novelty of the proposed TrajWorld architecture compared to TDM**. According to Fig.3 and descriptions in L322-324, the main difference between TDM[1] and the proposed TrajWorld is the newly introduced temporal dimension. However, leveraging the temporal dimension with additional attention modules has been widely studied in the literature on world models[2] and video generation models[3, 4]. Such an adaptation does not bring further insights to the community.
[1] A Generalist Dynamics Model for Control
[2] Generalized Predictive Model for Autonomous Driving
[3] AnimateDiff: Animate Your Personalized Text-to-Image Diffusion Models without Specific Tuning
[4] Align your Latents: High-Resolution Video Synthesis with Latent Diffusion Models
Theoretical Claims: No issues with the theoretical aspect of this work.
Experimental Designs Or Analyses: Issues of experimental designs:
- **Lack of experiments on decision-making**. The paper did provide one means of utilizing the pre-trained world model, which is off-policy evaluation in Sec.5.3. However, investigations on using this model to improve policy through reinforcement learning or sampling-based optimizations are underexplored.
Supplementary Material: Yes, I viewed all supplementary material.
Relation To Broader Scientific Literature: The key contributions of the paper relate to the areas of world models, reinforcement learning, and pre-training on large-scale dataset.
Essential References Not Discussed: N/A.
Other Strengths And Weaknesses: Strengths:
- The paper is well-organized and easy to follow
- Experiments on how the pre-training influences downstream fine-tuning are meaningful. As shown in Fig.5, the authors conducted a wide range of experiments to demonstrate that large-scale pre-training is helpful for downstream fine-tuning with various train-test pairs.
- The idea of unifying world modeling on heterogeneous environments through in-context variates is intriguing and worth exploring.
Other weakness:
See weaknesses in the above sections.
Other Comments Or Suggestions: N/A.
Questions For Authors: N/A.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We sincerely thank Reviewer 2GyG for the thoughtful review and valuable comments, especially the recognition of our idea of unifying world modeling across heterogeneous environments.
## Q1: Dataset contribution
**Dataset construction**: We respectfully disagree with the assessment that our dataset is a simple composition. We elaborate on the insights behind UniTraj as follows:
1. **Selection**: We carefully **selected** the subsets to assemble UniTraj. Unlike Schubert et al. (2023), which utilizes only expert or near-expert trajectories, our dataset emphasizes distribution diversity beyond sole environment diversity, as detailed in Sec 3.
2. **Additional collection**: To further enrich environment diversity, we **collected** new trajectories ourselves from Modular RL, going beyond existing datasets.
3. **Filtering**: As noted on Line 124, we **filtered** all trajectories from three downstream environments, contributing a reasonable testbed for cross-environment transfer to the community.
4. **Weighting**: We manually **weighted** different subsets, trying to balance size and diversity. For example, DB-1 is oversampled due to its too small size. We apologize for not including these weights in the appendix and provide them below:
| Subsets | ExoRL | RLU | JAT | DB-1 | TD-MPC2 | Modular RL |
| ------------------------------ | ----- | --- | --- | ---- | ------- | ---------- |
| (Unnormalized) sampling weight | 75 | 5 | 90 | 1 | 90 | 30 |
**Analysis of dataset scales and diversity**: We appreciate the suggestion to analyze the impact of pre-training data. We conducted new experiments by pre-training three versions of TrajWorld on different subsets of UniTraj—namely, 1/10 size, 1/100 size, and the JAT subset (with only expert trajectories from 5 environments)—followed by fine-tuning on downstream tasks.
For **transition prediction**, we adopt a challenging setting: for each environment, we train models on the expert dataset, and test them on datasets of all levels. We also provide results for **model-predictive control** (see experimental details below).
The results, shown in this [anonymous figure](https://anonymous.4open.science/r/TrajWorld/data-analysis.pdf), compare these new models with one pre-trained on the full UniTraj and another trained from scratch. We observe that all subset pre-trained models underperform the fully pre-trained one, revealing a scaling law with respect to data size. These findings underscore the **importance of both scale and diversity** in pre-training data, and strengthen our contribution in advocating for large-scale, heterogeneous pre-training and in constructing the UniTraj dataset to support it.
## Q2: Architecture novelty
We respectfully believe there may have been a misunderstanding regarding our architectural contributions in comparison to TDM:
- TDM actually models tokens across both the variate and temporal dimensions, similar to ours. But it **flattens them into a one-dimensional sequence** and applies the original GPT architecture. This approach discards the inherent 2D structure of trajectory data and may 'not bring further insights to the community'.
- Compared to TDM, our TrajWorld does not 'newly introduce the temporal dimension', but rather **preserves and exploits the natural 2D structure** by employing a two-way attention mechanism, with each one capturing relationships within its respective dimension.
The superior performance of TrajWorld underscores the importance of appropriate inductive biases for enhancing transferability in trajectory world models.
## Q3: Experiments on decision-making (MPC)
We have added experiments on improving policies via sampling-based optimization (**model-predictive control**). In this setting, **TrajWorld outperforms both baseline models and its counterpart trained from scratch** (see this [anonymous figure](https://anonymous.4open.science/r/TrajWorld/mpc.pdf)).
Due to space limitation, we kindly refer the reviewer to **response to W1 for Reviewer puvo** for detailed experimental setup and results.
---
Rebuttal Comment 1.1:
Comment: Thanks for the detailed response. The additional ablation study on data scales and the experiments on decision-making are convincing to me. Therefore, I'd like to increase my score to 3. Weak accept (i.e., leaning towards accept, but could also be rejected).
---
Reply to Comment 1.1.1:
Comment: Dear Reviewer 2GyG,
We sincerely appreciate your thoughtful re-evaluation of our paper and the subsequent positive rating. Your constructive feedback, particularly regarding the ablation study on data scaling and MPC experiments, has been invaluable in helping us improve the work.
Thank you again for your insightful feedback.
Best regards,
Authors | null | null | null | null | null | null |
M2PDE: Compositional Generative Multiphysics and Multi-component PDE Simulation | Accept (poster) | Summary: The paper proposes a compositional multiphysics and multicomponent simulation model that uses diffusion. The approach, MultiSimDiff, consists of learning conditional distributions of individual components conditional on the other physical processes. At test-time, the approach samples from the conditional distributions to build a sample from the joint distribution. The paper tests their approach on three tasks: reaction-diffusion, nuclear thermal coupling, and prismatic fuel thermal and mechanical analysis. The paper’s reported contributions are: a novel approach to multi-physics / multi-component modeling by framing in terms of a joint distribution; open-source data sets; demonstrating success for new simulation models.
Claims And Evidence: Claim 1: “To the best of our knowledge we are the first to introduce a compositional generative approach to Multiphysics and multi-component simulations”
* Splitting up a problem into its conditionals and sampling from them sequentially has been known for a long time. This is what Gibbs sampling is. The other relevant literature not covered is simulation-based inference. A paper that seems to be tackling a somewhat similar goal in that literature is Gloecker at al. (https://arxiv.org/pdf/2404.09636v1). I would say that potentially the claim could be either grounded in the specific architecture, or in the specific applications shown in the paper.
Claim 2: “We create and open-source benchmark datasets … ”. “The code is available at the anonymous repository”.
* I might have missed it, but I can’t see a link anywhere to the code or the benchmark datasets. Also, it would potentially be more valuable if it were the simulators as well as the data that were being released. Is that something the authors would consider releasing?
Claim 3: “MultiSimDiff, trained on single components, accurately predicts larger structures with up to 64 components.”
* I agree with this claim.
Methods And Evaluation Criteria: * The evaluation across three novel application datasets makes sense for the work.
* One question is why the validation dataset consists of decoupled data and not coupled data when it is known that the test data is coupled data. This would seem to put the surrogate models at a disadvantage, since they are being optimized on decoupled data but tested on coupled data.
Theoretical Claims: * Appendix E shows that there is a gap between models trained on coupled data vs. decoupled. My main question related to the theoretical claims of the paper is when is it appropriate to split up a problem into learning conditional distributions? For example, for Gibbs sampling, it may not be that easy to make this assumption. The Prismatic fuel element seems to make sense as it enables generalization. The paper seems to imply that it is taken for granted that all the problems can be split into the conditional distributions.
Experimental Designs Or Analyses: * No addition to what has previously been mentioned.
Supplementary Material: * I could not find anonymous linked code. I read through the supplementary materials.
Relation To Broader Scientific Literature: * The paper is focused at multiphysics/multi-component simulations. There has not been a large amount of work focused on these multi-component scenarios. This is in part due to a lack of available simulators/datasets.
Essential References Not Discussed: * As mentioned earlier, it seems like the area of simulation-based inference (SBI) is missing.
Other Strengths And Weaknesses: ### Strengths:
* Paper is well-written, and presentation is good.
* The application domain is a strength of the paper. The three proposed applications are nice to see and it is not easy to introduce three new examples in a single paper without relying on previous benchmarks.
### Weaknesses:
* The novelty of the approach does not seem especially strong given that splitting into conditional distributions is a common procedure for generative modeling and sampling.
Other Comments Or Suggestions: * See below
Questions For Authors: In addition to the above comments:
* When should a multiphysics approach be split into conditional models, and when should you model the full joint distribution?
* Is there any advantage to the order of the conditional distributions that are sampled from? For example, in Gibbs sampling, the order of sampling from the distributions can sometimes be varied.
* If the approach is like EM, does that mean the overall log likelihood always increases?
* How much compute is needed to train each individual conditional diffusion model? It looks like there is a different diffusion model for each component.
* Line 8 of Alg. 2 runs an additional update step using the function $f(\cdot)$. What is the purpose of this function, how costly is it, and why is it not needed for Alg. 1?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: > Re1: Relation to Gibbs Sampling.
Gibbs sampling splits a problem into conditional distributions and samples them sequentially. In our setting, this is essentially our baseline (named **surrogate model** in manuscript), where we iteratively update each physical field using a surrogate model (See Algorithm 3 in the manuscript). Specifically, in a multiphysics problem, if you randomly initialize all physical fields as:
$\mathbf{z}^{(0)} = \bigl(z_1^{(0)}, z_2^{(0)}, \ldots, z_d^{(0)}\bigr)$,
then at each iteration $k$, you loop over each physical field $z_i$ and update it with the conditional probability $p(z_i \mid z_{\neq i})$. If that conditional probability is replaced by our trained surrogate model, it essentially becomes Algorithm 3.
> Re2: Open-Source Dataset/Code.
We verified the anonymous repository is accessible. It contains solver input files and download links for the data, mentioned at line 294. We also provide the url here: https://anonymous.4open.science/r/MultiSimDiff-D5A3/README.md.
> Re3: Why the validation dataset consists of decoupled data and not coupled data when it is known that the test data is coupled data...
We believe this is fair for both the surrogate model and the diffusion model. For multiphysics problems, the goal is to train the model on decoupled data but eventually predict the coupled solution. Consequently, the training and validation sets are composed of decoupled data, and the test set is composed of coupled data. Both models use the same training, validation, and test sets.
> Re4: When is it appropriate to split up a problem into learning conditional distributions? Can all the problems be split into the conditional distributions?
Our tasks naturally decompose into conditional fields—each physical field or component is determined by the others. In multi-physics, each field typically has its own solver requiring boundary information from other fields. Similarly, in multi-component setups, a component’s solution depends on its neighbors. But there is a type of eigenvalue problem that cannot be solved by current methods, which can be seen in Appendix J.
> Re5: Why simulation-based inference (SBI) is missing.
We understand SBI as inferring model parameters from given data. Gloecker et al. trained a single diffusion model for $p(x, \theta)$, thus achieving their “all in one” model to obtain both the likelihood and posterior. But for our problem, due to the difficulty in modeling the joint distribution of multiple physical fields or components, our approach is to combine individual models to achieve similar functionality. Although these two methods look very similar, their directions of operation seem to be opposite.
> Re6: When should a multiphysics approach be split into conditional models, and when should you model the full joint distribution?
Modeling the full joint distribution (simultaneously solving all coupled equations) in a multiphysics system is difficult, especially in fields like nuclear engineering, where each physical process (e.g., neutron, fluid, mechanic) often has its own independently developed solver. Building a fully coupled solver to unify these modules is both development-intensive and computationally expensive. Instead, our approach trains simpler conditional distributions – each field conditioned on the others (decoupled solution) – and then composes these models during inference to approximate the fully coupled solution.
> Re7: Does the Sampling Order Matter?
We have found that in multiphysics, the order of updating each field has negligible influence on final results, as shown in https://anonymous.4open.science/r/MultiSimDiff-D5A3/order.md. For multi-component simulation, we update all components simultaneously, making order irrelevant.
> Re8: If the approach is like EM, does that mean the overall log likelihood always increases?
Theoretically, yes. The log-likelihood can be written as $-E(z) - \log Z$. Ignoring constants, it is $-E(z)$. Moving in the direction of $\nabla E$ decreases $E(z)$ and thereby increases the log-likelihood.
> Re9: How much compute is needed to train each individual conditional diffusion model? It looks like there is a different diffusion model for each component.
For multiphysics with d fields, we train d diffusion models. In Experiment 2 we used three (solid, neutron, fluid). For multi-component tasks, we only need one model because each component is analogous. Even in practical engineering, the number of "d" rarely exceeds four. So the training cost is not particularly high.
> Re10: Purpose and Cost of f in Alg. 2?
In multi-component setups, we update all components concurrently and need function f to gather neighboring solutions for each component, costing O(n) for n components but no extra neural inference, which is very fast. In Algorithm 1 (multiphysics), each field is updated sequentially, and there is no unified function f to update their inputs. | Summary: The paper proposed a compositional diffusion model framework to handle multi-physics multicomponent surrogate model for physics systems. It leverages the existing diffusion backbone and demonstrated it effects on three multi-physics/multicomponent PDE systems. The paper claims the contribution are: 1. Introducing the compositional diffusion model for multi-physics and 2. Creating novel benchmark dataset for multi-physics/multi-components surrogate models research. The metrics comparison also indicates the effectiveness of the proposed model compared with baselines.
Claims And Evidence: The claims that it introduces a effect multi-physics/multicomponents diffusion framework for physics application is supported by the result section. Moreover, some of the datasets are novel but not all of them. e.g, reaction-diffusion dataset is a standard questions researchers have used.
Methods And Evaluation Criteria: I don't think the proposed methods make sense for multiphysics/multicomponents surrogates. Firstly, the diffusion model itself doesn't have novelty. It just leverages the existing pipeline for a new dataset. Secondly, I am not convinced that the diffusion model is a top candidate for modeling multiphysics/multicomponents process. The underlying physics are all deterministic. And there exists extensive literatures based on domain decompositions or GNNS to build deterministic surrogates. Moreover, the success of the multicomponents model is more relied on the self-similar feature of the graphical data and the model that could capture these resolution invariants features, instead of the diffusion model itself. Moreover, the diffusion model is also not used to account for any uncertainty quantifications for the surrogate models in the current context to help explain the sample variety caused by diffusion models. Therefore, I am not convinced by the novelty contribution and the justification of using diffusion model for current applications.
Theoretical Claims: I have checked the equations in the main manuscript and they are correct with minor typos to the best of my knowledge.
Experimental Designs Or Analyses: I have checked the soundness and validity of experimental designs and have found issues.
For the multiphysics experiments. I think it is needed to compare with other domain-decomposition based surrogate models to justify the effectiveness of the papers. I also think it is beneficial to show spatial/temporal error plots to give better idea of how the coupling surface works more than a simple number.
For the multicomponents experiments, I think the GNN based benchmarks is not optimized for performance. I have reviewed research papers that leverage GNN to successfully spatially extrapolate to larger domains. I will list the reference below.
Supplementary Material: I reviewed part of Appendix B,E,G,H,I.
Relation To Broader Scientific Literature: I think the contribution lies in trying to extend the diffusion based framework to multi-physics/multi components surrogate modeling, altought I am not convinced by the current script. Domain decomposition and multi components (train small, test big) ideas have been explored in separate works and the authors tried to show that a diffusion model could be a unified work for these tasks.
Essential References Not Discussed: I think the several essential references about the benchmark needs to be included in the result comparison part. For example, [1] paper demonstrated that GNN itself could work very well on training on 64 by 64 domain and directly generalizes well to 1024 to 1024 domain for physics systems. However, the current paper reports that GNN-based model all performs very poor. Moreover, the author mentioned domain-decomposition based method like [2], but didn't compare with them in the result part.
[1] Fan, Shaoxun, et al. "Accelerate microstructure evolution simulation using graph neural networks with adaptive spatiotemporal resolution." Machine Learning: Science and Technology 5.2 (2024): 025027.
[2] Ranade, R., Hill, C., He, H., Maleki, A., Chang, N., andPathak, J. A composable autoencoder-based iterativealgorithm for accelerating numerical simulations. CoRR,abs/2110.03780, 2021. URL https://arxiv.org/abs/2110.03780.
Other Strengths And Weaknesses: Strength is trying to building a unified surrogate model for multiphysics/multicomponents systesm. These applications are time consuming and there is a strong research need to get faster surrogate. Moreover, the paper writing is clear to follow the key idea. The weakness is it seems directly apply the existing pipeline on a new dataset, without fair comparison to the high performance benchmarks.
Other Comments Or Suggestions: None
Questions For Authors: I have briefly mentioned my questions in the above sections but I would like to summarize it here.
1. What is the novelty for your proposed diffusion framework?
2. Why do you think it is justified to use diffusion model to model the deterministic PDE systems. The challenges for multi physics is how to model the interface accurately while not being too expensive. And the challenges of multi-components lies in learning a scale-invariant features leveraging GNN-like NNs. None of these are related to the strength of diffusion models.
3. Could yo compare with more baselines. For multi physics, it is better to include more advanced domain-decomposition based surrogate. And for the multicomponents, it is better to compare with existing GNN-based framework that alright shows great potential on doing the spatial extrapolation tasks. It could be related but not limited to the reference I mentioned above.
4. What are the error distributions respective to spatial and temporal dimensions.
5. As for the speed up, the numerical simulation cost heavily depends on the convergence criteria set in the interface. Could you report what is your convergence or residual set for numerical simulation. And the mean time, how accurate your diffusion surrogate is in the interface?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: > Re1: What is the novelty for your proposed diffusion framework?
Our study is application-driven rather than aiming to improve diffusion models directly. Our contribution is not diffusion model itself, but the higher-level algorithm on top of diffusion models for multiphysics and multi-component simulation tasks. Specifically, our framework can learn from single-field or small-scale data and generate complete, coupled solutions or full-structure predictions at inference. This cuts development costs for coupled solvers, simplifies large-scale simulations, and extends readily to more complex scenarios.
> Re2: Why use diffusion models for deterministic PDE systems?
We believe diffusion models can be used to simulate deterministic PDE systems because a deterministic structure can be considered a Gaussian distribution with a fixed mean and a very small variance—effectively negligible. **We provide experimental evidence showing this variance is very small** (see [link](https://anonymous.4open.science/r/MultiSimDiff-D5A3/rebuttul/std.md) and Re6 in our response to Reviewer WGGT). Moreover, when physical systems involve noise, diffusion models can also help quantify predictive uncertainty. Several studies have applied diffusion models to simulate physical systems, such as in weather prediction [1] and spatiotemporal field forecasting [2]. In our experiments, our baseline is effectively a deterministic surrogate model, which generally performs better on validation sets (decoupled data / small structures). However, our main objective is to do well on the test sets (coupled / large structures), and our experiments confirm that the diffusion model outperforms this deterministic baseline in that scenario. In summary, we believe diffusion models are a viable approach for modeling PDE systems.
[1] Mardani M, et al. Residual corrective diffusion modeling for km-scale atmospheric downscaling. Commun. Earth Environ. 2025.
[2] Li Z, et al. Learning spatiotemporal dynamics with a pretrained generative model. Nat. Mach. Intell. 2024.
> Re3: Could you compare with more baselines like domain-decomposition and GNN-based network?
Domain decomposition in numerical simulation splits the computational domain rather than multiple physical fields. Therefore, machine learning approaches derived from domain decomposition are not used to solve multi-physics problems. Hence we use such methods only for multi-component baselines. For multi-component simulations, our manuscript already compares domain decomposition (surrogate), Graph Neural Networks (GIN), and Graph Transformer (SAN). Based on your suggestion, we further added MeshGraphNet for comparison and tuned certain hyperparameters (e.g., hidden layer size, number of message passing layers). The result is shown in: https://anonymous.4open.science/r/MultiSimDiff-D5A3/rebuttul/Table3.png. Indeed, MeshGraphNet is a very strong baseline. We find that on the 16-component dataset used to train MeshGraphNet, it achieves performance significantly better than any of the other models; in the 64-component dataset, our method still performs the best, demonstrating that our method’s strong multi-component generalization capability.
> Re4: What are the error distributions respective to spatial and temporal dimensions.
Currently, our predictions are jointly conducted in both time and space. Therefore, theoretically, the errors in space and time should be similar. For multiphysics modeling, the results are shown in the figure at the following link: https://anonymous.4open.science/r/MultiSimDiff-D5A3/rebuttul/Fig5.png. Overall, due to the coupled physical fields, the spatial errors at the interfaces are slightly higher, while the temporal errors remain close. The flow field initially has larger errors, which decrease as the flow stabilizes. For multi-component simulations (see Fig.9 in the original submission), larger errors typically occur at the component boundaries.
> Re5: Convergence criteria and accuracy at the interface.
We did not deliberately loosen the convergence criteria to slow down the numerical simulation. We used MOOSE to create our dataset, and the code repository includes the input files used to generate the data. The convergence criteria include an outer nonlinear iteration loop and an inner linear iteration loop:
- Experiment 2: Nonlinear iteration has a relative error of 1e-8 (default 1e-8) and absolute error of 1e-8 (default 1e-50), with a maximum of 20 iterations (default 50). The linear iteration has a relative tolerance of 1e-5 (default 1e-5) and a maximum of 100 steps (default 10000).
- Experiment 3: The maximum number of linear iterations is set to 20, and the maximum number of nonlinear iterations is 5, with other settings left as default.
Compared to the program’s default settings, we have actually tried to make the simulation faster wherever possible.
Regarding accuracy, the spatial errors at the interfaces are somewhat higher, as analyzed in Re4.
---
Rebuttal Comment 1.1:
Comment: Thanks, the rebuttal is reasonable and I modified my score.
---
Reply to Comment 1.1.1:
Comment: Thank you for your constructive feedback and for raising our manuscript's score. Your insights have been invaluable in enhancing the quality of our work. | Summary: This paper proposes MultiSimDiff, a novel compositional generative model for multiphysics and multi-component simulations. The core idea is to use diffusion models to learn energy functions representing the conditional probability distributions of different physical processes or components. During inference, MultiSimDiff reconstructs the joint solution by sampling from these learned distributions. This approach circumvents the need for coupled numerical solvers and allows generalization from decoupled (small structure) training data to coupled (large structure) predictions. The authors validate the proposed method in several tasks.
Claims And Evidence: Yes
Methods And Evaluation Criteria: Yes.
Theoretical Claims: No theoretical claims.
Experimental Designs Or Analyses: Yes, the paper provides ablation studies on diffusion parameters and crucial hyper-paprameters, but a more systematic hyperparameter study (e.g., different architectures, sampling steps) would be encouraged.
Supplementary Material: Yes, all parts.
Relation To Broader Scientific Literature: This work provides valuable insights and new ways of using generating models to handle real-world physical problems.
Essential References Not Discussed: No.
Other Strengths And Weaknesses: Strength:
- The paper frames multiphysics and multi-component simulation as a generative modeling problem, leveraging diffusion models to compose energy-based representations. This is a pretty fresh and novel perspective on simulation-based learning.
- The setting of experiment, especially the prismatic fuel element part, is solid and impressive, which demonstrates strong generalization from small to large structures, which is crucial for real-world engineering applications.
Weaknesses:
- The presentation of the method still could be improved. There are some typos and inconsistent of notations, and more preliminary on the training part could help readers to better understand the work. For example:
- the line 145, 197, right column, "z=(z1,z2,...,zn)" and "V=v1∪v2∪...∪vn", should use capital "N" instead of "n" ?
- The statement of z_{i}^{e} in eq.9 is not clear enough. For readers who are familiar with diffusion, it's smooth to get the ituition of " estimate z_{i}^{0} when we at still at z_{i}^{s} " there. However, for readers who are not very familiar with diffusion, the mixure usage of z_{i}^{s} and z_{i}^{e} could lead to confusion.
- In the Algorithm1 table, the inner loop (step 8-11) is set over the "i", but before that, the notation of "i" is already used in step 1-7. My understanding is the operations invloved "i" in step 1-7 should be applied over i=1,2..N. Authors should make it clear.
Other Comments Or Suggestions: While the compositional approach is compelling, the choice of conditioning structure is manually designed and attached to single task.
I'm curious whether this method can self-adapt to different partitioning schemes for new physical systems, and whether the learned decoupled component (represnt. by diffusion model) has the generalizability to other task.
Questions For Authors: see other parts
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: > Re1: the line 145, 197, right column, "z=(z1,z2,...,zn)" and "V=v1∪v2∪...∪vn", should use capital "N" instead of "n" ?
**Answer**: Thank you for pointing this out. We wll make the correction.
> Re2: The statement of z\_{i}^{e} in eq.9 is not clear enough. For readers who are familiar with diffusion, it's smooth to get the intuition of " estimate z\_{i}^{0} when we at still at z\_{i}^{s} " there. However, for readers who are not very familiar with diffusion, the mixture usage of z\_{i}^{s} and z\_{i}^{e} could lead to confusion.
**Answer**: Thank you for your suggestion. We will add an explanation of the superscript “e” in the paper to indicate that it is an estimated value, distinguishing it from the subscripts $i$ and $s$.
> Re3: In the Algorithm1 table, the inner loop (step 8-11) is set over the "i", but before that, the notation of "i" is already used in step 1-7. My understanding is the operations involved "i" in step 1-7 should be applied over i=1,2..N. Authors should make it clear.
**Answer**: Thank you for pointing this out. Indeed, that is the meaning we intended to convey. We will add a statement clarifying that the operations in steps 1–7 are applied to all $i=1,\ldots,N$. You can see in: https://anonymous.4open.science/r/MultiSimDiff-D5A3/rebuttul/ALG1.png
> Re4: While the compositional approach is compelling, the choice of conditioning structure is manually designed and attached to single task. I'm curious whether this method can self-adapt to different partitioning schemes for new physical systems, and whether the learned decoupled component (represent. by diffusion model) has the generalizability to other task.
**Answer**: Your understanding is correct. For multi-physics problems, the choice of conditional structure does indeed depend on the specific task, because the conditional diffusion model needs the other physical fields in order to predict the current physical field. As such, the set of physical fields in the system is already fixed. If a new physical field is added or an existing one is removed, any physical field model that is coupled to it must be retrained. This is indeed a very interesting open question, and we will look into it in future work. For multi-component simulation, the current method can be extended to various combinations of components. | Summary: This paper introduces MultiSimDiff a new method for solving multi-physics/multi-compnennts simulations efficiently by learning the conditional score of each component's solution given its parameters and solutions of other components. Experiments demonstrate that MultiSimDiff outperforms largely a simpler surrogate that model each component's solution independently on a class of coupled cases.
Claims And Evidence: Overall the paper is well-written and claims are supported by evidence.
Methods And Evaluation Criteria: Yes, the idea of building a global solutions by representing each solution as a distribution conditioned on other components' solution appears original and well motivated.
Theoretical Claims: There is not strict theoretical claims.
Experimental Designs Or Analyses: Experiments are sound although I would have appreciated if other alternative strategies such as the ones discussed in the related works section would have been used as additional baselines.
Supplementary Material: No.
Relation To Broader Scientific Literature: In my opinion, the paper provides an insightful related work section which position this work well into the literature.
Essential References Not Discussed: -
Other Strengths And Weaknesses: Overall I very much enjoyed reading the paper and I believe the problem statement is very sound as well as the proposed solution.
That said, I am not very knowledgeable in the field of compositional mulitphysics/multi-component solvers and related works using ML for that sake. For that reason and for the few remarks below, I will only weakly support the acceptance of the paper but might increase my score in light of the other reviews and response from the author.
Here is a list of remarks/questions (ordered as noted when reading the manuscript):
- The end of the abstract (3 last sentences) appears a bit narrow and verbose. I am not sure it really helps the reader position your work.
- The intro is very clear
- Would be nice to mention better the gain in computation time you may have and exactly when using your method will be beneficial, what are the key ingredients to train it. For instance, it is not totally clear to me as whether you need a large datasets of coupled simulations or not for the method to work well. I understand this consideration is problem dependent. For some problems it may be easy and meaningful to simply solve independently each component conditioned on a plausible state for the other components that are part of the Markov blanket but I imagine that in many cases finding these "plausible" sets for the Markov blanket really requires to have jointly solved this Markov blanket... For Multi-components I understand this may still make your method a nice to scale to a larger number of components, however for multi-physics it seems that you cannot to very much.
- To emphasise my point above, I think you should discuss more clearly the issue of training the conditional scores and in particular that for tightly coupled systems having these sampled from $p_{\neq i}$ is not straightforward.
- I am a bit confused by the baselines you used. You discussed in the relate work that you compare to GNN and Graph Transformer but I did not see these results in the tables. Similar remarks for CoAE-MLSim.
- It seems that what [1] discusses in 3.1 regarding Markov Blanket and using diffusion model to jointly sample from dependent components is very close to your work from a technical standpoint.
- Figure 1. is pixelized and not very clear (or at least not informative compared to the space it takes), clean...
- By definition you algorithm will output a distribution over plausible solutions, it would interesting to discuss a bit better what exactly is modelled by that uncertainty and how you get rid of it in your numerical experiments. Also, how much uncertainty increases, decreases as a function of the exact setup considered.
[1]:https://proceedings.neurips.cc/paper_files/paper/2023/file/7f7fa581cc8a1970a4332920cdf87395-Paper-Conference.pdf
Other Comments Or Suggestions: -
Questions For Authors: See my comments above.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: > Re1: The end of the abstract (3 last sentences) appears a bit narrow and verbose.
Thank you for the suggestion! We will revise the ending of the abstract as follows:
We demonstrate the effectiveness of MultiSimDiff through two multiphysics tasks—reaction-diffusion and nuclear thermal coupling—where it achieves more accurate predictions than surrogate models in challenging scenarios. We then apply it to prismatic fuel element simulation, an exemplary multi-component problem, where MultiSimDiff successfully extrapolates from single-component training to a 64-component structure and outperforms existing domain-decomposition and graph-based approaches.
> Re2: Would be nice to mention better ... sampled from $p_{\neq z_i}$ is not straightforward.
I gather that this section focuses on two issues:
(1) Under which scenarios does our algorithm exhibit an advantage? The key factor to train it.
(2) For multiphysics problems, it is not easy to find a suitable $p_{\neq i}$, or in other words, you believe that finding a suitable $p_{\neq z_i}$ is almost equivalent to solving the problem itself.
For (1), our algorithm aims to solve multiphysics and multi-component simulation problems that can be numerically challenging. In the more complex experiments 2 and 3, we observed up to 29× and 41× speedups, with higher accuracy than other methods. In real engineering applications with large-scale coupling, these gains can be substantial. The key factor is to view multi physics/component simulation problems from the perspective of probability, and replace complex joint probabilities with easily obtainable conditional probability.
For (2), indeed, for multiphysics simulation, find $p_{\neq z_i}$ that perfectly respects all coupling is nearly as hard as solving the entire problem. But **we do not solve the coupled physical field equations**, we currently use a pre-iteration technique (lines 762–772) to approximate it; however, Figure 12 shows a notable gap from the true coupled data distribution. Hence, the accuracy of predicting the coupled solutions of physical fields still needs improvement, we discuss this limitation in Section 5 and plan further improvements.
> Re3: I am a bit confused by the baselines you used... Similar remarks for CoAE-MLSim.
For multi-component simulation, we use CoAE-MLSim as a baseline (implemented per the paper’s description) since it is not open-sourced. This corresponds to the “surrogate model” in Table 3. The Related Work section also discusses GNN (GIN) and Graph Transformer (SAN) approaches, which also can be seen in Table 3. We have also added MeshGraphNet for comparison, as noted in our response to Review QAdZ (Re3). However, these methods are not applicable to multiphysics simulations. The baseline for multiphysics simulations is shown in alg.3 in manuscript.
> Re4: It seems that what 1 discusses in 3.1 regarding Markov Blanket and using diffusion model to jointly sample from dependent components is very close to your work from a technical standpoint.
Their method replaces the log-likelihood gradient at one time step in a long sequence with a smaller subsequence. We instead replace the gradient of a complex joint distribution (for each physical field or component) with a tractable conditional distribution. For multiphysics problems, some fields typically depend on all other fields, so their subsequence substitution is not valid. For multi-component problems, the posterior estimation step (their Algorithm 3) introduces further challenges. In their scenario, the known information is observational data; in ours, it is the entire physical system’s inputs, which would constrain the model to the same scale as the training configuration. Overall, the core difference is that we must be able to **generalize to tasks beyond the training distribution**, while their method focuses on the same domain for training and inference.
> Re5: Figure 1. is pixelized and not very clear (or at least not informative compared to the space it takes), clean...
We have replaced Fig.1 with a clearer version at: https://anonymous.4open.science/r/MultiSimDiff-D5A3/rebuttul/schematic.pdf
> Re6: By definition you algorithm will output a distribution over plausible solutions, ... , decreases as a function of the exact setup considered.
We think that you are referring to uncertainty quantification. In general, there is model uncertainty and data uncertainty. In our current experiments, we learn from simulation data, which do not contain noise. Ideally, if a physical process is deterministic, the predictive uncertainty should be close to zero. We conducted uncertainty quantification experiments in both Experiment 2 and 3, and found that the standard deviation of the model predictions is extremely small, indicating that the diffusion model can approximate a deterministic physical process. We have drawn a table of the results: https://anonymous.4open.science/r/MultiSimDiff-D5A3/rebuttul/std.md. | null | null | null | null | null | null |
G-Sim: Generative Simulations with Large Language Models and Gradient-Free Calibration | Accept (poster) | Summary: The paper proposes a G-Sim, LLM-guided simulator with expert domain knowledge with gradient-free optimization while introducing a new problem with environment building. With experiments on three environments, the paper verified the flexibility of G-Sim.
Claims And Evidence: With limited experiments and no theoretical guarantee, it is hard to conclude the the claims are verified.
Methods And Evaluation Criteria: There are some parts that do not make sense so I will address them in the questions.
Theoretical Claims: There are no theoretical claims in this work.
Experimental Designs Or Analyses: I'm not sure that the experiments are well designed. The choice of benchmark methods seems unfair and the evaluation metric is also insufficient.
Supplementary Material: I checked the appendix.
Relation To Broader Scientific Literature: The work of a simulator can affect a huge domain of scientific and non-scientific domains since there are many use cases.
Essential References Not Discussed: I think the authors did most of the essential references.
Other Strengths And Weaknesses: **Weakness**
- The presentation of the paper should be improved a lot.
Other Comments Or Suggestions: - The abstract is too long so it makes it difficult to follow the key concept of the paper solely in the abstract.
- Overall, there are too many \paragraph, \enumerate and \itemize in the main text, which I think is not a good way to present a paper.
- I understand that defining the problems and introducing the previous works are very important. However, presenting the main method at the middle of page 5 might not be the best strategy.
- I think there should be a self-contained description of the figure on the label of Figure 1.
- In the right column line 284, "• Additional terms can incorporate other diagnostic criteria as needed, such as (Rauba et al., 2024) or stress-tests (Li & Yuan, 2024)", I think the author is missing the criteria in front of "(Rauba et al., 2024)"?
Questions For Authors: - It seems like the paper lacks a lot of details of the proposed model. Can you elaborate more on the parameter fitting steps of this method?
- What is $f$ in Section 4.2?
- How does the formulation of Score look like?
- Do you have any theoretical guarantees/insights that this fitting process will give you an optimal solution?
- Can you elaborate more on Section 4.3?
- How do you formulate $\delta$ and what is the explanation behind it?
- How do you choose the predefined threshold $\epsilon$?
- How accurate is the LLM feedback when the diag values are greater than $\epsilon$? Have you tested different scenarios and checked whether the LLM is outputting the right feedback to the current situation?
- I'm not sure whether the comparison with proposed benchmark methods is a fair choice. How is the training/inference time difference for different methods? or the number of parameters or computational complexity?
- Also, do you have results for "what if" questions for other methods as well?
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: We sincerely thank the Reviewer for the valuable and constructive feedback. Below, we address each concern and outline key improvements in the revised manuscript.
---
### **1. Experimental Validation and Benchmark Fairness**
We acknowledge the concerns regarding validation and benchmark selection:
- **New Metrics:** We have conducted additional experiments beyond Wasserstein distance, we now include **Mean Squared Error** and **Maximum Mean Discrepancy (MMD)** metrics for a more comprehensive assessment, https://imgur.com/a/yx228xx.
- **Computational Fairness:** To ensure fair comparisons, we will explicitly report training times and number of parameters for all baselines, as seen here: https://imgur.com/a/pgdvwWT.
### **2. Manuscript Clarity and Presentation**
We fully agree with the suggested improvements for clarity and readability. Specifically:
- **Concise Abstract:** The abstract will be shortened, succinctly summarizing existing method limitations and explicitly emphasizing our main contribution (LLM-guided, gradient-free simulator generation). Technical details will move entirely into the main text.
- **Formatting Improvements:** We significantly reduce itemized/enumerated lists and paragraph breaks:
- Merged "Current methods" and "General-purpose simulators" into a streamlined narrative introduction.
- Replaced itemized "Key properties" and "Contributions" with concise narrative descriptions.
- Removed unnecessary paragraph breaks (\paragraph{}) and lists on page 4.
- **Method Earlier in Manuscript:** To enhance readability, we move the "G-Sim: Hybrid Simulator Construction" section from page 5 to page 4, preceding related work.
- **Improved Fig. 1 Caption:** Revised caption for Figure 1 to be self-contained and clear:
*"Overview of G-Sim, an automatic simulator-generation framework integrating LLM-derived domain knowledge and empirical data. G-Sim iteratively: (1) proposes simulator structure using domain-informed LLM, (2) calibrates parameters via gradient-free optimization, and (3) refines through diagnostics (predictive checks, stress-tests, LLM-reflections), enabling robust ‘what-if’ scenario analyses."*
- **Minor Clarification:** Line 284 revised explicitly as: "imbalances (Rauba et al., 2024)."
---
### **3. Detailed Responses to Reviewer Questions**
**Parameter Fitting:**
In Appendix E. 3, we explicitly clarify gradient-free evolutionary optimization (population initialization, mutation strategy, selection criteria, and convergence checks). We minimize MSE using EvoTorch's genetic algorithm (population 200, simulated binary crossover, Gaussian mutation, and tournament selection). Furthermore, we warm-start reusing the best parameters from the previous iteration where possible.
**Score Function Clarification:**
The "Score" quantifies discrepancies between simulated and observed data in our implementation via MSE, as detailed explicitly in Appendix E.3.
**Theoretical Guarantees:**
We acknowledge the lack of rigorous global optimality guarantees but highlight known convergence properties of evolutionary methods towards global minima under suitable conditions [1]. We will explicitly include this discussion, clearly indicating assumptions and limitations.
*[1] Rudolph, G. (1994). IEEE Trans. Neural Networks, 5(1), 96-101.*
**Clarifications on Section 4.3:**
- **Diagnostic formulation ($\\delta$):**
Diagnostic discrepancies ($\\delta$) aggregate multiple metrics—predictive accuracy (e.g., MSE, Wasserstein distance) and domain constraints (non-negativity, cyclical patterns). Appendix B.3 explicitly details these diagnostics.
- **Threshold $\\varepsilon$ Selection:**
We implicitly set $\\varepsilon$ via iteration limits. We will clarify this explicitly in the manuscript.
- **LLM Feedback Robustness:**
Empirical validations (App. I.2 iterative refinement logs; App. E.4 prompt templates) show LLM feedback consistently improved accuracy, demonstrating robustness across diverse diagnostic scenarios. This evidence will be explicitly highlighted.
---
### **4. "What-If" Scenario Comparisons**
Baseline methods inherently lack structured mechanisms for performing counterfactual ("what-if") analyses. Thus, such scenarios are uniquely suited for our generative framework, clearly distinguishing G-Sim's capabilities. We will clarify this explicitly in the revision.
---
### **Summary of Improvements**
- Expanded experimental validation.
- Streamlined abstract.
- Improved manuscript readability.
- Clarified parameter-fitting and diagnostics.
- Enhanced clarity of Sec 4.3.
- Discussion of convergence.
*We hope that most of the reviewer’s concerns have been addressed and, if so, they would consider updating their score. We’d be happy to engage in further discussions.*
---
Rebuttal Comment 1.1:
Comment: Thank you for the authors' detailed rebuttal and the additional experimental results. I have also carefully reviewed the comments from the other reviewers. While I acknowledge the improvements made, I still believe the manuscript requires significant refinement before it can meet the standard for acceptance. My main concern remains the robustness of the proposed model, which, in my view, is not sufficiently supported by either theoretical guarantees or comprehensive empirical evaluations.
---
Reply to Comment 1.1.1:
Comment: Thank you for your continued engagement with our work. We understand your concerns about the robustness of our model and the need for stronger theoretical and empirical support. We believe our new SBI results directly address these concerns (https://imgur.com/a/rK4MtoO):
----
### **1. Theoretical and Empirical Robustness**
The addition of Simulation-Based Inference (SBI) provides both theoretical guarantees and comprehensive empirical validation:
**Theoretical Guarantees:**
- SBI provides principled Bayesian uncertainty quantification through posterior distributions
- Simulation-Based Calibration (SBC) ensures the reliability of our posterior approximations
- The neural posterior estimator's convergence properties are well-studied in the literature
**Empirical Validation:**
Our new results (https://imgur.com/a/HFnh9up, https://imgur.com/a/rK4MtoO) demonstrate robust performance across multiple dimensions:
- Parameter estimation accuracy: SBI consistently recovers true parameters within credible intervals
- Uncertainty quantification: Full posterior distributions capture parameter interactions and multi-modal solutions
- Calibration: SBC scores show reliable uncertainty estimates (mean absolute deviation from 0.5 < 0.1)
- Computational efficiency: Number of simulations (10,000) is comparable to GFO evaluations
---
### **2. Comprehensive Evaluation**
The visualization (https://imgur.com/a/HFnh9up) provides a comprehensive empirical evaluation:
- Direct comparison of GFO and SBI parameter estimates
- Visualization of posterior distributions showing parameter interactions
- Trajectory predictions with uncertainty bands
- Calibration metrics across multiple test scenarios
----
### **3. Manuscript Improvements**
We will make the following changes to address your concerns:
- Move SBI analysis from appendix to main methodology section
- Add theoretical discussion of SBI guarantees and limitations
- Include comprehensive empirical results in main results section
- Streamline presentation as previously discussed
---
### **4. Fair Comparison**
The SBI implementation provides a fair comparison with GFO:
- Similar computational budget (10,000 simulations vs 4,000-25,000 GFO evaluations)
- Direct comparison of point estimates (MAP vs GFO)
- Additional uncertainty quantification through posterior distributions
We believe these additions significantly strengthen the theoretical and empirical foundations of our work. The SBI results provide both theoretical guarantees through Bayesian inference and comprehensive empirical validation through calibration and uncertainty quantification.
---
*We hope that most of the reviewer's concerns have been addressed and, if so, they would consider updating their score. We'd be happy to engage in further discussions.* | Summary: This paper attempts to generate simulators via LLMs coupled with a gradient-free optimisation process to choose parameters. An LLM-guided search loop identified the simulator's structural components and a gradient-free optimisation procedure sets their parameters. The method relies on the generalisation ability of LLMs in other to generalise to OOD data. The paper can be seen as an orchestration framework for LLMs.
Claims And Evidence: The authors claim to have created a general framework for creating "what if" simulators across a wide variety of domains. The method description is unclear, so it is hard to understand exactly how this process works. In some ways, this seems related to a managed prompting framework. In the appendix it seems like the LLMs are generating Python code then gradient-free optimisation adjusts the prompts.
Methods And Evaluation Criteria: Please see my comments under "claims and evidence".
Theoretical Claims: There are limited theoretical claims or proofs - this is an empirical paper.
Experimental Designs Or Analyses: The experiment involves generating multiple simulators for data-driven problems, but it is unclear to what extent this process is actually automated.
Supplementary Material: The authors provide very extensive appendices, but the method should be understandable from the paper itself.
Relation To Broader Scientific Literature: The method is similar to other simulator generating methods, some of which are included in their experiments, but this method does not include any guarantees of accuracy.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: N/A
Other Comments Or Suggestions: I would be more explicit in the paper about the method. Is the LLM being prompted, generating python code and optimisation repeats this process? I would also give examples of things like "structural proposals" and be more explicit about the method as this is somewhat unusual construction.
Questions For Authors: N/A
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: We sincerely thank the Reviewer for their detailed and constructive feedback. We fully agree on the importance of clearly presenting our methodology within the manuscript itself. To comprehensively address these concerns, we will allocate the additional page in the camera-ready version specifically to enhance clarity. Below, we provide a shortened clarification of our method, explicitly referencing relevant sections and appendices, and address each of the reviewer's comments directly.
**Clarification of the Proposed Method:**
G-Sim automates the generation of domain-specific simulators by integrating structural proposals from Large Language Models and numerical calibration via Gradient-Free Optimization. The process involves an iterative loop between three distinct phases, outlined in Algorithm 1 and described in Section 4 and Appendix E.2:
1. **Structural Proposal via LLM (Section 4.1 and Appendix E.4):**
- The LLM generates Python code to outline the simulator’s structural components, guided by domain-specific textual descriptions and available background knowledge.
- Structural proposals explicitly specify modular Python functions and classes capturing domain-relevant mechanisms, such as epidemic spread dynamics or resource distribution processes. Importantly, the LLM defines the structural templates without numerical parameters, which are left open for subsequent calibration.
2. **Parameter Calibration via Gradient-Free Optimization (Section 4.2 and Appendix E.3):**
- Following structural generation, numerical parameters within these LLM-generated modules are independently calibrated using gradient-free methods, such as evolutionary algorithms, to align the simulation outcomes with empirical observations.
- This parameter optimization step is entirely decoupled from the structural proposals made by the LLM, which we hope clarifies potential confusion between the structural and numerical stages of the simulator generation process.
3. **Iterative Refinement via Diagnostic Feedback (Section 4.3 and Appendix E.4):**
- Simulations produced by the above steps are then evaluated against the available empirical data to identify discrepancies or inadequacies.
- These evaluation outcomes are synthesized into textual feedback (for example, "Simulator lacks weekly seasonality, consider incorporating periodic seasonal modules"), guiding the LLM to refine structural proposals.
- This iterative loop of evaluation, feedback, and refinement proceeds automatically until the resulting simulator meets the desired levels of accuracy and domain plausibility.
The combination of the symbolic and optimization approaches ensures G-Sim remains robust, transparent and precise, as justified empirically, offering strong generalization capabilities even in out-of-distribution scenarios.
**Extent of Automation:**
- The iterative refinement loop described above is fully automated once initial contextual inputs are provided, and our experiments follow this approach. However, the framework is flexible enough to optionally accommodate human expertise for interpreting nuanced feedback or integrating additional domain-specific constraints.
**Explicit References to Examples in Camera-Ready Version:**
- Explicit examples of the generated Python code and the iterative refinement process are already detailed in Appendix I.2. We will provide clearer cross-references to these examples within the main manuscript, enabling the reader to readily access practical demonstrations of structural proposals and refinement iterations.
- Moreover, Appendix F presents detailed prompts alongside the environment specifications provided to the LLM, illustrating the exact inputs guiding structural generation. We will reference these more explicitly in the main text to further clarify how our methodological approach leverages domain knowledge.
**Committed Enhancements for Final Manuscript:**
- A dedicated additional page in the manuscript clearly describing each component of our method: structural proposals (Appendix E.4), gradient-free parameter calibration (Appendix E.3), and diagnostic iterative refinement (Algorithm 1 in Appendix E.2).
- Explicit references within the main text to practical illustrative examples (Appendix I.2) and to detailed LLM prompts and environment details (Appendix F).
- Clarification on the scope of automation and the optional role of domain expertise.
---
*We hope that most of the reviewer’s concerns have been addressed and, if so, they would consider updating their score. We’d be happy to engage in further discussions.* | Summary: This paper introduces G-Sim, a framework for automatically constructing simulators by combining Large Language Models (LLMs) and gradient-free optimization (GFO). The LLM is used to generate the structural components of the simulator (submodules, causal relationships), based on provided domain knowledge. GFO is then employed to calibrate the parameters of these submodules to align with empirical data. The framework includes an iterative refinement loop, where discrepancies between simulator output and real-world data trigger LLM-guided adjustments to the simulator's structure, followed by re-calibration via GFO. The paper demonstrates G-Sim on epidemic modeling (COVID-19), supply chain, and hospital bed scheduling examples, claiming improved out-of-distribution generalization compared to purely data-driven methods.
## Update After Rebuttal
The authors provided a thorough rebuttal and engaged constructively with the feedback. I appreciate their efforts in running additional experiments during the discussion phase and, crucially, incorporating a Simulation-Based Inference (SBI) analysis into their framework and agreeing to elevate it from the appendix to a more central part of the main paper. This addition significantly strengthens the paper's potential contribution regarding uncertainty quantification.
However, based on the SBI results presented during the rebuttal (via the provided plots), the current implementation appears to require further refinement. The results showed inconsistent parameter recovery, overly broad posterior distributions, and posterior predictive checks that indicated issues. These problems seem likely related to implementation details (e.g., embedding network architecture, summary statistics, or training procedure) rather than fundamental limitations, as SBI is generally expected to perform well on this type of problem (SIR model). Specific suggestions for diagnosing and improving these results were provided to the authors.
Overall, the paper has been notably improved through the authors' responsiveness and the inclusion of the SBI analysis. While the current SBI results need further work, the commitment to incorporating this methodology addresses a key weakness identified in the initial review. Consequently, I have adapted my initial evaluation to reflect these positive developments.
Claims And Evidence: The main claim is that G-Sim can generate "robust and flexible" simulators that are "aligned with empirical evidence" and capable of "causally informed" decision-making. While the framework is conceptually appealing, the evidence supporting these broad claims is not entirely convincing:
1) Out-of-Distribution Generalization: The paper claims superior out-of-distribution generalization compared to purely data-driven methods (RNNs, Transformers). While the experiments suggest this might be the case, the comparisons are limited. It's unclear if the data-driven baselines were appropriately tuned for this task. A more comprehensive comparison, including a wider range of baselines and more challenging out-of-distribution scenarios, would be necessary to fully support this claim.
2) Causal Structure Recovery: A key aspect of G-Sim is the LLM-guided generation of causal structure. However, the paper doesn't convincingly demonstrate that the correct causal structure is recovered. For example, in the SIR modeling example, does the LLM generate the actual SIR equations, or just a functionally similar but causally incorrect model? The paper lacks a rigorous evaluation of the structural accuracy of the generated simulators, relying primarily on predictive performance.
3) GFO vs. SBI: The choice of gradient-free optimization (GFO) for parameter calibration is justified by the potential non-differentiability of the generated simulators. However, simulation-based inference (SBI) methods, which infer a distribution over parameters rather than a single point estimate, would likely be a more appropriate and robust choice. SBI naturally handles stochasticity in the simulator and provides uncertainty quantification, which is crucial given the potential for errors in the LLM-generated structure. GFO provides only a point estimate, lacks uncertainty estimation for predictive checks, does not provide any information about parameter interactions and potential compensation mechanisms between parameters, potentially failing to detect multi-modal solutions.
Methods And Evaluation Criteria: The proposed framework, combining LLMs and GFO, is a reasonable approach to the problem of automatic simulator construction. The use of real-world inspired examples (epidemic modeling, supply chains, hospital beds) is appropriate. However, the evaluation criteria primarily focus on predictive accuracy. While important, this is insufficient to assess the overall quality of the generated simulators. Additional criteria, specifically focusing on the structural accuracy and the causal validity of the learned models, are needed.
Theoretical Claims: The paper does not present significant theoretical contributions, focusing primarily on the framework and its application. Therefore, I did not check any proofs.
Experimental Designs Or Analyses: I reviewed the experimental designs. As mentioned above, the comparisons to purely
data-driven methods are limited, and the evaluation lacks a rigorous assessment of the
structural and causal accuracy of the generated simulators. The choice of GFO over SBI
is also a concern, especially given the initial strong claim in the abstract to
construct "uncertainty-aware simulators".
Supplementary Material: No.
Relation To Broader Scientific Literature: The paper positions itself at the intersection of LLMs, simulator learning, and
optimization. It relates to prior work on using LLMs for code generation and to the
broader field of system identification. However, the connection to the simulation-based
inference (SBI) literature, which offers powerful tools for calibrating simulators and
quantifying uncertainty, is not adequately explored.
Essential References Not Discussed: No, the paper seems to discuss directly related prior thoroughly.
Other Strengths And Weaknesses: **Originality**: The combination of LLMs and GFO for automatic simulator construction, along
with the iterative refinement loop, appears to be a novel approach.
**Significance**: The potential significance is high, as robust and flexible simulators are
crucial for many scientific and engineering domains. However, the current evidence does
not fully support the claimed significance.
**Clarity**: The paper is generally well-written and easy to follow. The overall framework
is clearly presented. However, some details regarding the experimental setup and the
evaluation criteria could be clarified.
Other Comments Or Suggestions: No
Questions For Authors: 1) GFO vs. SBI: Why was gradient-free optimization (GFO) chosen for parameter
calibration instead of simulation-based inference (SBI) methods? SBI seems like a
more natural fit, providing a posterior distribution over parameters and inherent
uncertainty quantification. Could you compare the performance and scalability of GFO
and SBI (e.g., using Neural Posterior Estimation) in this context?
2) Structural Accuracy: How do you assess the structural accuracy of the generated
simulators? Do you have any mechanisms to ensure that the LLM recovers the correct
causal relationships, and not just a model that fits the observed data well? How
would you evaluate the simulator if the true underlying structure is unknown?
3) Theoretical Contributions: The paper primarily presents an engineering framework. Are
there any novel theoretical contributions, or is the main contribution the
combination of existing techniques?
4) Intervention Modeling: Can you provide more details on the intervention modeling
capabilities? How are interventions represented and incorporated into the
LLM-generated simulators? Can you provide specific examples of interventions tested
in the experiments?
5) Limitations of the LLM prompt: Can you provide some insights on prompt engineering
effort? How much expert knowledge is required here?
6) Scalability to complex settings: Can you comment on the expected scalability to
use-cases with high-dimensional parameter vectors and many (coupled) submodules?
Ethical Review Flag: Flag this paper for an ethics review.
Ethics Expertise Needed: ['Legal Compliance (e.g., GDPR, copyright, terms of use)']
Ethical Review Concerns: The G-Sim framework, which automates the construction of simulators for domains like healthcare, logistics, and epidemic planning, has the potential to be classified as a high-risk AI system under the EU AI Act. This is because the generated simulators could be used to inform decisions with significant impacts on individuals' health, safety, and economic well-being. Therefore, an ethical review is warranted to assess the potential biases, risks, and societal consequences of deploying such a system, and how they may be mitigated.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We sincerely thank Reviewer for their insightful and constructive feedback, which significantly helps strengthen our paper. Below, we address each major concern explicitly and outline concrete improvements for the camera-ready version.
---
**Baseline Tuning**
We appreciate the reviewer’s concern about baseline comparisons. The baselines' hyperparameters are standard, and both the baselines and hyperparameters are similar to recently published works on similar simulation tasks, coming from the Hybrid Digital Twin work (L 245).
---
**Structural and Causal Accuracy**
The reviewer rightly emphasized the importance of validating structural and causal accuracy. Our intervention experiments implicitly verify structural correctness; simulators that produce accurate predictions under unseen interventions strongly indicate correct causal structure.
Additionally, we now include [quantitative evaluations](https://imgur.com/a/z1sJuFD) (F1 Score and Structural Hamming Distance - SHD) against their known causal structures. Specifically, the Supply Chain environment perfectly matches ground-truth causal relationships (F1=1.0, SHD=0), while Hospital and SIR environments yield F1 scores above 90% and minimal SHD (≤1.5), demonstrating that G-Sim reliably captures causal relationships. These metrics and their analysis will be prominently featured in the updated manuscript.
---
**Gradient-Free Optimization (GFO) vs. Simulation-Based Inference (SBI)**
The reviewer's suggestion regarding SBI methods is highly pertinent. Initially, we adopted evolutionary-based GFO primarily for scalability reasons, given its suitability for non-differentiable, stochastic simulator components. Nonetheless, we agree that SBI's uncertainty quantification and robustness are valuable. We have since integrated SBI into G-Sim, testing it on the COVID-19 environment. [Preliminary results](https://imgur.com/a/rK4MtoO) indicate comparable performance to GFO, with added benefits of uncertainty estimation. A detailed comparison between SBI and GFO, along with explicit recommendations for future work, will be included in the revised manuscript (Sections 1 and 4.2).
---
**Contributions**
The reviewer correctly identifies that our primary contribution is the innovative integration of existing techniques (LLM-driven structural reasoning combined with GFO).
---
**Intervention Modeling**
Interventions are directly modeled by explicitly modifying parameters in the transparent, human-readable code modules generated by the LLM, as described in 6.1. Our design ensures robustness under interventions outside the training distributions, providing valuable "what-if" analyses. We will expand on these scenarios in a dedicated appendix, explaining detailed examples to enhance clarity.
---
**Prompt Engineering Effort**
Prompt engineering required modest domain-specific adjustments, leveraging generalizable, environment-agnostic prompts (provided in Appendix E.4) supplemented with concise, environment-specific descriptions (Appendix F). Our approach minimizes the need for extensive expert intervention. We will explicitly discuss the extent of prompt engineering required in our revision. We optimized the prompts to support and understand the tool calls and iterative workflow.
---
**Scalability**
We recognize scalability as an essential consideration. Scaling discovery is often an NP-hard problem, and we also find that it is difficult to scale. However, future work can exploit decomposable structures, and we can scale with the number of parameters to optimize, inheriting the same scalability as ES.
We will add an expanded discussion of scalability and practical examples detailing scalability in a new appendix.
---
**Ethical Considerations**
We appreciate the reviewer's concern regarding ethical implications. Our approach prioritizes transparency, allowing easy inspection, stress-testing, and expert verification of simulator outputs prior to deployment. As explicitly stated in our Impact Statement (L2182-2199), we emphasize the critical role of domain expertise, transparency in assumptions, and rigorous oversight. To further address these concerns, we will include an expanded discussion on ethical considerations, biases, and mitigation strategies in a dedicated appendix.
---
**Summary of Revisions:**
- Clarified baseline comparisons.
- Added explicit quantitative evaluation of causal and structural accuracy.
- Provided a new experiment comparing GFO and SBI.
- Enhanced explanation and examples of intervention modeling.
- Clarified prompt engineering effort and detailed scalability strategies.
- Included thorough discussion of ethical considerations and mitigation strategies.
---
*We hope that most of the reviewer’s concerns have been addressed and, if so, they would consider updating their score. We’d be happy to engage in further discussions.*
---
Rebuttal Comment 1.1:
Comment: Thank you for your thorough rebuttal. I appreciate the efforts to address my concerns and the additional analyses you've included. The additions of F1 Score and Structural Hamming Distance metrics for evaluating causal accuracy are valuable improvements that enhance the paper's evaluation methodology.
I'm particularly encouraged to see that you've already incorporated SBI into your framework - this is an important step forward. Given that G-Sim aims to build simulators from scratch using potentially sparse data, proper uncertainty quantification and calibration are crucial for reliable deployment. To strengthen the SBI analysis and make it more prominent in the paper, please address these specific methodological points:
1. Provide details on the SBI implementation: How many simulation samples were used for training the neural posterior? Was the number of simulations comparable to function evaluations in GFO?
2. Demonstrate proper posterior calibration, ideally using Simulation-Based Calibration (SBC), before calculating predictive metrics. This would ensure the posterior approximation is reliable.
3. Include posterior predictive distributions alongside MAP estimates in your evaluation to properly account for uncertainty in predictions
4. Replace the MLP embedding network with an RNN or 1D causalCNN embedding that can better capture temporal dependencies in SIR trajectories
5. Add visualizations of the posterior distributions to reveal potential parameter interactions or multi-modal solutions
I would strongly encourage you to elevate the SBI analysis from an appendix comparison to a more central part of the paper. This could potentially be a significant contribution, as combining LLM-based structural generation with principled Bayesian parameter inference offers a powerful framework for scientific modeling under uncertainty.
Regarding prompt engineering efforts, could you provide more concrete details about the level of expert involvement required? For example, quantifying the number of prompt iterations needed per environment, or estimating the domain expertise level required (novice vs. expert) would help readers understand the practical implementation requirements.
---
Reply to Comment 1.1.1:
Comment: Thank you for continued engagement! We agree that having SBI now strengthens the work, particularly in providing principled uncertainty quantification and calibration.
> Provide details on the SBI implementation: How many simulation samples were used for training the neural posterior? Was the number of simulations comparable to function evaluations in GFO?
For the SBI implementation, we used Neural Posterior Estimation (NPE) with the following configuration:
- Training simulations: 10,000 samples for training the neural posterior
- Calibration samples: 1,000 samples for Simulation-Based Calibration (SBC)
- Posterior samples: 1,000 samples for inference
- We used an RNN-based embedding network (hidden_dim=64, output_dim=8) to better capture temporal dependencies in the SIR trajectories, as you suggested
The number of simulations (10,000) is comparable to the function evaluations in GFO, which typically uses 200-500 generations with population sizes of 20-50, resulting in 4,000-25,000 total evaluations. This ensures a fair comparison between the methods.
> Demonstrate proper posterior calibration, ideally using Simulation-Based Calibration (SBC), before calculating predictive metrics. This would ensure the posterior approximation is reliable.
We implemented Simulation-Based Calibration (SBC) to verify posterior calibration. Our custom SBC implementation:
1. Generates 1,000 calibration samples from the prior
2. For each sample, computes the rank of the true parameter value in the posterior distribution
3. Calculates a calibration score (mean absolute deviation from 0.5)
4. Our results showed good calibration across parameters, with ranks close to 0.5 (mean absolute deviation from 0.5 was <0.1)
> Include posterior predictive distributions alongside MAP estimates in your evaluation to properly account for uncertainty in predictions
We provide both MAP estimates and full posterior predictive distributions in our evaluation, as shown in the visualization (https://imgur.com/a/HFnh9up). The visualization includes:
- Parameter comparison showing ground truth, GFO, and SBI estimates
- Trajectory predictions with uncertainty bands
- Posterior distributions showing parameter interactions
- Posterior predictive distributions with 95% credible intervals
> Replace the MLP embedding network with an RNN or 1D causalCNN embedding that can better capture temporal dependencies in SIR trajectories
We implemented an RNN-based embedding network with the following architecture:
- Input dimension: (T+1) * 3 (for S, I, R components)
- Hidden dimension: 64
- Output dimension: 8
- Bidirectional GRU with 2 layers
- Additional fully connected layers for final embedding
This architecture better captures temporal dependencies in the SIR trajectories compared to the previous MLP approach, as evidenced by the improved trajectory predictions in the visualization.
> Add visualizations of the posterior distributions to reveal potential parameter interactions or multi-modal solutions
The visualization (https://imgur.com/a/HFnh9up) provides comprehensive visualizations of the posterior distributions:
1. 2D scatter plots of parameter interactions (e.g., beta vs gamma)
2. Contour plots showing the joint density
3. Marginal distributions for each parameter
4. Posterior predictive distributions with credible intervals
5. Comparison of true parameters, MAP estimates, and posterior samples
> I would strongly encourage you to elevate the SBI analysis from an appendix comparison to a more central part of the paper. This could potentially be a significant contribution, as combining LLM-based structural generation with principled Bayesian parameter inference offers a powerful framework for scientific modeling under uncertainty.
We agree completely and will move the SBI analysis to a more central position in the paper. Specifically:
1. Move the SBI methodology to the main methodology section
2. Add a dedicated section on uncertainty quantification and calibration
3. Include the visualization results (https://imgur.com/a/HFnh9up) in the main results section
4. Expand the discussion of how SBI complements LLM-based structural generation
> Regarding prompt engineering efforts, could you provide more concrete details about the level of expert involvement required?
The prompt engineering required modest domain-specific adjustments:
- Core prompts are environment-agnostic and reusable
- Each environment required 2-4 hours of expert review
- Most time was spent verifying causal structure rather than prompt engineering
- Domain expertise level: intermediate (familiar with the domain but not necessarily an expert)
- Number of prompt iterations: typically 3-5 per environment
- The prompts are designed to be self-documenting and maintainable
---
*We hope that most of the reviewer's concerns have been addressed and, if so, they would consider updating their score. We'd be happy to engage in further discussions.* | null | null | null | null | null | null | null | null |
Conformity Score Averaging for Classification | Accept (poster) | Summary: This paper proposes to improve conformal prediction by optimally averaging multiple conformity score functions. This papers explores various data splitting methods and optimal weights for aggregating the score functions.
Claims And Evidence: The main claim of this paper is that by optimally weighting multiple score functions, the resulting threshold can achieve better performance. This claim is validated both theoretically and numerically. However, in terms of theoretical results, this paper shows that optimizing weights has small impact on the validity. However, the validity of proposed threshold does not directly support the claim of improving performance. The numerical experiments are limited to two datasets.
Methods And Evaluation Criteria: * The proposed method makes sense but lacks principled guidance.
* Ensemble method is common in machine learning. Despite the claim, it is unclear where the novelty lies.
* The optimal weights are determined by grid search, which is potentially very inefficient. Instead of investigating further on the optimal weights, this paper go into different splitting methods, which blur the main focus and the main take away on different splitting is also not clear.
* In terms of evaluation, the benchmark datasets are not sufficient and missing out on others like variants of MNIST.
Theoretical Claims: Limited review. Appears to be correct in terms of statements. But it lacks interpretation in the main texts of the paper.
Experimental Designs Or Analyses: The experiment metric makes sense, but it lacks a comprehensive comparison with other alternative ensemble methods.
Supplementary Material: N/A
Relation To Broader Scientific Literature: N/A
Essential References Not Discussed: Gauraha, Niharika, and Ola Spjuth. "Synergy conformal prediction." Conformal and Probabilistic Prediction and Applications. PMLR, 2021.
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 detailed feedback and constructive suggestions.
---
### **1. About why our method can improve performance**
In our setting, there exist $d$ score functions corresponding to weights $w = e_1, \dots, e_d$, where $e_i$ is the $i$-th standard basis in $\mathbb{R}^d$. The optimal weight $w^* \in \Delta^d$ yields the most efficient score function. Since $\{e_1, \dots, e_d\} \subset \Delta^d$, the score function $\langle w^*, s(x, y) \rangle$ is at least as efficient as any single score function. The improvement of our method is quantified by the difference in prediction set size between $\langle w^*, s(x, y) \rangle$ and the best single-score function.
---
### **2. About novelty in the ensemble method literature**
We agree that ensemble methods are common in machine learning and statistics, and this motivates our proposal to apply model averaging to conformity scores.
Unlike standard ensemble methods, our approach aggregates scores in the final step during conformal prediction. This allows ensemble methods to be applied even when only one model is trained, by aggregating different score functions. To the best of our knowledge, this is the first work that enables ensemble techniques at the conformity score level.
Theoretically, our paper is the first to show that averaging conformity scores has a mild effect on validity while achieving near-optimal efficiency.
---
### **3. About inefficiency of grid search**
We acknowledge that grid search may not be efficient and view efficient weight optimization as future work. We have introduce some alternative method in the response to Reviewer j2fr and Reviewer gF9v. The methods include greedy search, golden section search, gradient descent after smoothing and stochastic optimization.
While we acknowledge the importance of efficient optimization, the focus of this work is on analyzing the properties of $\hat{w}$ and providing its statistical guarantees.
---
### **4. About why we consider different splitting methods**
We respectfully disagree with the assertion that introducing different splitting methods blurs the main focus of the paper. As described in Section 2.5, we use only 34 lines to introduce these methods, which we believe is a reasonable length. It is necessary to present the splitting methods here, as the statistical guarantees in the next section depend on them.
At least one splitting method is essential for finding $\hat{w}$. The main takeaway from introducing different splitting methods is to demonstrate that our conformity score averaging method is versatile and can be applied in various splitting scenarios.
As pointed out by Reviewer gF9v, examining a variety of splits and clarifying how coverage versus efficiency tradeoffs shift is one of the strengths of our work. Therefore, we will retain the splitting methods, along with their theoretical analysis and experiments, in the paper.
---
### **5. About lack of datasets, such as variants of MNIST**
We have conducted additional experiments to address this concern. Please see the updated experimental results in our response to Reviewer 82f9.
---
### **6. About interpretation of theoretical claims**
Thank you for confirming the correctness of our theoretical results. Section 3 provides a detailed interpretation of our theorems, with the key takeaway being that $\eta$ and $\xi$ are small as long as the dataset sizes are large.
As suggested by Reviewer 82f9, we will add additional intuition about the VC dimension and its connection to the DKW inequality to make the theoretical results more accessible.
---
### **7. About comparison with other alternative ensemble methods**
The most relevant ensemble method is in [1], which outputs the most efficient prediction set among a finite set of score functions. Our experiments already compare against single scores and models, including the most efficient ones. Please see Table 1 and Figures 3–5, where our method consistently outperforms these baselines.
---
### **8. About the suggested reference, "Synergy conformal prediction"**
Thank you for suggesting this reference. This paper also proposes an ensemble method for conformal prediction. However, our method differs in two key ways:
1. Our averaging occurs at the conformity score level, while their method aggregates models.
2. Our method optimizes the weights, whereas theirs does not.
We will cite this paper in the revised manuscript and clarify the distinctions between the two methods. Please see the experiment result in our response to Reviewer 82f9.
---
### **References**
[1] Yang, Y., and Kuchibhotla, A. K. (2024). Selection and aggregation of conformal prediction sets. *Journal of the American Statistical Association*, 1–13.
---
Rebuttal Comment 1.1:
Comment: I appreciate the authors’ detailed and helpful response. The added clarifications improved the theoretical exposition, and the new experimental results demonstrate the benefits of the proposed method. Overall, I find the paper more convincing and have increased my score accordingly. One last thing I wanted to mention is that a brief discussion or recommendation on selecting data splitting strategies could provide more practical value. | Summary: The paper proposes a method for improving prediction set efficiency in classification tasks through conformity score averaging. It introduces weighted averaging of multiple score functions and explores various data-splitting strategies to optimize the weight selection process. Theoretical guarantees for coverage and efficiency are established using VC theory, and experiments on CIFAR-10 and CIFAR-100 datasets demonstrate the method’s effectiveness over existing approaches.
Claims And Evidence: The claims are mostly supported by the evidence presented in the paper. More precisely:
- Averaging multiple conformity score functions leads to more efficient (i.e., smaller) prediction sets than using any single score alone.
- The method retains finite-sample coverage guarantees for multi-class classification.
- Empirical results on CIFAR-10 and CIFAR-100 show that the weighted method consistently achieves the target coverage while reducing prediction set size.
- Theoretical proofs based on VC theory support the coverage and efficiency claims.
- While convincing within the scope of the experiments, extending evaluations to more diverse or real-world datasets could further strengthen the evidence.
Methods And Evaluation Criteria: Yes, the proposed methods and evaluation criteria make sense. Some remarks in this regard:
- Weighted averaging of several nonconformity scores using a grid search over a discretized probability simplex.
- Implementation of different data splitting strategies (VFCP, EFCP, DLCP, DLCP+) to optimize weight selection.
- The use of grid search over the probability simplex to determine optimal weights is sensible, though computationally intensive.
- Evaluating the methods based on coverage probability and average prediction set size aligns well with the goals of both validity and efficiency in uncertainty quantification (and is standard practice in the CP literature).
Theoretical Claims: I tried to check all theoretical claims (and proofs thereof) in the paper. However, I did not check the corresponding Appendix line by line (mostly the "critical" parts to make sure that everything aligns).
Remarks:
- Finite-sample coverage guarantees are established via a theoretical analysis grounded in VC theory.
- The paper provides oracle inequalities that quantify the efficiency gap between the proposed weighted method and the ideal (optimal) prediction set.
- Consistency results demonstrate that the prediction set size approaches that of the optimal predictor as the sample size increases.
Experimental Designs Or Analyses: The experimental design and analysis is fine.
- Experiments conducted on benchmark datasets such as CIFAR-10 and CIFAR-100.
- Performance is compared against single-score methods (e.g., THR, APS, RANK) and competitive baselines (e.g., RAPS, SAPS).
- Multiple experimental runs (e.g., 100 different splits) and varying significance levels ($\alpha$ values).
- Key metrics include coverage probability and average prediction set size.
- Although the experiments on CIFAR datasets are well-conducted, incorporating additional datasets from different domains could enhance the findings.
Supplementary Material: I checked the supplementary material, while not as careful as the main paper itself.
- Additional experiments on data splitting ratios are provided in the supplementary file.
- Appendices include detailed proofs of theoretical results and specifics on the grid search implementation.
- Extra experimental results further validate the method’s robustness and efficiency.
Relation To Broader Scientific Literature: The work builds on the established framework of conformal prediction and extends it by integrating ideas from model averaging. It compares and contrasts with earlier methods such as APS, RAPS, and SAPS, highlighting improvements in efficiency.
Essential References Not Discussed: The related works in the paper is fine. While not strictly missing from the discussion, the following paper might be interesting to consider:
Gasparin, Matteo, and Aaditya Ramdas. "Merging uncertainty sets via majority vote." arXiv preprint arXiv:2401.09379 (2024).
Other Strengths And Weaknesses: Strengths:
- The linear combination of base scores is straightforward and can unify multiple advanced scoring rules.
- They rely on standard VC arguments to guarantee coverage and near-optimal size.
- They examine a variety of splits (VFCP, EFCP, DLCP, DLCP+), clarifying how coverage vs. efficiency can shift.
- In CIFAR tasks, the method consistently matches or outperforms single-score baselines, achieving the nominal coverage with smaller sets.
Weaknesses:
- The extension to regression remains open because the union-bounding trick used to handle classification does not trivially extend to real intervals (this limitation is acknowledged, though).
- The method does a full grid search over $\Delta^d$, which can be expensive if the number of base scores or the resolution is large.
- The paper’s experiments focus on CIFAR-10 and CIFAR-100. Additional or larger datasets (e.g., ImageNet) or real-world tasks could better test the method’s scalability.
Other Comments Or Suggestions: Some suggestions:
- Implementations might consider more direct/continuous optimization of the average set size, e.g., using subgradients w.r.t $\omega$.
- Extending to the label-conditional coverage or group-conditional coverage would be an interesting next step.
- The authors might systematically measure coverage vs. set size as a function of the calibration set size or the fraction used for weight selection.
Questions For Authors: Questions:
- Is it possible combine the data leakage idea with cross-validation or bootstrap to reduce coverage biases while still leveraging more data to pick $\hat{\omega}$?
- Have you considered applying a subgraph approach to real intervals for regression tasks? Perhaps bounding the capacity by restricting the family of linear transformations.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you very much for your positive review. Most of your questions are high-level and insightful. We will address them in order, starting with simpler questions and moving to more complex, open-ended ones.
---
### **1. About additional experiments**
We have conducted additional experiments on MNIST, Fashion-MNIST, and ImageNet-Val, as detailed in our response to Reviewer 82f9. These results will be included in the revised version of the paper.
---
### **2. Coverage vs. set size as a function of the calibration set size**
If we understand the question correctly, this refers to the relationship between calibration set size, coverage accuracy, and prediction set size. We have not systematically measured this relationship as a function, as this type of experiment is computationally expensive. Such an experiment would require multiple repetitions (e.g., 100 runs) to observe meaningful differences.
In Section F, we provide related experiments comparing two calibration set sizes. The results show that a larger calibration set provides more accurate coverage. However, the prediction set size also depends on the splitting method used.
---
### **3. About conditional coverage**
Our method can be applied to conditional coverage. The current work focuses on improving the efficiency of conformal prediction, with the prediction set size as the key optimization criterion. However, this criterion can be adapted to metrics related to conditional coverage, such as group-conditional coverage, label-conditional coverage, or ECE. By adjusting the criterion and allowing the algorithm to search for $\hat{w}$ that optimizes it, our method can generate conformal prediction sets tailored to meet conditional coverage requirements.
---
### **4. About cross-validation or bootstrap**
We do not believe the data leakage idea can be directly combined with cross-validation or bootstrap. The data leakage method uses the prediction set sizes of test samples to determine the weight $\hat{w}$. Below, we outline our thoughts on how cross-validation and bootstrap might connect to this idea.
A generalized version of the main algorithm could be considered. In Algorithm 2, $\mathcal{I}_1$ is used to find $\hat{w}$, and $\mathcal{I}_2$ is used to determine the quantile corresponding to $\hat{w}$. In VFCP, $\mathcal{I}_1$ and $\mathcal{I}_2$ are fixed partitions. A possible generalization would involve sampling $\mathcal{I}_1$ and $\mathcal{I}_2$ multiple times (e.g., through cross-validation or bootstrap). This process would result in multiple estimates of $\hat{w}$. Averaging these estimates could yield a final $\hat{w}$. The question is do we need another dataset to determine the threshold. This brings us back to the choice between VFCP and EFCP: whether to perform calibration on the same set or a separate set.
We do not have a clear theoretical answer on how these methods should be properly applied. We hypothesize that cross-validation or bootstrap could provide an intermediate solution between VFCP and EFCP.
---
### **5. About efficient methods to find $\hat{w}$**
We have explored several methods to improve the efficiency of finding $\hat{w}$. Some simpler methods are introduced in our response to Reviewer gF9v.
As you suggested, gradient descent is a potential approach. The main technical challenge is that the prediction set size is not a continuous function of $w$. To address this, we can approximate the indicator functions in the objective function using sigmoid functions as conformal training does. The success of this approach heavily depends on tuning the temperature parameter of the sigmoid function.
We have also considered stochastic optimization. For instance, starting from a random point $w$ on the grid $\Delta^d$, we evaluate the prediction set size for $w$ and its neighbors. We then move to a neighboring point with a probability based on the prediction set size. We record the smallest prediction set size encountered and use the corresponding $w$ as the final $\hat{w}$. Alternatively, discrete steps can be replaced with normal variable on $\Delta^d$. This energy-based method has shown promising results in some experiments, and we plan to include it in future work.
---
### **6. About extension to regression problems**
Our theoretical results can be extended to some families of score functions. Specifically, Lemma 1(b) relies on the VC dimension of the subgraph class:
$$\mathcal{A}:= \\{ \\{ y : \langle w, s(x, y) \rangle \geq t \\} : w \in \mathbb{R}^d, t \in \mathbb{R} \\}.$$
If the scores $s(x, y)$ are always concave in $y$, then the weighted score $\langle w, s(x, y) \rangle$ is also concave in $y$. In this case, all elements of $\mathcal{A}$ are intervals, and the VC dimension of $\mathcal{A}$ is 2. This result suggests that our method can handle any number of concave score functions, including those used in CQR. We believe this result will be useful to some readers and will include it in the revision. | Summary: In this paper, the authors presented an approach that enhances conformal prediction for multi-class classification by optimally averaging multiple conformity score functions, and a set of evaluation experiments showed that the weighted averaging approach consistently outperforms single-score methods by producing smaller prediction sets without sacrificing coverage.
Claims And Evidence: A set of the experiments using CIFAR10 and CIFAR100 using different significance levels, and the performance comparisons
of various models and their weighted combinations, *empirically* supported the outperformance of using the optimally averaging approach.
Methods And Evaluation Criteria: Some questions are listed as follows:
Could the authors provide insights into the complexity comparison between the proposed approach and single-score methods? A clearer understanding would help the community assess the balance between computational overhead and performance improvement.
It is not clear in the main body how many runs are conducted for each experimental setting.
Theoretical Claims: Given that the presented research field extends beyond my area of expertise, thoroughly assessing its theoretical soundness in detail is challenging. My current evaluation may be conservative and I will make my best effort to actively engage in discussions with the authors, other reviewers, and ACs.
Experimental Designs Or Analyses: Please refer to the questions in the Methods and Evaluation Criteria Section.
Supplementary Material: Appendix F was reviewed.
Relation To Broader Scientific Literature: It looks fine.
Essential References Not Discussed: Seems not applicable.
Other Strengths And Weaknesses: Additional strengths: The paper structure is well organised, the motivation is clearly described.
Other Comments Or Suggestions: Additional comment: Impact Statement is missing in the submission.
Questions For Authors: No futher questions.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your positive feedback and for appreciating the organization and motivation of our paper. Below, we address your questions and comments.
---
### **1. About the complexity of the proposed approach**
In our algorithm, the main source of complexity lies in finding the optimal weight $\hat{w}$. Specifically, we need to compute the prediction set size $O(1/\epsilon^d)$ times, where $\epsilon$ is the grid size, as detailed in Section A of the appendix.
We emphasize that evaluating prediction sets is computationally efficient for each iteration. Although the complexity is exponential in $d$, the process of finding $\hat{w}$ is still significantly faster than training deep learning models for classification tasks.
To address scalability when the number of score functions is small, we suggest the following greedy approach:
1. Start with $w_1 = 1$.
2. Add $w_2$ so that $w_1 s_1 + w_2 s_2$ minimizes the prediction set size.
3. Continue iteratively, adding $w_3, w_4, \dots$, ensuring each step minimizes the prediction set size.
Additionally, we observed in our experiments that the prediction set size is often quasi-convex in $w_i$, allowing for optimization via the golden-section search method. However, we cannot guarantee convexity in general, meaning this greedy approach may not yield the theoretically optimal $\hat{w}$ or satisfy the statistical guarantees in Section 3.
We discuss possible additional efficient methods in our response to Reviewer gF9v, who has suggested a useful approach. Kindly refer to that response for further details.
The focus of this work is on analyzing the properties of $\hat{w}$, rather than developing efficient algorithms to compute it. We believe that designing efficient methods to find $\hat{w}$ is an exciting direction for future work.
---
### **2. About the number of runs in the experiments**
If we understood your question correctly, the number of runs is 100. This is stated on line 368 of page 7. In each run, the data is randomly partitioned into training, calibration, and test sets.
---
### **3. About the impact statement**
Thank you for reminding us about the impact statement. We apologize for its omission. We will add the following statement to the revised manuscript:
*This work contributes to the broader goal of improving machine learning models' reliability and uncertainty quantification, which has the potential for positive societal impact across various domains.* | Summary: Existing conformal prediction methods typically rely on a single conformity score function, limiting both their efficiency and informativeness. In this paper, they propose a new approach that enhances conformal prediction by averaging multiple conformity score functions for the same classification task. They also provide a comprehensive theoretical analysis based on VC theory, demonstrating the effectiveness of our method.
Claims And Evidence: The proposed research problem is clearly defined, and the discussion around using a single score function is valid. The approach of combining multiple score functions with data splitting to enhance conformal prediction is logically sound. Furthermore, the paper provides comprehensive theoretical support to demonstrate the advantages of the proposed method, and the experiments empirically validate its claims.
Methods And Evaluation Criteria: The proposed methods and evaluation criteria are logically well-founded for the stated problem.
Theoretical Claims: Yes. The theoretical claims are comprehensive and are supported by a detailed proof.
Experimental Designs Or Analyses: Yes. The overall experimental design makes sense, but expanding the experimental settings would make the work more solid.
Supplementary Material: yes,all
Relation To Broader Scientific Literature: Conformal prediction is a flexible technique that can be applied in a variety of domains. The methods proposed in this work further advance the development of conformal prediction.
Essential References Not Discussed: n.a.
Other Strengths And Weaknesses: Strengths:
1. The research problem is intriguing, as it explores how to apply multiple conformal score functions to a single classification task.
2. The proposed method is both intuitive and logically sound.
3. The theoretical analysis is thorough, providing a comprehensive basis for the method’s correctness.
Weaknesses
1. The rationale for using the VC dimension should be explained in a more intuitive manner, making it easier for readers to understand its relevance.
2. Emphasize how the proposed theoretical contributions surpass or improve upon existing methods, which will help highlight the significance of the work.
3. For the experimental evaluation, only two datasets were used, which may limit the persuasiveness of the results. Including additional datasets or varying the experimental settings would further strengthen the evidence for the proposed method.
Other Comments Or Suggestions: see weakness
Questions For Authors: n.a.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your positive feedback and helpful suggestions. We also appreciate your careful review of the supplemental materials. Below, we will address your comments.
---
### **1. About the intuition of VC dimension in our proof**
We agree that providing this intuition would benefit readers. The primary idea relies on the Dvoretzky–Kiefer–Wolfowitz (DKW) inequality. If the supremum in equation (7) or (8) is taken over a single variable, e.g., $q \in \mathbb{R}$ or $w_1 \in \mathbb{R}$, the DKW inequality can be directly applied.
Using the VC dimension generalizes the DKW inequality, allowing the supremum to extend over multiple variables when the function is linear in those variables. This generalization underpins our proof's validity and efficiency. We will add this explanation to the revision.
---
### **2. About the theoretical contribution compared to existing papers**
In Section 5, we compare our method to two relevant approaches and can elaborate as follows:
- The method in [1] optimizes over $w \in \\{e_1, \dots, e_d\\}$, where $e_i$ is the $i$-th standard basis in $\mathbb{R}^d$. In contrast, we optimize over $w \in \Delta^d$, considering a much larger set of candidate score functions. Both methods show mild validity loss, but our approach is more efficient.
- The concurrent preprint [2] defines score functions as $s_w(x, y)$ compared to our $\langle w, s(x, y) \rangle$. While both use Rademacher complexity to analyze validity and efficiency, [2] cannot provide implicit bounds for validity or prediction set size via subgraph theory, as we do. This highlights our unique theoretical contribution.
---
### **3. About experiments**
We conducted additional experiments on MNIST, Fashion-MNIST, and ImageNet-Val, including comparisons with the Synergy Conformal Prediction (SCP) method [3], suggested by Reviewer bRdZ. Each experiment used 2000 samples, 100 runs with different calibration/test splits (as in Table 1, Section 4.1), the APS score function, and the EFCP split method. Results show our method consistently achieves smaller prediction sets while maintaining coverage at α= 0.01 and = 0.05.
#### **MNIST**
| Method | Coverage (α=0.01) | Size (α=0.01) | Coverage (α=0.05) | Size (α=0.05) |
|-----------------------|--------------------|---------------|--------------------|---------------|
| **Ours** | 0.988 (0.005) | **1.577 (0.061)** | 0.951 (0.011) | **1.001 (0.011)** |
| SVM | 0.990 (0.005) | 2.323 (0.135) | 0.950 (0.011) | 1.033 (0.014) |
| Random Forest | 0.990 (0.005) | 2.205 (0.108) | 0.951 (0.013) | 1.181 (0.023) |
| Logistic Regression | 0.990 (0.005) | 3.695 (0.123) | 0.950 (0.012) | 1.557 (0.065) |
| SCP | 0.990 (0.005) | 1.771 (0.083) | 0.951 (0.012) | 1.018 (0.011) |
#### **Fashion-MNIST**
| Method | Coverage (α=0.01) | Size (α=0.01) | Coverage (α=0.05) | Size (α=0.05) |
|-----------------------|--------------------|---------------|--------------------|---------------|
| **Ours** | 0.988 (0.006) | **2.296 (0.108)** | 0.948 (0.012) | **1.265 (0.031)** |
| SVM | 0.991 (0.005) | 2.941 (0.156) | 0.952 (0.012) | 1.449 (0.044) |
| Random Forest | 0.990 (0.006) | 3.264 (0.187) | 0.949 (0.012) | 1.612 (0.035) |
| Logistic Regression | 0.989 (0.006) | 3.325 (0.120) | 0.949 (0.012) | 1.841 (0.050) |
| SCP | 0.991 (0.005) | 2.446 (0.100) | 0.951 (0.013) | 1.315 (0.030) |
#### **ImageNet-Val**
| Method | Coverage (α=0.01) | Size (α=0.01) | Coverage (α=0.05) | Size (α=0.05) |
|-----------------------|--------------------|---------------|--------------------|---------------|
| **Ours** | 0.989 (0.006) | **48.264 (4.019)** | 0.949 (0.013) | **6.670 (0.618)** |
| ResNet101 | 0.990 (0.005) | 53.744 (3.940) | 0.950 (0.013) | 6.798 (0.631) |
| VGG16 | 0.991 (0.005) | 100.683 (9.445) | 0.950 (0.011) | 15.149 (0.831) |
| ResNet18 | 0.990 (0.006) | 110.401 (11.694) | 0.949 (0.011) | 18.323 (1.422) |
| SCP | 0.991 (0.005) | 77.243 (5.667) | 0.950 (0.011) | 10.661 (0.630) |
---
### **References**
[1] Yang, Y., and Kuchibhotla, A. K. (2024). Selection and aggregation of conformal prediction sets. _Journal of the American Statistical Association_, 1–13.
[2] Liang, R., Zhu, W., and Barber, R. F. (2024). Conformal prediction after efficiency-oriented model selection. _arXiv preprint arXiv:2408.07066_.
[3] Gauraha, N., and Spjuth, O. (2021). Synergy conformal prediction. _Conformal and Probabilistic Prediction and Applications. PMLR_. | null | null | null | null | null | null |
Improving Multi-Class Calibration through Normalization-Aware Isotonic Techniques | Accept (poster) | Summary: This paper addresses extending isotonic regression from binary calibration to multi-class calibration. It proposes isotonic normalization-aware techniques for multi-class calibration. In particular, it introduces two techniques to account for probability normalization: (1) NA-FIR that incorporates normalization directly into the optimization process and (2) SCIR that models the problem as a cumulative bivariate isotonic regression. Experiments are conducted on several text and image classification datasets across different model architectures, showing the proposed method can improve log-likelihood (NLL) and expected calibration error (ECE) metrics.
## update after rebuttal:
The experiments on ImageNet-1k During rebuttal indeed drive me towards positive, but not upon an accept. Even though my concerns on time cost still holds, the explanation (in particular the second round) indeed drive me to positive. I decide to raise my score from 2 (weak reject) to 3 (weak accept).
Claims And Evidence: The main claim of this paper is from the empirical perspective tha "our proposed methods consistently improve both negative log-likelihood (NLL) and calibration error across diverse datasets, achieving SOTA results and reaffirming the effectiveness of IR for calibration". While this claim is indeed supported by the experiments of the paper, I have concerns on the experiments, relating to the scalability, see the details of the comments on experimental designs.
Methods And Evaluation Criteria: The proposed method and evaluation criteria is overall make sense. But it misses the experiments in comparing the efficiency of the proposed methods and the benchmark is overall small-scale (see comments on experimental designs)
Theoretical Claims: I do not think this paper provides theoretical contributions. The method is based on previous work with some intuition, and the main technical contributions are the proposed algorithms.
Experimental Designs Or Analyses: Even thought the experiments support the claims, I still have concerns on the significance. My concerns are follows:
(1) The datasets used in this paper is almost small-scale, I think this paper should conduct experiments on more larger datasets, e.g., at least conduct experiments on ImageNet-1000 datasets (there are many pre-trained models for Imagenet-1000, I do not think the computing power is the problem).
(2) This paper should conduct experiments to compare the computation cost, e.g., wall clock time, especially on the Imagenet-1000 datasets. It is important show its scalability in practice. I think TS is a very simple (efficient) and effective method for calibration (even though I am not an experts in calibration), How does the proposed method compared to TS in efficiency?
Supplementary Material: This paper does not provide Supplementary Material
Relation To Broader Scientific Literature: This paper provides clear routing how this paper builds on. I acknowledge it. However, it seems incremental overall, from the perspective of methods.
Essential References Not Discussed: I believe this paper provides essential references, even though I am not familiar to the references about calibration.
Other Strengths And Weaknesses: NA
Other Comments Or Suggestions: (1) Line 124, missing "."
(2) eqn 2, what is the meaning of "$\preceq$" ?
(3) Line 205 (right) , missing "," before "we justify...."
Questions For Authors: How does the proposed method compared to TS in efficiency? especially with the increase on the size of classes and data samples? (better provide the results on ImageNet-1000)
Ethical Review Concerns: NA
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your thoughtful review.
As you rightfully pointed out, validating our methods on larger datasets such as ImageNet-1K is important for demonstrating scalability and generality. In the last few days we have made a concentrated effort and conducted additional experiments on ImageNet-1K using [eight pre-trained models](https://github.com/huggingface/pytorch-image-models/blob/main/results/results-imagenet.csv), using the 50k validation for both calibration (25%) and test (75%).
We show here preliminary results for the calibration measures used in the paper. The results are in the same format as Table 2 in the paper, and show average rank and % best. As can be seen, for all measures except cw-ECE one of our methods NA-FIR and SCIR is best, in most cases by far. cw-ECE is not really a relevant measure with 1000 classes (see paper for definition of cw-ECE), as a vector of all zeros is likely to be best.
| Metric | NA-FIR | SCIR | FIR | IR OvR | TS | VS | MS | Uncalibrated |
|------------------|-------------|-------------|-------------|-------------|-------------|-------------|-------------|---------------|
| **Cross Entropy (NLL)** | **1.0 (100%)** | 4.9 (0%) | 2.0 (0%) | 8.0 (0%) | 3.4 (0%) | 5.1 (0%) | 5.9 (0%) | 5.8 (0%) |
| **Brier Score (BS)** | **1.2 (75%)** | 3.4 (0%) | 2.4 (0%) | 6.5 (0%) | 4.1 (12%) | 5.8 (12%) | 6.6 (0%) | 6.0 (0%) |
| **conf-ECE**| **1.4 (75%)** | 2.0 (25%) | 3.0 (0%) | 5.5 (0%) | 4.0 (0%) | 6.1 (0%) | 7.4 (0%) | 6.6 (0%) |
| **cw-ECE** | 3.6 (0%) | 6.1 (0%) | 3.1 (12%) | 4.4 (0%) | **2.0 (50%)** | 4.1 (25%) | 5.4 (12%) | 7.2 (0%) |
| **TECE** | 2.9 (12%) | **2.1 (50%)** | 2.5 (0%) | 8.0 (0%) | 5.1 (0%) | 6.4 (0%) | 6.1 (0%) | 2.9 (38%) |
Regarding runtime, we acknowledge that our methods are **less efficient** than TS or FIR on large datasets as you justly were concerned.
While both TS and FIR run in a few seconds, for the algorithms presented in the paper it takes a mean time of 120 minutes for SCIR and 16 minutes for NA-FIR with the suggested algorithm.
We would like to add additional context regarding these results:
* SCIR has a theoretical worst case time complexity of $O(m^2k^4)$ (Appendix A), and though it scales better in practice, it remains resource-intensive for 𝑘=1000 classes. For example, fitting takes around 2 minutes for cifar100 (100 classes, 5k calibration samples - see Appendix C) and for imagenet-1k it takes around 120 minutes with 30 minutes std.
* NA-FIR scales more efficiently even as k grows, since it fits a PAVA step first, significantly reducing the number of effective parameters. After applying memorization to only update bins deltas in NLL calculation, NA-FIR for imagenet-1k (1000 classes) takes ~15 minute, in comparison to 5 minutes for food101 dataset (101 classes, 6.3k calibration samples). We also discuss several ways to optimize NA-FIR in the supplemental material which can result in significant time difference (using this approach results in about a minute fitting time, but results were less stable).
While we recognize that TS remains the most efficient method and is a strong baseline, our approach offers stronger calibration under normalization constraints not addressed by previous nonparametric methods. We provide both theoretical grounding (see Section D and our response to Reviewer 1) and empirical evidence including on large scale dataset as Imagent-1k to support this claim.
Finally, in many applications, calibration sets are limited (see for example [1]), and compute overhead from calibration is minor compared to model training costs. If accepted we will include wall-clock details in the final version for transparency, thus by offering complexity analysis and strong empirical gains, we allow practitioners to weigh the pros and cons depending on their application and compute resources. We believe our methods have a place in the literature, as they offer flexible and effective alternative where calibration quality is prioritized.
We also appreciate the note on typos and will revise accordingly. Regarding the use of $\preceq$, we follow convention where it denotes partial ordering.
[1] Patel et al, Multi-class uncertainty calibration via mutual information maximization-based binning, ICLR 2021
---
Rebuttal Comment 1.1:
Comment: Thanks for the response to my comments. The authors provide the results on ImageNet-1K during rebuttal. Even though the proposed method obtain overall better performances (calibration metrics) than the baselines, I still have concerns on its scalability, due to its low efficiency. It is clear the proposed method has high computation complexity, e.g. , "While both TS and FIR run in **a few seconds**, for the algorithms presented in the paper it takes a mean time of **120 minutes** for SCIR and **16 minutes** for NA-FIR with the suggested algorithm." (It is good the authors provide the results in the rebuttal, but this results should be provided in the submission.). Besides, I am not comfort to the respond that " **If accepted** **we will include wall-clock details** in the final version for transparency, thus by offering complexity analysis and strong empirical gains". I think the submission should include the wall-clock details, no matter whether the paper is accepted. Clearly, the main contribution of this paper is the proposed method , and the authors should provide a comprehensive comparisons, including effects and efficiency (no matter merits and drawbacks).
Overall, the proposed method is not better enough, compared to the TS method (a method proposed in 2017), by trade-offing the performance and the efficiency. Besides, I do not think this paper is a theoretical paper (I do not recognize its theoretical contribution). I thus keep negative to this paper currently.
---
Reply to Comment 1.1.1:
Comment: Thank you for your response.
Regarding the phrase "If accepted," our intention was simply to indicate that submissions cannot be modified unless they are accepted. As for the ImageNet-1K results, they were included in the rebuttal since the experiments were conducted during the rebuttal phase. Additionally, as previously mentioned, reporting wall-clock time is not standard practice in the calibration literature—in fact, to our knowledge, no prior work has reported these details.
As the reviewer notes, our main contribution lies in the two proposed non-parametric methods, which are grounded in well-articulated intuitions, have clear computational complexity, and are supported by a comprehensive experimental design. We believe that the information provided enables any practitioner to fairly evaluate the strengths and limitations of our approach—and, as the reviewer has effectively illustrated through their own reasoning, to decide whether the additional computation is worthwhile for improved calibration (which, we note, remains negligible compared to training most models in this area) | Summary: The paper addresses the critical challenge of multi-class calibration in supervised learning.
While isotonic regression has proven effective for binary calibration problems, its extension to multi-class settings through one-vs-rest (OvR) calibration has historically underperformed compared to parametric methods like Temperature Scaling.
The authors identify a key limitation: traditional approaches do not inherently account for probability normalization during optimization.
The primary contributions are two novel isotonic regression techniques for multi-class calibration:
1. Normalization-Aware Flattened Isotonic Regression (NA-FIR): This method explicitly incorporates normalization into the optimization process, modifying the standard isotonic regression approach.
2. Cumulative Bivariate Isotonic Regression (SCIR): Rather than treating each class as an independent binary task, this approach redefines the problem by addressing cumulative sub-problems.
The authors demonstrate that these normalization-aware techniques consistently improve calibration performance across diverse datasets and model architectures, asserting that their approach represents a state-of-the-art non-parametric alternative in scenarios where parametric assumptions may be limiting.
The paper presents empirical evaluations on text and image classification datasets, demonstrating that the proposed approach improves negative log-likelihood (NLL) and expected calibration error (ECE) metrics.
## update after rebuttal
I keep my score - the empirical results are enough IMHO, even though *some* of them are on rather small datasets.
Claims And Evidence: The main claim of the paper is that:
> NA-FIR and SCIR (the proposed methods) improve multi-class calibration by inherently accounting for probability normalization.
To which the autors provide the following empirical evidence
* Figure 1 visually supports this claim by showing improved calibration with NA-FIR and SCIR.
* Section 5 that show improvements in NLL and ECE, which are standard metrics for evaluating calibration.
* The results are presented in Table 2, where the proposed methods generally achieve better average rankings compared to other calibration techniques.
The evidence provided includes empirical results from experiments on six benchmark datasets (CIFAR-10, CIFAR-100, Food-101, R52, NG20, and Yelp Review) using various modern deep neural network architectures and classical machine learning models.
Methods And Evaluation Criteria: NLL and ECE are two of the most accepted ways to measure calibration in machine learning.
The authors also employ variations of ECE, such as class-wise ECE (cw-ECE), thresholded equal-mass binning ECE (TECE), and confidence-calibrated ECE (conf-ECE).
The authors use traditional benchmark datasets from both image and text domains, and compare methods against several existing calibration techniques (TS, MS, VS, IR-OvR, FIR).
Theoretical Claims: The paper includes a theoretical claim in *Proposition 4.1*, which states that the cumulative sorted problem defined in Eq. (5) can be solved in $O(m^2k^4)$ using *Algorithm 2*.
The proof for the proposition, which I could not follow, is provided in Appendix A.
Experimental Designs Or Analyses: The experimental section is following the accepted practice in the field, as I mention above.
I would commend the authors for using cross-validation (line 867) which is sadly not a common practice (IMHO)
Supplementary Material: I briefly skimmed the appendix B for more results and experimental design.
As mentioned, I could not follow the proof in appendix A in the time frame I had (apologies for waiting until the review deadline)
Relation To Broader Scientific Literature: The paper effectively situates itself within the broader calibration literature.
The authors acknowledge foundational works on calibration by Murphy (1973), Murphy & Winkler (1977), and DeGroot & Fienberg (1981), establishing historical context.
More recent developments are referenced, including Platt's (1999) logistic regression-based calibration for binary predictions and subsequent extensions by Kull et al. (2017).
For neural networks specifically, the authors discuss Guo et al.'s (2017) parametric methods: Matrix Scaling, Vector Scaling, and Temperature Scaling.
In the non-parametric domain, the paper builds upon Zadrozny & Elkan's (2002) work on decomposing multi-class problems into binary subproblems and more recent contributions by Patel et al. (2020) and Zhang et al. (2020) on Flattened Isotonic Regression.
The authors identify a gap in the literature where prior work reported state-of-the-art results for unnormalized predictions, which they argue conflicts with the fundamental goal of calibration: fostering trust in reported probabilities.
Essential References Not Discussed: I could not think of a major missing reference.
Other Strengths And Weaknesses: .
Other Comments Or Suggestions: .
Questions For Authors: .
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for your thoughtful and positive review.
As far as theoretical claims we would like to also refer the reviewer to Appendix 4 where we provide a theoretically valid motivation for our isotonic approach. | Summary: he paper discusses a tweak on a post-hoc recalibration method for the multi-class classification algorithm. One of the widely used methods for post-hoc recalibration in the binary setting is the isotonic regression: given already a classification algorithm, we can consider a new regression problem where the covariates $x_i$ are now the predictions $p_i$ of the previous algorithms, and the response variables $y_i \in \{0, 1\}$ are associated with the actual distributions. The isotonic regression finds a recalibration function $g : [0, 1] \to [0,1]$ minimizing a proper-scoring loss $\mathbb{E}_i \ell(g(p), y)$ among all non-decreasing functions $g: [0,1] \to [0,1]$. As it turns out, given sample $(p_1, y_1), \ldots (p_n, y_n)$, there exist an efficient algorithm solving this minimization problem exactly, and the solution is always a piecewise constant function.
The generalization of this recalibration method to multi-class classification setting is much more tricky; now, the algorithm outputs a probability vector $p \in \Delta^k$, and we would like to provide some re-parametrization of $p$ that improves the proper loss. A method proposed previously (Patel et al. 202, Zhang et al. 2020) is to just attempt to minimize over all univariate monotone functiosn $g$ the negative log likelihood loss
$\mathbb{E} \sum_i - y_i \log( g(p(x)\_i))$, and then report the normalized $g(p\_i)/\sum\_{j} g(p\_j)$ as the final probability vector.
The authos observe that in the objective function here, the log-likelihood is calculated with respect to a vector $g(p_i)$ over $i \in [k]$ which is not necessairly contained in the probability simplex. They suggest directly minimize over monotone $g$ the desired log-likelihood
$\mathbb{E} \sum_i - y_i \log(g(p(x)_i) / \sum_j g(p(x))_j)$.
This is relatively simple and natural tweak to the idea of Patel et al and Zhang et al. Since the empirical minimization problem is not convex anymore, in contrast with the simple one-dimensional situation where the global minimum could be obtained explicitly, here it is not clear how to actually find a reasonable function $g$.
The authors tried several optimization heuristics to solve the computational problem at hand, and report the best of the attempted solutions. They ended up starting with a piecewise-constant function provided by a standard one-dimensional isotonic regression for the unnormalized problem, splitting the regions on which the function is constant into shorter sub-intervals, and applying a simulated annealing to adjust the values in each interval.
Claims And Evidence: The authors claim that their modification of the known recalibration method FIR, despite looking relatively innocent, provides a significant adventage and results in noticably better calibration than state of the art alternatives. They compared several post-hoc calibration methods on six benchmarks, with varying number of classes. For each pair of recalibration methods they showed on a heat-map percentage of the times one method achieved a better score than the other. The newly proposed NA-FIR and SCIR seems to consistently outperform other six calibration methods.
Methods And Evaluation Criteria: The author has used quite a wide set of benchmark datasets, and compared a wide range of different recalibration algorithms. They also attempted to use various heuristic to solve the specific non-convex optimization problem they used in the definition of NA-FIR~---they only present the final results for the best heuristic, but it is valuable that they mention other attempts they tried.
Theoretical Claims: There are no theoretical claims in this paper~---they provide experimental evidence for the validity of their approach.
Experimental Designs Or Analyses: Experimental design seems sound, and --- importantly, it is using a wide range of datasets coming from different sources. Specific details of all experiments, and additional metrics of calibration errors can be found in the extensive supplementary material. I did not attempt to replicate their experiments.
Supplementary Material: I reviewed briefly the supplementary material, it provides very specific details of the experimental setup, making it in principle possible to attempt to replicate their results, as well as additional benchmarks.
Relation To Broader Scientific Literature: The problems of multi-class recalibration, and in general of understanding various aspects multi-class calibration are important areas with still a large room for further discoveries. The authors propose an improvement over known methods for recalibration, while applying the isotonic regression --- preserving the monotonicity of the post-processing function $g$.
Essential References Not Discussed: I am not aware of the essential references that are missing.
Other Strengths And Weaknesses: The experimental setup in this paper is very well prepared, with a wide range of data sets, wide range of other recalibration algorithms used as comparisons, and few calibration metrics to compare those algorithms. Moreover, the supplementary material providing very specific details of how the experiments were preformed, making it quite easy to attempt potential replication.
Other Comments Or Suggestions: -
Questions For Authors: -
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for your thoughtful and positive review.
The reviewer rightfully mentions that only final results for the best heuristic are being presented, but we refer to our Appendix C and comments to Reviewer 4 where we provide more details on computational considerations for adopting our suggested methods that will be added to our final version if accepted. | Summary: This paper proposes two isotonic regression based approaches that incorporate normalization into problem formulation of multiclass calibration:
* Normalized Aware Flattened Isotonic Regression, which finds a mapping g such that g(p(x)) is normalized before computing the NLL objective.
* Sorted Cumulative Isotonic Regression, which finds a g that minimizes binary cross entropy loss on some set.
Claims And Evidence: The paper proposes two calibration methods with builtin normalization. Those methods can ensure normalized output, but my major concern is the statistical consistency. That is, assuming the assumptions are correct for the underlying distribution, there is no guarantee that the proposed algorithms will achieve the meaningful optima as measured by some proper scoring rule (or even any weaker metrics such as different forms of calibration errors). For the first method, the authors point out that it may not recover global optima because of the nonconvexity. For the second method, the algorithmic convergence is given but the statistical convergence or consistency is missing.
Methods And Evaluation Criteria: The first approach: The intuition make sense. The assumptions are strong and needs more technical discussion. See my last point in the question section.
The second approach: I find it difficult to parse the equations. For example, in Equation (5), \tilde{y} is not defined; function g is not defined (why does it take two arguments?). As such, I'm not sure if the intuition checks out for this approach.
Theoretical Claims: The authors discussed the algorithmic convergence of the second algorithm. I did not check the correctness because my major concern is in statistical concistency/convergence.
Experimental Designs Or Analyses: No.
Supplementary Material: No.
Relation To Broader Scientific Literature: N/A
Essential References Not Discussed: * Both major assumptions discussed in Section 3 have been studied before [1]. Using the concept introduced in [1], Category Independence means p \mapsto P[Y|\hat{p}(X)=p] is diagonal, and Order Preserving means \hat{g} is intra-order preserving.
* Moreover, I think Section 4 needs improvement in terms of conciseness, clarity, and organization. [1] did a better job in terms of being precise with the language.
1. Rahimi et al., Intra Order-Preserving Functions for Calibration of Multi-Class Neural Networks, NeurIPS 2020
Other Strengths And Weaknesses: Strength: the experiments cover many datasets.
Other Comments Or Suggestions: Typo:
* There's an extra "2025" in the running title at the top of each page.
* L037 right: "have highlighted the effectiveness of ”simple” para-
metric approaches": please fix the left quotation mark.
- L268 left: Use macro \log (so that it's not displayed in italics). Use \left( and \right) around the fraction as in L273.
* L273 left: NA-FIR should be wrapped in \text{} as in L268.
Questions For Authors: - L189 right: "We believe valid probability predictions are essential for building trust among practitioners, especially in decision-making frameworks, thus the only alternative offered is assuming Category Independence."
- Can you elaborate the logic implied by "thus"? I understand that ensuring valid probability predictions is equivalent to requiring the calibration function is a mapping from the simplex to itself; why does it necessarily require the Category Independence assumption to hold?
- Also this paragraph seems out of place. The "This" at the beginning of the following paragraph refers to the weakness in the previous paragraph, and I'm not clear of the goal of this paragraph.
- L197 right: "...differences that cannot be solely attributed to observed miscalibration in the intervals around the marginal predictions of 0, 0.1, 0.2."
- I don't understand what this means.
- It is well known that marginal calibration (do you mean classwise-calibration in Def 2.2?) is strictly weaker than (canonical) calibration (Def 2.1). What is the point of using an example here to illustrate this?
- L268 left: Equation (4) is a sample version of NLL. I am generally skeptical about breaking down the classes in the objective function which requires strong assumptions. Summing over the classes in Equation (4) essentially treats every class dimension of every sample is independent. This is in general not true. However, I am aware that many prior works (most notably, see Step 1 Data Ensemble of Zhang'20 mix-and-match) take this assumption. My main concern is why minimizing such a loss function will optimize the proper scoring rule, or even any weaker metrics like canonical or classwise calibration error?
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: Thank you for your thoughtful review.
The major concern is regarding statistical properties of the algorithms we propose, in particular NA-FIR. This is expressed in the review sections on Claims and Evidence, Theoretical Claims and the last point of Questions for Authors.
Regarding the statistical properties, it is important to emphasize that the NA-FIR loss function in Eq. (4) is a standard multinomial NLL (with one expression for each observation), in contrast to the loss function for previous FIR variants (Eq. (3) in our paper) which is indeed “summing over the classes” as the reviewer notes. The first implication is that the reviewer’s last comment in Questions for Authors regarding Eq. (4) is incorrect since Eq. (4) is a standard multinomial NLL. It also means that NA-FIR indeed uses a proper scoring rule for calibration (it is well known since Good (1952) that multinomial NLL or “log score” is proper), which addresses the reviewer’s statistical consistency issue. NA-FIR is non-convex (as are other calibration methods), so does not guarantee algorithmic convergence, however, the loss function is proper and statistically consistent. We will make this point more explicit in the paper’s published version, if accepted. For our second algorithm SCIR in Eq. (5), indeed the loss function is similar to FIR and “sums over the classes”. We agree that this is not ideal in terms of statistical performance, but it is common practice, as the reviewer notes.
Additional issues:
* Clarity of the SCIR (second) approach, referred in second comment under Methods and Evaluation Criteria. We emphasize that all terms in Eq. (5) are defined, although we acknowledge that the definitions can (and should) be made clearer, especially given the conceptual complexity of the SCIR approach. Specifically, $\tilde{y}$ is the cumulative label, defined via the definition of $CU_{sorted}$ and explained right after Eq. (5). The function $g$ is the optimization objective (over 2d space of cumulative probability and rank), and is implicitly defined through that.
* The first two Questions for Authors note clarity issues in the beginning of Section 4, when motivating the desired properties of multi-class calibration. We agree that the discussion in this part should be improved. Specifically to the reviewer’s comments, the word “thus” was intended to refer to other non-parametric approaches that assume category independence during calibration, and normalize predictions in the actual prediction process. The example in l197 was indeed intended to demonstrate that marginal calibration is weaker than calibration in Def. 2.1 as the reviewer notes. This was intended for readers who may not be as familiar with these notions. We will make an effort to improve clarity of this part.
* Missing reference to Rahimi et al. (2020) who define similar criteria to the ones we do in Sec. 3.3. Thank you for this reference, which is indeed relevant, and will be added to our paper and properly referenced. We note that our focus is on the algorithmic non-parametric contributions we propose, which are not related to their paper.
* Typos noted under Comments and Suggestions. Thank you for these, we will address them. | null | null | null | null | null | null |
Human Cognition-Inspired Hierarchical Fuzzy Learning Machine | Accept (poster) | Summary: The paper extracts the similarities between concepts from the human knowledge system and uses these similarities to guide the learning process. As a result, the similarities between concepts are integrated into the sample similarity, thereby improving model performance. Meanwhile, the paper guarantees the effectiveness of the proposed method through theoretical analysis.
Claims And Evidence: Yes. The claims made in the paper are supported by theoretical and experimental evidence.
Methods And Evaluation Criteria: Yes. The proposed method is effective. And the evaluation criteria can verify the advantages of the proposed method
Theoretical Claims: Yes. I checked the main theoretical results of the paper, including Theorem 3.3, 4.11-4.13, and these conclusions are correct. Meanwhile, Section 5.1 provides a toy example which validates the conclusions in Theorem 4.11,4.12 and Corollary 4.13 step by step.
Experimental Designs Or Analyses: Yes. I checked the experiments and corresponding analysis in the paper. Specifically, the experimental results in Section 5.1 are consistent with the conclusions in Corollary 4.13. Meanwhile, the experimental results in Section 5.2 indicate that by incorporating class related knowledge, the proposed method can improve the generalization performance of the model, and the higher the quality of the knowledge, the greater the performance improvement.
Supplementary Material: Yes. I mainly checked the Preliminaries and Proofs in the Appendix.
Relation To Broader Scientific Literature: The paper develops the fuzzy similarity relation-based quotient space theory and establishes the connection between fuzzy similarity relation-based quotient space theory and fuzzy equivalence relation-based quotient space theory through Theorem 4.5, which enriches the theory of fuzzy quotient space.
At the same time, the paper proposes a universal method for integrating human knowledge into the machine learning model, providing new and promising idea for developing human cognition-inspired machine learning methods.
Essential References Not Discussed: To the best of my knowledge, no important reference is missing.
Other Strengths And Weaknesses: The strengths of the paper are as follows.
1. In classification problems, each class corresponds to a concept. Unlike most existing classifiers, this paper views the classification problems as the concept cognition problems and seeks universal principles from human cognition to improve classification performance.
2. The paper develops the fuzzy similarity relation-based quotient space theory and analyses the working mechanism of the proposed method based on this theory. These theories guarantee the interpretability and effectiveness of the proposed method.
3. The experiments in the paper also verify the interpretability and effectiveness of the proposed method.
The weaknesses of the paper are as follows.
1. The paper does not discuss the difference between the proposed method and CLIP, which is the typical method to align image and text.
2. The paper does not provide a detailed explanation on how to coarsen the low-quality knowledge. Specifically, what is the definitions of f_{coa} in formula (25)?
Other Comments Or Suggestions: 1. The fonts in Figure 1, Table 1, and Figure 2 should be enlarged.
Questions For Authors: Currently, multi-modal pre-trained models, e.g., CLIP, have been proposed, which aims to align image and textual information. What is the difference between these methods and the proposed methods?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: # 0. General Response
We sincerely appreciate the reviewer’s positive feedback and valuable comments. Below, we provide a point-by-point response to each comment.
# 1. Response to “Weaknesses”
(1) CLIP (Contrastive Language-Image Pre-training) is a self-supervised learning method that learns representations of images and texts by aligning them in a shared latent space. The proposed method differs from CLIP in several aspects.
- **Learning Paradigm.** CLIP is a self-supervised learning method, whereas the proposed method follows a fully supervised learning paradigm.
- **Interpretability.** CLIP maps images and texts into a shared Euclidean space with specified dimensions and then aligns them. However, the individual dimension of this space lacks explicit semantic meaning, making the alignment process less interpretable. In contrast, the proposed method establishes alignment between the hierarchical structures derived by class knowledge and data in the quotient space. Each component in the quotient space carries a well-defined semantic meaning, leading to a interpretable alignment process.
- **Scaling Effect.** CLIP is trained on large-scale image-text pairs, enabling good performance across various downstream tasks. Similarly, the proposed method can be extended to large-scale datasets to learn more generalized representations, enhancing its ability to handle diverse downstream tasks effectively.
- **Application Scenario.** The success of CLIP is largely attributed to the widespread availability of image-text pairs on the Internet. However, in many real-world applications, acquiring large-scale data along with corresponding textual descriptions is challenging. In such cases, leveraging class knowledge to enhance the model’s ability to understand concepts becomes crucial.
(2) Formula (25) defines a class of functions, where any function satisfying the given conditions can serve as a coarsening function. This function eliminates subtle difference in the original class fuzzy similarity relation, preserving a robust and salient ranking of class similarities.
# 2. Response to “Other Comments Or Suggestions”
In the final version, we will enlarge the fonts in Figures 1, 2 and Table 2 to enhance readability and provide greater convenience for the readers.
# 3. Response to “Questions For Authors”
See item (1) in **Response to “Weaknesses”**. | Summary: In general terms, the paper presents a new and innovative method called Human Cognition-Inspired Hierarchical Fuzzy Learning Machine (HC-HFLM), which is aimed at improving interpretability and performance in classification tasks. This method is based on human cognition and takes into account the ambiguity present in real-world concepts, which cannot always be precisely defined.
## Update after rebuttal:
Thank you to the authors for their detailed responses; my doubts and questions have been resolved.
Claims And Evidence: During the development of the paper the authors demonstrate theoretically that aligning data and knowledge structures improves interpretability and performance. Furthermore, the authors present experiments on various datasets and using various classifiers for comparison. The experiments show promising results compared to traditional classifiers, suggesting that it may have potential applications in open-world learning.
Methods And Evaluation Criteria: In this paper, the methods and evaluation criteria are appropriate and well justified for the problem studied. The authors also make use of several datasets and a comparison with several classifiers to validate the effectiveness of the proposed method, however it would be beneficial to include, in addition to accuracy, an evaluation of sensitivity, precision and F1-score. Finally, it would be very interesting to discuss limitations and scenarios in which the method might not be as effective.
Theoretical Claims: The paper contains several formulations and demonstrations, which are developed in detail in the annexes. Personally I have briefly reviewed the main theoretical claims and have not found any issues. Several demonstrations are extensive and demand a detailed review, which is time limiting.
Experimental Designs Or Analyses: In relation to the evaluation of the robustness and validity of the experimental designs and analyses presented, the paper uses well known public datasets such as MNIST, APY, ImageNet1K, AWA1, AWA2, FLO and CUB. These datasets are suitable for the classification task that is studied, but it should be mentioned if any preprocessing was performed, as it may affect the results. Further, the paper compares HC-HFLM with several traditional and also deep neural network based classifiers, this provides a solid benchmark to evaluate the performance, however the variability of the results is not discussed. Additionally, the results show an improvement in generalization, however it would be useful to discuss how the method performs on noisy data to better evaluate the robustness of HC-HFLM.
Supplementary Material: The supplementary material is very extensive and due to time constraints I have not been able to review all of it, but I have partially reviewed the proofs and the details of the experiments.
Relation To Broader Scientific Literature: The paper is based on theories of cognitive science, especially focusing on the ambiguity of concepts and context dependence (Wittgenstein, 1953; Rosch, 1975). Within the context of ML, the authors expand the idea of using human cognition of concepts to improve performance, as explored in previous work (Cui and Liang, 2022) with their Fuzzy Learning Machine (FLM). In addition the paper introduces fuzzy similarity relations (FSR) to model class knowledge, based on the fuzzy set theory (Zadeh, 1965), this allows capturing the ambiguity of concepts. The proposed hierarchical alignment loss integrates this knowledge into the learning process. This extends previous work on hierarchical learning (Silla & Freitas, 2011; Wang et al., 2020). Finally the paper develops the FSR-based quotient space theory for modeling data and knowledge, this expands previous work on quotient spaces (Zhang & Zhang, 2014).
References:
Wittgenstein, L. Philosophical Investigations. Blockwell Publishing, 1953.
Rosch, E. Cognitive representations of semantic categories. Journal of Experimental Psychology: General, 104(3): 192, 1975.
Cui, J. and Liang, J. Fuzzy learning machine. In Advances in Neural Information Processing Systems, pp. 3669336705, 2022.
Zadeh, L. A. Fuzzy sets. Information and Control, 8(3): 338–353, 1965.
Silla, C. N. and Freitas, A. A. A survey of hierarchical classification across different application domains. Data Mining and Knowledge Discovery, 22:31–72, 2011.
Wang, Y., Hu, Q., Zhu, P., Li, L., Lu, B., Garibaldi, J. M., and Li, X. Deep fuzzy tree for large-scale hierarchical visual classification. IEEE Transactions on Fuzzy Systems, 28(7):1395–1406, 2020.
Zhang, L. and Zhang, B. Quotient Space Based Problem Solving: A Theoretical Foundation of Granular Computing. Tsinghua University Press, Beijing, China, 2014.
Essential References Not Discussed: The references are good but more recent work integrating structured knowledge bases into neural networks is not mentioned. For example, representation-enhanced neural knowledge integration (Liu et al., 2024) and logical neural networks for knowledge base completion with embeddings and rules (Sen et al., 2022). In addition, there is an interesting and recently published paper on hierarchical representation learning (Yu et al., 2024) which also aligns representations learned via embedding hierarchical tree structures of concepts, it would be good to include it.
References:
Liu, S., Cai, T., and Li, X. Representation-Enhanced Neural Knowledge Integration. arXiv preprint arXiv:2410.07454, 2024.
P. Sen, B. W. Carvalho, I. Abdelaziz, P. Kapanipathi, S. Roukos, and A. Gray, “Logical Neural Networks for Knowledge Base Completion with Embeddings & Rules,” in Proceedings of the 2022 Conference on Empirical Methods in Natural Language Processing, Abu Dhabi, United Arab Emirates, Dec. 2022, pp. 3863–3875.
Yu, J., Zhang, C., Hu, Z. and Ji, Y. Embedding Hierarchical Tree Structure of Concepts in Knowledge Graph Embedding. Electronics. 2024
Other Strengths And Weaknesses: Strengths:
- The methodology presented by the authors has a considerable degree of originality as it uses fuzzy similarity along with human cognition for classification.
- The paper contributes significantly to the use of fuzzy learning machine, quotient spaces and knowledge based approaches for better classification methods.
- The paper addresses a problem present in classification methods, which is to assume that classes are well defined.
- The authors present well-defined experiments on 6 datasets, showing an improvement over classical classification methods.
- The presentation of the paper is well articulated and includes demonstrations that support its formulation.
Weaknesses:
- It would be useful to discuss how the method performs with noisy data and thus better evaluate its robustness to HC-HFLM.
- It would be beneficial to include, in addition to accuracy, an evaluation of sensitivity, precision and F1-score.
- It would be very interesting to discuss limitations and scenarios in which the method might not be as effective.
- It would be useful to include details on training efficiency, computational requirements and an explicit comparison of execution time with other methods.
Other Comments Or Suggestions: - In the introduction section, near line 051, “.. employs exemplar theory to capture the typicality effects (Smith et al., 1974; Rosch, 1975)”, you should quote (Medin & Schaffer, 1978) instead of (Rosch, 1975).
- Figure 2 looks very small and misses the details, which makes it difficult to understand, it is recommended to present a larger image.
- In section 5.2, near line 371, it says “WordNet (Miller, 1995) (CK1)”, but it should read “WordNet (Miller, 1995) (CK2)”.
- In section 5.2, near line 376, it is recommended that you name the techniques instead of their abbreviations (KNN, DT, SVM and NB). They are described in the supplementary material but it would be good to write their full names when mentioning them for the first time.
- In Table 3, the symbol “--” means that it takes more than 7 days for training? Also, what does N/A mean in this context?
Questions For Authors: - The proposed method is intended for classification, but could it be expanded for other machine learning tasks?
- What are the limitations of the proposed method and under which scenarios is it not so effective?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: # 0. General Response
We thank reviewer for the appreciation of our work and valuable comments. Below, we provide a point-by-point response to each comment.
# 1. Response to “Methods And Evaluation Criteria”
(1) We add the standard deviation of accuracy for all methods based on 5-fold cross-validation, except for ImageNet1K dataset. The experimental results are as follows.
||APY|AWA1|AWA2|FLO|CUB|
|:--:|:--:|:--:|:--:|:--:|:--:|
|KNN|85.35$\pm$0.46|86.61$\pm$0.51|89.83$\pm$0.28|83.39$\pm$1.00|47.30$\pm$1.07|
|DT|63.13$\pm$0.76|63.47$\pm$0.45|70.09$\pm$0.56|42.65$\pm$0.81|21.64$\pm$1.07|
|SVM|84.54$\pm$0.55|84.26$\pm$0.56|89.06$\pm$0.12|86.56$\pm$1.26|43.89$\pm$0.74|
|NB|76.13$\pm$1.06|84.67$\pm$0.70|87.68$\pm$0.18|85.53$\pm$1.22|60.27$\pm$0.27|
|CEC|89.08$\pm$0.72|88.48$\pm$0.14|91.67$\pm$0.35|93.58$\pm$0.91|61.49$\pm$2.47|
|FLM|89.42$\pm$0.36|89.95$\pm$0.29|92.79$\pm$0.31|94.05$\pm$0.83|66.19$\pm$0.92|
|**CK$_1$-HFLM**|**90.23$\pm$0.42**|**91.10$\pm$0.28**|**93.59$\pm$0.17**|**95.06$\pm$0.65**|**68.78$\pm$0.27**|
|**CK$_2$-HFLM**|90.21$\pm$0.32|90.87$\pm$0.27|93.35$\pm$0.26|N/A|N/A|
The results demonstrate that the proposed method outperforms all compared methods and exhibits a small standard deviation, indicating the stability of the performance.
(2) For binary classification, the hierarchical structure on class space is unique. In this case, the proposed method degenerates into fuzzy learning machine, where class knowledge only guides the selection of fuzzy parameters. Additionally, when the quality of class knowledge is poor or not relevant to the task, the performance gain brought by the proposed method will be limited.
# 2. Response to “Experimental Designs Or Analyses”
(1) For fairness in comparison, the 2048-dimensional features and class description vectors used for all datasets are sourced from (Xian et al., 2019) without any additional preprocessing.
(2) See item (1) in Section 1.
(3) Due to time constraints, we conduct label noise experiments on the APY dataset. We introduce label noises with 4 different ratios, i.e., 5%, 10%, 15%, and 20%. For each ratio, label noises are added randomly and the process is repeated 5 times. The experimental results are as follows.
||5%|10%|15%|20%|
|:---:|:---:|:---:|:---:|:---:|
|KNN|85.17|84.80|84.22|83.47|
|DT|59.05|56.22|52.91|49.20|
|SVM|77.44|76.57|75.70|74.72|
|NB|75.07|74.72|74.46|74.17|
|CEC|88.81|87.42|85.79|83.94|
|FLM|88.93|86.57|85.70|85.57|
|**CK$_1$-HFLM**|**89.75**|**89.26**|**88.62**|**88.02**|
|**CK$_2$-HFLM**|89.61|89.17|88.53|87.87|
The experimental results show that as the label noise ratio increases, the proposed method experiences the least performance degradation, highlighting its robustness against the label noise.
# 3. Response to “Essential References Not Discussed”
Thank you for the important literatures. Recent methods have successfully integrated structured knowledge with neural networks for knowledge graph representation and completion task. We will add the related discussions in the final version.
# 4. Response to “Weaknesses”
(1) See item (3) in Section 2.
(2) See item (1) in Section 1.
(3) See item (2) in Section 1.
(4) We report the average time (s) for running one epoch (mean over 50 epochs) for CEC, FLM, and the proposed method. Due to challenges in utilizing GPU acceleration for the other comparison methods, their running times are not comparable. All experiments are conducted on an NVIDIA A100-PCIE-40GB GPU, and the results are as follows.
||FLO|CUB|APY|AWA1|AWA2|ImageNet1K|
|:---:|:---:|:---:|:---:|:---:|:---:|:---:|
|CEC|0.29|0.33|0.51|0.99|1.10|88.29|
|FLM|0.37|0.52|0.72|1.33|1.63|86.17|
|**CK$_1$-HFLM**|0.78|1.12|1.55|2.92|3.52|169.50|
|**CK$_2$-HFLM**|N/A|N/A|0.94|1.77|2.18|113.61|
CEC computes the loss based on single sample, while FLM calculates the loss based on sample pair, leading to a longer runtime compared to CEC. The proposed method builds on FLM by incorporating class knowledge and further refining class similarities into different levels, leading to a longer runtime than FLM. Overall, the runtime of the proposed method is approximately 2-3 times that of CEC, which remains within an acceptable range.
# 5. Response to “Other Comments Or Suggestions”
Thank you for your thoughtful correction. We will incorporate the corresponding modifications in the final version. Additionally, N/A denotes the absence of the corresponding type of knowledge for these datasets, and we will include this explanation in the main paper.
# 6. Response to “Questions For Authors”
(1) The proposed method effectively models the hierarchical structure, positioning it as a promising approach for knowledge graph representation learning. It is also applicable to structured prediction tasks, such as ranking and hierarchical classification. Additionally, it provides an interpretable solution for aligning two information sources, making it well-suited for multimodal learning tasks.
(2) See item (2) in Section 1. | Summary: The authors propose a human cognition-inspired classifier. The method first mines the fuzzy similarity relation between concepts from human knowledge system. And then the authors design the hierarchical alignment loss based on the principles of concept cognition. Using this loss, the fuzzy similarity relation between concepts guides the learning process. At the same time, the authors demonstrate that minimizing the hierarchical alignment loss can achieve hierarchical structures in class space and sample space, thereby aligning data and knowledge in the quotient space. Finally, the experiments verify the advantages of the proposed method in interpretability and improving the generalization performance.
Claims And Evidence: The claims in this paper are supported by clear and convincing evidence.
Methods And Evaluation Criteria: The proposed method makes sense for the problem at hand. So dose the evaluation criteria.
Theoretical Claims: I checked the relevant proofs. The authors provide detailed proof steps. Given these proofs, the conclusion of the paper can be verified. Meanwhile, the lower part of Figure 1 presents a clear example. As stated in the main conclusion i.e., Corollary 4.13, the hierarchical structure corresponding to data is aligned with the hierarchical structure corresponding to class knowledge.
Experimental Designs Or Analyses: The experimental results in Section 5.1 verify the theoretical conclusions in Section 4. By minimizing the proposed hierarchical alignment loss, the hierarchical structure on the training set is indeed aligned with the hierarchical structure on the class space.
Supplementary Material: I checked the Appendix, especially the details of the method and the related proofs.
Relation To Broader Scientific Literature: The proposed method achieves the alignment between hierarchical structures of data and knowledge. What's more, each component in these hierarchical structures has clear semantics, so this alignment has strong interpretability. In many practical applications, aligning data and knowledge is a common requirement. Therefore, the proposed method is expected to achieve successful applications in more scenarios.
Essential References Not Discussed: As far as I know, no key reference is missing.
Other Strengths And Weaknesses: **Strengths**
1. The proposed method is novel. The authors use cognitive science principles to guide the design of the model, improving its interpretability and providing a new solution for the development of humanoid intelligence.
2. The theoretical analysis is sound. The authors propose a new hierarchical alignment loss to align training data and class knowledge, and this loss has the theoretical guarantee in aligning data and knowledge.
3. The experimental results are sufficient. The authors not only provide an example of hierarchical alignment in the quotient space, but also verify the effectiveness of the proposed method on the public datasets.
**Weaknesses**
1. The authors develop the fuzzy similarity relation-based quotient space theories. In order to help readers understand the thought process of the paper, the connection between these new theories and existing quotient space theories as well as the process of developing these new theories should be further discussed.
Other Comments Or Suggestions: 1. In order to make readers better follow the idea of the paper, some content in the Appendix should be adjusted to the main text, especially the relevant processing procedures involved in formulas (5) and (6).
2. The font in Figures 1 and 2 should be enlarged. The same issue also appears in Figure 3 of the Appendix.
Questions For Authors: As stated in the paper, the fuzzy learning machine also solves the classification problems from the view of concept cognition. Why can the proposed method significantly improve the performance of the fuzzy learning machine?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: # 0. General Response
We thank reviewer for the appreciation of our work and valuable comments. Below, we provide a point-by-point response to each comment.
# 1. Response to “Weakness”
- The fuzzy equivalence relation (FER) is a more restrictive form of the fuzzy similarity relation (FSR).
In practical applications, obtaining the FER is generally more challenging than obtaining the FSR.
Therefore, we employ the FSR to model class knowledge and sample similarity.
- The existing fuzzy quotient space theory is based on the FER and is therefore not suitable for analyzing the method proposed. In response, we develop a quotient space theory based on the FSR.
- **Theorem** 4.5 establishes the connection between the quotient spaces derived by FSR and FER, which allows the existing
theoretical results in FER-based quotient space to be extended to FSR-based quotient space.
We will incorporate the above content in the final version.
# 2. Response to “Other Comments Or Suggestions”
1. In the final version, we will incorporate the relevant content into the main paper to improve the overall coherence and readability.
2. In the final version, we will enlarge the figures in this paper to enhance readability and provide greater convenience for the readers.
# 3. Response to “Questions For Authors”
Unlike fuzzy learning machine, the proposed method further incorporates the class knowledge contained in human knowledge system into the sample fuzzy similarity relation. As a result, the proposed method enhances the model's understanding of concepts, leading to the performance gain. | Summary: This paper advocates solving classification problems from the perspective of concept cognition. Inspired by human cognition, this paper utilizes the relationships between concepts embedded in the human knowledge system to guide the learning process. This deepens the model's understanding of concepts. In addition, this paper develops the fuzzy similarity relation-based quotient space theory and then analyses the working mechanism of the proposed method. Meanwhile, the experimental results demonstrate that the proposed method can improve the generalization performance by incorporating human knowledge system.
Claims And Evidence: The main claims in this paper are supported by theoretical analysis.
Methods And Evaluation Criteria: The proposed method is effective for aligning data and class knowledge and then improving the generalization performance.
Theoretical Claims: I have checked the main conclusion, i.e. Corollary 4.13. The relevant proof process should be correct. Meanwhile, Figure 2 in Section 5.1 provides a typical example of this conclusion.
Experimental Designs Or Analyses: The experimental results in Section 5.2 demonstrate that the proposed method can deepen the model's understanding of concepts by incorporating human knowledge system, thereby improving the model's testing accuracy.
Supplementary Material: I have checked the details of relevant proofs and experiments in the Appendix.
Relation To Broader Scientific Literature: Many practical problems can be abstracted as aligning two pieces of information from different sources. Most existing methods achieve the alignment in Euclidean space. Unlike it, this paper achieves the alignment of two pieces of information in quotient space, and this alignment has clear semantics and strong interpretability. Therefore, the proposed method provides a new promising approach for aligning information from different sources.
Essential References Not Discussed: The references are complete and sufficient for understanding this paper.
Other Strengths And Weaknesses: Strengths:
1. In human cognition, there are rich relationships between concepts. Inspired by this, this paper integrates these relationships between concepts contained in human knowledge into the model, which improves the interpretability and generalization performance. It provides a new inspiring way to develop human cognition-inspired machine learning methods.
2. This paper has a solid theoretical analysis, which guarantees the effectiveness of the proposed method.
3. The proposed method models different types of knowledge as fuzzy similarity relation on class space, which has good universality.
Weaknesses:
1. In formula (9), the specific form of regularization term R (\Theta) and the value of the hyper-parameter \gamma are not given, which affects the reproducibility of the experiments.
Other Comments Or Suggestions: In order to enhance the readability of this paper, some content in the Appendix should be placed in the main text, such as the definition of “finer” and “coarser”, and the definition of “cut-relation”, etc.
Questions For Authors: Section 5.2 adopts fully connected networks as the backbone network for the deep neural network methods, the fuzzy learning machine, and the proposed method. As is known to all, the fully connected network is the simplest network structure. Why not
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: # 0. General Response
We sincerely appreciate the reviewer’s positive feedback and valuable comments. Below, we provide a point-by-point response to each comment.
# 1. Response to “Weakness”
- In the experiments, to directly highlight the performance improvement achieved by incorporating class knowledge contained in human knowledge system, the proposed method does not include the regularization term.
- In practical applications, appropriate regularization term can be introduced based on domain knowledge, which is expected to further enhance performance.
# 2. Response to “Other Comments Or Suggestions”
To improve the overall coherence and readability, we will incorporate the relevant content into the main paper in the final version.
# 3. Response to “Questions For Authors”
The primary goal of the experiments is to demonstrate that the proposed method improves model performance by incorporating the class knowledge contained in human knowledge system rather than merely aiming for higher accuracy. As the reviewer pointed out, employing more complex and advanced neural networks could potentially yield better accuracy. However, the subject lies beyond the scope of this paper. | null | null | null | null | null | null |
Scaling Off-Policy Reinforcement Learning with Batch and Weight Normalization | Reject | Summary: The paper discusses the failure of a previously proposed DRL algorithm, CrossQ, to reliably scale up to more complex environments than those considered in the original paper. To achieve this, the authors propose to use weight normalization.
### Update after rebuttal period
With additional context, I support the acceptance of this paper. All major questions were adequately addressed.
Claims And Evidence: The claims made in the paper are backed up with a standard set of experiments on DMC and MyoSuite (two environments where CrossQ previously failed to achieve reliable returns). As the main goal of the paper was to solve this issue, the evidence matches the claims.
Methods And Evaluation Criteria: The chosen method and evaluation is standard and applicable.
Theoretical Claims: No new theoretical claims are presented. Theorems used in the work are from prior literature. Overall, I would encourage the authors to connect the presented theory more closely with the results in the paper. As it stands, I am not fully sure how scale invariance helps the architecture.
Experimental Designs Or Analyses: The experimental design is standard. As a minor nitpick, BRO and CrossQ are evaluated with differing action repeat values, which has recently been shown to impact the performance of model-free methods massively [1]. It would be good to account for this design choice. ("The official BRO codebase is also based on jaxrl, and the authors followed the same evaluation protocol, making it a fair comparison." is therefore also technically an incorrect claim)
For easier comparison, it would be nice to have the plots in Figure 5 include the baselines.
Supplementary Material: Yes, briefly. The supplementary material presents additional experiments and implementation details.
Relation To Broader Scientific Literature: The paper is somewhat incremental, but still has some value for the community. It essentially combines the insights from CrossQ with the current literature which focuses on the impact of LayerNorm and other approaches.
Essential References Not Discussed: Note that MAD-TD is a very recent paper, and so I do not consider it an essential reference and do not account for it in my score. However, it influenced the questions I asked so I am listing it here.
[1] MAD-TD: MODEL-AUGMENTED DATA STABILIZES HIGH UPDATE RATIO RL, Voelcker, C. et al., ICLR 2025
[2] TD-MPC2: Scalable, Robust World Models for Continuous Control, Hansen, N., ICLR 2024
Other Strengths And Weaknesses: Overall the paper is very readable, kudos!
Other Comments Or Suggestions: n/a
Questions For Authors: The premise creates several questions which I would encourage the authors to discuss in more detail:
1) Why was WeightNorm specifically chosen to improve CrossQ? Could other proposals, such as Unit Sphere Normalization which was referenced in the paper also work?
2) What is the relative relevance of the CrossQ part of the architecture? Is weightnorm alone sufficient for strong performance, and if not, why not?
3) In an additional vein, why is BatchNorm useful for avoiding the reset strategy employed by BRO? Do additional resets give CrossQ any benefits? Other recent works, such as [1] (see below) have argued that deteriorating performance corresponds to out-of-distribution actions in off-policy learning, would such a hypothesis fit with the evidence presented here?
4) How does CrossQ perform compared to model-based approaches such as [1] and [2]?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We thank the reviewer for their review and positive feedback, as well as the additional questions. We will extend the paper with discussions, additional experiments for each question, and mentioned baselines and feedback. To answer them here:
- **Could Unit Sphere Normalization work (instead of the proposed WN)?** We need to differentiate between normalizing the features and normalizing the weights. The proposed Unit Sphere Normalization in Hussing et. al 2024, is with respect to the output features of the penultimate layer. In CrossQ + WN we use BN to normalize the intermediate features in the entire network and we normalize the network parameters with WN. We write that we ensure the "weights remain unit norm after each gradient step by projecting them onto the unit ball”, i.e. Unit Sphere Normalization. In the future, it would of course be very interesting to investigate using Unit Sphere Normalization instead of BN on the features.
We will update the paper to make these details much more clear to the reader.
- **What is the relative relevance of the CrossQ part.** In our response to reviewer `7a29` , we have added a SAC + LN + WN ablation. As SAC + BN does not work (finding of the CrossQ authors) and LN provides the same scale invariance, this is an interesting comparison. We refer the reviewer to our above answer to reviewer `7a29`.
- **Do additional resets give CrossQ + WN any benefits.** In our rebuttal to reviewer `7a29` we ran additional scaling experiments with increasing UTDs and CrossQ + WN + Resets on the Dog&Humanoid as well as the Myo Suite hard tasks (https://imgur.com/a/QPVuFfT). The only slight improvement is for Myo at UTD=5. How beneficial additional resets can be requires further experimentation which we will strongly consider for the camera ready version. However, the main take away is that ***Resetting is not required*** to train stably at higher UTD ratios with CrossQ + WN on the studied task suites.
- **Comparison to Model-based (TD-MPC2).** In the above plot we provide TD-MPC2 results (based on the official data provided by the authors). We can see, that CrossQ + WN outperforms TD-MPC2 on the provided tasks. However, a full and in depth comparison to more model-based approaches is an interesting future direction.
---
Rebuttal Comment 1.1:
Comment: Thanks for the additional clarifications. I'm happy to increase my score | Summary: The paper studies the scaling property of a previously proposed RL method, CrossQ, with high update-to-data ratio. CrossQ does not use target network updates and is known to be brittle to tune as also shown by the authors. The paper proposes to stabilize the training dynamics of CrossQ using weight normalization (in addition to the batch normalization that is already deployed in CrossQ) and adding back the target network updates. On the DeepMind Control Suite and Myosuite benchmark, the proposed CrossQ+WN is able to match BRO with 90% fewer parameters and does not need to periodically perform network resets.
Claims And Evidence: I mainly find the following claim to be problematic: "Our proposed approach reliably scales with increasing UTD ratios".
- Figure 4 fails to show the performance scaling with increasing UTD ratios (see "experimental designs or analyses")
- The authors only test the proposed method on three UTDs (UTD=1, UTD=2, UTD=5). UTD=5 is not a very high update-to-ratio value. I find it hard to be convinced that the proposed approach can scale to higher UTDs without further evidence.
Since this claim is central to the contribution of the paper, it is a critical weakness of the paper.
Methods And Evaluation Criteria: High update-to-data ratio is known to cause RL training instability. Normalization and regularization are well-known to be helpful in stabilizing RL and especially online RL training dynamics. While it is not surprising that the proposed weight normalization improves RL training stability, the proposed methods make sense and the benchmarks are challenging enough to showcase the effectiveness of the approach.
Theoretical Claims: There is no new theory in the paper. Both theorems in the paper are from prior work.
Experimental Designs Or Analyses: Figure 4 – “The sample efficiency scales reliably with increasing UTD ratios.” – in the graph three UTD ratios (1, 2, and 5) perform very similarly (with overlapping confidence intervals). It is unclear if the stated conclusion can be drawn from the plot itself.
The rest of the experimental designs and analyses are all sound and valid.
Supplementary Material: No.
Relation To Broader Scientific Literature: The paper presents a practical and simple method to improve the stability of CrossQ. In the field of sample efficient online RL, how to properly scale RL agents with high update-to-data ratio is an open question and one of the most commonly used tricks is to periodically reset the network to restore the plasticity of the agent. It is an effective yet unsatisfying approach as it forces the RL agent to unlearn before it relearns it better. The paper takes a step towards developing simple RL algorithms that can scale with the update-to-data ratio without the need of periodic resets.
Essential References Not Discussed: No.
Other Strengths And Weaknesses: Strengths:
- The idea is simple and the experimental results are convincing.
- The paper is easy to follow and the writing is clear.
Weaknesses:
- The paper lacks depth (especially since the method is very simple). More experiments on how weight normalization interacts with different network sizes, network architectures, initialization and target updates would be much more helpful for RL practitioners (e.g., know when WN is helpful).
- There are many other regularization techniques such as dropout, weight decay, layer normalization that could also be interesting to study. How do they interact with CrossQ?
- UTD=5 is not a very high update-to-ratio value. I find it hard to be convinced that the proposed approach can scale to higher UTDs without empirical evidence. For example, it would be helpful to show the experiments on higher UTDs (UTD>20), which is what has been studied in many prior works such as RedQ (UTD=20), DroQ (UTD=20), and prior works that use resets (UTD=32).
*References for papers that study high UTDs:*
- [RedQ] Chen, Xinyue, et al. "Randomized ensembled double q-learning: Learning fast without a model." arXiv preprint arXiv:2101.05982 (2021).
- [DroQ] Hiraoka, Takuya, et al. "Dropout q-functions for doubly efficient reinforcement learning." arXiv preprint arXiv:2110.02034 (2021).
- [Resets I] Nikishin, Evgenii, et al. "The primacy bias in deep reinforcement learning." International conference on machine learning. PMLR, 2022.
- [Resets II] D'Oro, Pierluca, et al. "Sample-efficient reinforcement learning by breaking the replay ratio barrier." Deep Reinforcement Learning Workshop NeurIPS 2022. 2022.
Other Comments Or Suggestions: N/A
Questions For Authors: N/A
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank the reviewer for their thorough and extensive review. We were happy to read that they found our experimental results convincing. We hope that our rebuttal manages to address their remaining concerns and open questions. We ran many additional experiments and ablations for the rebuttal, for which we provide anonymized URLs below.
****
**Scaling Claim.** To investigate the scaling behavior of CrossQ + WN, we ran additional experiments for UTD={10,20} and present the scaling behavior in Figure (https://imgur.com/a/QPVuFfT). In this Figure, we focus on the final performance at 1M steps, which is common practice among the baselines.
We observe three things:
1. CrossQ + WN **scales with increasing UTD** ratios, and plateaus on the provided tasks after UTD > 5. In general, we argue that the fact that the method plateaus at some point could be expected.
2. CrossQ + WN **remains stable for larger UTD ratios**, i.e. there are no performance drops (like the ones vanilla CrossQ suffers from).
3. CrossQ + WN **performance is competitive** with all other baselines that we provide here. Especially on the challening Myo Hard tasks. This includes approaches with much larger network architecutes (BRO, Simba), model-based approaches (TD-MPC2) and resetting (BRO, CrossQ + WN + Reset). CrossQ + WN is a relatively simple algorithm in comparison. The integration of other implementation details and ideas from the baselines could be interesting for future work to scale even further.
We believe, under those aspects, the phrasing “reliably scales with increasing UTD ratios” is justified. However, if the reviewers still disagree, we are open to suggestions for different phrases.
**Depth of the Analysis.** We agree with the reviewer's point and appreciate the many suggestions. In the limited rebuttal time, we have attempted to perform as many additional ablations and investigations as we could. We focused on
- higher UTDs and scaling behavior
- Metrics and analysis on the effectiveness of WN and why/how WN improves learning (see response to reviewer WbYM for details and Figures (https://imgur.com/a/o1ngeJD) and (https://imgur.com/a/bOnagfB))
- Ablations on **weight decay** and **layer normalization**. Figure (https://imgur.com/a/SRgUd0D) shows additional ablations, where we used L2 regularization with varying coefficients instead of WN (please refer to our answer to reviewer `WbYM`, where we analyze the results in detail). We can see that while L2 regularization can improve the performance of vanilla CrossQ, it requires tuning the penalty coefficient per task suite, and overall performance is significantly worse than CrossQ + WN.
While this deserves more investigation, we believe that WN is the more elegant solution since it does not require tuning and does not introduce additional hyperparameters. Moreover, we hypothesize that the constant parameter norm achieved through WN is more desirable.
To investigate LN, we ran SAC + LN + WN experiments (since CrossQ does not work with LN according to the original authors). We find that SAC + LN + WN does not manage to reach the performance of CrossQ + WN.
In the future, we plan to run additional ablations and experiments on network architectures, target updates and initialisations as suggested.
---
Rebuttal Comment 1.1:
Comment: Thanks for the additional experiments. The new results convinced me the effectiveness of CrossQ+WN and made the paper stronger. I will increase my score from 2 to 3. | Summary: This paper enhances the sample efficiency of reinforcement learning (RL) by improving CrossQ, a model-free algorithm that leverages Batch Normalization (BN). While CrossQ excelled at low update-to-data (UTD) ratios, it struggled to scale reliably. The authors found that scaling the UTD ratio in CrossQ leads to a sharp increase in weight norm, which destabilizes training. To address this, they incorporate Weight Normalization (WN), which mitigates this effect, stabilizes training and enables effective scaling to higher UTD values. Experiments on DeepMind Control and MyoSuite show that CrossQ + WN significantly improves stability and sample efficiency, providing a simple yet effective enhancement to state-of-the-art RL methods.
Claims And Evidence: The paper claims that Weight Normalization (WN) stabilizes CrossQ at high update-to-data (UTD) ratios, but the evidence is incomplete:
1. Stabilization of Weight Norm: The authors do not show whether WN effectively regulates weight norms across layers. Tracking weight norm dynamics throughout training would strengthen this claim.
2. Why WN Improves Performance: The authors attribute performance gains to a more stable effective learning rate, referencing prior work by Lyle. However, they do not explicitly demonstrate that combining WN and Batch Normalization (BN) results in a consistent effective learning rate. Further, other plasticity measures, such as dormant neurons or feature rank, are not discussed. These aspects could provide a more comprehensive explanation of why WN improves CrossQ's performance.
Methods And Evaluation Criteria: 1. The rationale for using Weight Normalization (WN) over standard L2 regularization is not well justified. While the authors argue that increasing weight norms can be harmful, they do not explain why L2 regularization alone is insufficient across layers. Additionally, the decision to project the layer before Batch Normalization (BN) rather than applying L2 regularization directly lacks clear motivation. A comparison of CrossQ + WN against varying strengths of L2 regularization would help clarify whether WN offers a distinct advantage.
2. Furthermore, while the authors evaluate CrossQ + WN on DeepMind Control (DMC) and MyoSuite, they do not compare it to CrossQ in MuJoCo, where the original CrossQ paper demonstrated strong performance. Including this comparison would provide a more complete assessment of WN’s impact across different environments.
Theoretical Claims: I've checked a proof of invariance in the Appendix.
Experimental Designs Or Analyses: 1. Unclear Mechanism Behind Performance Gains: The authors attribute improvements to a more stable effective learning rate, citing Lyle, but do not demonstrate that combining WN and Batch Normalization (BN) ensures this stability. Other plasticity measures, such as dormant neurons or feature rank, are also unexplored, leaving the underlying mechanism unclear.
2. Visualization Issues: The current visualizations make it difficult to compare methods. A bar chart for each domain would improve clarity when comparing performance against baselines.
3. Limited Baselines: The paper does not compare CrossQ + WN to other relevant baselines like TD-MPC2, SimBa, or Mr.Q. While this is a minor concern, including at least one of these baselines—if computationally feasible—would strengthen the evaluation.
Supplementary Material: Yes. Reviewed all sections.
Relation To Broader Scientific Literature: Improving sample efficiency is a key concern in robotics, where data collection is costly and constrained by real-world limitations.
Essential References Not Discussed: The paper lacks a discussion of key works on scaling and sample efficiency in deep RL.
1. Data-Efficient Reinforcement Learning with Self-Predictive Representations, ICLR’21.
2. Towards Deeper Deep Reinforcement Learning with Spectral Normalization, NeurIPS’21.
3. Mastering Diverse Domains through World Models, arXiv’23.
4. Bigger, Better, Faster: Human-level Atari with human-level efficiency, ICML’23.
5. PLASTIC: Improving Input and Label Plasticity for Sample Efficient Reinforcement Learning, NeurIPS’23.
6. TD-MPC2:Scalable, Robust World Models for Continuous Control, ICLR’24.
7. Mixtures of Experts Unlock Parameter Scaling for Deep RL, ICML’24.
8. Overestimation, Overfitting, and Plasticity in Actor-Critic: the Bitter Lesson of Reinforcement Learning, ICML’24.
9. SimBa: Simplicity Bias for Scaling Up Parameters in Deep Reinforcement Learning, ICLR’25.
10. Towards General-Purpose Model-Free Reinforcement Learning, ICLR’25.
11. MAD-TD: Model-Augmented Data stabilizes High Update Ratio RL, ICLR’25.
Other Strengths And Weaknesses: n/a
Other Comments Or Suggestions: I appreciate the idea and direction, but the paper needs more completeness. Strengthening connections to related work, providing a deeper analysis of Weight Normalization’s effects, and offering a more thorough comparison with existing methods would improve its clarity and impact. I am open to increasing my score if these concerns are well addressed.
Questions For Authors: n/a
Ethical Review Concerns: n/a
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank the reviewer for their thorough and extensive review. We were happy to read that they appreciate the idea and direction of our work and are open to increasing the score. We hope that our rebuttal manages to address their concerns and open questions. We ran many additional experiments and ablations for the rebuttal, for which we provide anonymized URLs below.
****
**Deeper Analysis of Weight Normalization’s Effects.** Our rebuttal focuses on showing scaling behavior, the effective regularization of weight norms, additional plasticity metrics, and ablations with L2 regularizations.
The results are aggregated per domain and over 10 seeds per environment. Due to restricted computing resources and the limited rebuttal period, we focused on the hard tasks, which total 12 environments (Dog&Humanoid for DMC and the “-hard” environments for Myo Suite).
- **Effectiveness across layers.** Figure (https://imgur.com/a/o1ngeJD) shows per-layer parameter norms during training. We can see the effectiveness of CrossQ + WN in keeping parameter norms on the intermediate layers (0,1) constant and reasonable parameter norms on the output layer (2) (which is not normalized).
On the contrary, vanilla CrossQ shows growing parameter norms on the intermediate layers. This is strongly emphasized by increasing the UTD.
- **Why WN Improves Performance.** The following Figure (https://imgur.com/a/bOnagfB) shows, the suggested metrics to measure plasticity. We can see, that feature and parameters norms grow drastically for vanilla CrossQ. The addition of WN mitigates that growth entirely. Due to the squared Bellmann error objective, the gradient norms are (as to be expected) visibly correlated with the Q values. The ELR remains on a constant, suitable level for CrossQ + WN and stable across training. For vanilla CrossQ, the ELR is significantly smaller and near zero (which supports our hypothesis), which can be linked to the much larger and growing parameter norms. Dead / Dormant Neurons are not an issue in either case, with less that 2% and less than 0.5% respectively.
- **"Why WN projection before BN?”**
WN is not part of the network architecture, i.e. not part of the forward pass. As such, the projection does not happen “before BN”. Rather, after each gradient step, we rescale the weights (WN) to unit norm. Theorems 4.1 and 4.2, justify this, since (thanks to BN) the network is scale invariant with respect to the parameter norms. While the rescaling does not influence the predictions, the benefit of such a rescaling operation is that the ELR is kept constant (since the magnitude of the weights stays constant).
- **Why WN over L2?** L2 regularization penalizes growing weights and introduces a bias towards a smaller ELR. However, attempting to control the weight magnitude through an L2 penalty term does not guarantee a certain weight magnitude and usually requires tuning (maybe even scheduling over time). To investigate, we ran additional ablations, where we used L2 instead of WN to confirm the above hypotheses in Figure (https://imgur.com/a/SRgUd0D).
We can see that while L2 regularization can improve performance in combination with CrossQ, tuning the penalty coefficient per task suite is required, however. Overall performance is significantly worse than CrossQ + WN.
While this deserves more investigation, we believe that WN is the more elegant solution since it does not require tuning and does not introduce additional hyperparameters. Moreover, we hypothesize that the constant parameter norm achieved by WN is more desirable.
**Visual Clarity.** We improve the visual clarity of our results by providing per-domain bar charts, as suggested (https://imgur.com/a/p4BZVVP). For comparison, we have included results for TD-MPC2 and Simba (we used the official results provided by the authors).
**Strengthen connections to related work.** We thank the reviewer for the list of additional references. We will make sure to discuss all the provided references in order to position our work better within the related literature. | Summary: The paper proposes an enhancement to the CrossQ reinforcement learning framework by integrating weight normalization (WN) with the existing batch normalization (BN) approach. The primary goal is to stabilize training when using higher update-to-data (UTD) ratios, which are typically associated with improved sample efficiency but can lead to training instabilities. The algorithm reintroduces target networks, which were removed from CrossQ and was considered as a positive effect. The paper demonstrates that by controlling the growth of network weight norms through WN, the modified algorithm---referred to as CrossQ + WN---can scale with increasing UTD ratios. The paper presents empirical results on DeepMind Control Suite and Myosuite benchmarks, comparing against baselines.
Claims And Evidence: Claim: Integrating weight normalization (WN) into CrossQ improves training stability and scalability with higher UTD ratios.
Evidence: Experiments and ablation studies on DeepMind Control Suite and Myosuite benchmarks show that WN controls network weight norm growth and enables stable learning across varying UTD ratios.
Methods And Evaluation Criteria: The methods and evaluation criteria are largely appropriate for continuous control tasks. However, the overlapping confidence intervals make it difficult to draw clear conclusions about the benefits of increased UTD ratios or the addition of WN. Ideally, the study would benefit from either running more random seeds to achieve tighter confidence intervals or designing controlled experiments that isolate the effects of these modifications. Additionally, expanding the evaluation to include discrete control tasks, vision-based tasks, or environments with inherent stochasticity would provide a more comprehensive assessment of the method’s applicability and robustness.
Theoretical Claims: None
Experimental Designs Or Analyses: Mentioned above in Methods and Evaluation Criteria.
Supplementary Material: Did not go through the supplementary material.
Relation To Broader Scientific Literature: There exists paper and methods which don't rely on reusing data and still perform as well as the state of the art. The work fits into the broader domain of continuous control tasks
Elsayed, M., Vasan, G., & Mahmood, A. R. (2024). Streaming deep reinforcement learning finally works. arXiv preprint arXiv:2410.14606.
Vasan, G., Elsayed, M., Azimi, S. A., He, J., Shahriar, F., Bellinger, C., White, M., & Mahmood, A. R. (2024). Deep policy gradient methods without batch updates, target networks, or replay buffers. In The Thirty-eighth Annual Conference on Neural Information Processing Systems (NeurIPS).
Essential References Not Discussed: Elsayed, M., Vasan, G., & Mahmood, A. R. (2024). Streaming deep reinforcement learning finally works. arXiv preprint arXiv:2410.14606.
Vasan, G., Elsayed, M., Azimi, S. A., He, J., Shahriar, F., Bellinger, C., White, M., & Mahmood, A. R. (2024). Deep policy gradient methods without batch updates, target networks, or replay buffers. In The Thirty-eighth Annual Conference on Neural Information Processing Systems (NeurIPS).
The above works show that you can make continuous control work without using a replay buffer and introduced similar normalization, the paper doesn't compare to the above method.
Other Strengths And Weaknesses: Strength: The paper is simple and easy to read.
Weaknesses: CrossQ is an algorithm and the paper seems to be improving on it, rather than talking about simply improving algorithms for contrinous control, there exists methods which implements similar heuristics and have not been compared against, referenced below, comparing performance against these would be essential to understand if most of the normalization provided in them are simply enough to offer good sample efficiency.
Also, better empirical evaluation is required to support the claims made in the paper.
**References:**
Elsayed, M., Vasan, G., & Mahmood, A. R. (2024). Streaming deep reinforcement learning finally works. arXiv preprint arXiv:2410.14606.
Vasan, G., Elsayed, M., Azimi, S. A., He, J., Shahriar, F., Bellinger, C., White, M., & Mahmood, A. R. (2024). Deep policy gradient methods without batch updates, target networks, or replay buffers. In The Thirty-eighth Annual Conference on Neural Information Processing Systems (NeurIPS).
Other Comments Or Suggestions: Line 106 (left col): $\pi^\star = \arg\max_\pi \mathbb{E}_{s\sim\mu_0} [ \sum_a \pi(s,a) Q^\pi(s,a)]$.
Questions For Authors: I have two concerns:
1. Number of random seeds for evaluation because of overlapping CIs.
2. Comparison to existing streaming RL methods.
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: We thank the reviewer for their thorough review and questions. We were especially pleased that they acknowledged the appropriateness of our methods and evaluation criteria and that they found the paper easy to read.
In the following, we want to address the reviewer’s three main concerns individually: empirical evaluation, comparison to streaming RL methods, and the extension to other domains. We ran many additional experiments and ablations for the rebuttal, for which we provide anonymized URLs below.
****
**Empirical Evaluation.**
For CrossQ + WN, Figure 1. shows a clear improvement from UTD 1 to 5 on all task suites. The improvement gap and confidence intervals are approximately the same as between BRO UTD=2 and UTD=5. More importantly, the improvement over vanilla CrossQ is significant, and the overall performance is competitive to BRO (while CrossQ + WN is algorithmically much simpler with 90% fewer parameters).
We believe that our empirical results are quite strong and extensive. We present experiments across 25 continuous control tasks with 10 random seeds each, which aligns with BRO and Simba. While we agree that more seeds can reduce evaluation noise, we believe this setting is a good tradeoff for the required compute resources. However, we will increase the number of random seeds for the camera-ready version, should the reviewer insist.
We agree that Figure 4. can be visually improved and does not bring the point of scaling across that well. To that end, we have run experiments with higher UTD ratios (10,20) and created a new Figure (https://imgur.com/a/QPVuFfT) that presents the scaling behaviors with respect to final performance (at 1M timesteps), as is common practice in other works (BRO, Simba). It shows
- a substantial improvement over vanilla CrossQ (which shows dropping performance with higher UTDs)
- CrossQ + WN is competitive to all baselines for varying UTDs, scales initially and stably plateaus on the provided tasks.
- Adding periodic resetting can slightly help in Myo Hard, but does not help on DMC. Overall, this can be investigated more. However, the main takeaway is that CrossQ + WN does not require resetting in order to scale stably.
> the overlapping confidence intervals make it difficult to draw clear conclusions about the benefits […] the addition of WN
>
We disagree with this statement and point the reviewer to Figure 1, which clearly shows that the addition of WN enables CrossQ to scale. Without WN, CrossQ shows worse performance with increasing UTDs. The benefits of higher UTDs are especially pronounced on the Hard tasks (Dog&Humaoid, Myo Hard), where the baselines take more time to learn.
****
**Comparison to existing streaming RL methods.**
We thank the reviewer for the references and believe it is interesting to discuss the relation to these works in the related work section. As such, we will integrate them into our discussion. We view these references as *concurrent work* in accordance with the ICML reviewing guidelines.
Further, while the removal of replay buffers is interesting, it is out of the scope for this work where we focus on sample efficiency. The provided streaming RL approaches use on the order of 10M samples to learning the dog environments (compared to <1M for the algorithms we consider in this work).
****
**Extension to different tasks.**
We agree that the extension to discrete control tasks and vision-based tasks would be an interesting study. Given the number of experiments and evaluations in our current draft, and the variaous experiments we added during the rebuttal, we believe this deserves a separate study and would leave this investigation for future work.
We want to note that while we do not provide experiments with stochastic dynamics yet, the Myo Suite hard tasks do have inherent stochasticity. In these tasks, goals and initial conditions are randomized.
---
Rebuttal Comment 1.1:
Comment: ### Motivation for the Paper:
The title Scaling Off-Policy Reinforcement Learning with Batch and Weight Normalization suggests a general scalability improvement across off-policy RL methods. However, the paper only investigates the effect of weight normalization on the specific algorithm, CrossQ. I believe the title and framing should more accurately reflect that the work demonstrates an improvement over a particular algorithm rather than implying broad scalability across diverse methods. Typically, "scaling" implies the ability to handle more complex problems with increased compute/time, which is not clearly demonstrated here.
### Empirical Evaluation:
**Improvement of CrossQ + WN**:
The goal is to provide a better algorithm, but Figure 1 shows significant overlap between BRO and CrossQ. The choice of UTD ratios from 1 to 5 appears too narrow, and the presented new figures---even when suggesting that BRO might be more scalable with higher UTD---lack sufficient error bars.
**Statistical Robustness**:
As an empirical study, this work would benefit from proper statistical analyses with an increased number of seeds. I would be happy to see more seeds included, but I cannot improve my score until I see such improvements. In Figure 4, which examines scaling with respect to UTD, the overlapping standard errors across all UTD values make it unclear if the method truly improves performance.
While I am open to not testing on additional tasks (and understand concurrence), I remain unconvinced by the current set of results without stronger statistical validation. If compute constraints are an issue, performing these ablations on simpler environments might help clarify the benefits of the approach.
I hope these comments help refine the paper
---
Reply to Comment 1.1.1:
Comment: We thank the reviewer for their comments and want to provide some additional comments and clarifications.
> the *overlapping standard errors* […].
>
There seems to be a misunderstanding. To clarify, we *DO NOT show the standard error* for the confidence intervals. Instead, we present **95% stratified bootstrap confidence intervals** with 50.000 resampling iterations.
> As an empirical study, this work would benefit from ***proper statistical analyses*** […].
>
Our evaluation protocol follows the suggestions of Agarwal et al. 2022 (Deep Reinforcement Learning at the Edge of the Statistical Precipice, NeurIPS). This protocol is statistically well-motivated. The presented inter quartile mean (IQM) is both robust to outliers (unlike the mean) and more statistically efficient than the median. Stratified bootstrap confidence intervals take statistical uncertainty into account. Agarwal et al. find that $N = 10$ runs already provide good CIs for the IQM. The results we present are aggregated over a total of 250 seeds ((15 DMC envs + 10 Myo Envs) * 10 seeds each).
To convince the reviewer, we re-plotted our results (https://imgur.com/a/engjRM6). For visual clarity, we have
- removed UTD=2 to observe the gap between UTD=1 and 5 better.
- changed the colors for better visual separability
We plot **IQM** and **95% stratified bootstrap confidence intervals**.
- On the very right, we aggregate over all 15 DMC envs (150 seeds) until 1M steps. We observe that UTD=5 dominates UTD=1. CIs overlap in some parts, however, not everywhere and keep a margin to the IQM.
- In the middle, we aggregate over the 8 easy and medium DMC envs (80 seeds). Since these environments are learned faster, and the improvement of the higher UTD happens in the earlier stage of training, we concentrate on the first 500k steps for this plot. We observe a large separation between the IQMs and CIs of the different UTDs.
- On the left, we aggregate over the 7 hard (Dog & Humanoid) DMC envs (70 seeds). These environments are harder to learn, and the benefit of UTD=5 shows later in training. The CIs are larger and slightly overlap. However, later in training, IQM distance increases and CI overlapping decreases.
We believe that our results provide **a proper statistical analysis** based on the protocol of Agarwal et al. We further believe that the benefits of larger UTDs are clearly visible, and we hope that with our new, improved visualization, we were able to convince the reviewer of the scalability of our approach.
> The goal is to provide a better algorithm, but Figure 1 shows significant overlap between BRO and CrossQ.
>
The goal is to scale CrossQ to higher UTD ratios. We analyze why it does not scale and propose a fix. We find that we end up with an algorithm that is competitive with the current SOTA methods while being much simpler.
Further, we can argue that our proposed algorithm is indeed **better** than BRO in the sense that the sample efficiency is competitive and at the same time the algorithm is simpler and more lightweight: 90% smaller networks, no distributional critics, does not require periodic resetting, and no dual policy optimistic exploration needed.
We hope that we could clarify the open questions and want to thank the reviewer again for their time and their review. | null | null | null | null | null | null |
Channel Normalization for Time Series Channel Identification | Accept (poster) | Summary: The paper talk about the importance of Channel Identifiability (CID) when modeling multivariate time series data. The paper talk about how existing methods failed to provide CID capability. To solve this problem, the model proposed various Channel Normalization (CN) method. CN is a type of normalization method that uses different affine transformation for different channel. In additional a simple CN method, the paper also provided two extension 1) the Adaptive CN (ACN) method which also models the dependency between input dimensions in a data dependent fashion and 2) Prototypical CN (PCN) method which uses learned prototype to model different dimensions.
Claims And Evidence: - Claims:
1. Some existing methods lack CID capability, potentially leading to suboptimal performance.
2. CN is a simple yet effective method to provide CID capability for different models.
3. ACN improves upon CN by performing normalization in a data-dependent fashion.
4. PCN also provides CID capability.
- Evidence:
1. This claim is supported by Figure 1 and Table 1.
2. This claim is backed by experimental results and can be easily inferred from the methodology, as the method is straightforward.
3. This claim is also supported by experimental results and can be easily inferred from the methodology.
4. This claim is not fully substantiated. Although PCN improves model performance, the source of the improvement is unclear. Moreover, I am not fully convinced that PCN provides CID, which I will elaborate on in later sections.
- Missing: Theoretical analysis is absent, but it is not necessary as it is easy to see how CN/ACN provides CID.
Methods And Evaluation Criteria: Yes, the proposed methods and evaluation criteria make sense for the problem at hand.
Theoretical Claims: I am not fully convinced that PCN provides CID capability. Comparing the algorithms for CN (Algorithm 1), ACN (Algorithm 2), and PCN (Algorithm 3), we can see that PCN is the only one without a global parameter for normalization. Without a global parameter, the normalization process cannot differentiate between two channels if they have identical inputs (Figure 1). This could be the main reason why PCN performs worse than CN and ACN. The paper would be stronger if PCN were not included in the main text. I believe PCN is more of an extension of CN (i.e., an effective channel normalization method that does not provide CID) and should be discussed in the appendix.
Experimental Designs Or Analyses: Yes, I have checked the experimental designs and analyses. No severe issues were found.
Supplementary Material: Yes, I reviewed both the appendix and the code.
Relation To Broader Scientific Literature: The proposed CN methods are simple yet effective, which is a novel contribution not seen in prior work.
Essential References Not Discussed: To the best of my knowledge, there are no essential references missing from the paper's discussion.
Other Strengths And Weaknesses: - Strengths: The motivation behind the proposed methods is clear, and the proposed methods are simple yet effective.
- Weaknesses: One of the proposed methods (PCN) seems out of place and may not fully align with the paper's main contributions.
Other Comments Or Suggestions: The variables used in Section 4 are not introduced. What are B, C, D, and K? It is difficult to understand the methods without looking at the source code.
Questions For Authors: 1. How does PCN provide CID?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: ## Weakness 1. PCN’s CID capability
> Reviewer: *I am not fully convinced that PCN provides CID capability. ~ I believe PCN is more of an extension of CN (i.e., an effective channel normalization method that does not provide CID) and should be discussed in the appendix.*
Thank you for pointing this out. We acknowledge that PCN indeed does not provide CID capability, as PCN does not assign an identity to **“individual channels”** but rather to **“channel clusters”**.
PCN is specifically designed for scenarios encountering **new** channels in **new** datasets (common settings for foundation models), where ***channel identification becomes infeasible***. Our proposed PCN address this challenge by assigning **“channel cluster”** identification via learnable prototypes as affine transformation parameters after normalization.
While the current manuscript presents PCN as an extension of CN in that it also provides **a form of identity (to either channels or channel clusters)**, we recognize the reviewer's concern that it may require a relaxed version of CID for channel clusters. We will clarify this distinction in the revision.
## Weakness 2. Missing notations
> Reviewer: *The variables used in Section 4 are not introduced. What are $B$, $C$, $D$, and $K$? It is difficult to understand the methods without looking at the source code.*
Thank you for pointing this out. We found some of these definitions were missing.
$B$ represents the batch size, $C$ denotes the number of channels, $D$ is the hidden dimension, and $K$ refers to the number of prototypes.
To improve clarity, we will explicitly define $B$, $C$, $D$, and $K$ in **Section 4** and also include them in the algorithm pseudocode.
**If there are any unresolved issues, please feel free to discuss them with us!**
---
Rebuttal Comment 1.1:
Comment: concerns resolved | Summary: - The Channel Normalization (CN) strategy is proposed to enhance the Channel Identifiability (CID) of Time Series (TS) models by assigning specific parameters to each channel.
- Two variants of CN, Adaptive CN (ACN) and Prototypical CN (PCN), are introduced to dynamically adjust parameters and handle datasets with unknown or varying numbers of channels, respectively.
Claims And Evidence: The paper proves the effectiveness of CN, ACN, and PCN in improving model performance through experiments on multiple models and datasets, such as 12 datasets and 4 backbone networks, using Mean Squared Error (MSE) and Mean Absolute Error (MAE) as indicators. The evidence is relatively sufficient.
Methods And Evaluation Criteria: - The proposed methods of CN, ACN, and PCN are designed to address the channel identifiability problem in TS models, with clear improvement goals and reasonable method designs.
- The selection of common TS datasets and evaluation metrics, MSE and MAE, can effectively measure the performance of models in TS forecasting tasks.
Theoretical Claims: The paper proves that CN can obtain more informative representations and potentially reduce forecasting errors from the perspective of theoretical entropy analysis. Its universality in practical applications remains to be further verified.
Experimental Designs Or Analyses: The experiments select multiple datasets and different backbone networks, and compare CN and its variants with other methods. The experimental design is relatively comprehensive.
Supplementary Material: There is no independent upload of supplementary materials, but the experimental details of CN are well presented in the appendix.
Relation To Broader Scientific Literature: Based on the literature related to TS forecasting models and normalization methods, the paper proposes a new method to enhance CID. Compared with recent similar studies (such as InjectTST, C - LoRA, etc.), it highlights the advantages and innovativeness of its own methods.
Essential References Not Discussed: There are no obvious unreferenced papers.
Other Strengths And Weaknesses: None.
Other Comments Or Suggestions: "Figure 1: Channel identifiability. Applying the proposed methods to non-CID models enables to distinguish among channels, producing different outputs (green) even with same inputs (yellow)." Maybe the colors are mispositioned.
Questions For Authors: - Q1: I have a concern about the performance of CN, ACN, PCN. The authors should provide some details about the performance.
- Q2: How do authors initialize the parameters of CN, ACN, PCN? How do the different initialization methods affect the metrics?
Code Of Conduct: Affirmed.
Overall Recommendation: 5 | Rebuttal 1:
Rebuttal: ## Weakness 1. Miscolored Figure 1
> Reviewer: *"Figure 1: ~ producing different outputs (green) even with same inputs (yellow)." Maybe the colors are mispositioned.*
Thank you for pointing that out. We will fix it in the revised version.
## Question 1. Details about the performance of CN, ACN, PCN
> Reviewer: *I have a concern about the performance of CN, ACN, PCN. The authors should provide some details about the performance.*
**[PCN vs. CN/ACN]**
If your concern is the comparison between PCN and CN/ACN, please refer to **Table 5**. Although PCN extends CN, it underperforms CN in the **”single”-task model**, as PCN is intended for scenarios where the ***number of channels is unknown***. As shown in **Table 3**, PCN is tailored for **zero-shot scenarios** and does not allocate parameters per channel but rather shares them across channels. For example, only PCN is applied in **Table 4**, as CN and ACN are not applicable to zero-shot scenarios.
**L324–326 (Right column)** We attribute this to the fact that, unlike CN and ACN which assign each channel a distinct parameter, PCN assigns each prototype a distinct parameter,
**[CN vs. ACN]**
If your concern is the comparison between CN and ACN, ACN extends CN by incorporating local parameters that **dynamically** adapt based on the input TS, considering its dynamic nature (**L20--23 (Left column)**). As seen in **Table 8**, this enhancement improves performance while introducing only a negligible increase in computational complexity.
**[Others]**
Alternatively, if your inquiry pertains to any of the following, we provide the relevant information:
- a) **Performance results**:
- [CN/ACN] **Tables 2, 6, 7**
- [PCN] **Tables 4, 5**
- b) **Interpretation of results**: **Section 5.1**
- c) **Experimental details**:
- [Datasets] **Appendix A.1**
- [Settings] **Appendix A.2**
If this response does not fully address your concern, we would appreciate any further clarification or specific details you could provide.
## Question 2. Initialization of parameters of CN, ACN, PCN
> Reviewer: *How do authors initialize the parameters of CN, ACN, PCN? How do the different initialization methods affect the metrics?*
The initialization of the parameters for CN, ACN, and PCN is designed to ensure that ***no normalization occurs when learning has not yet taken place***:
- The **scale** parameter ($\alpha$) is initialized to **1**.
- The **shift** parameter ($\beta$) is initialized to **0**.
This aligns with the default initialization used in **PyTorch normalization layers**:
- (Pytorch) **Layer** normalization initialization: https://github.com/pytorch/pytorch/blob/1eba9b3aa3c43f86f4a2c807ac8e12c4a7767340/torch/nn/modules/normalization.py#L210
- (Pytorch) **Batch** normalization initialization: https://github.com/pytorch/pytorch/blob/1eba9b3aa3c43f86f4a2c807ac8e12c4a7767340/torch/nn/modules/batchnorm.py#L93
Therefore, the parameters for CN, ACN, and PCN are initialized as follows:
- CN: $\alpha=1, \beta=0$
- ACN: $\alpha^{\text{G}}=1, \alpha^{\text{L}}=0, \beta^{\text{G}}=1, \beta^{\text{L}}=0$, so that $\alpha=1, \beta=0$
- PCN: $\alpha^{\text{P}}=1, \beta^{\text{P}}=0$
This initialization is documented in the Python files within `/layers` in the attached anonymous GitHub link.
We acknowledge that the explanation of initialization was omitted in the paper. As the reviewer pointed out, **we will include this explanation in the revised version**. Thank you for your feedback.
Additionally, after testing on four ETT datasets and running experiments three times with different random initialization seeds (using PyTorch's default `nn.Parameter` initialization), **the effect on the average across four horizons was negligible**, differing only at the fourth decimal place.
**If there are any unresolved issues, please feel free to discuss them with us!**
---
Rebuttal Comment 1.1:
Comment: - My expression is ambiguous. What I want to know is the **consumption of computation**. For example, I am more concerned about time complexity, space complexity, and running time.
- I can't get this detail from the article, but the rest of the paper is splendid. I will raise the score to 5 after the author adds the corresponding detail.
---
Reply to Comment 1.1.1:
Comment: Thank you for continuing to engage in the discussion.
Below we provide a computational analysis of CN, ACN, and PCN (compared to LN) from the following **three perspectives**:
1. **Time Complexity**
2. **Space Complexity**
3. **Running Time**
## Notation
$x \in \mathbb{R}^{B \times C \times D}$, where $K$ is the number of (predefined) clusters for PCN, $K < C$ in our experiments (as we set $K=5$ for all single-task settings (as referred in **L320–321 (Left column)**) and $K=20$ for TSFMs (as referred in **L418–419 (Right column)**).
$D$ is set to 256 or 512 following the setting of each backbone in previous works, while $C$ varies across datasets, as detailed in **Table A.1**.
## 1. Time Complexity
All methods (LN, CN, ACN, and PCN) share the basic four steps (1. calculating the mean, 2. calculating the variance, 3. normalization, and 4. affine transformation), while ACN and PCN require an additional step.
Among the basic four steps, steps 1--3 are **identical** across all methods, and step 4 is different among these methods; however, since they all employ element-wise multiplication, the time complexity of step 4 **remains unchanged**. Thus, **LN and CN have the same time complexity**, as CN follows the same computational steps as LN without any additional operations.
For ACN and PCN, we additionally compute the weighted average of the parameters used in the affine transformation in step 4, **incurring additional time complexity**. Specifically, ACN uses weights based on channel similarities, resulting in additional $\mathcal{O}(C^2 D)$ time, while PCN uses weights based on channel-prototype similarities, resulting in additional $\mathcal{O}(CDK)$ time.
The resulting time complexities are as follows:
- LN: $\mathcal{O}(CD)$
- CN: $\mathcal{O}(CD)$
- ACN: $\mathcal{O}(C^2 D)$
- PCN: $\mathcal{O}(CDK)$
## 2. Space Complexity
Before delving into the details, we note that the proposed normalization methods can easily be implemented by **changing/adding a few lines of code for LN**. For example, CN can be implemented by simply applying the following change (similar change to beta as well):
- LN: `alpha = nn.Parameter(torch.ones(D))`
- CN: `alpha = nn.Parameter(torch.ones(C, D))`
Unlike LN, our proposed method maintains learnable parameters **for each channel (or cluster)**, resulting in the following space complexity for the affine transformation parameters:
- LN: $\mathcal{O}(D)$
- CN: $\mathcal{O}(CD)$
- ACN: $\mathcal{O}(CD)$
- PCN: $\mathcal{O}(KD)$
## 3. Running Time (Training & Inference Time)
The comparison of LN, CN, and ACN is provided in **Table 8**. Since PCN is missing in that table, we summarize the results together with PCN below, where the original iTransformer setting corresponds to iTransformer+LN.
|iTransformer |+LN|+CN|+ACN|+PCN|
|-|-|-|-|-|
|Training time (sec/epoch)|7.7| 7.8|10.8|11.1|
|Inference time (ms)|2.0|2.1|2.5|2.7|
|Avg.MSE|.254|.159|.153|.176|
If you are wondering why PCN underperforms compared to CN/ACN, please refer to **Question 1** in our initial rebuttal above.
Again, **we sincerely appreciate your valuable feedback**. We will incorporate these points into the revision. | Summary: The authors propose a new method to adaptively normalize each time series channel distinctly through learned channel specific adaptive parameters. These adaptive parameters for each channel are data dependent are computed through a dynamic weighted summation of a similarity matrix computed between channel token embeddings.
This normalization allows models to incorporate channel identity information. This allows different channels to produce different outputs even when provided the same input data to forecast on
Equipped with this adaptive normalization, models can incorporate channel information when forecasting future values.
The authors also propose a variation of this normalization method that could be deployed for scenarios where the number of channels can change or are unknown (which is the case for time series foundation models). This can be done by reformulating the channel adaptive normalization parameters as the weighted sum of a learnable set of prototypes.
A major contribution of the proposed method is that this normalization scheme can be applied to any existing time series forecasting method.
The authors test their adaptive normalization scheme with various time series models (transformers, MLPs, Mamba). These include models which are already incorporate channel identification and models do not. When tested on different time series forecasting datasets, the results show that the adaptive normalization improves forecasting performance for all models, even models that already incorporate channel identify information .
The authors also show how their proposed prototype based adaptive channel normalization scheme helps improve performance for Time Series foundation models.
Claims And Evidence: The claims are supported by extensive experiments on different types of datasets and time series models. The improvement in performance over no adaptive normalization schemes suggest that the proposed scheme does enhance performance.
The authors also claim that the learned normalization enhances feature representation and improves uniqueness of channel representation. This is backed by their experiments which show how the proposed method increases the entropy associated with representations across channels.
Methods And Evaluation Criteria: Yes, the proposed method and the evaluation criteria make sense for the model.
The method is compared with other normalization schemes, with various time series forecasting models on a variety of datasets
Theoretical Claims: The main paper doesn't have e theoretical claim.
Experimental Designs Or Analyses: Yes, the soundness of the validity and experimental design makes sense.
The datasets used, and the baselines evaluated with all make sense. Particularly for results in Table2 and Table 3.
I checked the validity for experiments that showed how normalization learns feature representations which are more diverse/unique across channels.
Supplementary Material: I reviewed the supplementary material which provided details for different datasets, the training, validation, and test splits.
I also reviewed the qualitative improvement in forecasting results for non adaptive channel normalization.
Relation To Broader Scientific Literature: The authors appropriately relate their finding to broader scientific literature. They put their work in context with models that incorporate channel identification and those that not. They also put their work in context with commonly used normalization schemes or incorporate channel specific parameters (such as channel specific identified or Channel specific LORA)
Essential References Not Discussed: None that I can think of
Other Strengths And Weaknesses: I think the main contribution of the paper in terms of its methodology is strong, but a major weakness is the lack of clarity in the paper which hampers reading. I will gave examples of this in my comments/suggestions/questions
This is the main reason I would incline towards giving it a weak acceptance..
Other Comments Or Suggestions: It would be helpful for readers to provide what different legend in different figures represent.
For example, LN in Figure 5? Is that layer normalization? This needs to be clarified
Questions For Authors: - The description in Figure 1 is very confusing. The outputs are supposed to be yellow, and the inputs are supposed to be green. no?
- Why is the entropy values negative in Figure 5?
- Is $\hat{\alpha}_{b,c}^L$ a value or a vector in $d$? ? what dimension does it lie in (For equation 6) .
- What are $B$, $D$ in Algorithm 1 , text before equation4 . This is never clarified which makes things confusing for the end user
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: ## Suggestions 1. Explanation of Legends in Figures
> Reviewer: *"It would be helpful for readers to provide what different legend in different figures represent. For example, LN in Figure 5? Is that layer normalization? This needs to be clarified*
Thank you for your feedback. Due to **space limitations**, commonly used terms such as Channel Normalization (CN) and Layer Normalization (LN) **were not explicitly labeled** in the legends. To ensure clearer understanding, **we will add these clarifications in the revised version**.
## Question 1. [Figure 1] Confusing descriptions & Miscolored
> Reviewer: *The description in Figure 1 is very confusing. The outputs are supposed to be yellow, and the inputs are supposed to be green. no?*
**[Confusing descriptions]**
Regarding the description in the figure, **"Figure 1: Channel Identifiability"** is intended to motivate the **necessity of CID**.
To illustrate this, we present two cases: **“with CID”** and **“without CID”**. Specifically, in the **left** panel, when the local inputs are identical (green), non-CID models fail to distinguish between channels, producing identical outputs (yellow). In contrast, in the **right** panel, applying our proposed CN introduces CID, such that even if the local inputs are the same (green), CID models distinguish between channels, producing different outputs (yellow).
We **will revise and clarify them** in the updated version. If there are still any confusing aspects regarding the figure, please feel free to ask us; we are happy to provide additional clarification.
**[Miscolored]**
Regarding the **coloring mistake**, we will fix the colors (green & yellow) in the revised version. Thank you for pointing that out!
## Question 2. Negative (approximated) entropy
> Reviewer: *Why is the entropy values negative in Figure 5?*
As the Gaussian entropy is ***approximated*** based on the data samples, the negative entropy values in **Figure 5** emerge. Previous studies ([1]--[5]) have also adopted this approximation (as mentioned in **L369--374**), and, as seen in [5] Sequence Complementor (AAAI 2025), negative values are observed in **Figure 2-(c)**, **Figure 5**, and **Figure S.6**.
[1] Ma, et al. "Segmentation of multivariate mixed data via lossy data coding and compression." TPAMI (2007)
[2] Yu, et al. "Learning diverse and discriminative representations via the principle of maximal coding rate reduction." NeurIPS (2020)
[3] Chen, et al. "Learning on Bandwidth Constrained Multi-Source Data with MIMOinspired DPP MAP Inference." IEEE Transactions on Machine Learning in Communications and Networking (2024)
[4] Chen, et al. "Rd-dpp: Rate-distortion theory meets determinantal point process to diversify learning data samples." WACV (2025)
[5] Chen, et al. "Sequence Complementor: Complementing Transformers For Time Series Forecasting with Learnable Sequences." AAAI (2025)
## Question 3. Is $\hat{\alpha}_{b, c}^{L}$, a vector or a scalar?
> Reviewer: *Is $\hat{\alpha}_{b, c}^{L}$ a value or a vector in $d$? what dimension does it lie in (For equation 6)?*
In the **Equation (6)**,
- $\hat{S}_{b, c, i}$ is a scalar and
- $\alpha_i^{\mathrm{L}}$ (or $\alpha_{i,:}^{\mathrm{L}}$) is a $D$-dimensional vector,
resulting in a $D$-dimensional vector.
Thanks to the reviewer’s feedback, we found typos in **line 6 of Algorithm 2,3**: $\alpha_{b,c,d}$ should be the vector $\alpha_{b,c,:}$, not a scalar, and this also applies to the bias term $\beta_{b,c,d}$ in line 7.
We agree that this might be difficult to understand with the explanation around **Algorithm 2**, we will provide a more detailed description of the dimensions in the main text and correct the error.
## **Question 4. Missing notations**
> Reviewer: *What are $B$, $D$ in Algorithm 1, text before equation 4. This is never clarified which makes things confusing for the end user*
Thank you for pointing that out. We found some of these definitions were missing. $B$ and $D$ represent the **"batch size"** and the **"number of channels"**, respectively.
To improve clarity, we will explicitly define them in **Section 4** and also include them in the algorithm pseudocode.
**If there are any unresolved issues, please feel free to discuss them with us!**
---
Rebuttal Comment 1.1:
Comment: Thank you for providing answers to my questions. These changes would help improve clarity of the proposed work. | null | null | null | null | null | null | null | null |
One-Shot Heterogeneous Federated Learning with Local Model-Guided Diffusion Models | Accept (poster) | Summary: This paper addresses the important and interesting problem of one-shot federated learning (OSFL), aiming to reduce the communication round of FL to 1. With the help of pretrained Classifier-Guided Diffusion Models, this paper proposes to generate local clients' data distribution in the server side with the guidance of the locally update models. The generated data are further used to train an aggregated global model.
## update after rebuttal
After two iteractions with the Authors, my questions has been solved.
I would recommend **Accept** after the necessary revisions, including more accurate explanations to the theretical results and proper citations for the borrowed contents. This paper addresses the interesting and important topic of one-shot federated learning by proposing a effective and reasonable method of utilizing classifier-guided DM. Even though it adds more computational requirements to the server comparing with standard federated learning method, the benefits from single communication round worth the cost. After all, if your computaional ability can not even run a diffusion model, you are not qualified as a server.
Claims And Evidence: Clear and Convincing.
Methods And Evaluation Criteria: Make sense.
Theoretical Claims: I have checked the proofs.
However, the proof for Theorem 1 is not enough, specifically the explanation of the last two two terms in equation 5. See the questions for authors below.
Experimental Designs Or Analyses: Experimental designs and analyses totally make sense.
Supplementary Material: I have reviewed the proof and some of the additional experimental resuls. The additional experimental results make sense. The problem of proof will be addressed below.
Relation To Broader Scientific Literature: The proposed method effectively addressed the one-shot federated learning problem, with experimental results showing significant performance improvements. The proposed method is intersting and totally makes sense, providing remarkable contribution to soloving the one-shot federated learning problem.
Essential References Not Discussed: BN loss has been widely used, for example, [Yin'2020], while the related citations are missing.
[Yin'2020] Yin, Hongxu, et al. "Dreaming to distill: Data-free knowledge transfer via deepinversion." CVPR 2020.
Other Strengths And Weaknesses: Strength:
- This paper addresses the important and interesting setting, one-shot FL, which restricts communication round of FL to only 1.
- The proposed method generates synthetic images in the server side for aggregated model training, which makes sense considering computational ability.
- Even though this paper does not propose novel techniques, the creative combination of existing techniques to address the important and cutting-edge problem makes this paper interesting.
- Experiments are adequate and solid, especially the datasets are realistic and large-scale. Performance improvements are significant.
- I like the Privacy Issues part, which explains why the proposed method will not recover the original client data using meaningful experimental results, i.e. avoiding raising privacy concerns. It should also be highlighted in the abstract and introduction, avoiding confusion in the beginning.
Weaknesses:
- The explanation of theorem 1 is not enough. Refer to questions to authors below.
- BN loss only works with models with BN layers, while it does not work on others such as transformers or models for other data modalities.
Other Comments Or Suggestions: Typos.
- Theorem 1: error in right column of line 187.
- Eq 7, error in s (not bold)
- Eq 8, $\hat{\boldsymbol{s}}_{0,t}$
or
$\hat{\boldsymbol{s}}_{0}$?
- Right column of line 373, table 4.2?
- In line 437, it is claimed that the local model training only takes 1 iteration. I guess you mean a single round of optimization.
Questions For Authors: Theorem 1: the explanation of the last two terms are not clear enough.
1. Why is $\mathbb{E}(\log p_{\epsilon_\theta}(\boldsymbol{\theta}_k))$ a constant?
What does $p_{\epsilon_\theta}(\boldsymbol{\theta}_k)$ represent?
2. Why is that minimizing the negative log-likelihood is equivalent to minimizing the cross-entropy loss?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We sincerely appreciate your recognition of our work and your valuable feedback. Below, we provide detailed responses to the key concerns you raised:
>**(Essential References Not Discussed)** *"BN loss has been widely used, for example, [Yin'2020], while the related citations are missing."*
Thank you for pointing this out. In the revised version of our manuscript, we will incorporate relevant references[1,2,3] to ensure a more comprehensive discussion of BN Loss and its applications.
>**(Generality of BN Loss)** *Weaknesses #1 "BN loss only works with models with BN layers, while it does not work on others such as transformers or models for other data modalities."*
We refer to the loss function in our study as BN Loss primarily because BN has been widely adopted, as demonstrated in prior works [1,2,3]. However, the core mechanism of BN Loss involves leveraging statistics, such as mean and variance, which are also present in other normalization layers such as Layer Normalization [4]. Notably, Layer Normalization has been extensively used in transformer, including models like CLIP [5]. Therefore, our method is not strictly limited to models with BN layers but can be extended to transformers and other architectures employing various normalization layers.
>**(Further Explanation of Theorem 1)** *Weaknesses #1 "The explanation of theorem 1 is not enough."*
>* *"Why is $\mathbb{E}(\log p\_{\epsilon\_\theta}(\boldsymbol{\theta}\_k))$ a constant?"*
This term is solely dependent on the parameters of the diffusion model, which remain fixed during our method. Consequently, $\mathbb{E}(\log p_{\epsilon_\theta}(\boldsymbol{\theta}\_k))$ can be considered a constant.
>* *"What does $p\_{\epsilon_\theta}(\boldsymbol{\theta}\_k)$ represent?"*
This term represents the default data distribution of the diffusion model. After extensive pretraining, $p\_{\epsilon\_\theta}(\boldsymbol{\theta}\_k)$ approximates the data distribution of the diffusion model’s pre-train dataset.
>* *"Why is that minimizing the negative log-likelihood is equivalent to minimizing the cross-entropy loss?"*
The negative log-likelihood and the cross-entropy loss are formally equivalent. When the target distribution is a one-hot distribution, maximizing the likelihood corresponds to minimizing the cross-entropy loss. This equivalence is widely utilized in deep learning, particularly in the loss functions of softmax-based classification tasks[6].
>**(Typos)** *Other Comments Or Suggestions*
We appreciate your meticulous attention to detail in identifying typographical errors. These will be corrected in the revised manuscript. Additionally, we will conduct a thorough review to ensure the clarity and accuracy of our presentation.
Once again, thank you for your insightful review and constructive feedback. We look forward to any further comments you may have.
[1] Dreaming to distill: Data-free knowledge transfer via deepinversion, CVPR 2020.
[2] Are Large-scale Soft Labels Necessary for Large-scale Dataset Distillation? NIPS 2024.
[3] Source-Free Domain Adaptation for Semantic Segmentation, CVPR 2021.
[4] Layer Normalization, NIPS 2016.
[5] Learning transferable visual models from natural language supervision, ICML 2021.
[6] Machine learning: a probabilistic perspective, MIT press 2012.
---
Rebuttal Comment 1.1:
Comment: The questions to the theorem 1 remain unsolved after the rebuttal.
- The last two terms in Eq~ 5 do not make sense.
- The probability $\log p_{\epsilon_\theta}(\boldsymbol{\theta}_k)$ in the second term represent the distriubtion of model parameters in the diffusion model, while the parameters of pretrained diffusion model are deterministic not random. I also referred to the original paper proposing classifier guided diffusion model [Dhariwal & Nichol, 2021], where there are no such notations.
- The third term is totally different from cross-entropy loss, especially the third term measures the divergence between data distribution and parameters distribution, which does not make any sense.
- Most importantly, note that cross-entropy itself is not upper bounded, leaving the KL divergence in Eq~5 not upper-bounded.
---------------
**After author's reply to the rebuttal comment above.**
I apologize for the typo. Let me rephrase the questions as follow.
- What does $p_{\epsilon_\theta}(\boldsymbol{\theta}_k)$ represent?
Since $\theta_k$ denotes the parameters of local trained model, it is irrelevant to the DM $\epsilon_{\theta}$.
- Since the expectation in the second term is w.r.t. the local data distribution $p_k(\boldsymbol{x})$ and $\theta_k$ is trained based on the local data, is the second term still constant?
- The explanation to the third term is somwhat convincing, i.e. even though this term is not computable, it possibly represents the mismatch between local data distribution and local model parameters.
- Most importantly, this paper borrows content heavily from the paper **FedDEO**, especially the theoretical part, where the only difference is replacing the original $\boldsymbol{d}$ with $\boldsymbol{\theta}_k$. However, the related work FedDEO is not properly cited in the context of the borrowed content, which significantly degrades the quality of this paper.
------------------------
**After second iteraction with Authors**
My questions has been solved.
- After dropping the $\epsilon_\theta$ from both marginal and conditional distribution of local model parameters $\theta_k$, the two terms make more sense than before.
- For the second term, I would recommend carefully explaining it as intuitively local data distribution absolutely makes impact on local model. One possible explanation would be that given the local data distribution, fixed model parameters initialization and optimizer, the locally optimized model parameters remain fixed after fixed number of iterations.
- I agree that this paper has significant difference from FedDEO. As mentioned before, proper citation is extremely important.
I would recommend **Accept** after the revisions, including more accurate explanations to the two terms and proper citations. This paper addresses the interesting and importatnt topic of one-shot federated learning by proposing a effective and reasonable method of utilizing classifier-guided DM. Even though it adds more computational requirements to the server comparing with standard federated learning method, the benefits from single communication round worth the cost. After all, if your computaional ability can not even run a diffusion model, you are not qualified as a server.
---
Reply to Comment 1.1.1:
Comment: ---
We sincerely apologize for the typo in our initial rebuttal, which may have caused a misunderstanding of our method. We appreciate your careful reading and now provide clarifications and detailed responses below:
> * *"What does $p\_{\epsilon_\theta}(\boldsymbol{\theta}_k)$ represent?"*
In our paper, $p\_{\epsilon_\theta}(x)$ denotes the default data distribution learned by the DM. $p\_{\epsilon\_\theta}(\boldsymbol{\theta}\_k)$ refers to the distribution of local model parameters, and $p\_{\epsilon\_\theta}(\boldsymbol{\theta}\_k|\mathbf{x})$ represents the conditional distribution of local model parameters given the client data $\mathbf{x}$.
Since the latter two distributions are not related to the diffusion model parameters $\epsilon\_\theta$, it is more appropriate to express them as $p(\boldsymbol{\theta}\_k)$ and $p(\boldsymbol{\theta}\_k|\mathbf{x})$. We thank you for pointing out this inaccuracy, and we will revise the notation accordingly in the next version to improve precision and clarity.
> * *"... is the second term still constant?"*
Yes. As in our work and many other FL settings, once the local models are uploaded to the server, their parameters remain fixed during aggregation. Since the conditional distribution of the synthetic dataset $p_{\epsilon_\theta}(\mathbf{x}|\boldsymbol{\theta}_k)$ relies on the fixed local model parameters $\boldsymbol{\theta}_k$, the 2nd term is also constant in our analysis.
> * *"... the related work FedDEO is not properly cited in the context of the borrowed content, which significantly degrades the quality of this paper."*
We sincerely apologize for not explicitly citing FedDEO at the point of theoretical borrowing. During manuscript preparation, we indeed referred to some of FedDEO’s theoretical formulations to enhance the logical rigor of our paper. We will make the citation explicit and properly acknowledge their contribution in the revised version.
It is important to emphasize that despite some theoretical similarities, our method differs significantly from FedDEO [1] in terms of practical design: **FedDEO requires training based on the DMs on the clients**, which obviously introduces substantial computation and communication costs. In contrast, our method significantly reducing the client burden. What's more, our method employs local models rather than additional prompts for guiding generation, eliminating the need for compositional diffusion, imposing a lower server computation cost. Below we provide a detailed comparison of model performance and computation costs between FedDEO, OSCAR[2] and our method, which will be included in the final version.
### Server computation cost :
| | FedDISC | FGL | FedDEO | OSCAR | FedLMG |
|:--------:|:-------:|:------:|:------:|:------:|:------:|
| flops (T)| 135.71 | 102.83 | 101.78 | 67.85 | **38.87** |
### Client accuracy comparison :
| | client0 | client1 | client2 | client3 | client4 | client5 | average |
|:---------:|:-------:|:-------:|:-------:|:-------:|:-------:|:-------:|:-------:|
| FedLMG_FT | 48.99 | 51.66 | 55.59 | 52.80 | 62.41 | 58.86 | 55.05 |
| FedLMG_SD | 47.60 | **55.20** | **61.54** | 61.83 | 67.07 | **59.90** | **58.86** |
| FedLMG_MD | 44.70 | 53.08 | 58.67 | 60.13 | 64.06 | 58.06 | 56.45 |
| FedDEO | **51.08** | 52.53 | 61.22 | **62.18** | 67.31 | 56.68 | 58.50 |
| OSCAR | 50.89 | 53.51 | 60.05 | 61.98 | **68.76** | 56.52 | 58.61 |
---
We once again thank you for your thoughtful review and valuable feedback. Your comments helped us clarify critical aspects of our method and recognize areas where our explanations and citations can be improved. We will revise the corresponding parts accordingly, enrich the paper with further comparisons, and refine our writing to enhance the overall completeness and rigor. We sincerely hope that these improvements will better convey the contributions and practicality of our work.
[1] FedDEO: Description-Enhanced One-Shot Federated Learning with DMs, MM 2024.
[2] One-Shot Federated Learning with Classifier-Free Diffusion Models, ICME 2025. | Summary: This paper introduces FedLMG, a novel One-Shot Federated Learning (OSFL) method addressing limitations of diffusion model-based OSFL. FedLMG leverages locally trained client models to guide a server-side diffusion model in generating synthetic datasets tailored to individual client distributions. This approach eliminates the need for foundation models on clients, reducing computational burden and enhancing adaptability to heterogeneous clients. Extensive experiments on multiple datasets demonstrate FedLMG's superior performance over existing methods, even surpassing centralized training in some scenarios. Theoretical analysis and visualizations confirm the high quality and diversity of the generated synthetic data and the method's effectiveness in capturing client-specific distributions, highlighting the potential of diffusion models in practical OSFL.
Claims And Evidence: The paper's central claim - the effectiveness and superiority of FedLMG for OSFL - is strongly supported by comprehensive evidence. Extensive quantitative experiments across diverse datasets (Table 1) convincingly demonstrate FedLMG's outperformance against various baselines, including traditional FL and other diffusion-based OSFL methods. The claim of surpassing centralized training ceilings is also empirically supported. Ablation studies (Table 4, Figure 3, Appendix C.1) provide evidence for the roles of BN loss and classification loss. Theoretical analysis (Theorem 1, Appendix A.1) offers a formal justification for the method's ability to generate client-aligned data. Visualizations (Figures 2, 4, 7, 8) qualitatively support the high quality and diversity of synthetic datasets and privacy-preserving nature.
Methods And Evaluation Criteria: The paper proposes FedLMG, a novel method for one-shot federated learning utilizing diffusion models guided by locally trained client models. The methodology, encompassing local client training, guided synthetic data generation, and three aggregation strategies, is well-suited for addressing OSFL challenges, particularly in heterogeneous settings. The evaluation is comprehensive, employing large-scale datasets: OpenImage, DomainNet, and NICO++. Benchmarking against strong baselines, including traditional FL methods, diffusion-based OSFL methods, and a centralized training ceiling, provides a robust comparative analysis. Classification accuracy serves as a relevant and standard metric for evaluating model performance in image classification tasks within federated learning.
Theoretical Claims: The paper presents one main theoretical claim in Theorem 1, which is formally proven in Appendix A.1. I have carefully examined the provided proof of Theorem 1 and found it to be mathematically sound and logically consistent. The proof correctly demonstrates that, under Assumption 1 (bounded KL divergence between the diffusion model's unconditional distribution and client data distribution), the KL divergence between the synthetic dataset distribution and the client's local data distribution is indeed bounded.
Experimental Designs Or Analyses: The experimental designs are robust and effectively validate FedLMG. The core experiments (Table 1) comprehensively assess performance under feature distribution skew across diverse datasets, using appropriate baselines and metrics (accuracy). Ablation studies systematically dissect the contributions of key components like BN loss and diffusion model choices (Table 4, Appendix C.1), strengthening mechanistic understanding. The exploration of heterogeneous client models and label distribution skew (Appendix C.1) broadens the evaluation scope. Privacy experiments employing FID and visualizations (Figure 4, Appendix C.2) directly address privacy concerns. Visualization of synthetic data (Figures 2, 7, 8) provides qualitative validation of data quality and diversity.
Supplementary Material: I reviewed the supplementary material, focusing on Appendix A (Method Details), Appendix B (Experimental Setting Details), and Appendix C (Supplementary Experiments). These sections provide essential details omitted from the main text due to space constraints. Appendix A offers pseudocode and expanded proofs. Appendix B elaborates on datasets, client partitioning, and implementation specifics. Appendix C includes additional ablation studies, privacy evaluations, and further visualizations.
Relation To Broader Scientific Literature: FedLMG makes significant contributions to the intersection of Federated Learning (FL) and Diffusion Models (DMs). It addresses limitations of existing DM-based One-Shot FL (OSFL) methods (FedDISC, FGL) by eliminating the need for foundation models on clients. Unlike methods relying on public auxiliary data, FedLMG cleverly utilizes locally trained client models to guide DM-based data generation, a novel approach compared to generator-based OSFL and auxiliary information transfer methods. The distillation-based aggregation strategies build upon knowledge distillation in FL but introduce specific adaptations for OSFL with synthetic data.
Essential References Not Discussed: No.
Other Strengths And Weaknesses: Strengths:
1.FedLMG presents a new approach to OSFL by innovatively using locally trained client models to guide diffusion-based synthetic data generation.
2.The paper provides theoretical justification for the method, adding rigor and confidence to the empirical findings.
3. The method significantly enhances the practicality of OSFL by eliminating the need for foundation models on resource-constrained clients and effectively addressing heterogeneous client scenarios.
Weaknesses:
1.Although the paper provides a theory about KL divergence boundary, the specific selection of BN loss as a guiding mechanism lacks a strong theoretical basis.
2.Of the three polymerization strategies, FedLMG_SD (i.e. distillation using the synthetic sample and its corresponding client model) should theoretically give the best result, but in the experiment shown in Table 9 in the appendix, FedLMG_SD lags behind FedLMG_MD by a large margin. There is no relevant analysis in this paper.
3.Privacy assessments that rely on FID thresholds are not rigorous or convincing enough. The FID is not a specific privacy indicator, and the threshold chosen is subjective.
Other Comments Or Suggestions: In this paper, a reference error occurred in Ablation Experiments in 4.3, that is, Table4.2 should be Table 4.
Questions For Authors: 1.Assumption 1's "boundedness" of KL divergence is overly broad and lacks quantitative validation, leading to a fragile theoretical foundation. If client data distributions differ significantly from the diffusion model's default distribution, FedLMG performance may substantially degrade.
2.The paper lacks quantitative analysis of the guidance signal effectiveness in image generation. The quality and effectiveness of client model guidance are unevaluated, obscuring FedLMG's working mechanism.
3.While the client side computation is reduced, server-side data generation can become a bottleneck for large-scale federated scenarios, limiting the actual application scale. The paper lacks a detailed breakdown of server-side computing costs and how they vary with dataset size.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for recognizing our work. Below, we provide detailed responses to your concerns:
>**(Server Cost)** *Questions #3"... server computing costs."*
In FL, the server is generally designed to have sufficient resources to handle the model aggregation, but clients often exhibit significant heterogeneity, necessitating constraints on costs[1]. Our method adheres to this principle by reducing client burdens.
Additionally, the following table presents a comparision of the server computation costs with other DM-based FL methods. Our method employs local models rather than additional prompts for guiding generation, eliminating the need for compositional diffusion, imposing a lower server computation cost.
||FedDISC| FGL|FedDEO|OSCAR|FedLMG|
|:----:|:----:|:----:|:----:|:----:|:----:|
|flops (T)|135.71|102.83|101.78|67.85|**38.87**|
>**(Additional Ablation Experiments)** *Questions #4 "… vary with dataset size."*
We appreciate the reviewer’s suggestion. The following table show that increasing the number of generated images leads to an improvement in the performance. Moreover, we observe that the improvement does not saturate as the dataset size increases, further demonstrating the diversity of the synthetic dataset.
|the number of generated images|clipart|infograph|painting|quickdraw|real|sketch|average|
|:----:|:----:|:----:|:----:|:----:|:----:|:----:|:----:|
|10|40.77|15.95|35.66|8.51|55.81|37.1|32.3|
|30|44.25|17.51|38.74|9.43|57.31|38.44|34.28|
|50|46.03|18.61|40.07|10.7|59.27|40.72|35.9|
>**(Experimental Analysis)** *Weaknesses #2 "FedLMG_SD should give the best result ... no relevant analysis."*
We would like to clarify that we include a dedicated analysis in line 937. We argue that due to the varying architectures of client models, some clients with more complex model structures demonstrate superior performance, allowing them to provide more accurate knowledge than the specific teacher in FedLMG_SD.
>**(Privacy-Related Experiments)**: *Weaknesses #3 "… the threshold chosen is subjective."*
We appreciate your suggestion, to further verify our method’s effectiveness in privacy protection, we employe [2] to ensure differential privacy and evaluate its impact on model performance. The results in the table below indicate that since our method only involves uploading local models, aligning with traditional FL, most privacy preserving methods in FL can be directly applied to our method without significantly degrading model effectiveness.
|noise level $\epsilon$|clipart |infograph|painting|quickdraw|real|sketch|average|
|:----:|:----:|:----:|:----:|:----:|:----:|:----:|:----:|
|0|**44.25**|**17.51**|**38.74**|**9.43**|**57.31**|**38.44**|**34.28**|
|20|43.53|17.06|38.49|9.13|57.08|38.15|33.91|
|50|42.82|16.73|37.63|8.67|56.51|37.25|33.273|
|100|40.86|16.04|35.28|8.19|55.68|35.14|31.86|
>**(Distribution Similarity)** *Questions #1 "Boundedness lacks quantitative validation ... client data distributions differ significantly..."*
Quantitatively evaluating the similarity between the default distribution of a DM and client distributions is challenging, particularly given the large-scale pre-training datasets of DM. However, with the recent advancements, pre-trained DMs tailored for various domains[3,4] have become increasingly available. We believe that servers can select appropriate DMs based on the target application. Even where the data distribution is challenging, a pre-trained DM from a similar domain can be fine-tuned on the server. Thus, We assert that our method possesses practicality in diverse application scenarios.
>**(BN Loss)** *Weaknesses #1 "... BN loss lacks a strong theoretical basis."*
As noted by Reviewer #xTsg, BN Loss has been widely applied[5]. Since BN Loss compares statistics, it provides an intuitive guidance and is adopted in studies such as [5,6] without additional theoretical analysis. We plan to further explore its theoretical underpinnings in future to strengthen our method’s theoretical foundation.
>**(Effectiveness of Guidance)** *Questions #2"... lacks quantitative analysis of the guidance effectiveness."*
We would like to clarify that we provide quantitative analyses of the effectiveness of guidance. The Prompts Only in Table 1 represent results where no local model guidance was used, whereas FedLMG denotes results with guidance. We believe that the comparison between these settings sufficiently demonstrates the effectiveness of the guidance in our method.
[1] A survey on federated learning: challenges and applications, IJMLC 2023.
[2] Federated Learning with Differential Privacy: Algorithms and Performance Analysis, TIFS 2020.
[3] Diffusion probabilistic models for 3d point cloud generation, CVPR 2021.
[4] DiffuSeq: Sequence to Sequence Text Generation with DMs, ICLR 2023.
[5] Dreaming to distill: Data-free knowledge transfer via deepinversion, CVPR 2020.
[6] Are Large-scale Soft Labels Necessary for Large-scale Dataset Distillation? NIPS 2024. | Summary: This paper introduces FedLMG, a novel approach for One-shot Federated Learning (OSFL) designed to establish an aggregated model within a single communication round. Specifically, FedLMG leverages fully-trained client models as classifier guidance to facilitate diffusion generation at the server. The generated images can represent the data distributions of the clients and are subsequently used for training an aggregated model. Experimental results demonstrate that FedLMG achieves superior performance compared to conventional Federated Learning (FL) and alternative diffusion-based OSFL methods, and sometimes even outperforms centralized training, which typically serves as the upper bound for FL.
Claims And Evidence: In Line 99 (in the left column), the paper states “we propose FedLMG, a novel OSFL method, to
achieve real-world OSFL without utilizing any foundation models on the clients, ensuring no additional
communicational or computational burden compared to traditional FL methods.” However, FedLMG needs image generation with diffusion models on the server, which can be an additional computation cost because traditional Federated Learning does not require this step.
In Line 214 (in the left column), the paper mentions “Even if the clients specialize in certain professional domains, like medical images, it’s entirely viable to train specialized diffusion models on the server. Hence, this assumption is entirely reasonable, considering a comprehensive assessment of practical scenarios.”
However, within the context of Federated Learning, we do not know if the clients’ data are in specialized domains, and the server may not have the data and computation resources to train a specialized diffusion model. Therefore, rather than characterizing the aforementioned assumption as "entirely reasonable," it would be more accurate to consider it as a potential limitation of the proposed method.
Methods And Evaluation Criteria: The proposed method, FedLMG, involves transmitting fully trained client models to a central server, where they are utilized to synthesize images for establishing an aggregated model. As the trained client model can be regarded as a compressed representation of its data distribution, the proposed method makes sense and is aligned with the setting of One-shot Federated Learning.
Theoretical Claims: In Theorem 1, the paper claims that the KL divergence between the client’s data distribution and the conditional distribution of the synthetic data is upper-bounded. Moreover, minimizing the cross-entropy loss within a client reduces the upper bound of the KL divergence. I’ve checked the proof in Appendix A, and the result seems to be correct.
Experimental Designs Or Analyses: The experiments are conducted under standard Federated Learning settings, where heterogeneous class and style distributions are distributed across different clients. The performance metric is the accuracy of the aggregated model evaluated across all clients. In addition, the paper presents an ablation study on the classification and BN losses of the proposed method. Overall, the experimental design and analysis are considered valid.
Supplementary Material: I’ve reviewed the supplementary material, including the proof of Theorem 1 in Appendix A, the experimental settings in Appendix B, and the privacy-related experiments in Appendix C.2.
Relation To Broader Scientific Literature: This paper applies an existing idea of classifier-guidance diffusion models to the domain of One-shot Federated Learning (OSFL). The main contribution resides in the connection between these two distinct areas and the introduction of a BN loss to further improve the OSFL performance. Compared to existing OSFL methods such as FGL and FedDISC, a key advantage of the proposed FedLMG is that it eliminates the need for foundation model inference on clients, which may have limited computational resources.
Essential References Not Discussed: Some related papers that follow the similar idea of using guidance for diffusion model generation in OSFL are missing, such as FedDEO [1], OSCAR [2], and FedCADO [3].
[1] 2024 ACM MM FedDEO: Description-Enhanced One-Shot Federated Learning with Diffusion Models
[2] 2025 arXiv One-Shot Federated Learning with Classifier-Free Diffusion Models
[3] 2023 arXiv One-Shot Federated Learning with Classifier-Guided Diffusion Models
Other Strengths And Weaknesses: Strengths
- The paper is well-written and easy to follow. The proposed FedLMG also demonstrates promising performance in experimental evaluations.
- The paper addresses privacy concerns related to regenerating client data distributions using guided diffusion models and demonstrates, through visualization, that specific privacy-sensitive information may remain concealed and preserved.
Weaknesses
- The main idea of the paper lies in improving the use of diffusion models in OSFL by leveraging trained client classifiers as guidance and introducing the BN loss. However, the paper does not thoroughly discuss prior work on guided diffusion models [1][2], making it unclear whether the proposed BN loss is the most suitable choice for the OSFL setting or if existing methods could be equally applicable.
- A potential limitation arises from the requirement for some degree of overlap between the client data distributions and the diffusion model’s data distribution, as determined by the parameter $\lambda$ in Equation 4. Specifically, when clients have highly specialized data distributions, such as medical images, the diffusion model may struggle to reconstruct these distributions accurately due to a large $\lambda$ value. Although the paper suggests that a specialized diffusion model could be trained on the server to address this issue, doing so may not be feasible in practice due to limited data or computational resources.
[1] 2024 NeurIPS TFG: Unified Training-Free Guidance for Diffusion Models
[2] 2023 CVPR Universal Guidance for Diffusion Models
Other Comments Or Suggestions: There are several typos from Line 178 and Line 188 (in the right column).
- Eq. 15 should be Eq. 5.
- Eq. 14 should be Eq. 4.
- It should be $p_k(x)$ instead of $p_n(x)$
In Appendix A, the proof is cut by Algorithm 1, making it a little hard to read.
Questions For Authors: Besides the weakness in the above sections, please also check the questions below:
1. Although the paper provides some visualizations suggesting that privacy-sensitive information may not be revealed by the guided diffusion generation, would applying noisy SGD (or related techniques) during client model training offer stronger privacy protection with formal differential privacy guarantees? How would this impact the performance of FedLMG?
2. How does the different degree of $\lambda$ impact the performance of FedLMG? For example, if clients hold data such as medical or aerial images, the diffusion model might struggle to reconstruct such distributions accurately. In this case, could FedAvg potentially perform better since it is indirectly trained on client data? Alternatively, how could FedLMG be adapted to handle such scenarios effectively?
3. Compared to FedAvg, which performs model aggregation through a simple averaging process, FedLMG requires significantly more computational resources on the server side due to image generation via diffusion models. What is the computational cost associated with this image-generation process? In Table 3, only the client-side cost is considered. How might the results change if the server-side cost is also taken into account?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We appreciate your positive comments of our work and address each of your concerns as follows:
>**(Server Cost)** *Claims #1 & Questions #3: "… DMs on the server, which can be an additional computation cost"*
In FL, the server is generally designed to have sufficient resources to handle the aggregation of client models, but clients often exhibit significant heterogeneity, necessitating constraints on computation costs[1]. Our method adheres to this principle by reducing client burdens.
Additionally, the following table presents a comparision of the server computation costs with other DM-based FL methods. Our method employs local models rather than additional prompts for guiding generation, eliminating the need for compositional diffusion, imposing a lower server computation cost.
| |FedDISC| FGL|FedDEO|OSCAR|FedLMG|
| :----: |:----: |:----: |:----: |:----: |:----: |
|flops (T) |135.71|102.83|101.78|67.85|**38.87**|
>**(Uncertain Clients)** *Claims #2: "… we do not know if the clients’ data are in specialized domains"*
The setting that the specific client tasks is uncertain for the server is Many-Task FL[2], where clients have diverse tasks simultaneously. However, this setting is not common. Most FL research presumes that the client task is known[1,3]. Therefore, we consider that our task setting is reasonable in real-world applications.
>**(Applicability)** *Claims #2 & Weaknesses #2 & Questions #2: "… may not have the data and computation resources to train a specialized DM."*
Currently, pre-trained DMs have been widely applied across various domains[4,5,6]. Based on the above discussion, we posit that the server know the overall task and can select an appropriate DM. Even where the data distribution is challenging, a pre-trained DM from a similar domain can be fine-tuned on the server. We assert that our method possesses practicality in diverse application scenarios.
>**(References)** *Essential References: "... similar idea of using guidance for DM generation in OSFL are missing …"*
We appreciate your suggestion. We incorporate the relevant works into our compared methods. As shown in the table below, our method achieves comparable performance without the employment of any foundational models on the clients, further demonstrating the performance of our method.
||client0| client1| client2| client3| client4| client5| average|
| :----: |:----: |:----: |:----: |:----: |:----: |:----: |:----: |
|FedLMG_FT| 48.99| 51.66| 55.59| 52.80| 62.41| 58.86| 55.05|
|FedLMG_SD| 47.60| **55.20**| **61.54**| 61.83| 67.07| **59.90**| **58.86**|
|FedLMG_MD| 44.70| 53.08| 58.67| 60.13| 64.06| 58.06| 56.45|
|FedDEO | **51.08**| 52.53| 61.22| **62.18**| 67.31| 56.68| 58.50|
|OSCAR | 50.89| 53.51| 60.05| 61.98| **68.76**| 56.52| 58.61|
>**(BN Loss)** *Weaknesses #1: "… whether the proposed BN loss is the most suitable choice"*
As noted by Reviewer #xTsg, BN Loss has been widely utilized[7]. Although there is no prior precedent for employing BN Loss in the DMs, the general method of designing task-specific loss functions and guiding the diffusion process is well established[8]. While we acknowledge that BN Loss might not be the optimal choice in all circumstances, its effectiveness has been clearly validated by the ablation experiments presented in Table 4.
>**(Privacy)** *Questions #1: "… applying noisy SGD during client model training offer stronger privacy protection"*
We appreciate your suggestion. Since our method only involves uploading local models, aligning with traditional FL, most privacy preserving methods in FL can be directly applied to our method. To validate this, we adopt [8] to ensure differential privacy and evaluate its impact on model performance. The experimental results shown in the table below indicate that traditional FL privacy protection measures remain effective within our framework without significantly degrading model performance.
|noise level $\epsilon$ | clipart |infograph| painting| quickdraw| real| sketch| average|
| :----: |:----: |:----: |:----: |:----: |:----: |:----: |:----: |
|0| **44.25**| **17.51**| **38.74** |**9.43** |**57.31**| **38.44** |**34.28**|
|20| 43.53| 17.06| 38.49| 9.13| 57.08 |38.15 |33.91|
|50|42.82| 16.73| 37.63 |8.67| 56.51 |37.25 |33.273|
|100| 40.86 |16.04| 35.28| 8.19 |55.68 |35.14| 31.86|
[1] A survey on federated learning: challenges and applications, IJMLC 2023.
[2] Many-Task Federated Learning: A New Problem Setting and A Simple Baseline, CVPR 2023.
[3] A survey on federated learning systems: Vision, hype and reality for data privacy and protection, TKDE 2021.
[4] DMs in medical imaging: A comprehensive survey, MIA 2023.
[5] DiffuSeq: Sequence to Sequence Text Generation with DMs, ICLR 2023.
[6] DiffWave: A Versatile DM for Audio Synthesis, ICLR 2021.
[7] Dreaming to distill: Data-free knowledge transfer via deepinversion, CVPR 2020.
[8] Federated Learning with Differential Privacy: Algorithms and Performance Analysis, TIFS 2020. | Summary: In response to the increasing demand for efficient One-Shot Federated Learning (OSFL) solutions, this paper introduces FedLMG, a novel OSFL method leveraging Local Model-Guided diffusion models. Unlike existing OSFL methods that rely on foundation models deployed on client devices—causing significant computational overhead—FedLMG allows clients to train and upload only their local models, maintaining the lightweight nature of traditional Federated Learning (FL).
Claims And Evidence: 1. The privacy issue of the proposed approach remain questioned. Although the paper visualized the synthetic data, the limited discussions do not convince that the proposed method preserves user privacy. The proposed method highly relies on the generated synthetic dataset to present server-side model aggregation, which is naturally a negative part of diffusion-based FL that contradicts the privacy nature of FL.
2. The paper also claims that using the proposed method is computationally efficient. However, neither training the stable diffusion model to generate synthetic data nor the multi-teacher distillation process for knowledge aggregation is efficient. Compared with traditional FL, this raises much more burdens to the server. Also, does the proposed aggregation method via distillation introduces instability due to wrong teacher selection?
Methods And Evaluation Criteria: 1. The evaluations and discussions in the paper are only based on the image dataset. It is questioning how the proposed method will perform on non-image and other modality datasets, especially the privacy issues of generated data in the other modalities.
2. The computation costs comparison in the paper includes the communication cost and client computation costs. However, the cost of model aggregation on the server is not mentioned, which should be less-important but still necessary metric of the algorithm.
Theoretical Claims: No issues on proofs.
Experimental Designs Or Analyses: 1. More ablation experiments are needed to prove the effectiveness of the proposed method, such as hyper-parameter studies, the size of synthetic data, the teacher selection constraints during distillation, etc.
2. The impact of the heterogeneity of datasets in the paper should be mentioned.
3. In Table 3, comparing the client computation costs between FedAvg and FedLMG to show that FedLMG is even more efficient than the traditional FedAvg does not make sense without simultaneously providing the convergence speed over communication rounds.
Supplementary Material: I reviewed all the part of the supplementary material.
Relation To Broader Scientific Literature: The key contribution of the paper is in the knowledge aggregation part -- leveraging a synthetic dataset as the aggregated knowledge of all clients instead of leveraging a unified model as the aggregated knowledge. In terms of federated learning, this might be new.
However, the data synthesis associated with multi-teacher distillation is not new in domain generalization and knowledge distillation fields. The paper itself does not seem contribute significantly to the broader ML community.
Essential References Not Discussed: None.
Other Strengths And Weaknesses: 1. Privacy discussions of the synthetic dataset are based on selected visualization results and FID scores. However, FID is not an official metrics for privacy protecting performance. How does it perform in terms of general quantitative metrics for privacy of FL, such as Gradient Leakage or Differential privacy, if applicable?
Other Comments Or Suggestions: Typo "Table 4.2" -> Table 4 in section 4.3.
Questions For Authors: The aggregated information from clients on server is represented as a synthetic dataset instead of an aggregated model like traditional FL.
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: We sincerely appreciate your review and valuable comments and provide detailed responses to the key concerns:
>**(Privacy Concerns)** *Claims And Evidence #1 & Weaknesses "general quantitative metrics for privacy of FL, such as Gradient Leakage (GL) or Differential privacy (DP)."*
Regarding GL, as discussed in [1] and [2], such attacks occur during the sharing of gradients , where attackers infer client data by analyzing gradients. However, our method does not involve sharing gradients, mitigating the risk of GL.
Regarding DP, because our method only involves uploading local models, aligning with traditional FL, most DP preserving methods in FL can be directly applied to our method. To further validate this, we incorporated the method proposed in [3] to ensure DP and assessed its impact on performance. The following table demonstrate that the DP preserving methods remain applicable to our method without significantly compromising its effectiveness.
|noise level $\epsilon$ | clipart |infograph| painting| quickdraw| real| sketch| average|
| :----: |:----: |:----: |:----: |:----: |:----: |:----: |:----: |
|0| **44.25**| **17.51**| **38.74** |**9.43** |**57.31**| **38.44** |**34.28**|
|20| 43.53| 17.06| 38.49| 9.13| 57.08 |38.15 |33.91|
|50|42.82| 16.73| 37.63 |8.67| 56.51 |37.25 |33.27|
|100| 40.86 |16.04| 35.28| 8.19 |55.68 |35.14| 31.86|
>**(Server Computation Cost)** *Claims And Evidence #2 & Methods And Evaluation Criteria #2: "... much more burdens to the server."*
In FL, the server is generally designed to have sufficient resources to handle the aggregation of client models, but clients often exhibit significant heterogeneity, necessitating constraints on computation costs[5]. Our method adheres to this principle by reducing client burdens.
Additionally, the following table presents a comparision of the server computation costs with other DM-based FL methods. Our method employs local models rather than additional prompts for guiding generation, eliminating the need for compositional diffusion, imposing a lower server computation cost.
| |FedDISC| FGL |FedDEO| OSCAR| FedLMG|
| :----: |:----: |:----: |:----: |:----: |:----: |
|flops (T) |135.71 |102.83| 101.78| 67.85 |**38.87**|
>**(Additional Ablation Experiments)** *Experimental Designs Or Analyses #1: "More ablation experiments are needed to prove the effectiveness of the proposed method."*
We appreciate the reviewer’s suggestion. The following table show that increasing the number of generated images leads to an improvement in the performance. Moreover, we observe that the improvement does not saturate as the dataset size increases, further demonstrating the diversity of the synthetic dataset.
|the number of generated images| clipart |infograph |painting| quickdraw| real| sketch |average|
| :----: |:----: |:----: |:----: |:----: |:----: |:----: |:----: |
|10| 40.77| 15.95 |35.66| 8.51| 55.81| 37.1| 32.3|
|30 |44.25 |17.51 |38.74 |9.43| 57.31 |38.44| 34.28|
|50 |**46.03**| **18.61** |**40.07**| **10.7** |**59.27** |**40.72** |**35.9**|
>**(Multimodality)** *Methods And Evaluation Criteria #1: "... how the proposed method will perform on non-image and other modality datasets."*
Similar to many FL studies[5], we select image as the primary modality in our paper. However, our method is not restricted to the image modality. By utilizing DMs for other modalities such as [6, 7], our method can be seamlessly adapted to other modalities.
>**(Dataset Heterogeneity)** *Experimental Designs Or Analyses #2: "The impact of the heterogeneity of datasets in the paper should be mentioned."*
Dataset heterogeneity in FL primarily manifests as feature distribution skew and label distribution skew [8]. In Tables 1 and 10, we demonstrate the impact of both types of heterogeneities. Therefore, we respectfully disagree with this concern.
>**(Contribution of the Paper)** *Relation To Broader Scientific Literature: "The key contribution of the paper is in the knowledge aggregation part..."*
As stated in the Introduction and acknowledged by Reviewer #A93d and #5oFb, a key advantage of our method is eliminating the need for foundation model inference on clients. We believe this characteristic significantly enhances the practicality of diffusion-based FL methods and represents a meaningful contribution to the field.
[1] Deep leakage from gradients, NIPS 2019.
[2] Understanding Deep Gradient Leakage via Inversion Influence Functions, NIPS 2023
[3] Federated Learning with Differential Privacy: Algorithms and Performance Analysis, TIFS 2020.
[4] FedDEO: Description-Enhanced One-Shot Federated Learning with Diffusion Models, MM 2024.
[5] A survey on federated learning: challenges and applications, IJMLC 2023.
[6] DiffuSeq: Sequence to Sequence Text Generation with Diffusion Models, ICLR 2023.
[7] DiffWave: A Versatile Diffusion Model for Audio Synthesis, ICLR 2021.
[8] Federated Learning on Non-IID Data Silos: An Experimental Study, ICDE 2022. | null | null | null | null | null | null |
A Generalization Result for Convergence in Learning-to-Optimize | Accept (oral) | Summary: This paper proposes a new method for analyzing the generalization ability of learning to optimize (L2O). The authors aim to formulate the convergence of L2O to unseen data as a random event measured by a posterior distribution of neural network's (NN) parameters. By assuming training ensures that the L2O generates a perfect convergence sequence with fast convergence and bounds on solutions, the authors bound the random event's probability by the probability of the convergence event on training data and the KL-divergence between the posterior and prior distributions of NN's parameters before and after training. Experimental results on synthetic test data demonstrate its generalization ability.
## update after rebuttal
I increase my final recommendation (from 2 to 4) due to the following reason:
1. This paper proposes a novel probabilistic perspective to demonstrate the generalization ability of L2O.
2. Although the proposed method imposes some strict conditions on training, the scheme shows that generalization ability can be guaranteed through well-designed training. The success of LLM seems to prove this to some extent.
Claims And Evidence: No. This paper is quite hard to follow. Most technical details are not clearly introduced.
Methods And Evaluation Criteria: No. The optimization problem (i.e., quadratic programming) in the experiment is too simple, which is insufficient to demonstrate that critical condition that training can be easily achieved. For example, non-convex and large-scale optimization problems, e.g., interference reduction problems in wireless communication, are more challenging and harder to converge even in training.
Theoretical Claims: No.
Experimental Designs Or Analyses: Yes. The performance of the proposed method is a little better than Adam's, which may be much worse than other state-of-the-art, e.g., Math-L2O ICML 2023.
Supplementary Material: Yes. Sections except for the proofs.
Relation To Broader Scientific Literature: This paper aims to give a general formulation of the generalization of learning-to-optimize with a probabilistic method. The method is related to the PAC-Bayesian learning theory and the paper Sucker & Ochs (2024). The method is also related to the generalization of neural networks, which is a hot topic in the field of machine learning.
Essential References Not Discussed: No
Other Strengths And Weaknesses: Strength:
1. This paper proposes a new paradigm for generalization demonstration of learning to optimize (L2O). The generalization is formulated as the random event of L2O's convergence on unseen data. The ability of generalization is measured by the posterior probability of convergence. Moreover, the probability is upper bound by the convergence of training and the KL divergence between posterior and prior distributions after and before training.
Weakness:
1. The effectiveness of the proposed method is limited. First, the main theorem, i.e., theorem 7.6 is loose, where the KL-divergence term illustrates the differences in the parameter distribution after and before training, which will be large unless training leads to little change from random initialization. Second, the conditions in lemmas 7.2-7.4 that the theorem relies on are too strict. For example, lemmas 7.2 and 7.3 require the trained L2O to converge fast and lemma 7.4 requires the solution generated by L2O to be bounded by a constant. These conditions are more than the empirical convergence of training but also additionally require a specific shape of sequences generated by L2O, which may be hard to satisfy in practice.
Other Comments Or Suggestions: NA
Questions For Authors: 1. Can you give some explanation for the claim that most functions satisfy KL inequality?
2. Can you demonstrate how training ensures lemmas 7.2-7.4?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We would like to thank the reviewer for taking the time to provide this feedback, even it was unfortunately rather negative.
Regarding the claim that the paper is hard to follow and that most technical details are not clearly introduced:
1) Could you please be more specific here? Otherwise, we cannot improve the paper.
2) In principle, we agree with you that our paper is not straightforward. However, we think that this is rather due to the fact that it combines many advanced and abstract concepts (conditional distributions over the space of trajectories). This is why we have explained our main idea in a separate section, such that it does not get obscured by the technical details. On the other hand, we kindly disagree with the fact that we did not introduce the technical details: We devoted half a page for the notation, and another 1.5 pages just to explain the setup. Besides that, we have provided basically all other needed notions in the appendix or defined them in the text.
Regarding methods, evaluation criteria and the experiments:
1) We do not claim that training the algorithm in such a way that it satisfies the properties of our theorem is actually easy. In fact, we explained in the conclusion that there are cases where it is hard. Since our setting is very abstract and applies to many optimization algorithms, there will probably always be cases where training is hard, and future research should address how to make this simpler.
2) We also train a neural network, that is, a non-smooth non-convex optimization problem.
3) While it is true that the results are only a bit better than Adam, this does not apply to the other experiment. Additionally, the main contribution of this paper are not the experiments; they are just to showcase the validity of our theoretical claims, that is, the generalization and thus convergence of the methods.
Regarding your posed weakness: We agree that there are limitations to the PAC-Bayesian approach. However, these are well-known and people have come up with ways how to circumvent them, for example data-dependent priors. We did not comment on it, because it is well-known and not the actual scope of our paper. \
We partly agree and partly disagree with the claim that the used conditions are too strict:
1) Since these conditions are based on the theorem due to Attouch et al., you basically just claim that this theorem uses unreasonably restrictive assumptions. Additionally, please note that our proof-strategy can be combined with different theorems with potentially milder assumptions!
2) It is true that Lemmas 7.2 and 7.3 are related to the convergence rate of the algorithm. However, most of the time a faster convergence of the learned algorithm is the only reason why we use learning-to-optimize. Thus, claiming that fast convergence is problematic seems not appropriate.
3) We agree that the boundedness condition is problematic. However, this is a common problem also for many conventional optimization algorithms, that is, even the convergence proofs of many conventional optimization algorithms rely on boundedness, such that we do not expect to solve it in this more difficult setting here.
4) We might be mistaken, but it feels like there is a certain confusion: You claim that “These conditions are more than the empirical convergence of training but also additionally require a specific shape of sequences generated by L2O, which may be hard to satisfy in practice.”. Please note that there is a subtle yet decisive problem: *Often you simply cannot observe convergence empirically.* This is due to the fact that convergence is an asymptotic notion and therefore, by definition, not observable in practice. Thus, if we want to judge about it from observations, we need to change the perspective and try to observe properties (the "specific shape" of the trajectory) that allow for *deducing* convergence. And this is accomplished by our theorem.
We would like to point out again that, while these properties are used in our main theorem, a large part of our contribution is actually the *proof-strategy*, which allows to derive similar theorems under different assumptions.
Regarding your questions:
1) E.g, semi-algebraic functions satisfy the KL-inequality. These are “functions whose epigraph can be written as a finite union of sets, each defined by finitely many polynomial inequalities”, which is a very large class of functions. These are the “prototypical nonpathological functions
in nonsmooth optimization” (Drusvyatskiy et al., ”Curves of descent”). Even more generally, functions that are definable in an o-minimal structure or that are tame do satisfy the KL-inequality (for example, see the paper by Attouch et al.).
2) We do not claim that training necessarily ensures these conditions. Actually,sometimes it is hard, which is why future research should solve this. Anyways, one could try an explicit optimization of the parameters a and b.
---
Rebuttal Comment 1.1:
Comment: Thank you for your detailed feedback.
My main concern is for the triviality of the conditions proposed in Lemmas 7.1-7.4 (also Theorem 6.5). Although the presented experiment on meta-train a L2O model to train a $L_2$-norm regression problem with NN, the target NN is too small that its convergence is easy to achieve. However, in general, L2O does not always win. Otherwise, conventional solvers will no longer be used. For example, the famous LISTA [Lecun et al., ICML 2010] still suffers poor convergence on high-dimensional problems.
Moreover, two counterexamples in Appendix B are not sufficient to demonstrate it is non-trivial. I am not sure whether it is a typo or not, the LHS is on iteration $^{(t+1)}$ but not $^{(t)}$. One can easily verify that gradient descent also may violate the condition for some sequences.
However, I agree with the author's statement about the contribution. The rating is updated. | Summary: Learn-to-optimize has been a popular research topic in recent years.
However, many theoretical guarantees are still lacking.
This paper develops a probabilistic framework that resembles
classical optimization and allows for transferring geometric
arguments into learn-to-optimize. The paper establishes
a generalization result for very general loss functions and shows
convergence of learned optimization algorithm to critical points
with high probability. Numerical experiments
are provided for solving a quadratic problem and training neural networks.
Claims And Evidence: Yes.
Methods And Evaluation Criteria: Yes.
Theoretical Claims: The paper seems to be correct though I didn't check the proofs in details.
Experimental Designs Or Analyses: Yes.
Supplementary Material: Yes.
Relation To Broader Scientific Literature: Learn-to-optimize has been a popular research topic in recent years.
However, many theoretical guarantees are still lacking.
This paper develops a probabilistic framework that resembles
classical optimization and allows for transferring geometric
arguments into learn-to-optimize to fill in this gap.
Essential References Not Discussed: N.A.
Other Strengths And Weaknesses: Strengths
(1) The paper is well-written.
(2) The theory is accompanied by experiments.
(3) The theory is rigorously derived by paying a lot of attention to the technical details.
For example, the paper devotes an entire Section 7.1. to show measurability condition
holds in order to apply some existing results. A measurability condition is often taken
as granted. But the paper digs deep into checking this technical condition, and provides
a very details and non-trivial proof in the Appendix.
Weaknesses
(1) The proofs of the main results seem to be direct consequence by applying
Theorem 6.3. and Theorem 6.5 that are both available from the recent literature.
This makes the paper seem to be an application built upon the very recent literature
and makes the contributions less significant.
(2) The paper mentions four weaknesses in the conclusion section, which is fair and honest.
I think some of the weaknesses seem to be inherent. But some might be overcome which
can be left as future research directions.
Other Comments Or Suggestions: (1) In Theorem 6.3. and later Theorem 7.6., $\Phi_{a}^{-1}(p):=\frac{1-\exp(-ap)}{1-\exp(-a)}$ plays a central role.
It would be nice if you can provide some intuition explanations what this function $\Phi_{a}^{-1}(p)$
is about and where it comes from.
(2) In the references, please be more consistent. For example, In Langford and Caruana, the booktitle is capitalized,
but not in Langford and Shawe-Taylor. In addition, the book name by Nesterov should be capitalized.
(3) In the proof of Lemma 7.1., you wrote $B_{\varepsilon}(p,z)$ ult. What is ult.?
Questions For Authors: N.A.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We would like to thank the reviewer for giving this feedback, and we would like to take the opportunity to shortly comment on the weaknesses and to answer the questions.
Regarding your first posed weakness: It is true that, on an abstract level, in the end the result follows by combining Theorems 6.3 and 6.5. However, we think that it is still a significant step, because:
1) There is a very subtle problem with convergence results: In general, convergence is an asymptotic notion, that is, it belongs to the so-called tail-$\sigma$-algebra and therefore is *simply not observable* in practice. Thus, if we want to judge about convergence based on observations during training, we need to observe properties that allow to *deduce* convergence again. And this is accomplished by our new proof-strategy.
2) You have to know both results, which are both rather abstract and advanced in their respective fields (PAC-Bayes and non-smooth non-convex optimization), and you have to combine them in the correct way, that is, you have to see that all resulting properties have to be phrased as sets in the space of trajectories. Since we have done it now here, it will also be comparably easy to adapt for follow-up work.
4) You have to do the proofs, which are by no means trivial in this abstract setting dealing with
spaces of sequences.
Lastly, we want to point out that this proof-strategy is actually also part of our contribution. It bridges the gap between conventional optimization theory and generalization bounds. And finding a completely new proof-strategy is often harder than adapting an existing one to a new problem.
Regarding your second posed weakness: We do not fully understand why you regard this as a weakness of our paper? Could you elaborate on that?
Regarding your comments:
1) The function $\Phi_a$ is related to the log-Laplace transform of a Bernoulli random variable (see Catoni (2007)). This in turn is related to the moment-generating function, which can be used to characterize how the random variables concentrates. And this is commonly used to get generalization
results. $\Phi_a$ and $\Phi_a^{-1}$ a were both introduced like this by Catoni (2007). \
2) Thanks for the hint! We will check and update the references. \
3) “ult.” is an abbreviation for “ultimately” and refers to the fact that the sequences only ultimately have to lie in the ball with radius ϵ, that is, asymptotically (this is why we have this union/intersection over all iterates in the definition). This notation is used in analogy to the notation from probability theory (for example, see Kallenberg). | Summary: While learning-to-optimize has shown to be a powerful paradigm to enhance the efficiency of the optimisation phase for problems similar to the one encountered during training, it is unsure how such a trained algorithm will behave on unseen problems with different internal structure. This work tackles this issue by proposing a novel PAC-Bayes generalization bound for the learning-to-optimize problem when the considered learning algorithm possesses a Markovian structure and that the (potentially non-smooth, non-convex) loss satisfies the Kurdyka-Lojasiewicz condition.
Claims And Evidence: This is a truly solid mathematical paper, with a well-explained and convincing proof-strategy. I read the proof of measurability of Section 7 which are well-written, sound and rigorous.
Methods And Evaluation Criteria: I did not check the experimental protocol, however the nature of the problem (quadratic or small neural networks) look reasonable.
Theoretical Claims: Once the setup of measurable events is well-posed and proof of the main-results are a quite straightforward combination of results of Catoni 2007 and Attouch et al. 2013.
Experimental Designs Or Analyses: No.
Supplementary Material: I checked the measurability proofs of Section 7, which are, to me, rigorous and correct.
Relation To Broader Scientific Literature: Could the authors expand a bit more on the comparison between your results and those of Sucker&Ochs 2024, which looks quite close according to what you say. Would it be possible to state such a theorem in the appendix to highlight the originality of your contribution?
Essential References Not Discussed: I do not know enough Sucker & Ochs 2024 and the associated references to be aware of the SOTA in the links between PAC-Bayes and learning-to-optimize.
Other Strengths And Weaknesses: None, this is a good theoretical paper involving an innovative use of PAC-Bayes. However, I may overestimate the novelty of those techniques as I was not aware of Sucker&Ochs 2024
Other Comments Or Suggestions: None.
Questions For Authors: - Would it be possible to discuss more the influence of the prior in Theorem 6.3 and 7.6?
- The reference (Theorem 42, Sucker&Ochs 2024) for theorem 6.3 does not seem correct, can you update it?
- In Theorem 7.6 is it possible to implement the sum $\frac{1}{N}\sum_{i=1}^N \mathbb{P}\_{(P,\xi)| H}(A^c)$ can you expand on it?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Also here, we would like to thank the reviewer for taking the time to provide this feedback. We are glad that you considered the proof-strategy as “well-explained”, because it is one of our main contributions.
Regarding your question whether we could expand a bit more on the comparison between our results and those of Sucker&Ochs (2024): First, while Sucker&Ochs state Theorem 42, they only use it for a small remark, where they explain that this result can be used to bound a function r that is used to estimate something like a linear rate of convergence. If one would perform a similar analysis
as we have done here for the case that a) the loss function has a unique minimizer and b) the algorithm does indeed converge with a linear rate, this could be used to deduce convergence, which, however, Sucker&Ochs also left completely unaddressed. \
Furthermore, this setting would be a very specific case in which you can get convergence by just observing a certain function-value. In general, however, this is not the case, due to the following subtle problem: Convergence is an asymptotic notion, such that it belongs to the so-called tail-$\sigma$-algebra, that is, in practice it is *inherently non-observable*. Thus, if we want to judge about convergence from observations during training, we need to switch the perspective and try to observe properties, that allow to *deduce* convergence again. And this is what our proof-strategy accomplishes. Although this difference is very subtle, it is still crucial. For L2O this applies in particular to the non-smooth and non-convex case, because the (sub-)gradient does not necessarily say anything about the distance to a critical point. \
Additionally, we would like to point out that part of our contribution is also to show how we can actually combine results from conventional optimization theory with generalization results, such that it can be adapted to other cases quite easily.
Regarding the follow-up question of whether we could state such a theorem in the appendix to highlight the originality of our contribution: What exactly do you mean by “such a theorem”? Theorem 6.3 is the theorem by Sucker&Ochs.
Regarding the discussion of the prior: The prior is highly important, because the generalization bound is more tight, if the posterior stays close to prior (KL-term is smaller). On the other hand, this means that the prior should already yield some reasonable
performance. Therefore, a well-known remedy is that one typically has a two-step learning process: First, the prior gets optimized to yield a reasonably good performance and then the posterior gets chosen, which provides the guarantee.
We did not comment on it, because it is not the actual contribution of our paper and the approach is already well-known.
Regarding your comment that the reference (Theorem 42, Sucker& Ochs 2024) for Theorem 6.3 seems to be wrong: We think it is correct. Maybe it is confusing, because Sucker&Ochs are again referencing to Catoni (2007). However, we think that this is just to acknowledge that their result turns out to be basically the same as the one by Catoni (who considered Bernoulli random variables).
Regarding your question for Theorem 7.6: In our case, the conditional probability is simply an indicator-function (note that in your comment there is a $P_n$ missing!), because the algorithm is deterministic and everything else is given from the data. So it turns into an empirical mean over indicator functions. However, we did state it in this more general version, because the proof-idea could also be used for stochastic algorithms, in which case one would have to estimate the probability, for example over several runs of the algorithm. | Summary: This paper presents a probabilistic framework to establish convergence guarantees for L2O algorithms, addressing the challenge that conventional geometric arguments for convergence do not readily apply to learned optimizers. The key contribution is a generalization result that combines PAC-Bayesian learning theory with variational analysis, specifically leveraging the KL inequality, to show that L2O algorithms converge to critical points with high probability. The authors develop a novel proof strategy that translates worst-case convergence analysis into a probabilistic setting, removing the need for restrictive safeguard mechanisms in algorithm design. Experimental results on quadratic optimization problems and neural network training demonstrate that the learned optimizers outperform traditional methods such as heavy-ball acceleration and Adam, while the PAC-Bayesian framework provides nontrivial guarantees on their generalization.
## update after rebuttal
The author's response has persuaded me that this is strong work, so I'm increasing my score from 3 to 4.
Claims And Evidence: Yes.
Methods And Evaluation Criteria: Yes.
Theoretical Claims: I did not verify all the proofs in detail, but based on a high-level review, they appear to be reasonable.
Experimental Designs Or Analyses: The experiments appear to be sound.
Supplementary Material: I have reviewed some key proofs in the supplementary material.
Relation To Broader Scientific Literature: L2O has been widely studied as a means of leveraging machine learning to design optimization algorithms that adapt to specific problem structures, with earlier works focusing on empirical performance but lacking rigorous convergence guarantees. This paper advances the field by introducing a probabilistic framework that integrates PAC-Bayesian generalization theory with variational analysis to provide convergence guarantees in generalization. Prior works on PAC-Bayesian learning have established generalization bounds for learning-based methods, and KL-based convergence analysis has been used in traditional optimization, but their combination in the context of L2O is novel. Additionally, the paper addresses limitations of safeguard-based approaches, which constrain learned optimizers to fit classical convergence analyses, by formulating a more flexible probabilistic guarantee.
Essential References Not Discussed: No.
Other Strengths And Weaknesses: Strengths
1. The paper tackles a really interesting and important problem—the convergence of L2O. This is an open question that very few papers have addressed, despite L2O’s growing popularity. Most work in this area has focused on empirical performance without theoretical guarantees, so I appreciate that this paper makes an effort to analyze convergence, which is a crucial missing piece in the field.
2. I also like the core idea of the paper—moving away from traditional geometric analysis, which often requires the learned optimizer to have specific properties that may not hold in practice. Since L2O relies on neural networks, their outputs are difficult to control, and enforcing geometric constraints can limit their flexibility. Instead, this paper uses a PAC-Bayesian framework combined with the KL inequality, which provides a more natural way to study convergence without imposing artificial restrictions. This makes the approach both theoretically interesting and practically relevant.
Weaknesses
1. One key assumption in this paper is that L2O converges on the training set, and the main focus is on whether this convergence generalizes to new optimization problems. While this assumption is reasonable and intuitive, it is itself an open question that remains unaddressed. The paper does not explore whether or under what conditions L2O is actually guaranteed to converge during training, which makes the overall analysis feel somewhat incomplete. I understand that this is beyond the scope of the paper, as the focus is on generalization rather than training dynamics, but leaving this assumption undiscussed does create some discomfort. This issue is particularly important because L2O training is not a trivial process. The convergence of NN training itself is already a complex and open problem, with theoretical frameworks like NTK providing some insights but requiring unrealistic infinite-width assumptions. L2O, being an even more complex NN that integrates both the optimization process and neural network prediction, presents a significantly harder convergence problem than standard architectures like MLPs, which are already difficult to analyze. Given this, the absence of a solid consensus on the convergence of L2O during training greatly weakens confidence in the overall framework presented in the paper.
2. The presentation of the paper could be significantly improved. The structure feels disorganized, making it harder to follow the key ideas and contributions. Some sections could be better structured to improve clarity, and certain explanations—especially in the theoretical parts—could be made more intuitive. A clearer organization would help readers grasp the core insights more effectively.
Other Comments Or Suggestions: N.A.
Questions For Authors: N.A.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We would like to thank the reviewer for taking the time to provide this detailed feedback.
We shortly want to comment on the stated weaknesses:
We agree that such convergence guarantees are highly desirable, but we also think that
this is asking for too much: We are considering an abstract algorithm (think of a neural network) and an
abstract loss function, and such an analysis is typically performed in a problemspecific
way, even for conventional optimization algorithms. Thus, while we could
provide hypothetical examples that explain our contributions for a concrete setting,
we do not think that we can prove the convergence of such a learned
method in general, also because it additionally is influenced by the used training
procedure. Further, if we could perform such an analysis and provide the
corresponding guarantees, we might be able to do the same for the test data,
such that we would not even need the generalization anymore. However, the
key idea is exactly that we acknowledge the fact that we are often not able to perform
such an analysis, in which case we have to rely on observations during training. And for these cases we can apply our generalization result,
which is widely applicable, exactly because our setting is so abstract. \
Furthermore, how to train optimization algorithms
so that they do satisfy these convergence-ensuring properties for most of the
training data is actually also part of future research. \
Lastly, we want to stress again that a large part of our contribution is also the *proof-strategy* which,
after it has been established, can be applied or adapted quite easily to several
different applications. Here, we want to emphasize one thing, because the problem is very subtle: For many applications, convergence of the learned algorithm is a so-called asymptotic event and belongs to the tail-$\sigma$ algebra, that is, by definition it is *practically impossible* to observe it directly. Thus, if we want to judge about it based on observations (like in L2O), we need to observe something that allows us to *deduce* it. And this is exactly what our strategy is exploiting.
Regarding your claim that the presentation could be significantly improved:
Could you please be a bit more concrete here? We are of course always interested
in improving the clarity of our paper, but, like this, it is rather hard to see which
parts should be restructured or presented differently, such that, for now, we would
rather kindly disagree with this remark. For us, the paper has a clear inherent
flow, which is the following:
1) Start of the paper (introduction/motivation + related work)
2) Presentation of main idea in a simplified way, so that readers can grasp it
more easily.
3) Notation and background material, such that claims can be made rigorous.
4) Recalling main idea and concretizing it for the setting of learning-to-optimize
(lemmas preparing the main result + main result)
5) Experiments
---
Rebuttal Comment 1.1:
Comment: Thank you for the detailed response. I think the paper would benefit from expanding Section 4 to better highlight the core idea in a more intuitive way, without too much mathematical detail. It would also be helpful to include more discussion on the convergence behavior of L2O during training, even if only at a high level. Overall, this is a solid contribution, and I have raised my score to 4. | null | null | null | null | null | null |
New Bounds for Sparse Variational Gaussian Processes | Accept (spotlight poster) | Summary: The authors introduce a tighter ELBO bound for inducing-point-based Gaussian process regression à la SVGP (Titsias 2009) and its mini-batchable extension (Hensman et al. 2013). The main idea is to use a more flexible ansatz for $q({\bf f} | {\bf u})$ than the conditional prior $p({\bf f} | {\bf u})$, in particular by introducing $N$ variational parameters into the covariance of $q({\bf f} | {\bf u})$, where $N$ is the total number of training data points. This leads to a small change in the form of the ELBO while retaining the same computational cost as SVGP and retaining mini-batchability in the case of the tightened Hensman-et-al-like objective (i.e. in the case where $\bf u$ is not integrated out optimally). The authors provide a careful discussion of how the new bound differs from previous alternative bounds. The authors also consider how this construction can be applied to the setting with a non-gaussian likelihood. Experiments suggest that the new method can lead to higher ELBOs and better predictive distributions in practice.
Claims And Evidence: The main claims made by the authors are that their method can:
1. reduce bias when learning the hyperparameters of the kernel
2. can lead to better predictive performance
3. result in tighter ELBOs
I would say that the evidence for 2 and 3 is convincing, while the evidence for 1 is somewhat weak. If this is to be a central claim of the submission, it should be supported with more empirical evidence, in particular in the simulated data setting where "bias" has a particularly straightforward meaning.
Methods And Evaluation Criteria: While the empirical evaluation is not extraordinarily extensive, it is enough to convince me of the basic soundness and advantages of the proposed approach. Nevertheless, I would love to see the experiments and/or reported results extended in a few directions:
- The authors note the tendency of SVGP to overestimate the observation noise and provide hints that the new objective lessens this bias. It would be great to see a more extensive study of this particular question, especially on simulated data, and reporting more detailed results for other kernel hyperparameters (e.g. the learned kernel scale).
- I would love to get more details on the nature of the learned $v$s. Can the authors report a histogram and/or summary statistics for a few sample cases? Similarly in the non-gaussian case where $v$ is a scalar, what values of $v$ are you finding in practice? It's perhaps somewhat surprising to me that a single additional degree of freedom in the variational distribution can have the moderately large effect we can read off from Figure 3 (though in truth without predictive NLLs and the like it's a bit hard to measure the magnitude of the improvement/effect).
Theoretical Claims: I have not checked the derivations in detail, but they are all intuitive/non-surprising and as such I have no reason to doubt their correctness.
Experimental Designs Or Analyses: The setup of the experiments seems to follow best practices and otherwise looks sound. (Though personally I would never use a fixed Adam learning rate of $0.01$ without decaying it at least to some extent, as this is generically unlikely to result in particularly well-optimized objectives).
Supplementary Material: I only skimmed the derivations and the description of the experimental setup.
Relation To Broader Scientific Literature: The discussion of related work and how this new bound fits into the existing methodological landscape is extensive, very clear, and generally excellent.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: I would like to again stress the great clarity of the manuscript and thank the authors for taking the time to write a very clear and well-argued manuscript.
Other Comments Or Suggestions: - typo in abstract: "hyperpaparameters"
- typo in sec 3.2: whiten => whitened
- typo: "intiliazed" in Fig 1
Questions For Authors: Have you considered adding a new $N$-dimensional "mean shift" variational parameter to your ansatz for $q({\bf f } | {\bf u})$? In particular this would mean using a mean of $\bf K_{fu} K^{-1}_{uu} u + \Delta$ for ${\bf \Delta} \in \mathbb{R}^N$. This would seem to be a natural companion to your adjustment of the covariance matrix. And the exact form for $p({\bf f}|{\bf u}, {\bf y})$ in Sec. 3 suggests that there should be some slackness in the ELBO resulting from using the prior conditional mean without any modification. Granted this new parameter might conceivably be difficult to optimize (say because its entangled with the variational mean for ${\bf u}$), or such a modification may have little effect on ELBO tightness or the learned hyperparameters or the learned predictive distribution, but from a methodological point of view it seems a very natural question to ask, so its omission is unfortunate. Why not satisfy the reader's curiosity?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for the insightful comments.
> I would say that the evidence for 2 and 3 is convincing, while the evidence for 1 is somewhat weak. If this is to be a central claim of the submission, it should be supported with more empirical evidence, in particular in the simulated data setting where "bias" has a particularly straightforward meaning.
> The authors note the tendency of SVGP to overestimate the observation noise and provide hints that the new objective lessens this bias. It would be great to see a more extensive study of this particular question, especially on simulated data, and reporting more detailed results for other kernel hyperparameters (e.g. the learned kernel scale).
We provide here the learned hyperparameters for the 1-D Snelson dataset:
| Noise Variance | Scale/amplitude | Lengthscale|
Exact GP | 0.0715 | 0.712 | 0.597 |
SVGP-new | 0.087 | 0.485 | 0.615|
SVGP | 0.108 | 0.331 | 0.617 |
which show that SVGP-new has less bias than SVGP in this example. We plan to add further simulated regression examples
in the appendix by following Reviewer's suggestion.
> I would love to get more details on the nature of the learned vs. Can the authors report a histogram and/or summary statistics
Yes, we can add histograms for the learned $v_i$s for some of the GP regression datasets (e.g. Snelson, Pol, Bike, Elevators) in the appendix. We give here some summary statistics (min, median and max values) of the learned $v_i$s for the 1-D Snelson example (from Figure 1):
|min | median | max |
|0.172 | 0.952 | 0.9998 |
This indicates that there are few $v_i$s having quite small values but most of them are close to one in this example. We will update the Appendix to add histograms that visualize the final values of $v_i$s.
Regarding the scalar values of $v$ for the non-Gaussian Poisson regression runs, we report here the
learned values. For the toy Poisson regression the learned value was around $v=0.675$. Interestingly, for the real Poisson example in NYBikes, the value gets very small below $0.01$. Perhaps this suggests that in this example the expected Poisson log-likelihood reconstruction term has a very strong influence in ELBO optimization, so that the optimization prefers to set $v$ very small (which allows to reduce the posterior variance in $q(f_i)$ since the term $v( k_{ii} - q_{ii})$ becomes small). If the number of inducing points becomes sufficiently large and each $k_{ii} - q_{ii}$ becomes small, then of course the learned $v$ will become close to 1.
| Have you considered adding a new $N$-dimensional "mean shift"
This is a great suggestion. Yes, we tried to do this but we were unable to find to way to add a drift vector $\Delta$ that gives a computational efficient ELBO of $O(N M^2)$ cost. Here, is a short derivation of this. In the KL divergence $KL[q(f|u) || p(f|u)]$ and since the $q(f|u)$ and $p(f|u)$ do not have the same mean anymore the term $\frac{1}{2} \Delta^\top (K_{f f} - Q_{f f })^{-1} \Delta$ appears which has $O(N^3)$ cost. If we try to add some preconditioning to $\Delta$, e.g., $(K_{ff } - Q_{ff})^{1/2} \Delta$ then the $O(N^3)$ remains (although this time will appear in the expected log-likelihood term). We can add an appendix about these derivations, since they could be useful for future research. | Summary: The paper revisits the widely-used variational approximation for sparse Gaussian processes (GPs). It proposes a refined variational formulation, introducing a more flexible conditional posterior distribution in place of the traditional assumption (where the conditional posterior matches the prior). This adjustment results in a tighter variational bound on the marginal likelihood, improving inference quality. Additionally, the method naturally supports stochastic mini-batch optimization, making it scalable to large datasets and practical for a broader range of applications.
Claims And Evidence: Yes, the claims made in the submission are supported by clear and convincing evidence. The paper provides a well-structured theoretical foundation for the proposed variational approximation, including a derivation that justifies the tighter variational bound.
Methods And Evaluation Criteria: Yes, mainly. The proposed methods and evaluation criteria are appropriate for the problem at hand, and the experiments effectively demonstrate the benefits of the tighter variational bound. However, the datasets used in the evaluation seem somewhat simple, and the paper could have further strengthened its empirical validation by including a more complex benchmark, such as MNIST or a real-world dataset. This would provide additional evidence of the method’s scalability and effectiveness in practical applications.
Theoretical Claims: I went over the proofs, and they appear to be correct. The derivations follow standard results from the literature, and the steps are well-structured and logically sound.
Experimental Designs Or Analyses: NA
Supplementary Material: I skimmed over the supplementary material
Relation To Broader Scientific Literature: Yes, the key contributions of the paper are well-situated within the broader scientific literature.
Essential References Not Discussed: There is another paper that was released at a similar time that essentially uses the same formulation and results in very similar findings. While I understand that this work can be considered concurrent, it would be beneficial for the authors to acknowledge and discuss this related research. Including a mention of this paper would provide readers with a clearer understanding of how the contributions of this work fit into the broader context and help differentiate any unique aspects of the approach.
Tighter sparse variational Gaussian processes, Bui et al (2025), Under review TMLR.
Other Strengths And Weaknesses: The main strength of the paper lies in its effort to improve the approximation of sparse variational Gaussian processes (SVGP), a crucial technique for scaling Gaussian processes. Additionally, the experimental results on benchmark datasets are compelling, providing strong empirical support for the proposed method. The paper is well-written, and the core idea is clearly explained.
The main weakness of the paper is that the results demonstrate only marginal improvements with the new bound across all evaluated tasks, without a clear example where the standard approach would fail without it. This makes it difficult to assess the practical necessity of the proposed refinement. Additionally, in the non-Gaussian likelihood setting, the paper opts for a simpler approximation rather than leveraging the more expressive variational form, seemingly due to computational constraints.
Other Comments Or Suggestions: - Table 2 is confusing. The top methods are baselines but have nothing to do with your method I assume. The bottom methods both have ours but isn't your method only SVGP-new?
Questions For Authors: - When moving to the minibatch setting, the paper is essentially minibatching a KL term for the $q(f|u)$. How does this work exactly and how do you scale all the terms.
- It’s unclear how the hyperparameters interact with the new approximation. Do they lead to better-calibrated predictive variances? Providing more details or empirical results on this aspect would help clarify the impact of the proposed method.
- In the non-Gaussian case, the paper resorts to the standard SVGP prediction, as using the proposed approach directly would be computationally too expensive. This suggests that the main benefit of the method in this setting is primarily improved hyperparameter estimation rather than a fundamentally better approximation of the posterior. If so you should also mention some related work in this ara.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We would like to thank the reviewer. We respond to the main comments below.
> Yes, mainly. The proposed methods and evaluation criteria are appropriate for the problem at hand, and the experiments effectively demonstrate the benefits of the tighter variational bound. However, the datasets used in the evaluation seem somewhat simple, and the paper could have further strengthened its empirical validation by including a more complex benchmark, such as MNIST or a real-world dataset. This would provide additional evidence of the method’s scalability and effectiveness in practical applications.
Thank you for this comment. Here, we have focused mainly on the GP regression, large GP regression and we provide
also an experiment with Poisson regression which is a non-Gaussian likelihood example.
> The main weakness of the paper is that the results demonstrate only marginal improvements with the new bound across all evaluated tasks, without a clear example where the standard approach would fail without it. This makes it difficult to assess the practical necessity of the proposed refinement. Additionally, in the non-Gaussian likelihood setting, the paper opts for a simpler approximation rather than leveraging the more expressive variational form, seemingly due to computational constraints.
Please note that we do observe noticeable improvements in predictive performance in some experiments (Pol, Bike, Kin40k, Protein, Buzz). For some datasets, like Pol and Kin40k, the improvement is significant. We believe that a very practical feature of the new ELBO is that in GP regression it requires a minor modification to existing code. So a practitioner can easily train a GP with the new ELBO
while keeping the computational cost the same as in the previous SVGP bound.
> Tighter sparse variational Gaussian processes, Bui et al (2025), Under review TMLR.
Thank you for pointing to concurrent work. We will cite this work in the next version of our paper.
> Table 2 is confusing. The top methods are baselines but have nothing to do with your method I assume. The bottom methods both have ours but isn't your method only SVGP-new?
We agree with the reviewer. We will modify the table to keep "ours" only for SVGP-new as suggested by the reviewer. The upper part of table gives two strong baselines from the literature (discussed in the first paragraph in the Related Work) that are based on different-type of extensions of the SVGP that allow to increase the number of inducing points. Indeed, they are unrelated to our method which replaces
$p(f|u)$ by $q(f|u)$, but we have included them for comparison reasons.
> When moving to the minibatch setting, the paper is essentially minibatching a KL term for the $q(f|u)$
. How does this work exactly and how do you scale all the terms.
Starting from the following expression for the ELBO (Equation 18 in the paper)
$$
\sum_{i=1}^N \left( E_{q(u)} [\log \mathcal{N}(y_i | k_{f_i u} K_{u u}^{-1} u, \sigma^2 )] - \frac{1}{2} \log (1+\frac{k_{ii} - q_{ii}}{\sigma^2}) \right) - \text{KL}[q(u) || p(u)],
$$
we observe that each term in the sum (i.e., the full term inside the big brackets) depends only on a single data point $(x_i, y_i)$, which is what is needed for minibatch training. Based on this, we can obtain an unbiased ELBO (and gradient) using a minibatch of $b$ data as
$$
\frac{N}{b} \sum_{i \in minibatch} \left( E_{q(u)} [\log \mathcal{N}(y_i | k_{f_i u} K_{u u}^{-1} u, \sigma^2 )] - \frac{1}{2} \log (1+\frac{k_{ii} - q_{ii}}{\sigma^2}) \right) - \text{KL}[q(u) || p(u)],
$$
where note also that $E_{q(u)} [\log \mathcal{N}(y_i | k_{f_i u} K_{u u}^{-1} u, \sigma^2 )]$ is analytic. We can include an appendix to describe the above details.
> It’s unclear how the hyperparameters interact with the new approximation. Do they lead to better-calibrated predictive variances? Providing more details or empirical results on this aspect would help clarify the impact of the proposed method.
After training with the new ELBO, we still use the previous standard SVGP predictive density as discussed in Section 3.1.
So the only difference is that the new ELBO can provide different hyperparameters (and inducing inputs $Z$). Figure 1 and Table 1, 2 indicate that this can lead to better predictions in terms of test log-likelihoods. We can try to add an ablation to further study
the effect on the predictive variances.
| In the non-Gaussian case, the paper resorts to the standard SVGP prediction, as using the proposed approach directly would be computationally too expensive. This suggests that the main benefit of the method in this setting is primarily improved hyperparameter estimation rather than a fundamentally better approximation of the posterior. If so you should also mention some related work in this ara.
Just to clarify here that for both Gaussian and non-Gaussian likelihoods we do predictions with previous SVGP predictive
equations. We can clarify this further in the paper. | Summary: The paper introduces new evidence lower bounds (ELBOs) for sparse variational Gaussian processes (SVGP) by relaxing the traditional assumption that the variational distribution must factorize with the conditional GP prior p(f|u). Instead, the authors propose a more flexible variational distribution q(f|u), which allows for a tighter bound. Theoretical analysis shows that the new bound is provably tighter than previous SVGP bounds, and experiments on regression and non-Gaussian likelihood tasks demonstrate improved hyperparameter learning and predictive performance. However, the proposed methods between theoretical analysis and practical experiments are slightly different, which reduces the soundness of this paper. The practical method is computationally efficient, requires minimal code modifications, and is compatible with stochastic optimization.
Claims And Evidence: The claims are supported by clear theoretical derivations (Lemmas 3.1–3.3, Proposition 3.5) and extensive experiments. The theoretical proofs are straightforward, and experiments on synthetic/real-world datasets (e.g., Snelson, UCI datasets, NYBikes) validate reduced bias in hyperparameters (e.g., noise variance) and better test log-likelihoods.
Methods And Evaluation Criteria: The methods are appropriate for scalable GP inference. The evaluation uses standard metrics (test log-likelihood, RMSE) and datasets (UCI, Kin40k), with comparisons to common baselines (SGPR, SVGP, SOLVE-GP). Experiments include multiple trials to report standard errors, ensuring statistical reliability.
Theoretical Claims: The key insight, replacing p(f|u) with a diagonal-covariance q(f|u), is sound. However, the gap between diagonal V and spherical V is not thoroughly assessed.
Experimental Designs Or Analyses: The comprehensive experiments cover regression (Gaussian/non-Gaussian) and varying dataset sizes.
Supplementary Material: NA
Relation To Broader Scientific Literature: The work builds on SVGP, positioning the new bound as a tighter alternative. This applies to all of the sparse GP utilizing the inducing points.
Essential References Not Discussed: NA
Other Strengths And Weaknesses: NA
Other Comments Or Suggestions: Typos: "hyperpaparameters" (Abstract), "minibathes" (Section 3.2).
Questions For Authors: The insight presented in this paper is promising, but the details may require further discussion. The key question is: to what extent does assuming a spherical V influence the results? The potential risks associated with this assumption are not explored, nor is there a theoretical or experimental analysis addressing its impact.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for your comments. Below we provide some responses.
> The key insight, replacing $p(f|u)$ with a diagonal-covariance $q(f|u)$, is sound. However, the gap between diagonal V and spherical V is not thoroughly assessed.
Please note that in the medium-size regression experiments reported in Table 1 and Figure 2 we do compare with the method that assumes spherical $V = v^* I$ which uses the optimal scalar value $v^* = \left( 1 + \frac{\text{tr}(K_{f f} - Q_{f f})}{N \sigma^2} \right)^{-1}$. This is precisely, the method denoted in the experiments as "SGPR-artemev". We will clarify this further in the paper. Note, that currently we briefly explain the spherical case $V = v I$ for GP regression and the connection with Artemev et al's bound in Related Work (Section 4) and also in Appendix B.4. From Table 1 and Figure 2 we can observe that diagonal V does work better than the scalar $v$.
> The insight presented in this paper is promising, but the details may require further discussion. The key question is: to what extent does assuming a spherical V influence the results? The potential risks associated with this assumption are not explored, nor is there a theoretical or experimental analysis addressing its impact.
We agree with the reviewer that the fact that the non-Gaussian likelihood case requires spherical $V = v I$ is not ideal. In seems that for such non-Gaussian likelihoods the only option that works is to use a spherical $V = v I$ and, as explained in Section 3.3, the diagonal $V$ (that works for GP regression) has cubic cost when trying to obtain each marginal $q(f_i)$. Notice also that if someone heuristically tries to use diagonal $V$ for the non-Gaussian likelihood case and approximate the marginal $q(f_i)$ by
$$
q(f_i) = \mathcal{N}(f_i | k_{f_i u} K_{u u}^{-1} m, v_i (k_{ii} - q_{ii}) + k_{f_i u} K_{u u}^{-1} S K_{u u}^{-1} k_{u f_i}),
$$
(which is not the correct marginal under $q(f|u) q(u)$ since the variance term $v_i (k_{ii} - q_{ii})$ is wrong) then this creates an inconsistency in the variational distribution in the ELBO, since the $q(f_i)$ used to compute the expected log-likelihood term will be inconsistent with the $q(f|u) q(u)$ in the KL divergence term $KL[q(f|u) q(u) || p(f|u) p(u)]$), and the objective is not a rigorous ELBO anymore.
We can add further discussion to clarify that the spherical $V= v I$ is needed for non-Gaussian likelihoods in order to obtain a rigorous ELBO. | Summary: The authors present an improvement on the standard SVGP approximation by departing from the standard conditional GP prior distribution. The approach introduces an additional $N$ variational parameters which modify the covariance matrix of the conditional distribution. This leads to an improvement on the resultant bound for the log marginal likelihood. The authors demonstrate that their method works in the stochastic minibatch optimisation setting, and can be extended effectively to non-Gaussian likelihoods by judicious constraints on the additional variational parameters. The theoretical findings are shown to hold in practice on a number of small to large scale regression experiments.
Claims And Evidence: Yes---claims are theoretical and demonstrated through experiments.
Methods And Evaluation Criteria: Yes.
Theoretical Claims: Yes.
Experimental Designs Or Analyses: Yes.
Supplementary Material: No.
Relation To Broader Scientific Literature: N/A.
Essential References Not Discussed: N/A.
Other Strengths And Weaknesses: ## Strengths
* The proposed approach is novel (together with https://arxiv.org/abs/2502.04750 which, coincidentally, was released at the same time), straightforward to both understand and implement, and effective in practice, demonstrating improved or on-par performance relative to baselines across almost all experiments. Collectively, the paper is very convincing.
## Weaknesses
* A key strength of the proposed method is in its generality---I suspect that it can be applied to improve a wealth of SVGP approximations such as SOLVE-GP, and different forms of approximations such those used for SVGP-LVMs and Deep-SVGPs. I believe that further extensions in the paper would improve it further, although the authors do touch upon this as future work.
Other Comments Or Suggestions: N/A.
Questions For Authors: N/A.
Code Of Conduct: Affirmed.
Overall Recommendation: 5 | Rebuttal 1:
Rebuttal: Thank you for very accurately describing the contribution of the paper and for pointing to concurrent work. As also mentioned in the response to Reviewer Pyzb below, we plan to discuss the concurrent work in the next version of our paper. | null | null | null | null | null | null |
Adapter Naturally Serves as Decoupler for Cross-Domain Few-Shot Semantic Segmentation | Accept (spotlight poster) | Summary: The paper proposes utilizing an adapter for cross-domain few-shot semantic segmentation. The authors first demonstrate that the adapter naturally serves as a decoupler, and then design a DFN network to decouple source domain information into domain-agnostic and domain-specific components. They also propose SAM-SVN to mitigate potential overfitting issues of DFN on the source samples, achieving good performance.
Claims And Evidence: The claims made in the paper is that the adapter naturally serves as a decoupler for domain-specific information. The authors provide detailed experiments and analysis to support this claim.
Methods And Evaluation Criteria: The proposed method is well explained, and the evaluation criteria and datasets used are appropriate for the task.
Theoretical Claims: There are no theoretical claims.
Experimental Designs Or Analyses: The main experiments are comprehensive and demonstrate the effectiveness of the proposed method. However, since SAM-SVN requires an additional forward-backward computation that may be computationally expensive, it would be useful to compare the model's computational efficiency with other baselines.
Supplementary Material: I reviewed the additional results provided in the supplementary material.
Relation To Broader Scientific Literature: The proposed designs complement the broader literature and introduce new designs.
Essential References Not Discussed: The following papers are related to the model’s hypercorrelation design and should be cited:
- CVPR 2024, Rethinking Few-shot 3D Point Cloud Semantic Segmentation
- ICLR 2025, Multimodality Helps Few-shot 3D Point Cloud Semantic Segmentation
Other Strengths And Weaknesses: The paper is clearly written and easy to follow. The motivations for the design choices are clear and reasonable, and the experiments demonstrate the superior performance achieved by the proposed method.
Other Comments Or Suggestions: Please see the Questions.
Questions For Authors: Since SAM-SVN requires an additional forward-backward computation that may be computationally expensive, could you compare the model's parameter count and computational efficiency with other baselines?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: ## 1. The computational efficiency of SAM-SVN：
Our SAM-SVN is used only during source domain training and not during fine-tuning or inference, so it does not affect the computational efficiency during inference. Regarding efficiency during training in the source domain, although it requires double backpropagation, it is applied only to the singular value matrix of DFN, resulting in negligible additional computation. We demonstrate the computational efficiency of SAM-SVN by measuring the efficiency of the baseline, PATNet (which adopts the same baseline as ours), SAM applied to the entire model, SAM applied to DFN, and SAM applied to SVN (singular value matrix of DFN). The results are shown in the table below:
| | baseline | PATNet [1] | SAM-Whole | SAM-DFN | SAM-SVN |
| -------------- | :------: | :--------: | :-------: | :-----: | :-------: |
| FLOPs(G) | 20.12 | 22.63 | 26.83 | 22.69 | 20.52 |
| increase ratio | / | 12.4% | 33.35% | 12.77% | **1.99%** |
[1] Cross-Domain Few-Shot Semantic Segmentation
## 2. References：
We promise to cite the listed references in the final version.
---
Rebuttal Comment 1.1:
Comment: Thank you for the response. My concerns have been addressed and I would update my recommendation to accept.
---
Reply to Comment 1.1.1:
Comment: We sincerely appreciate your response and recognition of our rebuttal. | Summary: This paper find an interesting phenomenon that a sort of adapters naturally serve as domain-information decoupler for the CDFSS task. By comprehensive experiments, the authors validate the condition that makes adapters to be decouplers. Then, they extend such a natural decoupler by sharpness-aware minimization to build the DFN for CDFSS, which shows state-of-the-art performance.
Claims And Evidence: The phenomenon that adapters naturally serve as decoupler is novel to me. Most claims are validated in the experiments. I like the writing of this paper to detailly study each component of the phenomenon and methods.
However, this paper claims the decoupler phenomenon for CDFSS methods, but it majorly studies the HSNet structure. Nowadays many other structures are available to achieve state-of-the-art performance, such as [1] and [2]. Indeed, HSNet is prevailing, but I wish to see whether this phenomenon and method could fit other structures.
[1] Lightweight Frequency Masker for Cross-Domain Few-Shot Semantic Segmentation
[2] Feature-Proxy Transformer for Few-Shot Segmentation
Methods And Evaluation Criteria: The proposed method is a kind of adapter found to decouple source-domain information, and a training strategy to resist the overfitting, which are reasonable and novel to me. The performance in table 6 is good compared with current works.
However, in table 6, I see resnet50 and vit-base achieves state-of-the-art performance differently on these four datasets. Similarly, in appendix, table 12 and 13 show that the proposed method contribute differently to resnet and vit. Could you give some insights on these results?
Theoretical Claims: The theoretical side of this paper is in the sharpness-aware minimization. Experiments validate the influence that DFN brings to the sharpness.
However, do other choice of adapters also influence the sharpness? I suggest adding these experiments to validate from the sharpness side that only the DFN can decouple domain information.
Experimental Designs Or Analyses: The experiments and analysis are comprehensive and thorough. I appreciate the author to validate each aspect of this problem and design choice.
However, I wonder how the proposed method influence the source-domain performance. Since the adapter decouples domain information which is important for the source domain, will it harm the source-domain performance? I know the FSS dataset is close to Pascal, but I wish to see the experiments on Pascal.
Supplementary Material: I read the whole appendix. The experiments provide more convincing validation of the effectiveness. Minor mistakes: Section D title, whit -> with.
Relation To Broader Scientific Literature: This work can be applied to medical analysis (e.g., ISIC for skin diseases, chest x-ray for lung diseases), so it will help the scientific study by providing a easy-to-adapt model.
Essential References Not Discussed: I think the authors can supplement the related work with some latest work about adapters such as [1], although some of the most famous ones have been studied in section 2.
[1] Lightweight Frequency Masker for Cross-Domain Few-Shot Semantic Segmentation
Other Strengths And Weaknesses: I see in section 2 the authors use CKA to validate the domain similarity, but in section 4 the MMD is used for validation. Although the CKA experiments are included in the appendix, I still suggest keeping the criteria consistent in the paper.
Other Comments Or Suggestions: Typos: Section D title, whit -> with.
Questions For Authors: I wonder what will happen if a trained adapter is removed from network. That is, after the source-domain training, since adapters grab domain information that is harmful for target domains, how is the performance if we directly remove these adapters and only keep the remaining structures and weights for segmentation? Will it be higher than appending the source-domain-trained adapter but not finetuning it? Furthermore, during the target-domain finetuning, how is the performance if we directly use a scratch adapter for finetuning? These experiments can help understand the information captured by the source-domain-trained adapter.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: ## 1. Our method can fit different structures：
Our structure and the APM[1] structure are both based on HSNet, while our ViT structure is based on FPTrans[2]. Additionally, in the appendix, we used the SSP-based architecture for comparison with IFA. Thus, our method can be applied to networks with various architectures.
## 2. The reason for the different performance between ResNet and ViT：
The difference is due to the datasets' bias towards local recognition cues or global ones.
We use KL divergence (DisFB) to measure the similarity between the foreground and background of datasets. A higher DisFB suggests a greater requirement for the model's global resolution capability, with ISIC having the highest DisFB. ResNet, due to its convolution-based design, has local prior characteristics, making it more effective for datasets like DeepGlobe that demand detailed local features. On the other hand, ViT, based on attention mechanism, excels in long-range dependencies and global resolution, offering better performance for datasets like ISIC that rely more on global perception.
| | FSS1000 | Deepglobe | ISIC | ChestX |
| ----- | :-----: | :-------: | :---: | :----: |
| DisFB | 0.113 | 0.125 | 0.156 | 0.131 |
## 3. Validating adapter choice impact on sharpness
In the main text, we measured loss fluctuations by adding Gaussian noise to observe the changes in the sharpness of loss landscapes before and after integrating DFN. Here, we further measure the impact of different adapter choices on sharpness. Consistent with Fig3 and Fig5 in the main text, we analyze based on position and structure (res: residual, ser: serial, BKB: backbone, enc-dec: encoder-decoder):
| Position | Baseline | BKB shallower | BKB deeper | Between enc-dec |
| :--------: | :------: | :-----------: | :--------: | :-------------: |
| loss fluc. | 0.398 | 0.402 | 0.521 | 0.405 |
| Structure | Baseline | conventional+res | LoRA+res | conventional+ser |
| :--------: | :------: | :--------------: | :------: | :--------------: |
| loss fluc. | 0.398 | 0.521 | 0.533 | 0.399 |
The results above show that, from the perspective of sharpness, significant changes in loss fluctuations occur only when residual links are satisfied and the position is deep within the backbone (with the adapter structure not being a determining factor). This indicates that the adapter has captured domain-specific related information, which is consistent with the conclusions drawn in the main text.
## 4. Our methods can benefit general few-shot segmentation tasks
We tested the performance of DFN on the source domain (Pascal). Pascal consists of 20 classes and is set to a 4-fold configuration in the FSS setup. This means training is conducted on 5 classes, while testing is performed on 15 classes that were not seen during the training phase. Due to its ability to enhance the model's adaptation to new domains/classes, it also provides benefits for general few-shot segmentation. After fine-tuning DFN, its positive impact becomes even more pronounced.
| 1shot（Pascal） | Fold0 | Fold1 | Fold2 | Fold3 | Mean |
| --------------- | :---: | :---: | :---: | :---: | :--: |
| Baseline | 64.3 | 70.7 | 60.3 | 60.5 | 64.0 |
| DFN w/o ft | 65.2 | 70.9 | 60.8 | 61.3 | 64.6 |
| DFN w/ ft | 66.8 | 72.4 | 62.5 | 62.7 | 66.1 |
## 5. More settings to DFN：
Here, we include more experiments on the DFN training and fine-tuning settings：1）DFN is involved in source domain training but removed in the target domain. 2）DFN is involved in source domain training, but its original parameters are discarded and it learns from scratch in the target domain (using different initialization methods).
| 1-shot | FSS1000 | Deepglobe | ISIC | ChestX | Mean |
| :------: | :-----: | :-------: | :---: | :----: | ----- |
|baseline|77.53|29.65|31.20|51.88|47.57|
|DFN (remove in target)|78.16|38.21|34.12|76.92|56.85|
|DFN(scratch, kaiming init)|79.02|42.53| 36.63 | 82.03 |60.05|
|DFN(scratch, xavier init)|79.83|45.57| 34.79|79.46|59.91|
|DFN(random gauss init)|78.97|38.75| 33.82 |78.59|57.53|
|DFN|80.73|45.66| 36.30|85.21|61.98|
For the setting that DFN is removed in the target domain, DFN captures domain-specific information during source domain training and guides the model to learn domain-agnostic knowledge, resulting in a significant performance improvement compared to the baseline. However, due to a lack of target-specific knowledge, this approach is suboptimal. In the setting that DFN learns from scratch, its performance is influenced by the initialization method, yet it still performs well under various initializations. Our approach (i.e., DFN+SAM-SVN) is seen as using DFN to guide the model to focus on domain-agnostic knowledge in the source domain, while simultaneously providing DFN with a reasonable initialization value beneficial for adapting to various domains. Therefore, it achieves the best performance. | Summary: The paper proposes that adapters naturally serve as domain information decouplers in Cross-Domain Few-Shot Segmentation (CD-FSS) by separating domain-specific and domain-agnostic features. Based on this insight, the authors introduce Domain Feature Navigator (DFN), a structure-based decoupler that captures domain-specific knowledge without requiring explicit domain losses. To prevent DFN from overfitting to source samples, they propose SAM-SVN, which applies Sharpness-Aware Minimization (SAM) on Singular Value Norms (SVN) to constrain overfitting while preserving domain decoupling. The approach is evaluated on FSS-1000, DeepGlobe, ISIC, and Chest X-ray datasets, showing gains over SOTA methods. Ablation studies confirm that DFN improves domain decoupling, while SAM-SVN enhances generalization by reducing loss sharpness. Qualitative results demonstrate that DFN redirects model attention toward domain-invariant features, improving segmentation.
Claims And Evidence: The paper provides strong empirical evidence supporting its claims through quantitative results, ablation studies, and qualitative visualizations. The effectiveness of DFN as a domain decoupler is demonstrated through domain similarity CKA analysis.
However, some potential weaknesses exist:
(1) The claim that DFN naturally serves as a domain decoupler is supported by empirical observations (CKA similarity changes) but lacks a theoretical foundation explaining why this occurs.
(2) While SAM-SVN is shown to reduce sharpness and improve generalization, the trade-off between decoupling and domain knowledge retention is not deeply analyzed.
Methods And Evaluation Criteria: Yes, both the proposed methods and evaluation criteria are well-aligned in my opinion.
Theoretical Claims: The paper does not present formal theoretical proofs but instead supports its claims through empirical observations and experimental validation.
Experimental Designs Or Analyses: Yes, I reviewed the experimental design and analyses, which are generally well-structured and sound.
Supplementary Material: yes, mainly on the section A CKA part.
Relation To Broader Scientific Literature: The paper builds on prior work in Cross-Domain Few-Shot Segmentation (CD-FSS), domain adaptation.
Essential References Not Discussed: No, just one related work that also found residual connect is important, aligns with the finding of this paper.
Wang, Pei, Yijun Li, and Nuno Vasconcelos. "Rethinking and improving the robustness of image style transfer." Proceedings of the IEEE/CVF conference on computer vision and pattern recognition. 2021.
Other Strengths And Weaknesses: No
Other Comments Or Suggestions: Figure 1 is hard to understand. So half of feature maps is to learn domain-agnostic knowledge and half for domain-specific knowledge? Exactly half? Any references? What is DFN? Maybe need to clarify in the caption.
Line 95, I can feel what the authors want to deliver, but hope to see more explanations why the decrease means the adapter captures domain-specific information
Table 1, is the relative or absolute change can hint something like for FSS-1000, only 0.0024 increase but for Deepglobe, it is almost 0.02.
The analysis relies on CKA, is it trustworthy? Any other metric to use for reference?
Questions For Authors: No
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: ## 1. Deeper theoretical analysis for “natural decoupling”：
Due to space limitation, please refer to reviewer ueDb's reply 1 for theoretical analysis.
## 2. Analysis of trade-off between decoupling and domain knowledge retention:
For any $\rho>0$ and any distribution $\mathscr{D}$, with probability $1-\delta$ over the choice of the training set $\mathcal{S}\sim \mathscr{D}$, SAM bounds the generalization error as
$$
L\_\mathscr{D}(\boldsymbol{w}) \leq \max\_{\|\boldsymbol{\epsilon}\|\_2 \leq \rho} L\_\mathcal{S}(\boldsymbol{w} + \boldsymbol{\epsilon}) + \sqrt{\frac{k\log\left(1+\frac{\|\boldsymbol{w}\|\_2^2}{\rho^2}\left(1+\sqrt{\frac{\log(n)}{k}}\right)^2\right)+ \frac{4\log\frac{n}{\delta} + \tilde{O}(1)}{n-1}}{n-1}}
$$
where $n=|\mathcal{S}|$, $k$ is the number of parameters, and we assume $L\_\mathscr{D}(\boldsymbol{w}) \leq \mathbb{E}\_{\epsilon\_i \sim \mathcal{N}(0,\rho)}[L\_\mathscr{D}(\boldsymbol{w}+\boldsymbol{\epsilon})]$. The trade-off is controlled by $\rho$. For $\rho$, a larger value indicates more perturbations are added, emphasizing domain knowledge retention (experiment is in Appendix Tab11 left)；For $w$, a larger perturbation range signifies a greater focus on knowledge retention (experiment is in Tab7 right). All experiments regarding SAM-SVN are presented in Tab7 left, Fig10, Tab8, and Tab11 left.
## 3. Clarity for Figure 1:
In fact, the feature does not contain domain-agnostic and domain-specific knowledge in equal parts; our diagram merely indicates that the feature includes both specific and agnostic information. Regarding DFN, which is a structure-based decoupler rather than a loss-based one like current approaches, it captures domain-specific information, thereby directing the model’s attention towards domain-agnostic knowledge (described in abstract and discussed in section 2). We will add a brief explanation of DFN in the caption to make it clearer for readers. Thank you very much for your suggestion.
## 4. More explanations for why cka decrease means "domain-specific"
CKA is a metric used to measure domain similarity by comparing the distances between kernel centers of two sets of data. If the kernel centers of the representations extracted by neural networks from the two data sets are closer (resulting in a higher CKA value), it indicates that their data distributions in the feature space are more consistent, meaning their feature representations are more similar and they share more patterns. Conversely, a lower CKA value implies lower domain similarity, with the kernel centers being farther apart in the feature space. Lower domain similarity suggests that the extracted features are less similar, indicating that the two sets of representations share fewer common patterns and have more characteristics specific to their own data distributions (more domain-specific).
To verify it is the domain gap that influences CKA, we divided the data in the Pascal into 20 groups based on categories and measured the CKA between different groups. We reported the CKA between the two most divergent groups, as well as the mean CKA and standard deviation (std) CKA. The results are as follows: It can be seen that even for the most divergent feature groups within the same dataset, the CKA is above 0.85, indicating the validity of using CKA to measure domain similarity.
| CKA | max diff | mean | std |
| :----: | :------: | :----: | :----: |
| Pascal | 0.8656 | 0.8895 | 0.0179 |
## 5. Reliability of the CKA metric
Absolute change is used here. We choose CKA as a measurement metric for several reasons: 1) CKA employs kernel center alignment, which eliminates measurement errors caused by extreme feature representations (noise); 2) Compared to other metrics like MMD and cosine similarity, CKA removes the effects of scaling differences; 3) CKA is more sensitive to differences in data distribution, allowing it to more accurately reflect distribution changes (detailed theory in the appendix).
The discrepancy in change between FSS and DeepGlobe is consistent due to: 1) CKA's sensitivity to data distribution differences; 2) The smaller domain gap between FSS and Pascal (both being natural image datasets) results in smaller changes, whereas the larger domain gap between Deepglobe (remote sensing images) and Pascal leads to greater gains and changes.
Additional metrics: In the experimental section (Figure 8), we also used MMD to validate our viewpoint, which is consistent with CKA. Furthermore, in the appendix, we employed relative CKA to mitigate the impact of data distribution (Figure 15). | Summary: This paper introduces a novel perspective on using adapters as structural domain decouplers for cross-domain few-shot semantic segmentation (CD-FSS). They introduce the Domain Feature Navigator (DFN), a structure-based decoupler inserted into deeper network layers with residual connections, and SAM-SVN, a sharpness-aware regularization method applied to the singular values of DFN weights to prevent overfitting.
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: A recent work on cd-fss is not discussed: SAM-Aware Graph Prompt Reasoning Network for Cross-Domain Few-Shot Segmentation, aaai 2025
Other Strengths And Weaknesses: Strengths:
1. The discovery that adapters structurally decouple domain information (without explicit loss functions) is innovative and challenges existing loss-based domain adaptation paradigms.
2. SAM-SVN effectively balances domain-specific knowledge absorption and overfitting prevention.
3. Experiments demonstrate state-of-the-art performance on four benchmarks. Comprehensive ablation studies validate design choices (adapter position, residual connections, SAM-SVN). Experiments span multiple datasets (FSS-1000, DeepGlobe, ISIC, Chest X-ray) and backbones (ResNet-50, ViT), demonstrating robustness.
Weaknesses
1. The term "natural decoupling" lacks intuitive explanation. While experiments show reduced CKA similarity, a deeper theoretical analysis (e.g., information bottleneck principles) could strengthen claims. The rationale for perturbing singular values (vs. other parameters) in SAM-SVN needs further justification.
2. Comparisons with IFA use different batch sizes (96 vs. 1). Why?
3. Why is there an impact statement analysis on page 9? Does it exceed the page limit?
Other Comments Or Suggestions: please see weakness
Questions For Authors: please see weakness
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: ## 1. Deeper theoretical analysis for “natural decoupling”：
The behavior of adapters as decouplers can be analyzed through the Information Bottleneck (IB) theory. The IB objective is:
$\mathcal{L}_{IB} = I(X;Z) - \beta I(Z;Y)$
where $I(\cdot;\cdot)$ is mutual information, X is the input, Y is the final output label, $Z$ is the intermediate representation, and $\beta$ is the balance parameter. Decomposing the input as $X = X_{inv} + X_{spec}$, the IB objective becomes:
$\mathcal{L}_{IB} = I(X\_{inv} + X\_{spec};Z) - \beta I(Z;Y)$
For encoder-decoder network (ED) parameters $\theta_f$ and adapter parameters $\theta_g$ where $\theta_f \gg \theta_g$, the adapter's information capacity is much smaller than the ED, causing it to selectively absorb source domain-specific information that better optimizes the current training objective, resulting in $I(X_{spec};Z) \gg I(X_{inv};Z)$, which promotes gradient flow differentiation. In a network $f$ with residual adapter $g$, the forward propagation is: $F(x) = f(x) + g(f(x))$
For ED parameters $\theta_f$, the gradient is: $\frac{\partial \mathcal{L}}{\partial \theta_f} = \frac{\partial \mathcal{L}}{\partial F(x)} \cdot \frac{\partial F(x)}{\partial f(x)} \cdot \frac{\partial f(x)}{\partial \theta_f}$, expanding the middle term: $\frac{\partial F(x)}{\partial f(x)} = I + \frac{\partial g(f(x))}{\partial f(x)}$
where $I$ is the identity matrix (from the direct residual path), and the second term is the Jacobian matrix of the adapter function.
For adapter parameters $\theta_g$, the gradient is proved to be $\frac{\partial \mathcal{L}}{\partial \theta_g} = \frac{\partial \mathcal{L}}{\partial F(x)} \cdot \frac{\partial g(f(x))}{\partial \theta_g}$
Differentiated gradients: Due to the adapter's selective absorption of domain-specific information and the residual adapter structure, gradient flow naturally separates network optimization into two complementary learning objectives.
## 2. Further justification for perturbing singular values in SAM-SVN:
For any $\rho>0$ and any distribution $\mathscr{D}$, with probability $1-\delta$ over the choice of the training set $\mathcal{S}\sim \mathscr{D}$, SAM bounds the generalization error as
$$
L\_\mathscr{D}(\boldsymbol{w}) \leq \max\_{\|\boldsymbol{\epsilon}\|\_2 \leq \rho} L\_\mathcal{S}(\boldsymbol{w} + \boldsymbol{\epsilon}) + \sqrt{\frac{k\log\left(1+\frac{\|\boldsymbol{w}\|\_2^2}{\rho^2}\left(1+\sqrt{\frac{\log(n)}{k}}\right)^2\right)+ \frac{4\log\frac{n}{\delta} + \tilde{O}(1)}{n-1}}{n-1}}
$$
where $n=|\mathcal{S}|$, $k$ is the number of parameters, and we assume $L\_\mathscr{D}(\boldsymbol{w}) \leq \mathbb{E}\_{\epsilon\_i \sim \mathcal{N}(0,\rho)}[L\_\mathscr{D}(\boldsymbol{w}+\boldsymbol{\epsilon})]$. This condition implies that adding Gaussian perturbations should not reduce the test error, which generally holds for the final solution but not necessarily for all $\boldsymbol{w}$. $w$ represent the parameters influenced by SAM. Applying SAM to the entire network or the entire DFN introduces excessive perturbations, which can hinder DFN’s ability to capture domain-specific information. SAM-SVN strikes a balance by decomposing $w_{DFN}$ and applying perturbations only to the singular value matrix of DFN. The singular value matrix governs the representation space of DFN, thus limiting perturbations to a reasonable spatial range. This prevents DFN from overfitting to the source domain while maintaining its ability to capture domain-specific information during training.
We also quantitatively compared the perturbation on the singular values and other weights in Tab.7.
## 3. Comparisons with IFA use a batch size of 96:
IFA is set to a batch size (bsz) of 96, so we adopt the same setting of bsz=96 for comparison to ensure fairness, as stated in appendix section D. Moreover, we also found using different bsz leads to different performance in IFA. For example, for Deepglobe, the performance is 50.1 when bsz=96, while it is 44.7 when bsz=1.
## 4. Discussion on GPRN (AAAI'25)：
Since the work had not been published at the time of our submission, we did not include a comparison. We are now offering a discussion on GPRN. GPRN exploits SAM’s generalizability by converting SAM-extracted masks into semantic prompts, aggregating prompt information through graph-based reasoning, and adaptively choosing feedback points. Our approach highlights that adapters naturally function as decouplers. We explore this concept further, proposing a decoupling strategy that is applicable to a variety of models.
## 5. Impact statement in page 9:
Thank you very much for your kind reminder, but the official guidelines indicate that the impact statement is not subject to page limitations. Here is the original wording: “Papers must be prepared and submitted as a single file: 8 pages for the main paper, **with unlimited pages for references, the impact statement, and appendices.**" | null | null | null | null | null | null |
PROTOCOL: Partial Optimal Transport-enhanced Contrastive Learning for Imbalanced Multi-view Clustering | Accept (poster) | Summary: The paper addresses the class imbalance issue in multi-view clustering by combining UOT and POT to perceive class imbalance, and uses POT-enhanced class rebalance to mitigate the representation degradation of minority samples in contrastive learning. Through comparisons across multiple datasets and multi-view clustering algorithms, the paper demonstrates the superiority of the proposed method under different imbalance ratios.
Claims And Evidence: No. The paper proposes achieving adaptive perception of class imbalance through the adjustment of lambda. However, the explanation does not provide readers with a clear understanding of the adaptive adjustment process of lambda.
Methods And Evaluation Criteria: The comparative experimental results and related analysis demonstrate the superiority of the proposed method in addressing the class imbalance problem. However, the explanation of the proposed method is difficult to understand.
Theoretical Claims: The main text does not include proofs for the theoretical claims.
Experimental Designs Or Analyses: The study conducts experimental comparisons based on five commonly used multi-view datasets. However, the experimental setup does not clearly explain how the class-imbalanced datasets were constructed from these five datasets for the comparative experiments in Table 2. Additionally, the experimental procedures for Figures 1 and 2 are not clearly described.
Supplementary Material: Yes. Appendix A and B
Relation To Broader Scientific Literature: The primary contribution of this study lies in addressing the class imbalance problem in multi-view clustering by optimizing it with partial optimal transport. Optimal transport has demonstrated strong capability in handling class imbalance problems in previous studies. Based on this, the authors introduce it into multi-view clustering, aiming to mitigate class imbalance within this context.
Essential References Not Discussed: The core of the paper lies in introducing Optimal Transport into multi-view clustering. Although the paper provides some transitions and background, the process is not clearly articulated, making it difficult to understand.
Other Strengths And Weaknesses: Strength:
The authors keenly identified the class imbalance problem in multi-view clustering and addressed it by introducing Optimal Transport, tackling the issue from two perspectives: perceiving class imbalance and mitigating representation degradation of minority samples.
Weakness:
1) he paper does not provide a clear and intuitive explanation of how Optimal Transport addresses class imbalance, making it difficult for readers to comprehend the construction of the proposed method.
2) The authors conducted experiments with different imbalance ratios on common multi-view datasets, but the specific preprocessing steps were not detailed.
3) Furthermore, the experimental procedures for Tables 1 and 2 were not provided.
Other Comments Or Suggestions: [1]Given that the paper does not provide an easily understandable explanation of the proposed method and that data preprocessing is required to evaluate its clustering performance on class-imbalanced multi-view data, this process should be explicitly presented. Therefore, anonymized open-source code should be considered to facilitate a comprehensive understanding and verification of the proposed method’s effectiveness.
Questions For Authors: [1]Why do the constraint conditions in Equation (12) reflect the distribution pattern of class imbalance?
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: We sincerely appreciate your recognition of our work's motivation and method.We are also deeply grateful for your thorough review and valuable suggestions.
**Q1:** A intuitive explanation of how Optimal Transport addresses class imbalance.
**A1:** Thanks for your suggestion. We would like to draw your attention to **Subsection 4.1.3**. Specifically, our method perceives class imbalance distributions through the following process:
Given the model's label predictions $\hat{\mathbf{P}}$ and prior distribution constraints $U$, PROTOCOL dynamically adjusts the transport mass (via $\lambda$) to gradually assign samples to imbalanced clusters (POT label matrix $\mathbf{T}$):
(1) First assigns high-confidence samples (low transport costs);
(2) Gradually incorporates lower-confidence samples as transport mass increases;
(3) Naturally forms labels reflecting true class distribution.
Combines **imbalanced labels** with **class-rebalanced learning (Section 4.2)** to address minority class representation.
We will enhance the logical connections between modules in the **Methodology** section of our revised version.
**Q2:** Specific preprocessing.
**A2:** Thank you for your helpful suggestion. The data preprocessing steps are as follows:
step1: We start with the class-balanced datasets.
step2: Based on the imbalance ratio $R$ as defined in Eq. (7), we calculate the sample size for each class in descending order. For instance, with Hdigit dataset at $R$=0.1, class 1 retains all 1000 samples while class 10 keeps 100 samples. The intermediate classes' sample sizes grow linearly. Samples: {1000, 774, 599, 464, 359, 278, 215, 167, 129, 100}.
step3: For each class, we ensure that the same sample indices are maintained across all views.
step4: To ensure stability, we employ fixed random seeds during sample selection.
This preprocessing transforms the dataset into an imbalanced class distribution. The code will be made publicly available upon acceptance.
**Q3:** The experimental procedures for Tables 1 and 2.
**A3:** Thank you for your suggestion. Since you also mentioned Figure 1 and 2, we explain them together.
* Tables 1 and 2: PROTOCOL's implementation is given in Appendix B. Dataset and preprocessing are provided in Table 4 and A2, respectively.
* Figures 1 and 2:
* Figure 1: The model is trained on imbalanced training sets and evaluated on balanced test sets to assess its perception of different classes. The results demonstrate PROTOCOL's robustness.
* Figure 2: We categorize all classes into three groups: Head, Medium, and Tail. The distribution varies by class size:
* For 10-class: Head (first 3 classes), Medium (middle 4 classes), Tail (last 3 classes).
* For 7-class: Head (2), Medium (3), Tail (2).
* For 5-class: Head (1), Medium (3), Tail (1).
This categorization aligns with the Head-Medium-Tail definition, as majority samples fall into head classes while minority samples belong to tail classes. The results demonstrate our method's superiority, validating its effectiveness in perceiving actual class distributions.
**Q4:** An easy explanation of the proposed method, data preprocessing, and the anonymous code for validation.
**A4:** Thank you for your suggestion.
* **About an easily explanation of PROTOCOL:** See A1.
* **Data preprocessing:** See A2.
* **Anonymous code:** We have provided our code through anonymous link (https://zenodo.org/records/15119555).
* **For Testing:** We provide a pre-trained model on the Hdigit dataset with $R$=0.1 to help verify our method's effectiveness.
* **For Training:** We have released network.py and train.py, which demonstrate the training pipeline to facilitate understanding of our framework.
* **Environment Setup:** Please create a virtual environment following our instructions for smooth execution of our code.
The complete source code will be made publicly available upon paper acceptance.
**Q5:** Analysis that Eq. (12)'s constraints reflect class imbalance distribution.
**A5:** Thank you for your suggestion. Eq. (12) captures the class imbalance distribution pattern through two key mechanisms:
(1) The constraints $\sum_{k=1}^K \mathbf{T}_{i,k} \leq 1$ implement a soft label assignment mechanism, enabling flexible sample-to-class assignments. This allows samples to have varying degrees of association with different classes.
(2) The constraint $\sum_{i=1}^N \mathbf{T}_{i,k} \leq \lambda$ introduces an adaptive parameter $\lambda$ to regulate the maximum mass for each class. During the dynamic adjustment of $\lambda$, higher confidence samples (majority classes) receive larger mass assignments, while lower confidence samples (minority classes) receive smaller mass assignments.
Then, we transform Eq. (12) into Eq. (15), enabling the model to adaptively capture the inherent patterns of imbalanced class distributions. | Summary: In this paper, a novel Partial Optimal Transmission (POT) enhanced contrast learning framework, PROTOCOL, is proposed to address the class imbalance challenge in multi-view clustering. A two-level rebalancing strategy achieves balanced feature learning as well as consistency in view-specific and view-sharing allocation.
Claims And Evidence: Yes
Methods And Evaluation Criteria: Yes
Theoretical Claims: Yes
Experimental Designs Or Analyses: Yes
Supplementary Material: Only part B, experimental supplements.
Relation To Broader Scientific Literature: Unbalanced multi-view data is very common in real-world scenarios, but has not been explored much. This paper achieves balanced learning by modifying the paradigm of contrastive learning to make the model more sensitive to minority samples.
Essential References Not Discussed: No
Other Strengths And Weaknesses: Strengths:
- Good representation.
- Comprehensive experiments: The superiority and robustness of the method are verified on multiple datasets, covering different imbalance ratios, and ablation studies and visualization analysis are performed.
Weaknesses:
- Is w(p+) set empirically? Why manually specify such a ratio between view-specific and consensus class alignment? Why not let the model learn adaptively.
Other Comments Or Suggestions: no
Questions For Authors: - How to aggregate view-specific representations into consensus representation U?
- In Figure 1, why is there still an imbalanced ratio on the balanced test set?
- It may be clearer for the authors to show a comparison of the effects of different methods' visualizations on synthetic extreme imbalance dataset. Since the visualization results from Fig. 3 show that most of the methods can identify those small clusters, such a demonstration may not achieve the authors' original intention.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We sincerely appreciate your recognition of both the novelty of our method and the practical value of our motivation, as well as your positive feedback on our paper's representation and experiments. We are also deeply grateful for your thorough review and valuable suggestions.
**Q1:** The empirical setting of w(p+) and the possibility of adaptive learning by the model.
**A1:** Thank you for your helpful suggestion.
Yes, we empirically set $w(p_+)$ to 0.8 and 0.2 for the two settings based on experimental validation.
Following your suggestion, we implemented adaptive learning for $w(p_+)$ and validated it on three datasets with $R$=0.1. The results show performance improvements of 0.3%\~0.5% compared to fixed parameters. Notably, the learned parameters (ranging from 0.664\~0.805 and 0.195\~0.336) align well with our empirical values (0.8/0.2), validating our empirical setting. We implemented this by randomly initializing the two settings in [0,1], with their sum constrained to 1.
| | ACC (Fixed: 0.8/0.2) | ACC (Adaptive) | $w(p_+)$ (Learned) |
| :-----: | :----------------------: | :---------------------: | :---------------------: |
| Caltech | 0.791 | 0.796 ($\uparrow$ 0.05) | 0.805/0.195 |
| Hdigit | 0.892 | 0.895 ($\uparrow$ 0.03) | 0.664/0.336 |
| CIFAR10 | 0.861 | 0.864 ($\uparrow$ 0.03) | 0.782/0.218 |
Given the improved performance and greater flexibility of adaptive learning, we will adopt this improvement in the revised version. We again thank you for the constructive suggestion.
**Q2:** Aggregation of view-specific representations into consensus representation.
**A2:** Thank you for your comment. The consensus representation $\mathbf{U}$ is obtained through the following steps:
step1: View-specific representations $\mathbf{Z}^v$ are learned through autoencoders from original data.
step2: Inter-sample structural relationships are captured in relationship matrix $\mathbf{G}$ through a Transformer-based self-attention mechanism.
step3: Structure-aware representations are computed as $\mathbf{S}^v=\mathbf{Z}^v\mathbf{G}$ for each view.
step4: View weights $\mathbf{w}^v$ are learned through a view weight learning module.
step5: Final consensus representation is obtained by weighted fusion: $\mathbf{U}= \sum_{v=1}^{V}\mathbf{w}^v\mathbf{S}^v$.
**Q3:** Regarding the imbalanced ratio $R$ in Figure 1.
**A3:** Thank you for your comment. The imbalance ratio $R$ only applies to the training set, while the test set remains balanced. PROTOCOL maintains superior performance across different train imbalance ratios, demonstrating its effectiveness and robustness in handling class-imbalanced multi-view data.
**Q4:** Adding visualization results for more extreme imbalance data.
**A4:** Thank you for your insightful suggestion. Following your recommendation, we conducted tests on the Hdigit dataset with an even more extreme imbalance ratio of $R$=0.05, with visualization results shown in **Figure A3** of the PDF file provided in the anonymous link (https://zenodo.org/records/15117646). The results demonstrate that, compared to baseline methods, PROTOCOL can effectively identify smaller clusters and clearly distinguish cluster structures of varying scales, validating our method's effectiveness and robustness under extreme imbalance ratios.
To more intuitively demonstrate PROTOCOL's ability to perceive imbalanced data distributions, we conducted a quantitative analysis of the clustering results from Figure 3 in the original paper and **Figure A3**, where we calculated the number of samples in each class from the test results and computed the actual imbalance ratios.
As shown in the table below, when the imbalance ratio $R$=0.1, other methods produced actual imbalance ratios between **0.26~0.38**, while PROTOCOL achieved an actual imbalance ratio of only **0.14**. Similarity, when the imbalance ratio $R$=0.05, other methods produced actual imbalance ratios between **0.23~0.37**, while PROTOCOL achieved an actual imbalance ratio of only **0.12**. This indicates that our method can more accurately perceive and maintain the class distribution characteristics of the original data.
| Actual_$R$ | MFLVC | CSOT | GCFAggMVC | SEM | PROTOCOL |
| :----: | :---: | :--: | :-------: | :--: | :------: |
| $R$=0.1 | 0.26 | 0.28 | 0.39 | 0.38 | **0.14** |
| $R$=0.05 | 0.28 | 0.25 | 0.23 | 0.37 | **0.12** |
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Rebuttal Comment 1.1:
Comment: I appreciate the answers and clarification. I have no concerns about the work and hence keep the rating.
---
Reply to Comment 1.1.1:
Comment: Thank you for your positive assessment of our work. We sincerely appreciate your time and effort. | Summary: The paper introduces PROTOCOL, a new method for imbalanced multi-view clustering. It combines partial optimal transport (POT) with contrastive learning. The approach solves two main problems: perceiving class imbalance distributions through POT-based label assignment and reducing the representation degradation of minority samples using rebalancing strategies at the feature and class levels. Tests on multiple datasets show that PROTOCOL performs better, especially when data is highly imbalanced.
Claims And Evidence: The claims presented in the paper are robustly bolstered by the experimental evidence.
1.The claims about POT’s effectiveness for imbalanced MVC are supported by ablation studies and t-SNE visualizations, showing clearer cluster boundaries for imbalanced multi-view clustering.
2.The superiority over baselines is validated across all datasets and metrics.
Methods And Evaluation Criteria: Yes
Theoretical Claims: Yes. The paper is based on theoretical concepts of OT and contrastive learning.
Experimental Designs Or Analyses: The work performs several experiments on 5 datasets with three different imblance ratios
Supplementary Material: Yes.
Relation To Broader Scientific Literature: The paper introduces a new method for imbalanced multi-view clustering by combining partial optimal transport (POT) with contrastive learning.
Essential References Not Discussed: The literature research section of the paper is quite substantial, but there are still some related papers that have not been mentioned.
Including recent single-view and multi-view class imbalance approaches (e.g., [1]) would enhance the paper's comprehensiveness and contextualize its contributions more effectively.
[1] Zhou Q, Sun B. Adaptive K-means clustering based under-sampling methods to solve the class imbalance problem[J]. Data and Information Management, 2024, 8(3): 100064.
Other Strengths And Weaknesses: Strengths:
1. Originality: The novel integration of POT and contrastive learning offers a fresh approach to imbalanced multi-view clustering.
2. Practical Value: Addressing real-world imbalanced data challenges highlights the paper’s potential impact in applications like ecological monitoring.
3. Thorough Evaluation: Rigorous experiments across datasets and imbalance scenarios demonstrate the framework’s performance.
Weaknesses:
1. The computational cost of POT might pose challenges for large-scale applications, which could be a direction for future optimization.
2. The paper's structure could be clarified to better highlight the logical connections between components. A more explicit explanation of how each module addresses specific challenges would help readers appreciate the framework's coherence.
Other Comments Or Suggestions: Refer to the weakness
Questions For Authors: 1. Theoretical Justification: Could the authors elaborate on the theoretical foundation of the POT scaling algorithm, such as its convergence properties? This would significantly enhance the paper's theoretical contributions.
2. Runtime Analysis: How does the computational cost of PROTOCOL scale with dataset size?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We sincerely appreciate your recognition of our work's novelty and its potential impact in enhancing multi-view clustering for real-world imbalanced scenarios, as well as your positive feedback on our experimental results. We are also deeply grateful for your thorough review and helpful suggestions.
**Q1:** The computational cost of POT for large-scale applications could be a direction for future optimization.
**A1:** Thank you for your insightful suggestion. In Q4, we have validated PROTOCOL's computational cost on varying data scales (from 5K to 40K data points). The results demonstrate **near-linear growth**, showing PROTOCOL's potential for large-scale applications. In future work, we will continue to investigate and analyze POT's computational efficiency on datasets of even larger scale.
**Q2:** Strengthen the logical connections between components.
**A2:** Good suggestion! We will enhance the logical structure of **Section 4 (Methodology)** as follows:
**4.1 Motivation**. First, we will clearly articulate the two major challenges in imbalanced multi-view clustering, helping readers better understand the correspondence between challenges and their respective solutions.
**4.2 Multi-view POT Label Allocation** (originally 4.1). We will explicitly state at the beginning: "We propose a multi-view POT label allocation method that learns imbalanced class distribution of multi-view data through multi-view representation learning and a POT-based self-labeling mechanism." Additional logical connections will be added between subsubsections to strengthen coherence. At the end, we will add a transition paragraph: "Through the learning of these components, PROTOCOL can effectively perceive the imbalanced distribution of multi-view data. This leads to the next challenge: how to mitigate representation degradation of minority samples, which we will address in next subsection."
**4.3 Multi-view Class-rebalanced Contrastive Learning** (originally 4.2). We will first analyze the fundamental causes of representation degradation in minority samples, then introduce our solution.
At the end of **Methodology**, we will summarize how PROTOCOL systematically addresses the two challenges. Specifically, we will add the following description:"Imbalanced multi-view data is a more realistic application setting. PROTOCOL addresses the two key challenges of imbalanced multi-view data through POT self-label allocation and class-rebalanced contrastive learning."
These modifications will make the logical connections between components more prominent.
**Q3:** Convergence theory analysis.
**A3:** Thank you for your constructive suggestion. Due to space limitations, we provide a brief theoretical analysis of convergence here. In the revised version, we will provide theoretical foundations for the convergence analysis.
Our POT scaling algorithm extends the Sinkhorn-Knopp iteration by incorporating partial optimal transport with weighted KL divergence constraints. The algorithm achieves optimal label assignment through an efficient dual-form scaling iteration process. Based on [1], we prove that when $\epsilon, \beta > 0$, the algorithm guarantees linear convergence to a unique solution. The convergence rate depends on the entropic regularization parameter, weighted KL divergence weight, and cost matrix condition number. Our method introduces a dynamic mass parameter $\lambda$ for smooth transition from high-confidence samples to global optimal solutions. Moreover, experimental results validate both the efficiency and effectiveness of PROTOCOL, demonstrating its stability in handling imbalanced multi-view clustering.
[1] Scaling Algorithms for Unbalanced Optimal Transport Problems (Mathematics of Computation 2018)
**Q4:** About PROTOCOL's computational cost scaling with dataset size.
**A4:** Thank you for your valuable suggestion. Per your suggestion, we evaluated PROTOCOL's computational cost across four different data scales (5K to 40K samples) on the CIFAR10 dataset. As shown in **Figure A2** of the PDF file provided in the anonymous link (https://zenodo.org/records/15119555), the results demonstrate that PROTOCOL's computational cost scales **nearly linearly** with the number of samples. All experiments were conducted on an NVIDIA GeForce RTX 3090 GPU.
**Q5:** About recent works on imbalanced multi-view clustering and suggested Ref [1].
**A5:** Thank you for your suggestion. To the best of our knowledge, we are the first to systematically study the imbalanced multi-view clustering problem. While [1] is a single-view method for class imbalance problems, different from our multi-view approach, we will discuss it in our revised version.
[1] Adaptive K-means clustering based under-sampling methods to solve the class imbalance problem (Data and Information Management 2024) | Summary: This paper proposes the first systematic study on the common class imbalance problem in multi-view clustering and develops a new framework called PROTOCOL. This method reformulates the imbalanced clustering problem as a partial optimal transfer problem by mapping multi-view features to a consensus space, and introduces step-by-step quality constraints and weighted KL divergence to perceive class imbalance. At the same time, class rebalanced contrastive learning enhanced by partial optimal transfer is used at the feature and category levels, combined with logit adjustment and category-sensitive learning, to alleviate the representation degradation problem of minority samples.
Claims And Evidence: Yes
Methods And Evaluation Criteria: Yes
Theoretical Claims: Yes. The methodology of the paper has been reviewed.
Experimental Designs Or Analyses: Yes. The experimental setting and results have been reviewed.
Supplementary Material: Yes. The ‘Details of Experiments’ and ‘Algorithm’ have been reviewed.
Relation To Broader Scientific Literature: The key contributions of the paper are related to the broader scientific literature on Multi-View Clustering.
Essential References Not Discussed: The paper comprehensively reviews the most relevant literature in the fields of Multi-View Clustering.
Other Strengths And Weaknesses: Strengths:
1. The paper innovatively integrates partial optimal transport with contrastive learning, utilizing progressive quality constraints and a weighted KL divergence to effectively perceive and model imbalanced distributions, while simultaneously enhancing the representation of minority samples at multiple levels.
2. Extensive experiments conducted on five datasets convincingly demonstrate the method’s superior performance in handling imbalanced multi-view data, providing robust empirical support for the proposed approach.
Weaknesses:
1. Although the paper targets imbalanced clustering, it does not clearly describe the specific operations involved nor adequately articulate the inherent challenges of imbalanced clustering in the motivation section.
2. The experiments are limited to datasets with a maximum scale of only 50,000 samples; the authors should consider validating their approach on larger-scale datasets.
3. In regard to Equation 28, which introduces the common semantic loss, the paper should provide a clearer explanation of its advantages and its specific impact on imbalanced clustering scenarios.
Other Comments Or Suggestions: NA
Questions For Authors: NA
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We sincerely appreciate your recognition of our work's novelty as the first to identify and systematically study the class imbalance problem in multi-view clustering, as well as your positive feedback on our method's effectiveness and robustness. Furthermore, we are deeply grateful for your thorough review and constructive suggestions on our manuscript.
**Q1:** The inherent challenges of imbalanced clustering.
**A1:** Thank you for your constructive suggestion. We will further clarify the two main challenges of imbalanced multi-view clustering (see lines 43 and 61) in the **Motivation** subsection of the revised version.
We will add a **Motivation** subsection in the **Methodology** section to clarify the two key challenges and explicitly indicate how each module of our method addresses these challenges:
**(1) How to perceive class imbalance distribution.** The challenge lies in detecting imbalanced distributions without labeled data in unsupervised settings. Existing methods, assuming uniform class distributions, often fail to handle imbalanced data effectively. This challenge will be addressed in **Multi-view POT Label Allocation** subsection.
**(2) How to mitigate representation degradation of minority samples.** Minority samples, due to their scarcity, often receive insufficient attention during learning, resulting in poor feature representations that inadequately characterize their classes. This challenge will be addressed in **Multi-view Class-rebalanced Contrastive Learning** subsection.
This creates a more coherent flow from challenges to solutions, helping readers better understand both our motivation and technical approach.
**Q2:** Validate our method on larger-scale datasets.
**A2:** Thank you for your insightful suggestion. Per your suggestion, we validated our method on larger-scale dataset (CIFAR100 with 60,000 samples). As shown in **Figure A1** of the PDF file provided in the anonymous link (https://zenodo.org/records/15119555), PROTOCOL achieves the best performance compared to other methods, demonstrating its effectiveness in handling class imbalance ($R$=0.1) on large-scale datasets.
CIFAR100 is considered a large-scale dataset among those commonly used in multi-view clustering [1-4]. In future work, we will continue to explore PROTOCOL's potential on even larger-scale datasets.
[1] A Comprehensive Survey on Multi-View Clustering (TKDE 2023)
[2] Representation Learning in Multi‑view Clustering: A Literature Review (Data Sci. Eng 2022)
[3] Differentiable Hierarchical Optimal Transport for Robust Multi-View Learning (TPAMI 2023)
[4] Adversarially Robust Deep Multi-View Clustering: ANovel Attack and Defense Framework (ICML 2024)
**Q3:** The advantages of Eq. (28) in imbalanced multi-view clustering scenarios.
**A3:** Good suggestion! Eq. (28) employs contrastive learning to maintain semantic consistency across views for the same class. The denominator term $\sum_{j=1,j\neq i}^{K} \mathcal{D}(\{P_i^v, P_j^v\})$ measures negative pair similarities, ensuring comprehensive discrimination between classes. This design helps distinguish minority from majority classes while preserving cross-view semantic consistency, thereby enhancing representation learning for minority classes.
In imbalanced multi-view clustering, cross-view semantic alignment is crucial due to minority classes' lower error tolerance. Unlike balanced scenarios where abundant samples can help correct semantic bias, minority classes have limited samples to rely on. Cross-view semantic alignment enables different views to complement each other, effectively reducing representation bias for minority classes.
We will add a clear explanation of Eq. (28) in the revised version to highlight its advantages in imbalanced multi-view clustering scenarios.
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Rebuttal Comment 1.1:
Comment: Thanks to the author for the response, I decided to keep my rating unchanged.
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Reply to Comment 1.1.1:
Comment: We appreciate your recognition of our work and thank you for your time and effort. | null | null | null | null | null | null |
Aguvis: Unified Pure Vision Agents for Autonomous GUI Interaction | Accept (poster) | Summary: This paper focuses on the autonomous GUI interaction task from the pure vision agent perspective. A large-scale cross-platform dataset of GUI agent trajectories is constructed. A two-stage training pipeline is proposed to separate GUI grounding from planning and reasoning. The experiments demonstrate the effectiveness of the proposed method in both offline and real-world online benchmarks.
## update after rebuttal
I appreciate the authors' clarifications. Most of my concerns have been addressed by the rebuttal. I would lean to accept the paper by involving the additional discussions in the revised version.
Claims And Evidence: Yes.
Methods And Evaluation Criteria: Yes.
Theoretical Claims: Yes.
Experimental Designs Or Analyses: The current experiments are not thorough enough. Specifically, the evaluation metrics on different benchmarks are not the same. For example, the computational cost analysis is only conducted on Mind2Web-Live, and the element accuracy and Operation F1 are only conducted on Multimodal Mind2Web. To make the results more convincing, it would be better to add additional evaluations and discussions.
Supplementary Material: Yes.
Relation To Broader Scientific Literature: The proposed datasets and models could benefit future research in autonomous vision-based GUI agents.
Essential References Not Discussed: No.
Other Strengths And Weaknesses: The proposed two-stage training pipeline could incorporate structured thought processes to enhance the performance of autonomous vision-based GUI agents. The collected dataset could also be useful for future research in the community.
Other Comments Or Suggestions: The first paragraph in Section 3.3 claims that “we evaluated AGUVIS across four comprehensive benchmarks”. But only three benchmarks are mentioned here.
Questions For Authors: 1. Which metric is used for the result comparison in Table 1?
2. Why are the evaluation metrics used on different benchmark datasets different? For example, the computational cost analysis is only conducted on Mind2Web-Live, and the element accuracy and Operation F1 are only conducted on Multimodal Mind2Web.
3. Based on the results in Table 8, it seems that the proposed method paired with GPT-4o for planning, the result is better than that of the AGUVIS-72B. I was wondering about the results of the same configuration on other benchmarks.
4. For the VLM-based trajectory augmentation process, the current inner monologue components are generated by GPT-4o. Can other latest VLMs be used and compared?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for taking the time to review our work and providing constructive feedback! We greatly appreciate your recognition of our contribution in the realm of pure-vision based autonomous GUI agents, including our grounding-then-planning training pipeline and open-sourcing the large-scale, curated data. We are also delighted that you recognized the promising performance of our approach in both offline and real-world online benchmarks, which highlights its generalizability across multiple digital platforms. We have fully open-sourced our roadmap towards building pure-vision based autonomous agents, and are committed to support further research in this field.
We also noticed you have some constructive questions about our work, and we're happy to elaborate further below!
> C1: The first paragraph in Section 3.3 claims that “we evaluated AGUVIS across four comprehensive benchmarks”. But only three benchmarks are mentioned here.
Thank you for pointing out this inconsistency! We will correct it in the revised version of the manuscript.
> Q1: Which metric is used for the result comparison in Table 1?
For Table 1 (results on Screenspot), we report Click Accuracy as the evaluation metric, following the definitions provided in the original benchmark paper [1]. Specifically, Click Accuracy measures the proportion of test samples where the predicted location falls within the ground truth element's bounding box.
[1] SeeClick: Harnessing GUI Grounding for Advanced Visual GUI Agents. Cheng et al., 2024.
> Q2: Why are the evaluation metrics used on different benchmark datasets different? For example, the computational cost analysis is only conducted on Mind2Web-Live, and the element accuracy and Operation F1 are only conducted on Multimodal Mind2Web.
Thank you for your thoughtful feedback! The differences in evaluation metrics arise because each benchmark is designed to assess different aspects of the agent's performance, and we adhere to the metric definitions specific to each benchmark. This approach ensures that our results remain comparable to previous methods and provides a clear understanding of the agent's performance under distinct conditions.
- **Offline vs. Online Evaluations**: Some metrics, such as element accuracy and Operation F1, are more suitable for offline evaluations (e.g., Multimodal Mind2Web), where the goal is to evaluate step-level accuracy and action predictions without environments. In contrast, online evaluations like those on Mind2Web-Live focus on final trajectory-level execution results, which offer a more holistic view of the agent's ability to complete tasks in dynamic environments.
- **Benchmark-Specific Metrics**: Different benchmarks introduce their own unique metrics to capture specific aspects of performance. For instance, Mind2Web-Live introduces the USD Efficiency Score, which evaluates the efficiency of resource utilization during task execution. This metric provides insights into the agent’s performance in real-world settings, where efficiency is a key factor.
While we acknowledge the importance of following standardized evaluation metrics, we also agree that it is valuable to align the evaluation criteria with the specific needs and goals of each benchmark. Developing unified metrics across benchmarks requires significant effort but remains an important direction for our future work.
> Q3: Based on the results in Table 8, it seems that the proposed method paired with GPT-4o for planning, the result is better than that of the AGUVIS-72B. I was wondering about the results of the same configuration on other benchmarks.
We appreciate your interest in this observation! In addition to the AGUVIS-7B paired with GPT-4o for planning shown in Table 8 of OSWorld, we have also applied this configuration to other online GUI agent benchmarks, such as Mind2Web-Live, AndroidWorld, and MobileMiniWob, as detailed in Tables 4 and 5.
> Q4: For the VLM-based trajectory augmentation process, the current inner monologue components are generated by GPT-4o. Can other latest VLMs be used and compared?
Our data processing pipeline is model-agnostic and can be extended to more recent VLMs. Our data pipeline utilizes a VLM annotator to generate inner monologue reasoning from human-annotated actions. This is a natural fit for human behavior, where humans easily generate actions but find it costly to record their inner monologue. Conversely, current VLM struggle to make accurate action decisions but can more easily infer inner monologues given action decisions. This novel approach provides a promising pipeline for building agent trajectories with reasoning. We believe such annotations could equivalently be generated by open-source VLMs. Although time and cost constraints during rebuttal have prevented us from fully re-collecting data and retraining with alternative models, we believe that exploring other open-source VLMs for this process is an exciting avenue for future work! | Summary: The paper introduces AGUVIS, a unified vision-based framework for autonomous GUI agents designed to overcome limitations of existing approaches, which rely on textual representations, platform-specific actions, and closed-source models for reasoning. AGUVIS enables direct operation on screen images, standardizes cross-platform interactions via a plugin system, and incorporates inner monologue-structured reasoning through explicit thought processes—to handle complex tasks requiring planning.
Claims And Evidence: They are clear.
Methods And Evaluation Criteria: Yes.
Theoretical Claims: Proofs for theoretical claims are correct
Experimental Designs Or Analyses: Yes
Supplementary Material: Yes
Relation To Broader Scientific Literature: Related to the GUI understanding and Agent Reasoning.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: Strengths:
1. It achieves good results across offline and real-world online benchmarks.
2. It provides an effective framework to collect the GUI grounding and planning data.
Weaknesses:
1. The training method proposed in this paper does not have technical innovation. Most of the existing end-to-end GUI Agent training methods include Grounding pre-training and decision training[1,3,4], which is a general idea.
2. I do not agree about what authors claim in.the paper “first fully autonomous vision-based GUI agent that operates without relying on closed-source models”. Firstly, it is disputable that data collection pipline in this paper also need to leverage closed-source model (GPT). This is essentially distilling the common sense capability in from closed source models. Additionally, several studies have attempted to create algorithms that can enable open-source models to achieve the same or even better performance compared to the current open-source models [1,2,3]. This statement exaggerates the contribution of the article.
3. During the testing, is the model tested based on the setting of multi-image trajectories, or on the setting of text history + single image? Suffice it to say, is a setting based on multi-graph trajectories more appropriate.
4. I suggest author to consider to evaluate the model on other frequently-used datasets (e.g., AITZ[4]).
[1]. OS-ATLAS: A Foundation Action Model for Generalist GUI Agents
[2]. InfiGUIAgent: A Multimodal Generalist GUI Agent with Native Reasoning and Reflection
[3]. GUI Odyssey: A Comprehensive Dataset for Cross-App GUI Navigation on Mobile Devices
[4]. MobileVLM: A Vision-Language Model for Better Intra- and Inter-UI Understanding
[5]. Android in the Zoo: Chain-of-Action-Thought for GUI Agents
Other Comments Or Suggestions: N/A
Questions For Authors: When comparing GPT-4o+AGUVIS-7B and AGUVIS-72B, I found that the conclusion on Mind2Web-Live （Table 4) is not consistent with the conclusion on AndroidWorld (Table 5). Can you explain the reason?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We sincerely appreciate your thoughtful review and the opportunity to further clarify our contributions.
> **W1: Technical Innovation in Training Method**
Thank you for your insightful comments regarding the training methodology! We recognize that recent approaches share similar high-level components, such as grounding pre-training and decision training. However, AGUVIS's primary innovation lies in its unified framework that incorporates inner monologue reasoning. This enables the agent to operate effectively in new, previously unseen platforms without additional retraining. This integration, along with our training methods, distinctly sets AGUVIS apart from recent methods [1,3,4].
These innovations are empirically validated:
- Section 4.1 shows that our two-stage training strategy outperforms joint training and ablations.
- Section 4.2 highlights how inner monologue enables explicit planning and task decomposition, surpassing reactive action decision methods.
- Section 4.3 demonstrates cross-platform generalization, where AGUVIS trained on web/mobile tasks transfers well to desktop GUIs in OSWorld.
We would also greatly appreciate it if you could review these contributions highlighted by other reviewers as well. We strongly believe that the framework design, analyses, open-source model, and data contributions could significantly benefit and advance the GUI agent community.
> **W2: Claim of “first fully autonomous vision-based GUI agent that operates without relying on closed-source models”**
Thank you for highlighting this important aspect of our work. Our claim specifically emphasizes that AGUVIS, once trained, operates fully autonomously during task execution without dependence on closed-source models. Crucially, the model itself—including all training data, architectures, and procedures—is completely open-sourced, enabling full transparency and reproducibility.
While our data pipeline leveraged GPT-4o to generate inner monologue reasoning from human-annotated actions, this step was employed solely to enrich reasoning data rather than define action policies. And we believe such annotations could equivalently be generated by open-source VLMs, and exploring this capability with open-source models is definitely an important part of our future work.
Moreover, while recent research ([1, 2, 3]) has similarly aimed at competitive performance using open-source models, AGUVIS uniquely provides a unified vision-based framework capable of seamlessly operating across multiple diverse GUI environments. We will further clarify this comparative context in our revised manuscript to better highlight AGUVIS’s contributions and clearly differentiate it from concurrent work.
> **W3. Testing settings with multi-image trajectories vs. text history + single image.**
We appreciate the suggestion. AGUVIS currently uses text history + single image, balancing context richness and computational feasibility. Incorporating multiple images poses significant token cost challenges (~1200 tokens/image), especially when paired with inner monologue reasoning and 72B model size.
Nonetheless, we recognize the potential of multi-image context and plan to explore it in future iterations. Our open-source format supports multi-image inputs, enabling future work to build on this. As models like Qwen2.5-VL with advanced video ability, we anticipate AGUVIS will scale to multi-frame settings more efficiently.
> **W4. Evaluation on other datasets, such as AITZ.**
Thank you for this suggestion. We evaluated AGUVIS on the AITZ benchmark. Results are summarized below and demonstrate AGUVIS’s advanced performance:
|Model|Total Match|
|----|----|
|CogAgent(Zero-shot)|44.5|
|CogAgent(CoAT-finetuned) | 53.3 |
|AUTO-UI(Zero-shot)|34.5|
|AUTO-UI (CoAT-finetuned)|47.7|
|OS-Atlas-Pro-7B (CoAT-finetuned)|58.3|
|AGUVIS-7B|63.3|
|AGUVIS-72B|66.1|
These results will also be included in our revision to strengthen the paper’s empirical validation.
> **Q1. Discrepancy between results on Mind2Web-Live and AndroidWorld.**
We appreciate your attention to the detailed results. We think the discrepancy between Mind2Web-Live (Table 4) and AndroidWorld (Table 5) may stem from the differences in how GPT-4o understands and interacts with web interfaces versus mobile interfaces. We observed that GPT-4o tends to be distracted by extraneous details in high-resolution, information-rich web interfaces, which can lead to failures in planning. We will clarify these environmental factors and their impact on agent performance in our revision. | Summary: This paper introduces Aguvis, a vision-based framework that operates directly on screen images, providing a standardized cross-platform interaction method enhanced by structured reasoning through inner monologue. The researchers developed a comprehensive dataset with multimodal annotations and implemented a two-stage training approach that separately handles GUI grounding and planning. Experimental results demonstrate that Aguvis achieves leading performance on both offline and real-world benchmarks.
Claims And Evidence: The claim is clear, focusing primarily on the data construction methodology with inner monologue in GUI data. The experiments also confirm its effectiveness.
Methods And Evaluation Criteria: The mode architecture's innovation is relatively weak, as it appears quite similar to the baseline Qwen2-VL. However, the paper mainly proposes a new pipeline for GUI data construction. And it shows promising results on a wide range of benchmarks.
Theoretical Claims: This is not a theoretical paper.
Experimental Designs Or Analyses: The authors employ a comprehensive evaluation across both offline benchmarks (ScreenSpot, Multimodal-Mind2Web, AndroidControl) and online benchmarks (Mind2Web-Live, AndroidWorld, MobileMiniWob).
The ablation studies in Section 4 are well-structured, particularly those examining the impact of training stages, inner monologue, and cross-platform benefits. The error analysis in Section 4.5 provides a balanced view of the model's limitations.
Supplementary Material: The supplementary material is well-organized and provides valuable context for understanding the data collection and training details.
Relation To Broader Scientific Literature: Unified Vision and Action Model: AGUVIS extends research on GUI understanding through vision models, moving beyond traditional approaches that rely on accessibility trees or HTML (like WebGPT, Mind2Web).
CoT on GUI Domain: It also incorporates inner monologue techniques to enhance reasoning capabilities in multimodal contexts.
Essential References Not Discussed: The paper has a comprehensive literature review covering most relevant work.
Other Strengths And Weaknesses: Strengths:
- The performance is outstanding across multiple benchmarks.
Weaknesses:
- Recently, many co-current works have proposed similar unified model architectures, such as UI-TARS, OS-ATLAS, ShowUI, and CogAgent-9B. Could the authors compare their approach with these works, particularly in terms of data? The proposed method in this paper appears to be one of the best in balancing data utilization efficiency and model performance.
Other Comments Or Suggestions: The paper is well-written and structured logically.
Questions For Authors: The paper is well-prepared, and I have no further questions.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your thoughtful review of our AGUVIS paper. We appreciate your recognition of our comprehensive roadmap for developing a pure-vision GUI agent, particularly our data curation approach and training strategies. Your positive assessment of our experimental validations across multiple benchmarks is encouraging.
> Q1. Recently, many co-current works have proposed similar unified model architectures, such as UI-TARS, OS-ATLAS, ShowUI, and CogAgent-9B. Could the authors compare their approach with these works, particularly in terms of data? The proposed method in this paper appears to be one of the best in balancing data utilization efficiency and model performance.
We're pleased to see the growing interest in GUI agent research through concurrent works like UI-TARS, OS-ATLAS, ShowUI, and CogAgent-9B[4]. In comparison with these impressive efforts, we believe that AGUVIS makes a unique and complementary data contribution to the GUI agent community in several important ways:
- **Reasoning via Inner Monologue:** A defining feature of AGUVIS is the use of reasoning via inner monologue, which is not present in many concurrent works such as OS-ATLAS, ShowUI, and CogAgent-9B. This inner monologue allows AGUVIS to perform reasoning during interaction, which is crucial for the effective handling of complex tasks across multiple platforms (mobile, desktop, web). As shown in Section 4.3, AGUVIS achieves strong generalization by using a unified action space after inner monologue reasoning, enabling knowledge transfer across diverse environments. Additionally, the inner monologue surprisingly enhances GUI grounding performance, as detailed in Section 4.2 and Appendix E.1.2, as well as in our response to [Reviewer cBz9 Q1](https://openreview.net/forum?id=PlihOwfx4r¬eId=AzjUJ6TwN5). We believe that these contributions jointly underpin our balance between data utilization efficiency and model performance.
- **Open-Source Data Collection and Pipeline:** While recent concurrent works, such as OS-ATLAS and ShowUI, focus on grounding-centric training data, and more recent UI-TARS has made significant strides in leveraging in-house human-annotated trajectories with reasoning, AGUVIS offers a unique advantage with its large-scale, open-source data collection. Our dataset collection not only includes both unified grounding and trajectory annotations but also integrates reasoning into the data pipeline. This transparency and open-source nature of our data collection make AGUVIS a valuable resource for the community to build upon and extend our work more easily.
We greatly appreciate your recognition of AGUVIS as one of the leading approaches in balancing data efficiency and model performance. We believe that our open-source data and the novel inner monologue reasoning offer complementary contributions that will drive continued progress in the development of autonomous GUI agents. | Summary: This paper introduces AGUVIS, a vision-based UI agent designed to operate across diverse digital platforms. The authors collect data from existing resources and do some essential augmentation. They then leverage a vision-language model to train AGUVIS in two stages, grounding and planning, to improve interaction capabilities. The framework is evaluated on multiple datasets, including grounding, offline agent and online agent benchmarks, demonstrating strong performance across various GUI benchmarks.
Claims And Evidence: The claims are adequately supported with sufficient experimental results.
Methods And Evaluation Criteria: The method is simple and straightforward. The authors use GPT-4o to "translate" GUI actions into natural language, which helps agent understanding during fine-tuning. They then apply standard fine-tuning on the aggregated grounding data and augmented planning trajectories. Essentially, they do not create a new dataset or propose a novel framework, so the methodological novelty may seem limited. However, significant engineering effort is also involved, such as aggregating datasets from various sources, standardizing formats, validating through human studies, etc. Also, the authors open-source their trained models and datasets, which could benefit the academic community. These altogether could build up sufficient contribution for the paper overall.
The evaluation benchmarks are comprehensive, including grounding, offline GUI agent and online GUI agent evaluation.
Theoretical Claims: N/A. The paper does not include much theoretical claim. (Not a weakness)
Experimental Designs Or Analyses: In Section 4.2 and Table 6, the authors state that Inner Monologue benefits both grounding and planning. However, only the planning stage (Stage 2) incorporates Inner Monologue, while the grounding stage (Stage 1) only relies on existing datasets without such augmentation. So I wonder how Inner Monologue contributes to performance gains in grounding? I notice that the authors provide some explanation in Appendix E.1.2 that "This is mainly because the low-level instructions of inner monologue act as atomic instruction and grounding action pairs, also enhancing the grounding ability of our GUI agents." However, it's kind of hard to understand this explanation. It would be helpful if the authors could elaborate further on this point.
Supplementary Material: Yes. The prompt format, data statistics, and most additional experimental results and analysis.
Relation To Broader Scientific Literature: The open-sourced dataset and model checkpoints are helpful for future academic research.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: See above.
Other Comments Or Suggestions: N/A
Questions For Authors: 1. Could the authors further clarify the difference between the self-plan and enforced plan settings? I reviewed the prompt templates on pages 27 and 28 but couldn’t identify any differences between them. Could the authors provide an explanation?
2. Regarding the proposed Aguvis model, does it generate the next step iteratively, or does it first generate an overall plan and then generate each step iteratively? I assume it's the first one, but would like to confirm.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We sincerely appreciate your thorough review and positive assessment of our work. We're particularly encouraged by your recognition of our comprehensive evaluation benchmarks, the engineering effort involved in dataset aggregation and standardization, and the value of our open-sourced models and datasets to the research community.
Regarding your questions and comments:
> **Q1: On Inner Monologue's Contribution to Grounding Performance**
Thank you for this insightful question. You correctly observed that while Inner Monologue is introduced in Stage 2, it also enhances grounding performance, which might seem counterintuitive. Let us clarify:
In standard trajectories without inner monologue, the data structure is:
> (High-level goal G, observation $o_1$, action $a_1$, observation $o_2$, action $a_2$, ...)
When we augment with inner monologue, we introduce low-level instructions, transforming it to:
> (High-level goal G, observation $o_1$, low-level instruction $a_1^{inst}$, action $a_1$, observation $o_2$, low-level instruction $a_2^{inst}$, action $a_2$, ...)
This transformation creates high-quality explicit instruction-action pairs ($o_i$, $a_i^{inst}$, $a_i$) within each step, essentially embedding "grounding examples" throughout the trajectory. The model learns to:
1. Interpret high-level goals into precise low-level instructions
2. Ground these instructions to specific UI elements
3. Generate appropriate actions
As shown in Table 6, removing inner monologue reduces performance on ScreenSpot from 84.4% to 79.3% and also has a strong impact on AndroidControl Low-Level tasks (80.5% → 69.1%). This suggests that the ability to decompose tasks into explicit low-level instructions significantly improves grounding precision.
> **Q2: On Self-Plan vs. Enforced Plan Settings**
Thank you for pointing out this confusion. As shown in Appendix E.2.1 and Figure, the difference between these settings lies in how we prompt the model in response:
**Self-Plan Setting:**
```
<|im_start|>assistant<|recipient|>
[The model decides whether to plan first with all or directly execute actions with os]
```
In this setting, the model autonomously determines whether to generate planning thoughts based on task complexity. For simple tasks like "Click the 'Buy' button," it might directly output:
```
<|im_start|>user
Click the 'Buy' button.
<|im_end|>
<|im_start|>assistant<|recipient|>os
pyautogui.click(0.34, 0.45)
<|im_end|>
```
While for some implicit tasks, it might choose to plan first:
```
<|im_start|>user
Send current webpage.
<|im_end|>
<|im_start|>assistant<|recipient|>all
Thought: To share the current page, I need to find and click the share icon, which is typically represented by a network or link symbol. This icon is usually located in the browser's toolbar or menu.\nAction: Click the share icon in the browser to share the current page.
<|im_end|>
<|im_start|>assistant<|recipient|>os
pyautogui.click(0.34, 0.45)
<|im_end|>
```
**Enforced Plan Setting:**
```
<|im_start|>assistant<|recipient|>all
Thought: [The model is forced to generate planning thoughts before actions]
```
The enforced plan setting explicitly requires the model to engage in high-level reasoning before taking actions. As noted in our error analysis (Section 4.5), this enforced planning resolves approximately 20% of grounding errors by encouraging the model to carefully consider the task context, potential ambiguities, and available UI elements before committing to action.
We will further clarify this part in our revised manuscript. Thanks for helping improve our work!
> **Q3: On AGUVIS Model's Generation Approach**
Yes, AGUVIS generates the next step iteratively rather than first generating an overall plan and then executing steps. At each time step, given the current observation and task history, the model:
1. Generates thoughts about the current state in relation to the goal
2. Determines the appropriate next action
3. Executes the action and receives a new observation
4. Repeats the process until task completion
This iterative approach allows AGUVIS to adapt to changing UI states and unexpected outcomes during task execution, rather than rigidly following a predetermined plan. | null | null | null | null | null | null |
Towards Trustworthy Federated Learning with Untrusted Participants | Accept (poster) | Summary: Achieving robustness against Byzantine workers and preserving data privacy are two important objectives in distributed learning. Existing work primarily studies each problem separately, and achieving both simultaneously is a challenging task. In this paper, the authors propose CAFCOR, an algorithm designed to achieve both robustness and data privacy without relying on a fully trusted central server. The CAFCOR algorithm combines robust gradient aggregation with correlated noise injection, using shared randomness between workers. In this setting, each worker perturbs its gradient update using a combination of independent noise and correlated noise. The server then applies CAF (covariance-bound agnostic filter), which adjusts weights based on variance contributions to suppress the influence of Byzantine workers. The authors demonstrate that CAFCOR achieves privacy guarantees comparable to central differential privacy while maintaining robustness against Byzantine attacks.
Claims And Evidence: I think the claims are generally well-supported. However, please see the Experimental Designs or Analyses section.
## update after rebuttal
I thank the authors for their responses.
While some of my concerns have been addressed, my main concern regarding the limited scope of the experiments remains unresolved. I think this paper has the potential to make a significant contribution, but it would require a major revision to reach that stage. I have decided to lower my initial rating.
Methods And Evaluation Criteria: - The authors introduce a refined version of secret-based local differential privacy (SecLDP), which extends traditional LDP by assuming that workers share randomness. This relaxation of the trust assumption in CDP seems to improve utility over LDP models while still maintaining privacy.
- The authors provide a theoretical analysis of the privacy-utility trade-off and robustness against Byzantine workers achieved by CAFCOR.
- The proposed CAF algorithm appears to be sensible and with theoretical guarantees. The requirement of shared randomness, achieved through a one-time encrypted communication round, seems reasonable.
- The complexity of the proposed CAF aggregation appears to be high, making it impractical for high-dimensional models, e.g., deep learning. While the authors mention a power method-based approximation, its practical applicability in large-scale problems needs to be verified.
- The assumption of bounded heterogeneity seems to limit the applicability. In real-world distributed learning scenarios, data can be highly heterogeneous.
Theoretical Claims: I checked briefly the main theoretical results but not their proofs.
Experimental Designs Or Analyses: - The experiments are weak. Even considering the theoretical contributions of the paper, evaluating on MNIST and Fashion-MNIST is insufficient. To demonstrate the practical utility of the algorithm, the authors should perform experiments on more challenging real-world datasets (e.g., ImageNet, CIFAR-100).
Supplementary Material: I read through the theoretical statements in the appendix, but did not check their proofs.
Relation To Broader Scientific Literature: Please see the Summary section.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: N/A
Other Comments Or Suggestions: - Gradient clipping appears to be performed at the client-side, it is not clear why this is necessary. Given that gradient clipping could potentially be handled at the server-side, requiring additional client-side operations beyond momentum generation may reduce the practical applicability of CAFCOR.
- Please explicitly define the nature of Byzantine workers. Do they have access to the entire learning process, or are there any limitations on their capabilities?
- Please clarify how data heterogeneity is modeled in the experiments. Specifically, how are the datasets distributed among clients, and what level of heterogeneity is introduced?
Questions For Authors: N/A
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: We thank the reviewer for their insightful feedback. Below, we address the key points raised:
### **Experimental Scope**
> evaluating on MNIST and Fashion-MNIST is insufficient [...]
The reviewer’s suggestion to evaluate additional datasets is highly valid. We stress, however, that our current evaluation on MNIST and Fashion-MNIST is already extensive, rigorously testing our algorithm CafCor across multiple threat models, robust aggregation methods, and varying data heterogeneity levels (Section 5). Crucially, our setting is quite *challenging* even on these standard datasets, since we enforce **both** differential privacy without trusting the server and Byzantine resilience under state-of-the-art attacks. Indeed, as Figure 2 clearly illustrates, prior state-of-the-art methods suffer substantial accuracy losses under these combined constraints. Also, the SOTA method by Allouah et al. (2023b, ICML) could only scale to small logistic regression tasks with weaker theoretical guarantees, highlighting the novelty and practical significance of our results.
We recall that our core contribution is a rigorous theoretical framework that significantly advances the resolution of the privacy–robustness–utility trilemma (Allouah et al. 2023b, ICML), with minimal trust assumptions. Theoretically, we approach the minimax-optimal privacy-utility trade-off achievable in the ideal scenario (trusted server, no Byzantine adversaries—Corollary 4.1). Empirically, CafCor closely matches this optimal baseline even under Byzantine threats (Figure 1). Extending to larger datasets such as ImageNet is an important and exciting future step, which we will explicitly mention.
### **Computational Complexity**
> The complexity of the proposed CAF aggregation appears to be high, making it impractical for high-dimensional models, e.g., deep learning
We thank the reviewer for highlighting this important aspect. CafCor’s aggregation complexity, while higher than simple averaging, is significantly lower than previous state-of-the-art methods like SMEA, whose runtime complexity is exponential in the number of Byzantine workers $f$. Specifically, SMEA performs an exhaustive subset search across subsets of size $n-f$, making it computationally infeasible. In contrast, our covariance-based CAF aggregation with power-method approximation achieves an efficient runtime of $\mathcal{O}(f n d \log d)$, enabling scalability to high-dimensional models, far beyond the closest prior work (Allouah et al. 2023b), which only scaled to small logistic regression tasks.
We refer the reviewer to new experiments, included in our response to Reviewer 6PZT due to space constraints, that explicitly demonstrate this complexity advantage over SMEA, and will include these new experiments in the revision.
### **Clarifications on Definitions and Methods**
> Gradient clipping appears to be performed at the client-side, it is not clear why this is necessary.
> Please explicitly define the nature of Byzantine workers
> Please clarify how data heterogeneity is modeled in the experiments
We thank the reviewer for this helpful request for clarity.
Byzantine workers are defined as workers capable of arbitrary deviation from the protocol and collusion, with full knowledge of the algorithm. Data heterogeneity is modeled through a Dirichlet distribution (following Hsu et al. 2019, see Section 5), simulating realistic conditions.
Besides, bounded heterogeneity is a common assumption in distributed learning for convergence analyses (Karimireddy et al. 2022, Farhadkhani et al. 2022, Allouah et al. 2023b), although heterogeneity is not the focus of our current work.
Finally, gradient clipping at the client side is standard practice, essential for differential privacy guarantees, and carries low computational overhead. | Summary: The paper proposes a technique to perform distributed mean estimation with differential privacy guarantees and robustness to byzantine participants. To achieve privacy, if first adopts the anti-correlated noise method of [1,2]. To achieve robustness, it uses the empirical covariance matrix of the contributions to filter byzantine inputs, a technique which is specially tailored to work under correlated DP noise. The resulting protocol inherits the accuracy improvement that approaches central DP of [1,2] while improving the resilience to malicious participants of related byzantine aggregation techniques that are less prepared to work under DP noise.
References (will be also used below):
[1] Sabater, César, Aurélien Bellet, and Jan Ramon. "An accurate, scalable and verifiable protocol for federated differentially private averaging." Machine Learning 111.11 (2022): 4249-4293.
[2] Allouah, Youssef, et al. "The privacy power of correlated noise in decentralized learning." arXiv preprint arXiv:2405.01031 (2024).
[3] Allouah, Youssef, et al. "On the privacy-robustness-utility trilemma in distributed learning." International Conference on Machine Learning. PMLR, 2023.
## update
The authors have successfully addressed all my concerns and therefore I raise my score. As long as the discussed aspects are clarified, I think the paper deserves to be accepted.
Claims And Evidence: The main claim of the paper is that the proposed byzantine aggregation technique outperforms previous techniques for FL updates that are hidden under correlated DP noise. This is theoretically and empirically backed for standard aggregation techniques.
However, it is not clear why the SMEA aggregation method [3] is not included in the comparison. Theoretically, it seems that SMEA has the same robustness as CafCor. However, it is not present in the comparison of the empirical evaluation.
Therefore, the claim is not completely backed for related previous aggregation techniques.
Methods And Evaluation Criteria: The paper provides a theoretical analysis and an experimental evaluation.
The experimental analysis is performed for using MNIST and fashion-MNIST datasets under homogeneous and heterogeneous distributions, which is reasonable. Attacks also seem reasonable.
The theoretical analysis of utility/robustness (i.e. Proposition 4.1) is reasonable as it provides clear comparisons with previous techniques. The rest of the theoretical results have a less clear message. First, I am not sure why a new privacy analysis is necessary, as current trade-offs are inherited from [1,2] and the novel part of the contribution (i.e. the CAF filter) is a post processing of such protocols. Second, I do not see a clear take-away from the convergence analysis that relates to the claims of the paper, whose results and techniques seem standard.
Theoretical Claims: I have checked the proofs theoretical claims of Theorem 4.1 and Proposition 4.1 and I did not see problems. Proofs of Theorems 4.2 and Corollary 4.1 seem in shape, but I have not checked all the derivations of the appendix related to them.
Experimental Designs Or Analyses: The experimental design is reasonable in general. However there are a few issues:
- The number of runs of the protocol to get the confidence intervals on the reported accuracy is rather small (5 seeds).
- I am not really sure why Opacus is used to estimate the privacy budget if the paper provides a clear privacy analysis which gives explicit $\epsilon$ and $\delta$ after execution
Supplementary Material: I have reviewed appendices A, B and D.
Relation To Broader Scientific Literature: - The contributions are well positioned with respect to what are called within the paper as standard byzantine aggregation techniques: coordinate-wise trimmed mean and median (Yin et al., 2018), geometric median (Chen et al., 2017), Multi-Krum (Blanchard et al., 2017), and mean around median (Xie et al., 2018). However, as said before, the contribution is not well positioned with respect to the resilience of SMEA [3]. In addition, it is not sufficiently clear how different is the proposed technique with respect to SMEA.
- The paper states that previous literature has not studied the resilience of correlated DP noise to malicious participants. This does not seem to be true, as [1] studies cryptographic techniques (in particular, zero knowledge proofs) to deal with malicious participants under privacy constraints. The paper should broadly position to such techniques.
- The paper claims that [1] does not use Renyi divergences for their privacy guarantees. I am not sure why that is a disadvantage. Renyi divergences are a tool for privacy accounting but it is not mandatory to use it as long as guarantees are provided. What makes the protocol private are the obtained with $(\epsilon, \delta)$ parameters and their trade-off with respect to $\sigma_{cor}^2$ and $\sigma_{ind}^2$. Moreover, [1] provides equal or better trade-offs between privacy and the variance of the correlated noise $\sigma_{cor}^2$ than [2] for the extreme cases of communication topologies, which suggests that the privacy analysis is tighter.
Essential References Not Discussed: To the best of my knowledge, I don't see any key reference that has been ignored.
Other Strengths And Weaknesses: - The communication cost is not discussed: implementing the pairwise shared randomness requires that all parties communicate with each other to minimize $\sigma_{cor}^2$. This incurs in a high communication cost ($O(n^2)$ messages). Considering that the authors claim efficiency as a feature of the protocol, this should be brought to the table.
Other Comments Or Suggestions: I have no further comments.
Questions For Authors: Please address the raised points with respect to the comparison with SMEA [3] and [1,2] raised in my review.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We thank the reviewer for their detailed and thoughtful feedback. Below, we address the points raised:
### **Empirical Comparison with SMEA**
> it is not clear why [...] SMEA [3] is not included in the comparison. Theoretically, it seems that SMEA has the same robustness as CafCor.
We thank the reviewer for this valuable suggestion. As noted, SMEA (Allouah et al., 2023b) was initially excluded from our main experiments due to its exponential complexity. Specifically, SMEA exhaustively searches all subsets of size $n - f$ for the minimal covariance top eigenvalue, incurring prohibitive computational costs. In contrast, our CAF aggregation method achieves a runtime of $\mathcal{O}(f n d \log d)$ using an iterative spectral reweighting scheme.
**1\. Computational Complexity Comparison**
To explicitly demonstrate SMEA's prohibitive computational complexity, we report runtime ratios relative to simple averaging (smaller is better), with $n=30$ workers and $f=3$ Byzantine workers, on models of varying dimension $d$.
| Dimension ($d$) | SMEA | CAF | MeaMed | Geometric Median (GM) |
|---------------------|--------------|-------|--------|------------------|
| $2.5 \times 10^6$ | 30,251 | **28**| 112 | 62 |
| $5 \times 10^6$ | 61,142 | **51**| 197 | 78 |
| $10^7$ | 117,255 | **100**| 378 | 126 |
CAF clearly achieves a dramatically lower complexity than SMEA and can even be more efficient than standard aggregations such as MeaMed and Geometric Median.
**2\. Utility Comparison**
We also execute SMEA in the setting of Figure 2 (MNIST), where we consider a small system comprised only of $n=15$ and $f=5$ Byzantine workers.
| Method | Accuracy (\%) |
|------------------------|----------------------|
| Averaging (no attack) | $93.05$ |
| SMEA | $89.96$ |
| **CAF** | ${\bf 89.60}$ |
| MeaMed | $44.81$ |
| Median (CWMED) | $29.66$ |
| Trimmed mean (CWTM) | $12.74$ |
| Geometric Median (GM) | $9.73$ |
CAF matches SMEA's accuracy, significantly outperforming other standard robust methods, and approaching the averaging baseline (thanks also to our correlated noise scheme). This result aligns with our theory (Proposition 4.1), as the reviewer helpfully pointed out.
We will clearly highlight these new results in the revised manuscript.
### **Theoretical Analysis**
> The theoretical analysis [...] is reasonable [...] First, I am not sure why a new privacy analysis is necessary [...]. Second, I do not see a clear take-away from the convergence analysis [...]
This comment is insightful. Our privacy analysis (Theorem 4.1) is distinct from [1,2], addressing a new threat model where Byzantine adversaries partially collude with the untrusted server. A notable insight (Section 4.1) is that honest workers require no independent noise injection when a non-colluding Byzantine worker exists. Further, Proposition 4.1 alone cannot derive our final privacy-utility result (Corollary 4.1); Theorem 4.2 is essential to quantify correlated noise effects across iterations, controlled by CAF aggregation and local momentum in CafCor. These dependencies were not analyzed in [1,2]. We will explicitly clarify these points.
### **Positioning relative to Reference [1]**
> [1] studies cryptographic techniques [...] to deal with malicious participants [...]. The paper should broadly position to such techniques.
Reference [1], included in our paper, uses cryptographic checks (e.g., correct computation, bounded inputs) to verify malicious participants' messages but provides no explicit utility guarantees under arbitrary Byzantine attacks passing these checks. In contrast, CafCor addresses a more challenging scenario: adversaries crafting inputs that pass such verification yet harm model performance. Thus, cryptographic verification alone is insufficient for our Byzantine robustness objective. CafCor explicitly guarantees privacy and utility even under these stronger adversarial conditions (Corollary 4.1). We agree the privacy analysis in [1] may be tighter than [2], though both focus on decentralized topologies unlike our federated setting. We will highlight this explicitly.
### **Communication Cost**
> The communication cost is not discussed [...]
Pairwise shared randomness (exchanging at most $n(n-1)$ integers) occurs offline once, incurring negligible quadratic communication compared to repeated training communications (model weights of size $d$ over many iterations). We will clarify this explicitly.
### **Additional Clarifications**
> I am not really sure why Opacus is used to estimate the privacy budget [...]
We use Opacus solely for tighter practical composition of per-round privacy budgets (using per-round theoretical guarantees of Theorem 4.1 with $T=1$). We will explicitly clarify this usage.
---
Rebuttal Comment 1.1:
Comment: Dear Authors,
Thank you for your clarifications. They were very helpful. Some of my concerns have been clarified. Here are some additional comments:
- Privacy analysis: You say that "Our privacy analysis (Theorem 4.1) is distinct from [1,2], addressing a new threat model where Byzantine adversaries partially collude with the untrusted server. ". However, [1] *does* take into account adversarial parties that collude with the server. Therefore I am not sure what is the difference. I will revise the paper and take it into account in my final score.
- Regarding the use of Opacus: I have no complain on the use of Opacus on the experiments as long as the used composition technique is cited in priority to the software.
---
Reply to Comment 1.1.1:
Comment: Thank you very much for your feedback. We hope that our clarifications address your concerns and that you will consider increasing your score.
**Privacy Analysis Comment**
Thank you for this helpful comment. We agree that [1] considers adversaries that can collude with the server, and we will update the paper to give [1] proper credit and clarify the positioning.
Our setting includes a new aspect: we model not only honest users and malicious users who collude with the server, but also *malicious users who do not collude* with the server to violate privacy.
A key implication is that when such non-colluding malicious users are present, honest users do not need to add independent noise for privacy. The correlated noise shares from these users act as a mask (see discussion following Theorem 4.1). This leads to improved empirical performance and, to our knowledge, was not addressed in prior work. Specifically, Figure 1 shows a significant performance gap between the case where all malicious users collude with the server (noted "ByzLDP" in the legend) and where none do (noted "SecLDP" in the legend). This difference is captured thanks to the privacy analysis in Theorem 4.1.
While the privacy analysis in Theorem 4.1 is not our main contribution, we agree it is important to clarify. We will update the paper to make this distinction clearer and to acknowledge the contributions of [1] more explicitly.
We also recall, as mentioned in the initial rebuttal, that [1] focuses on cryptographic verification (e.g., checking message correctness and bounded inputs), but does not offer explicit utility guarantees under general malicious behavior. In contrast, our work combines privacy guarantees with a novel robust aggregation to ensure utility even under stronger adversarial conditions.
**Opacus Comment**
Thank you for the suggestion. We confirm that our privacy accounting uses the RDP framework of Balle et al., “Hypothesis testing interpretations and Rényi differential privacy”, AISTATS 2020. We will cite this directly as the main reference for the composition method. | Summary: This paper proposes a novel methodology to achieve resilience in the face of malicious parties colluding with an untrusted server in the distributed learning framework as well as privacy guarantees, based on a weak assumption that each pair of communicating workers secretly share a seed of randomness, used to inject correlated noise when aggregating gradients. As experiments show, the proposed method achieves stronger guarantees than methods based on local differential privacy and even approach those of centralized differential privacy, which do rely on an assumption of a fully trusted server. Empirical results validate.
Claims And Evidence: The claims are supported theoretically and experimentally.
Methods And Evaluation Criteria: Methods and data are well-chosen.
Theoretical Claims: Theorems 4.1 and 4.2 seem sound.
Experimental Designs Or Analyses: The proposed method builds upon DSGD, and also compares against its plain version as a baseline.
Supplementary Material: Results on Rényi differential privacy.
Relation To Broader Scientific Literature: First analysis of secret-based local differential privacy in adversarial distributed learning, considering an untrusted server and workers who aim to disrupt the learning as well as to compromise the privacy of honest workers by colluding with the server. Most of the works is based on previous works by Mironov and Allouah et al.
Essential References Not Discussed: The claim that [Lamport 1982] labeled misbehaving workers in a certain way is false. That paper narrates a parable and applies a certain label to all workers (i.e., generals), not only misbehaving ones.
Other Strengths And Weaknesses: NA
Other Comments Or Suggestions: NA
Questions For Authors: Is there a reason for the main body of the paper to continuously invoke a cultural bias that labels people of a certain cultural heritage as dishonest or malicious?
Ethical Review Flag: Flag this paper for an ethics review.
Ethics Expertise Needed: ['Discrimination / Bias / Fairness Concerns', 'Other expertise']
Ethical Review Concerns: The paper continuously alludes to a prejudice that labels people of a certain cultural heritage as dishonest and untrustworthy.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We clarify our intent and recall our contributions below following the reviewer's comments, and we welcome further discussion to refine our presentation.
### **Use of "Byzantine” Terminology**
This is a standard term in distributed computing literature (Lamport et al., 1982), referring strictly to arbitrary malicious behavior, with no cultural implications. Nevertheless, we remain open to adopting alternative phrasing.
We recall that our core contribution is a rigorous theoretical framework that significantly advances the resolution of the privacy–robustness–utility trilemma (Allouah et al. 2023b, ICML), with minimal trust assumptions. Theoretically, we approach the minimax-optimal privacy-utility trade-off achievable in the ideal scenario (trusted server and no attacks, see Corollary 4.1). Empirically, CafCor closely matches this optimal baseline even under state-of-the-art attacks (Figure 1).
---
Rebuttal Comment 1.1:
Comment: 1st comment:
A term that is an exonym for a people or culture cannot be 'with no cultural implications'. This term was chosen because of its pejorative sense recorded in dictionaries, which reflects a historically ingrained cultural bias disparaging a group of people as devious, treacherous, and potentially malicious. If the goal is to refer to devious workers without invoking a cultural prejudice, how about calling them 'devious workers'?
2nd comment:
The decision made here and the accompanying arguments about the contribution are appreciated.
Considering the cited references, it is worth highlighting the following key points:
(A) [Lamport et al., 1982] was published at a time when there was less awareness around cultural stereotyping, and the review process did not include ethical considerations; besides, it does not endorse the use cultural terms for concepts like deviousness or dishonesty; it merely recounts a historical parable involving a group of generals.
(B) [Blanchard et al., 2017] presents a troubling example of cultural bias, endorsing the use of a cultural term as a synonym for 'devious' and 'dishonest', and naming the proposed function after a Bulgarian khan who "undertook offensive attacks against the Byzantine empire" and is known for acts such as fashioning drinking vessels from, and toasting with, the skulls of defeated leaders [1]. Regardless of the historical accuracy of such accounts, which all derive from Greek sources, technical scientific terminology should not rest on specific interpretations of historical events and personalities. As historical understanding evolves, any given narrative may come to seem outdated and even embarrassing. In any case, the glorification of violence and the reinforcement of stereotypes distract from scientific objectives and contribute to an unhealthy narrative within the field.
To foster an ethically responsible and inclusive research environment, we must critically reflect on the implications of such historical references and ensure that the language used in our field is technically precise and culturally sensitive. Unlike mythology, which invites creative interpretation, history demands careful, evidence-based refinement and bears directly on people’s identities. It is therefore inappropriate to single out any people as a symbol of deceit. Mythological figures are more fitting for such symbolic purposes. For instance, Norse mythology offers a useful term for describing something arbitrary, deceptive, and devious: Lokian.
[1] E. N. Luttwak, The Grand Strategy of the Byzantine Empire, Harvard University Press, 2009.
---
Reply to Comment 1.1.1:
Comment: We appreciate your feedback regarding the use of the term “Byzantine.” Although this term has long been established in distributed computing and federated learning (e.g., Lamport et al., 1982; Blanchard et al., 2017), we understand your concerns.
We have decided to adopt alternative phrasing in the revised manuscript (changing “Byzantine” everywhere to “adversarial”).
We trust that this modification, alongside our theoretical and empirical contributions, addresses your concerns. | Summary: The paper introduces an algorithm (CAFCOR) to achieve privacy and robustness in distributed learning without relying on a trusted central server. In particular, it employs correlated noise injection inspired by secret sharing and combines it with a robust aggregation technique to mitigate Byzantine workers' impact. The algorithm achieves near-central DP (CDP) utility by leveraging secret-based local differential privacy. Extensive experiments on MNIST and Fashion-MNIST datasets demonstrate CAFCOR's superior performance under various Byzantine attack scenarios compared to existing methods.
Claims And Evidence: - The CAF aggregation method is shown to be resilient to a significant number of Byzantine workers.
- The experimental results support the theoretical claims, demonstrating improved accuracy compared to Local Differential Privacy (LDP) baselines.
- However, the experiments are limited to only MNISST and Fashion-MNIST.
- The explanation of how it practically handles high-dimensional data could be clarified.
Methods And Evaluation Criteria: - The use of shared randomness and correlated noise injection can improve the privacy-utility trade-off.
- It is necessary to compare against more existing state-of-the-art methods beyond LDP and CDP.
Theoretical Claims: The theoretical claims are thoroughly developed. However, to improve clarity, more intuitive explanations of the theoretical results should be included.
Experimental Designs Or Analyses: The experimental design is limited.
Supplementary Material: NA
Relation To Broader Scientific Literature: The paper discusses related work in differential privacy, Byzantine robustness, and secret sharing.
Essential References Not Discussed: The related works discussed are sufficient.
Other Strengths And Weaknesses: ### Strengths:
- Effective handling of Byzantine workers through robust aggregation.
- Empirical results support the theoretical findings.
### Weaknesses:
- Limited evaluation datasets.
- The complexity of CAF aggregation may hinder real-time deployment in large-scale systems.
- Lack of comparison with recent privacy-preserving FL methods like DP-FL or DP-SGD.
Other Comments Or Suggestions: NA
Questions For Authors: 1. How does CAFCOR perform on datasets with real-world heterogeneity and natural label noise?
2. What is the computational overhead of the CAF aggregation technique, particularly for large-scale models?
3. Can CAFCOR be integrated with gradient compression or sparsification techniques to improve communication efficiency?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank the reviewer for their insightful feedback. Below, we address the key points raised:
### **Experimental Scope**
> Limited evaluation datasets.
The reviewer’s suggestion to evaluate additional datasets is highly valid. We stress, however, that our current evaluation on MNIST and Fashion-MNIST is already extensive, rigorously testing our algorithm CafCor across multiple threat models, robust aggregation methods, and varying data heterogeneity levels (Section 5). Crucially, our setting is quite *challenging* even on these standard datasets, since we enforce **both** differential privacy without trusting the server and Byzantine resilience under state-of-the-art attacks. Indeed, as Figure 2 clearly illustrates, prior state-of-the-art methods suffer substantial accuracy losses under these combined constraints. Also, the SOTA method by Allouah et al. (2023b, ICML) could only scale to small logistic regression tasks with weaker theoretical guarantees, highlighting the novelty and practical significance of our results.
We recall that our core contribution is a rigorous theoretical framework that significantly advances the resolution of the privacy–robustness–utility trilemma (Allouah et al. 2023b, ICML), with minimal trust assumptions. Theoretically, we approach the minimax-optimal privacy-utility trade-off achievable in the ideal scenario (trusted server, no Byzantine adversaries—Corollary 4.1). Empirically, CafCor closely matches this optimal baseline even under Byzantine threats (Figure 1). Extending to larger datasets such as ImageNet is an important and exciting future step, which we will explicitly mention.
### **Comparison with State-of-the-Art Methods**
> Lack of comparison with recent privacy-preserving FL methods like DP-FL or DP-SGD.
We believe there is a misunderstanding regarding our comparisons. In fact, we already benchmark CafCor against strong, theoretically optimal baselines in the paper: DP-SGD (pointed out by the reviewer) adapted for federated learning under local (LDP) and central (CDP) differential privacy. Figures 1 and 2, where "DSGD" denotes FL-adapted DP-SGD, demonstrate that CafCor outperforms LDP and closely approaches CDP (i.e., trusted server) utility. Moreover, in Section 5.2, we compare to numerous standard Byzantine-robust defenses. We will clarify this in the paper.
### **Computational Complexity**
> The complexity of CAF aggregation may hinder real-time deployment in large-scale systems.
We thank the reviewer for highlighting this important aspect. CafCor’s aggregation complexity, while higher than simple averaging, is significantly lower than previous state-of-the-art methods like SMEA, whose runtime complexity is exponential in the number of Byzantine workers $f$. Specifically, SMEA performs an exhaustive subset search across subsets of size $n-f$, making it computationally infeasible. In contrast, our covariance-based CAF aggregation with power-method approximation achieves an efficient runtime of $\mathcal{O}(f n d \log d)$, enabling scalability to high-dimensional models, far beyond the closest prior work (Allouah et al. 2023b), which only scaled to small logistic regression tasks.
Finally, compression is feasible but beyond our current focus on privacy and robustness.
We refer the reviewer to new experiments, included in our response to Reviewer 6PZT due to space constraints, that explicitly demonstrate this complexity advantage over SMEA, and will include these new experiments in the revision.
---
Rebuttal Comment 1.1:
Comment: I want to thank the authors for responding to my concerns with more explicit clarification and a new experiment. Hence, I decided to change my recommendation for this paper. | null | null | null | null | null | null |
Tuning Sequential Monte Carlo Samplers via Greedy Incremental Divergence Minimization | Accept (poster) | Summary: The authors propose a method for tuning kernels in SMC by minimising a KL-divergence between proposal paths and target paths. This optimisation is done using a gradient free method. They show that by adapting the step size with their method they get better normalising constant estimates than using fixed step sizes, and that their adaptation scheme has a smaller computation cost compared to setting the step size using gradients.
## update after rebuttal
I maintain my recommendation for acceptance.
Claims And Evidence: From the paper the two key empirical claims are:
1) Our methods achieve lower variance in normalizing
constant estimates compared to the best fixed step sizes
obtained through grid search or SGD-based tuning methods
Figures 2,3,8 and 9 evidence this, with the exception of one or two examples. Some interpretation as to why, eg, the method under-performed on the rats dataset would be welcome.
2) Additionally, the computational cost of our adaptation
scheme is several orders of magnitude lower than that of
SGD-based approaches (Section 5).
Figures 5, 10, 11, 12 and 13 show this. The choices made in the experimental setups for these didn't seem unreasonable so I think these claims were well evidenced.
Methods And Evaluation Criteria: The datasets used seem quite standard for evaluating SMC methods. One thing I am not sure of is whether just reporting normalising constant is sufficient to show the superiority of this method, it would have been nice to see something like ESS or some assessment of posterior quality like moment estimates.
For comparing against end to end optimisation it wasn't clear to me why a neural network as opposed to any other method would be chosen for learning the step size.
Theoretical Claims: I didn't check these very closely, but appreciated that some empirical study was done to see how realistic the assumptions were (figure 1.)
Experimental Designs Or Analyses: The experiments seem sound if a bit limited (as I previously mentioned) from what is relayed in the paper. I am curious why 32 replications were used to get the confidence intervals in the adaptive tuning vs fixed experiments but only 5 in the end-to-end optimisation experiments.
Supplementary Material: Plots in the appendix that were referred to in the main text, as well as the sections outlining implementation details.
Relation To Broader Scientific Literature: This paper aims to tune the hyperparameters of SMC kernels by minimising the divergence between the proposal path and the target path. This idea has similarities to annealed flow transport Monte Carlo and normalising flow.
The issue of adapting the hyperparamters of SMC kernels is a long standing one (P Fearnhead and Benjamin M. Taylor, An Adaptive Sequential Monte Carlo Sampler).
The idea of using the KL divergence to tune parameters of the proposal distribution in SMC also appears in (Shixiang et. al. Neural Adaptive Sequential Monte Carlo).
Essential References Not Discussed: Not that I know of.
Other Strengths And Weaknesses: I found this paper quite clear and this method seems much simpler than previous methods for tuning SMC samplers.
Other Comments Or Suggestions: On line 210 in the second column you refer to h_t before it has been introduced which is potentially confusing. Also I wasn't sure what \theta_t contains h_t meant.
"distribution" is repeated on line 85 in the second column.
Questions For Authors: Is there any indication that this method under-explored the posterior or suffered more from particle degeneracy than the other compared methods?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for your review.
> The datasets used seem quite standard for evaluating SMC methods. One thing I am not sure of is whether just reporting normalising constant is sufficient to show the superiority of this method, it would have been nice to see something like ESS or some assessment of posterior quality like moment estimates.
Thank you for the suggestion! Theoretically speaking, the accuracy of the normalizing constant and expectations taken over the particles are closely related. That is, the variance of the normalizing constant estimate is the cumulation of the variance of the normalizing constant ratios $Z_t/Z_{t-1}$, which corresponds to setting the integrand of expectation taken over the particles to be the indicator function as $\varphi = \mathbb{1}$. Therefore, if the normalizing constant estimate is accurate, the particle expectations will also be reasonably accurate. Indeed, we ran some experiments on two benchmarks: seeds and radon, where we computed the Wasserstein-2 distance of $N = 1024$ particles from SMC-LMC against ground truth samples from $10^5$ samples from the no-u-turn sampler. The Wasserstein-2 distance is closely related to the accuracy of the first and second moments. Also, it bounds the Wasserstein-1 distance, an integral probability metric, which quantifies the worst-case absolute error for 1-Lipschitz integrands. Therefore, it is a good metric for quantifying the error of particle expectations.
The results are shown in the following link:
https://imgur.com/a/80l62vS
(red line: Wasserstein-2 distance between the samples from vanilla SMC with the corresponding fixed stepsize and NUTS; blue line: Wasserstein-2 distance between the samples from our adaptive SMC sampler and NUTS.)
We can see that our adaptive SMC samplers achieve Wasserstein-2 distances close to the best fixed step size. However, it does not outperform fixed stepsizes as much as for estimating normalizing constants. This suggests that our adaptation scheme could be tailored to expectations taken over the particles for better performance.
> Some interpretation as to why, eg, the method under-performed on the rats dataset would be welcome.
Thank you for pointing this out. With full honesty, it is unclear why this is the case. Upon close inspection, the optimization algorithm seems to correctly find the minimizer of the objective. Therefore, two explanations are possible: Either the sampler is underperforming for the given budget such that the estimate of the incremental KL is inaccurate, or the greediness of the scheme results in a suboptimal solution.
> The experiments seem sound if a bit limited (as I previously mentioned) from what is relayed in the paper. I am curious why 32 replications were used to get the confidence intervals in the adaptive tuning vs fixed experiments but only 5 in the end-to-end optimisation experiments.
We agree with the reviewer that more than 5 evaluations for the end-to-end results would have been better. Therefore, since the submission, we re-ran the experiments using 32 replications for evaluation, which is now the same number as adaptive SMC, and included a more challenging problem (Pines). We observe that on Pines, our method does not outperform end-to-end optimization, which is unsurprising: end-to-end optimization should outperform our greedy scheme on some problems where the gradient noise is negligible. For the grid search experiments, we ran more problems from PosteriorDB, which now totals 21 benchmark problems. Please refer to the response reviewer 3HR9 above!
> The idea of using the KL divergence to tune parameters of the proposal distribution in SMC also appears in (Shixiang et. al. Neural Adaptive Sequential Monte Carlo).
Thank you for pointing this out! We will add this to the list of works performing end-to-end optimization.
> Is there any indication that this method under-explored the posterior or suffered more from particle degeneracy than the other compared methods?
Generally, our method should perform as well as a well-tuned vanilla SMC sampler, which may or may not fully explore the posterior depending on the problem and other configurations. In terms of particle degeneracy, our method should be the least susceptible since we are essentially maximizing the incremental weights. In a sense, our scheme is actively preventing degeneracy. The side effect would be that the biased normalizing constant estimates obtained during adaptive runs will be overestimated.
---
Rebuttal Comment 1.1:
Comment: Thank you for addressing my concerns and for the additional experiments. I maintain my recommendation. | Summary: The paper provides a gradient-free, hyperparameter-free tuning algorithm for proposal step sizes and particle refresh/resampling rates in Sequential Monte Carlo pipelines. Experiments on example graphical models from PosteriorDB demonstrate that the new algorithm not only provides a great advantage in log-evidence estimation relative to a fixed step size, but in fact quickly approaches the true log-evidence after adaptation. In experiments comparing to end-to-end adaptive SMC approaches, the new method performs no worse than end-to-end optimization and, in one experiment, significantly better.
Claims And Evidence: This paper poses a bit of a clarity problem, at least for this reviewer. The paper takes its starting notation from "Introduction to Sequential Monte Carlo" by Chopin and Papaspiliopoulos, and as a result, is somewhat notationally overloaded.
Methods And Evaluation Criteria: Yes, in fact PosteriorDB is just the benchmark for Bayesian inference problems that I would recommend.
Theoretical Claims: Proposition 1 more-or-less follows from the definition of a divergence, though a proof summary in the main text would be preferable.
Experimental Designs Or Analyses: PosteriorDB is the gold-standard for benchmarking Bayesian inference and the numerical metrics used here are the valid ones.
Supplementary Material: No, unfortunately.
Relation To Broader Scientific Literature: SMC is a back-end workhorse for many scientific computations, and so the paper fits well into the broader literature. I do not know of a previous paper doing what this paper does.
Essential References Not Discussed: I do not have any missing references to report.
Other Strengths And Weaknesses: The problem of approximating an idealized annealing path distribution is, to my knowledge, a relatively original one to pose. I would somewhat like the authors to motivate it more.
Other Comments Or Suggestions: There are a few grammar and usage typos, such as "distribution distribution" and "the goal is often to infer... or estimating" (either the infinitive or gerund should be used consistently).
Score has been revised in light of the authors' response to both my review and to others asking for additional experiments.
Questions For Authors: Solved in author response.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for your review.
> Do the authors want to minimize incremental divergences in order to target the path measure of the annealed importance sampling procedure, or fine-tune an annealed importance sampling procedure in order to later perform SMC on the target density?
We kindly request more details on this question as our tuning procedure does not involve nor is specialized to annealed importance sampling (AIS).
Perhaps the question arose from the fact that the Feynman-Kac model formalism does not explicitly involve resampling, which might have led to the impression that optimizing the target path of the Feynman-Kac model is tuning an AIS procedure, not an SMC procedure. If this is the case, we would like to clarify that while our procedure can absolutely be applied to AIS (after all, SMC and AIS are a few resampling steps away from each other), our focus is purely on SMC samplers. That is, both AIS and SMC are algorithms for simulating the same Feynman-Kac model (it’s only the procedure for simulation that differs.) To be clear, we would like to bring attention to Algorithm 1, which shows the adaptive SMC implementation with our tuning scheme embedded in it. All we do is run Algorithm 1.
If this does not fully address the Reviewer’s question, we would be very happy to further clarify any point of ambiguity.
---
Rebuttal Comment 1.1:
Comment: Equation 1 on line 123 shows the geometric annealing path, hence my reference to annealed importance sampling. In algorithm 1, the potential G is subscripted by a time index, and its definition is a density ratio that helps to weight samples from \pi_{t-1} to target \pi_{t}.
My understanding of your response here is that you want to sample from the path measure via SMC; the path of density ratios chosen can be more-or-less arbitrary (not just the geometric annealing path); and that your incremental divergence objective enables incremental adaptation (i.e. the \theta_{t} step inside the outer loop in Algorithm 1) towards that goal.
Revising my score in that light. | Summary: This paper proposes a novel method for tuning sequential Monte Carlo (SMC) samplers by greedily minimizing the incremental KL divergence between the target and proposal path measures. The authors develop efficient, gradient-free algorithms for tuning key parameters—such as step sizes in unadjusted Langevin Monte Carlo kernels. Experimental results demonstrate that their approach reduces variance in estimates and outperforms both fixed-parameter and gradient-based tuning methods on various benchmark problems.
Claims And Evidence: The submission's claims are largely supported by comprehensive empirical results. The authors verified their method through experiments on multiple benchmarks that their adaptive tuning yields lower variance estimates and comparable or improved performance compared to fixed or gradient-based methods. One potential caveat is that some theoretical guarantees rely on assumptions (e.g., unimodality of the tuning objective) that may limit generalizability, but within the presented contexts the evidence is clear and convincing.
Methods And Evaluation Criteria: The proposed methods and evaluation criteria are well-aligned with the problem at hand. The paper’s approach—minimizing incremental KL divergence to tune SMC samplers—is both innovative and practical, addressing the challenges of tuning unadjusted kernels without incurring high computational costs. The evaluation criteria, such as the variance and accuracy of normalizing constant estimates, are standard in the SMC literature. Additionally, the benchmark datasets are used.
Theoretical Claims: I only checked the main body of the theoretical claims and did not find any issues.
Experimental Designs Or Analyses: I briefly reviewed the experiments; however, I have some concerns about whether they accurately reflect real-world scenarios.
Supplementary Material: No, I did not review the supplementary material; I focused solely on the main content of the paper.
Relation To Broader Scientific Literature: The paper’s contributions build directly on a rich body of work in sequential Monte Carlo (SMC) methods and adaptive tuning techniques.
Essential References Not Discussed: No, all the essential related works appear to be appropriately cited and discussed.
Other Strengths And Weaknesses: Strengths:
- Novel and efficient approach that combines divergence minimization with adaptive SMC tuning.
- Provides effective empirical results.
Other Comments Or Suggestions: The document is well written and the technical terminology is used correctly.
Questions For Authors: - How sensitive are the experimental results to changes in key parameters, and does this sensitivity mirror the challenges encountered in practical scenarios?
- Can the proposed method scale efficiently with the increased dimensionality and sample sizes often found in real-world problems?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your review.
> One potential caveat is that some theoretical guarantees rely on assumptions (e.g., unimodality of the tuning objective) that may limit generalizability,
We agree that those theoretical assumptions are restrictive. As such, we are happy to mention that we were able to relax those assumptions during the review period. Now, even without unimodality, we are able to guarantee that our algorithm finds a point $\epsilon$-close to a local minimum with similar computational cost. Additionally assuming unimodality strengthens the guarantee so that the returned point is $\epsilon$-close to the global optimum.
The only major change we had to introduce is that we now use a different variant of the golden section search algorithm. In particular, we use the version described in “Numerical Recipes” (Section 10.1 in [1]). We found that this variant is able to guarantee finding a local minimum as long as the initialization satisfies a certain condition implying that the initial search interval contains a local minimum.
> How sensitive are the experimental results to changes in key parameters, and does this sensitivity mirror the challenges encountered in practical scenarios?
Thank you for the great question. Overall, we didn’t spend much effort tuning the parameters, and all of our experiments were run with a single fixed set of parameters for each type of kernel. In more detail though, the only parameters that primarily affect the results are the regularization strength $\tau$ and the optimization accuracy budget $\epsilon$. (The rest of the parameters only change the amount of computation spent obtaining similar solutions.) $\epsilon$, for instance, does not affect the result much as long as it is small enough. On the other hand, the effect of the regularization strength $\tau$ seems to depend on the kernel but not so much on the problem. For instance, the performance of LMC isn’t very sensitive to $\tau$, and we thus use a small amount. On the other hand, KLMC seems to require stronger regularization to obtain good performance. While we suspect this has something with the persistence of the momentum, it is not entirely clear why. Overall, we do not expect the parameters to require much tuning, except when swapping the MCMC kernel.
> Can the proposed method scale efficiently with the increased dimensionality and sample sizes often found in real-world problems?
We extended our experiments with higher dimensional problems since the initial submission. (Please refer to the response to 3HR9 for the new results.) In principle, dimensionality shouldn’t be a problem for our method. As shown in the experiment, our method should perform better or as well as the best-tuned vanilla SMC sampler. Therefore, as long as vanilla SMC can scale, our method should be able to scale as well. In terms of scaling with respect to the sample size $N$, as long as the subsampling size $B$ is smaller than $N$, the added overhead of our method should be negligible. More concretely, if at most $C$ objective evaluations are spent during each adaptation step, the total cost of running SMC with our adaptation is $O(B C + N)$. Thus, if $BC = o(N)$, our adaptive SMC scheme is just as scalable as vanilla SMC.
1. Press, William H. Numerical recipes 3rd edition: The art of scientific computing. Cambridge University Press, 2007. | Summary: Main problem and approach: The performance of sequential Monte Carlo (SMC) samplers heavily depends on the tuning of the Markov kernels used in the path proposal. The paper proposes a framework for tuning the Markov kernels in SMC samplers by minimizing the incremental Kullback-Leibler (KL) divergence between the proposal and target paths.
Main Result: the paper show that the approach and implementation are able to obtain a full schedule of tuned parameters at the cost of a few vanilla SMC runs, which is a fraction of gradient-based approaches.
Claims And Evidence: Yes
Methods And Evaluation Criteria: The method is sound. The evaluation and benchmark datasets are too simple.
Theoretical Claims: No fully check the correctness of theoretical claims
Experimental Designs Or Analyses: The experiment set up is too simple on a collection of toy benchmark datsets. It is not clear how it is applicable to the application domains of SMC, such as steering large language models and conditional generation from diffusion models.
Supplementary Material: Yes. All the appendix
Relation To Broader Scientific Literature: It address an open questions in the broader scientific literature. Tuning SMC is often a significant challenge. methods and criteria for tuning the path proposal kernels are relatively scarce. This paper focuses on the setting where a few scalar parameters (e.g., step size) subject to tuning. In this setting, the full generality (and cost) of SGD is not required; it is possible to design a simpler and more efficient method for tuning each
transition kernel sequentially in a single SMC/AIS run.
Essential References Not Discussed: I am not familiar with the domain and did not check thoroughly.
Other Strengths And Weaknesses: I am not familiar with the domain. The paper is well written and the claims seem solid. The experiment setup is too simple, it is hard to assess the practical value of this work.
Other Comments Or Suggestions: Provide a practical example to demonstrate the value of this work.
Questions For Authors: How the proposed tuned SMC samplers can bring benefit to its applications such as steering large language models and conditional generation from diffusion models.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your review.
> The experiment set up is too simple on a collection of toy benchmark datasets. It is not clear how it is applicable to the application domains of SMC, such as steering large language models and conditional generation from diffusion models.
We agree that more realistic experiments are always a good thing. As such, we added new benchmarks from both PosteriorDB and Inference Gym, including a high-dimensional benchmark problem (Pines) from Inference Gym, which is 1600 dimensional and multiple problems from PosteriorDB, including TIMSS and Three Men, both of which have more than 500 dimensions. Here is the full list of problems with their corresponding dimensionality:
| Name | dims. | Source |
| ----- | --- | ---- |
| Funnel | 10 | Inference Gym |
| Brownian | 32 | Inference Gym |
| Sonar | 61 | Inference Gym |
| Pines | 1600 | Inference Gym |
| Bones | 13 | PosteriorDB |
| Surgical | 14 | PosteriorDB |
| HMM | 14 | PosteriorDB |
| Loss Curves | 15 | PosteriorDB |
| Pilots | 18 | PosteriorDB |
| Diamonds | 26 | PosteriorDB |
| Seeds | 26 | PosteriorDB |
| Rats | 65 | PosteriorDB |
| Radon | 90 | PosteriorDB |
| Election88 | 90 | PosteriorDB |
| Butterfly | 106 | PosteriorDB |
| Birds | 237 | PosteriorDB |
| Drivers | 389 | PosteriorDB |
| Capture | 388 | PosteriorDB |
| Science | 408 | PosteriorDB |
| Three Men | 505 | PosteriorDB |
| TIMSS | 530 | PosteriorDB |
The new experimental results can be found in the anonymized links below.
Comparison against end-to-end optimization:
https://imgur.com/pdk3Bza
(red dot: normalizing constant estimate obtained by our adaptive SMC sampler; blue line: normalizing constant estimate obtained by end-to-end optimization; dotted line: ground truth)
Here, we can see the comparison against end-to-end optimization results with the new Pines benchmark problem. Furthermore, unlike the experiments included in the original submission, we use the official code provided by Geffner and Domke [1], which we find to be better tuned. In particular, on Pines, we observe that end-to-end optimization performs slightly better than our adaptive SMC procedure, while on other problems, we obtain more accurate results.
Comparison against grid search for SMC with Langevin Monte Carlo kernels:
https://imgur.com/9JjJEiK
Comparison against grid search for SMC with kinetic Langevin Monte Carlo kernels:
https://imgur.com/mUeWbuz
(red line: the normalizing constant obtained by our adaptive SMC sampler; purple line: the normalizing constant obtained by vanilla SMC with a fixed stepsize; dotted line: ground truth estimate.)
Overall, for the comparisons against grid search, we observe a similar trend where our tuning procedure finds better or comparable results to the best-fixed step size. The only exception appears to be Rat, as observed in the original submission.
We would also like to point out that PosteriorDB is a state-of-the-art benchmark (with the corresponding paper published this year at AISTATS’25 [2]) that contains problems that have actually been used for practical applications or closely resemble such problems. As such, we believe our experiments adequately represent problems to which SMC is expected to be applied in practice. While evaluating our method on applications such as LLM steering and conditional generation from diffusion models would definitely be interesting, they will probably need their own investigation with more specialized solutions.
1. Geffner, Tomas, and Justin Domke. "Langevin diffusion variational inference." International Conference on Artificial Intelligence and Statistics. PMLR, 2023.
2. Magnusson, Måns, et al. "posteriordb: Testing, benchmarking and developing Bayesian inference algorithms." AISTATS’25, to be presented. | null | null | null | null | null | null |
Representative Ranking for Deliberation in the Public Sphere | Accept (poster) | Summary: The paper studies a setting of algorithmic comment ranking/selection incorporating fairness. There is a given set of comments, together with "likes" and based on these likes, a representative set of comments needs to be selected. The paper studies the impact of a group fairness concept called "justified representation" (JR) from the computational social choice literature. While in the worst-case, JR might inhibit the maximization of objective functions, in experiments on real-world comment data, as well as restricted settings, JR is compatible with approximately optimal function maximization.
Claims And Evidence: They seem both clear and convincing.
Methods And Evaluation Criteria: Yes, I would say so.
Theoretical Claims: I did for the most part. Did not fully check the Mallows stuff.
Experimental Designs Or Analyses: Yes, checked them
Supplementary Material: Read through it for the most part, skipped the Mallows stuff.
Relation To Broader Scientific Literature: The paper builds upon the concept of justified representation from computational social choice. This paper provides a novel application for justified representation and provides a few new theoretical results. In particular, the problem of maximizing an arbitrary function subject to JR was not really studied before. In general, the theoretical ideas and results in the paper are quite similar to already present stuff in the computational social choice literature.
Essential References Not Discussed: I do not believe so
Other Strengths And Weaknesses: In general, I like the idea of the paper. Applying social choice fairness concepts to machine learning problems is a very interesting topic, and of growing importance in the last few years. The problem of comment ranking seems also quite important and well motivated.
There are a few things I am not too satisfied with, though:
(i) firstly, the whole paper builds upon the notion of JR. However, JR is an incredibly weak axiom. As the authors note themselves, in a lot of their experiments 2 comments are already enough to satisfy JR (this is inline with other experimental works in social choice, see for instance the cited Bredereck et al. paper). Further, JR does not meet the intuitive notion of proportionality suggested by the paper itself ("Let a world with 60 people who approve the 10 items in set A and another 40 people
who approve of a distinct set A↑ of 10 items. If a committee of size 10 is selected based on approval scores, the winning committee,
A would fail to represent 40% of the world. Instead, a committee composed of 6 items from A and 4 items from A↑ would respect
an intuitive notion of proportionality.") In this example, JR would only require 1 item to be selected from each group (in the computational social literature the property the paper suggests here is also known as "lower quota"). There are significantly stronger yet still intuitive fairness axioms than JR, which could have been used instead, for instance priceability[1] or EJR+[2] (I would also encourage the authors to look at the recent work of Boehmer et al. [3] on proportional representation in a real-world approval-based committee voting setting). I believe using such stronger axioms would significantly improve the quality of the experiments and results.
(ii) The theoretical results sadly seem quite weak. It is already known from the literature that the price of JR is \sqrt(k), so quite bad. It is not really surprising that for arbitrary functions this gets worse. Further, Theorem 5.1 is also not really that new, see for instance Proposition 3 of Lackner and Skowron [4].
(iii) One thing I found quite confusing is that the paper styles itself as being about ranking comments. The paper itself, however, is only about set selection, and I am not sure the results would entirely transfer to the ranking setting. In particular, Theorem 5.1 needs the set structure, if I see correctly.
References
[1] Proportionality and the Limits of Welfarism. Dominik Peters and Piotr Skowron 2020
[2] Robust and verifiable proportionality axioms for multiwinner voting. Markus Brill and Jannik Peters 2023
[3] Approval-based committee voting in practice: a case study of (over-) representation in the Polkadot blockchain. Niclas Boehmer et al. 2024
[4] Utilitarian welfare and representation guarantees of approval-based multiwinner rules. Martin Lackner and Piotr Skowron 2020.
Other Comments Or Suggestions: Line 94: e.g,
Line 104: For cultural reasons, I think using such country specific examples should be avoided. No one outside of the US would understand this example.
Related Work: The related work section is currently missing computational social choice works entirely, even though the paper is on computational social choice. This seems wrong to me.
Line 152: \cdots -> \dots (also elsewhere)
Line 143 (right): \cup -> \bigcup (also elsewhere)
Line 199 (left): the use of quantors in the text is quite ugly
Line 195 (right): \subset -> \subseteq (also elsewhere)
"It appears as though there could be perverse sets that satisfy JR where
most people do not approve of the selected comments. However,
research has found that common algorithms used to
satisfy JR do not lead to such perverse outcomes" Yes, common algorithms selecting JR outcomes are usually good. However, this does not mean that all JR outcomes are usually good (which might also be quite relevant here)
Theorem 4.2: \gamma is never used in the theorem statement
Theorem 5.1: I was wondering if you cant replace this whole construction by requiring that there is a small justifying set? I believe this is the only thing you need for the theorem.
I find Figure 2 quite overwhelming at the moment. I believe it could be a bit simplified or spread out.
You are citing the Bredereck et al paper twice.
The Elkind et al paper has a journal version
"W¨”uthrich" -> "Wüthrich"
"Landemore, H. 39Can Artificial Intelligence Bring Deliberation
to the Masses?" Cut the 39
While searching for related work I came across the paper "Combining Voting and Abstract Argumentation
to Understand Online Discussions" by Bernreiter et al., they seem to have a quite similar motivation to this work, but the results are different. Might still be worth to cite them though.
You are currently missing an impact statement. I believe this paper might actually be one that needs one.
Questions For Authors: Can Theorem 5.1 be rephrased using justifying sets?
Why does the paper focus on JR and not stronger axioms?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank the reviewer for their comprehensive and thoughtful comments.
The reviewer seems to be evaluating our paper primarily as a contribution to social choice. However, the main goal of our work was not to contribute to social choice, but rather to facilitate deliberation online (particularly on social media platforms). Since this area is lacking any representation axioms, we ground our algorithmic approach in social choice, specifically JR, and demonstrate the efficacy of this approach both theoretically and empirically under real-world conditions. We believe this is an important and novel contribution that can open up new directions in the research on prosocial recommender systems. This goal explains many of the decisions we made, and we will try to make this context clearer in our revision.
**Our focus on JR**
The reviewer asked why we did not focus on stronger variants of JR. Practically speaking, a representation constraint is unlikely to be implemented on a social media platform if it also comes at a substantial decrease in user engagement or a substantial increase in the toxicity of comments. This is why in this initial work we started with the basic JR axiom, which is most likely to be compatible with the optimization of other score functions (engagement, civility classifiers, etc).
However, in response to the reviewer’s concern, we also checked how many of the JR committees in our experiments satisfied EJR+ (and will add this to the paper). Across the 48 JR feeds, only one JR feed did not also satisfy EJR+. The paper that the reviewer mentioned by Boehmer et al. makes similar observations (e.g., "All four proportional rules [including three rules not guaranteed to satisfy EJR+] return committees satisfying EJR+ for all tested instances.’’).
Overall, we believe focusing on JR was a reasonable first step in our work due to (i) the need to demonstrate that the representation axiom is compatible with other arbitrary score functions, and (ii) the observed alignment of JR and EJR+ in real-world settings despite the theoretical gap. Nonetheless, we very much agree with the reviewer that studying stronger axioms would be a promising direction for future research.
**Theoretical results**
We respectfully disagree with the reader’s assessment of our theoretical results. Coming back to our motivation of integrating JR into online platforms, the goal of our theoretical analysis was to show that, in natural settings, JR is compatible with the optimization of other score functions the platform may care about. While we agree that it is not surprising that the worst-care price of JR becomes higher for arbitrary score functions, these worst-case results primarily serve as motivation for our more novel contribution where we show that, in natural settings, the price is still low (Section 5). This result is crucial, as high prices would likely deter the incorporation of representation constraints on these platforms.
Theorem 5.1 could be re-written in terms of n/k-justifying sets—that is essentially the proof of the theorem. However, our goal was to show a natural condition for why one might expect a small n/k-justifying set, and thus a low price of JR, on social media. In the social media context, when bridging interventions (diverse approval) are done, users are already partitioned into non-overlapping groups that are supposed to be distinctive in their preferences (these groups are typically learned by basically clustering the vote matrix). Theorem 5.1 says that if those groups are also cohesive in the JR sense, then we have a low price. We will clarify this reasoning and motivation, while acknowledging the prior related results, in our revised text.
We also note that, in practice, each group may not necessarily be fully cohesive in the JR sense. Thus, Theorem 5.1 was also primarily meant to serve as intuition for the extended Mallows model result (Theorem 5.4).
**Set selection and ranking**
The reviewer is puzzled about the focus on set selection for comment ranking. We do not see a discrepancy here. In recommender systems, a very common method for showing a diverse set of items (e.g. videos that span your interests) is to re-rank items greedily so that the set of top items is diverse (see Algorithm 1 in “Fairness and Diversity in Recommender Systems: A Survey” by Zhao et al). Moreover, real-world recommender systems proceed in multiple steps that are actually set selection problems (e.g. retrieval -> early stage-ranking -> late-stage ranking). In our revision, we will clarify the connection between set selection and ranking.
**Related Work & Impact Statement**
We appreciate the many references that the reviewer shared. We will incorporate them into our paper with a more comprehensive section on related work in social choice. We will also add an impact statement. Lastly, we will correct the typos the reviewer found.
Once again, we thank the reviewer for their thoughtful consideration of our paper.
---
Rebuttal Comment 1.1:
Comment: Thank you for the nice rebuttal!
Yes, it is correct, I tried to evaluate the paper from a social choice perspective, I guess that is what happens with such an "interdisciplinary" paper. I still maintain my position regarding the strength of the paper as a pure social choice work, namely, that in this regard it is quite thin content-wise, and that the presented content could be substantially improved without too much added effort. Now if this was a journal submission this would be easy, the paper would get a revision, and would appear soon, in a better state. Now, with conference submissions, this is a bit more tricky, and I feel quite conflicted here. On the one hand, I quite appreciate the paper building a bridge between deliberation and social choice, and think that this is definitely something that would be appreciated by both communities. On the other hand, it is hard not to look at the paper, and see the potential for improvement, both in terms of strength of the results, but also presentation of the results and I believe this paper could easily be a significantly stronger NeurIPS submission next month.
**Our focus on JR**
Thank you for checking this. Looks good!
**Theoretical results**
Thank you for disagreeing, I like this motivation :)
** Set selection and ranking**
I still see a slight discrepancy here, especially as there are several works on fair or proportional ranking, but I see what you mean.
I personally think that the scores are somewhat meaningless, I will still update it to a 3, and let's see where the reviewer discussion will lead. Thanks again for the nice response. I hope that if the paper gets accepted, the authors take the comments provided by the reviews here seriously (I have been "hurt" far too many times, by authors not doing it...) | Summary: The authors propose a comment ranking approach for public deliberation that incorporates justified representation, a concept from the social choice literature. The goal is to rank high quality comments, without losing the representation of groups that are present in the discussion. The approach relies on user approval mechanisms, making it more feasible than algorithms that require external user information. The authors can show that their implementation of enforcing justified representation, using the greedycc algorithm improves representation at a low cost.
Claims And Evidence: The claims made are supported by clear evidence. The experiments resemble a real-world application. There could be some potential bias, because the process relies on user approval (likes or upvotes), which could easily be manipulated in political discussions. This potential drawback is mentioned by the authors themselves and should be investigated in the future.
Methods And Evaluation Criteria: Yes, the proposed methods and evaluation criteria make sense.
Theoretical Claims: I didn't identify any issues in the proofs in the Appendix.
Experimental Designs Or Analyses: The experimental designs and analyses are sound. More experiments are needed to investigate potential effects in the future, but since the paper only outlines the approach and theoretical assumptions, this is left for future work.
Supplementary Material: There is a lot of supplementary material in the appendix, I looked at the proofs and the supplementary material regarding the experiments.
Relation To Broader Scientific Literature: The authors contribute to the literature on algorithmic fairness by proposing an approach to fair representation that is more feasible in practice than, for example, approaches based on demographics. It is shown that by approximation, sets of comments that satisfy JR can be found at low cost on real-world discussions.
Essential References Not Discussed: I did not identify essential references that are missing.
Other Strengths And Weaknesses: The paper is well written and easy to follow. The experiments and theoretical assumptions are clear. The results concerning the use of a score based on the Perspective API are surprising and could also be investigated in the future. It remains unclear if people would acutally feel represented by the algorithms choice and if the algorithm is able to guarantee content-wise diversity. This could be investigated in the future.
Other Comments Or Suggestions: Small errors:
- line 142 (right column): "for all item i" should be "all items i"
- line 203 (right column): "It seems that there could be perverse sets that satisfy JR." I am not sure if the wording is right here this seems off
- line 225 (right column): "the price of JR need to be bounded" should be "needs to be bounded"
- line 226: "need not be compatible" should rather be "does not need to be" or "does not have to be.."
Questions For Authors: - Can you give some details about fc (the Perspective API scoring function)? It's an average of all the bridging attribute scores. What is the range of the individual bridging scores?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We appreciate the reviewer’s careful reading of our paper and thank them for their constructive comments. We will correct all the typos that they identified.
With regards to the Perspective API bridging score $f_C$, it is the average of the scores for the seven available bridging attributes:
* “Affinity”: References shared interests, motivations or outlooks between the comment author and another individual, group or entity
* “Compassion”: Identifies with or shows concern, empathy, or support for the feelings/emotions of others.
* “Curiosity”: Attempts to clarify or ask follow-up questions to better understand another person or idea.
* “Nuance”: Incorporates multiple points of view in an attempt to provide a full picture or contribute useful detail and/or context.
* “Personal Story”: Includes a personal experience or story as a source of support for the statements made in the comment.
* “Reasoning”: Makes specific or well-reasoned points to provide a fuller understanding of the topic without disrespect or provocation.
* “Respect”: Shows deference or appreciation to others, or acknowledges the validity of another person.
The score for each individual attribute is a probability between 0 and 1. We provide results broken down by each individual attribute in Appendix E.7.
Additional references for the Perspective API bridging classifiers:
* https://developers.perspectiveapi.com/s/about-the-api-attributes-and-languages?language=en_US
* https://medium.com/jigsaw/announcing-experimental-bridging-attributes-in-perspective-api-578a9d59ac37
* Saltz et al. Re-Ranking News Comments by Constructiveness and Curiosity Significantly Increases Perceived Respect, Trustworthiness, and Interest. arXiv 2024.
* Schmer-Galunder et al. Annotator in the Loop: A Case Study of In-Depth Rater Engagement to Create a Prosocial Benchmark Dataset. AIES 2025.
We thank the reviewer once again for their consideration of our paper.
---
Rebuttal Comment 1.1:
Comment: Thank you very much for the further clarification. Since I was already convinced that this paper should be accepted, I will not revise my score. | Summary: The authors take the problem of content ranking in online social deliberation, and adds justified representation (JR) constraints to the quality optimization problem to ensure diversity and representation. Theoretically, they show that under assumptions of user clusterization, the extra constraint leads to low cost in terms of the quality metric (e.g. civility, engagement). Empirically, they show that adding a greedy implementation of JR significantly improves the representation by existing ranking methods, while imposing only a modest cost in quality.
Claims And Evidence: All claims are backed up by evidence. There are very few logical steps that I find unconvincing (which I detail in later sections).
Methods And Evaluation Criteria: The authors aim to address an import problem (online public deliberation) with a very interesting approach (content ranking), and give impressive theoretical & empirical evidence to support their approach. I find the approach reasonable and practical.
Theoretical Claims: - My main uncertainty on the theoretical results lie in the assumptions and how they can be tested on empirical data. Specifically:
- For theorem 5.1, what is the value $\gamma$ on each of the questions in your dataset?
- For theorem 5.2, what are the $\gamma$ and $\phi$ values that (statistically speaking) best explains your dataset? This can be done with, for example, a maximum likelihood estimation.
- In reality, there are often cases where each user only reads a very small portion of entries (e.g. someone only reading tweets from people you follow; or someone only upvoting one or two comments before leaving) - do the theoretical bounds remain practical in that case? Would (n/k)-sized cohesive groups exist in that case?
- I did not check the proofs.
Experimental Designs Or Analyses: - **[important]** GreedyCC is, in some sense, specifically optimized for the coverage metric. It first searches for a tiny core of comments that satisfy minimum coverage (at least one comment per group), and then fill in the rest with no consideration for representation. Does it remain representative when we use other representation metrics that focuses on not just minimum coverage, but also proportionality? If not, is there another JR approximation algorithm that does well under proportionality?
- It would be helpful to visualize where these methods lie (with & without GreedyCC) on the quality-representation tradeoff plane.
- Have you tried other simple heuristics other than JR, and how well do they work?
Supplementary Material: I read Appendices E.1-E.4.
Relation To Broader Scientific Literature: Content ranking, including content ranking with pro-social constraints, is a problem widely studied outside the algorithmic mechanism design literature - for example by RecSys researchers. This paper shows that JR constraint and its variants may be a valuable addition to their toolkit.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: - The work is not ground-breaking in the sense that it draws from previous literature on JR and its approximation algorithms. But it gives significant contribution by applying the idea in a important domain, and give a range of theoretical & empirical evidence to back up such an application.
Other Comments Or Suggestions: - Typo: The y axis of Fig 2 & E.2 are not percentages despite the "%" sign in the axis labels.
- Potentially important as a future direction: The “one member approves one item” condition in JR is too weak (as the authors have acknowledged in the paper). How can we improve this, either theoretically or empirically?
Questions For Authors: I have listed my questions in previous sections. The ones most likely to change my mind are marked with "[important]".
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you to the reviewer for their comprehensive review. We address their questions below.
**Connection Between Theoretical and Empirical Results**
The reviewer asks about how our theoretical results connect to the empirical findings. Even without considering Theorem 5.4, the bound from Theorem 5.1 already provides a close upper bound to the observed prices in practice. We will highlight this connection in our revised text. For Theorem 5.1, the bound holds if there exists an $n/k$-justifying set of size less than or equal to gamma (which the partition of gamma cohesive groups implies). In all ten questions, the GreedyCC algorithm finds an $n/k$-justifying set of size less than or equal to two (see Table E.3). Our bound from Theorem 5.1 would then imply that the price for all three score functions is at most 8/(8-2) = 1.33. The average empirical prices that we observe (see “Enforcing JR comes at a low price” in Section 6) are 1.05 for engagement, 1.06 for diverse approval, and 1.18 for Perspective API.
**Handling Partially Observed Votes**
The reviewer also asks how the theoretical results hold when each user only reads a very small portion of items. In practice, the full approval matrix will need to be inferred from the partially observed votes—which is what we do in our Remesh experiments (see Footnote 10). Since this is a standard recommender system task, we do not focus on this approval inference in our paper. However, when implementing this on a real platform, it is very important to ensure that the inferred approvals are faithful to users’ actual approval. We touch on this issue in our discussion section: “on many platforms, users’ approval will need to be inferred from some form of engagement such as upvotes or likes. If the chosen engagement significantly diverges from actual user approval, the validity of the process could be compromised.”
**Experimental Results and Stronger Proportionality Axioms**
With regards to experimental results, the reviewer asks how our experiments with GreedyCC may hold up against stronger proportionality axioms. In response, we have checked how many of the JR feeds in our experiments also satisfy EJR+ (Brill and Peters, 2023), a much stronger extension of JR. We found that 47 out of 48 feeds also satisfy EJR+ (and will add this result to the paper).
I. Diverse Approval
- 5/10 DA feeds are JR, all of them are also EJR+
- 10/10 JR feeds are also EJR+
II. Engagement
- 3/10 engagement feeds are JR, all of them are also EJR+
- 9/10 JR feeds are also EJR+
III. Perspective API
- 10/10 Perspective API feeds are JR, all of them are also EJR+
- 10/10 JR feeds are also EJR+
This suggests that, although GreedyCC is only optimizing for coverage, it nevertheless satisfies stronger axioms in practice. This result has also been corroborated in other empirical research which has found that JR and EJR+ tend to empirically coincide despite their large theoretical gap (e.g. “Approval-Based Committee Voting in Practice: A Case Study of (Over-)Representation in the Polkadot Blockchain” by Boehmer et al (2024)).
> Potentially important as a future direction: The “one member approves one item” condition in JR is too weak (as the authors have acknowledged in the paper). How can we improve this, either theoretically or empirically?
Empirically, the results just described suggest that our approach may satisfy axioms stronger than JR in real-world datasets. We concur with the reviewer that theoretically studying and guaranteeing stronger extensions of JR would be an interesting direction for future research.
**Other Comments**
> “Have you tried other simple heuristics other than JR, and how well do they work?”
We have not tried other heuristics that are weaker than JR, since the GreedyCC algorithm on its own is already quite simple, and as noted above, it has the advantage of satisfying stronger axioms empirically as well.
> “It would be helpful to visualize where these methods lie (with & without GreedyCC) on the quality-representation tradeoff plane.”
This is a great idea, and we will add these figures to the appendix. Right now, the trade-offs can be understood through the representation results + the prices of JR shown in Figure 2, but we agree that an explicit visualization would make this clearer.
We thank the reviewer again for their thoughtful comments. | Summary: This work applies the principle of "justified representation" as a means to algorithmically surface public comment for the end-goal of public deliberation. This is, in part, motivated by the ideals of deliberative democracy and normative reasons for selected public comments to satisfy some notion of "representativeness." Mathematically, the work studies formalizations of justified representation (and the price of justified representation) from prior work and shows that, assuming that preferences can be modeled as mixtures of Mallows noise model, stronger bounds on the price of JR can be achieved. Finally, the authors run a previously-proposed (approximation) algorithm on real data and show that enforcing JR, even approximately, tangibly improves representation for a variety of score functions $f$.
## Update after rebuttal
My initial review was overall positive; my main concern was about the roles that section 5/6 played in the contribution of the work - the rebuttal provided narrative clarification and I would be happy with seeing this paper in the conference with that discussion incorporated.
Claims And Evidence: * Generally yes, see below for further comments
Methods And Evaluation Criteria: * Typically one would think that the experiments help to evaluate/validate the theory, but that doesn't appear to be the case here, and it's not actually a priori obvious that sections 5 and 6 are rather different and mostly unrelated contributions. That is, section 6 is not validating the theory given in section 5; instead, it is providing experimental evidence with real-world data for the theory work from the prior Elkind work (which does not have experiments). Section 5 is a distinct conceptual contribution about conditions under which we might expect JR to still do well in a utilitarian sense (and could, e.g., even be an explanatory mechanism for what is observed in section 6, though the paper itself doesn't make this connection as far as I can tell). This is not necessarily a problem with the paper itself but perhaps more so with presentation (e.g. if someone was not familiar with Elkind 22 and didn't know that they didn't run real-data experiments, then they might be confused what the message of section 6 is).
* The actual data being used in experiments is highly relevant to the work.
Theoretical Claims: * I did not check proofs in detail.
* Based on the statement of Theorem 5.4, I think it could be narratively useful to highlight that the bound is (a) in the worst case over all instances, and (b) therefore not about any particular algorithm or algorithmic strategy; in fact is is unclear how or whether to design algorithms that would have been specific to the Mallows mixture idea.
* A lower bound would be nice (especially wrt identifiability, whether $\gamma$ needs to be known, etc) but I am happy to defer that to future work.
Experimental Designs Or Analyses: * See above. Main comment is that section 6 is _not_ a direct extension of section 5 and it would be nice to make that clearer; however the experiments themselves are reasonable for what they are.
Supplementary Material: * I did not check proofs, but reviewed appendices A/B/D/E.
Relation To Broader Scientific Literature: * This work contributes to concretely realizing the ideal of achieving better (democratic) deliberation, doing so by developing ideas from social choice.
* More specifically, the sufficiency conditions implied by the Mallows mixture analysis are new for this problem setting/ and for JR (as far as I can tell), and build on prior social choice work that studies Mallows mixtures.
* The experiments are followups to prior theory work on JR, and show that previously-proposed algorithms can be practically useful.
Essential References Not Discussed: N/A to my knowledge
Other Strengths And Weaknesses: The paper is overall well-written and easy to follow.
Other Comments Or Suggestions: N/A
Questions For Authors: * Can you clarify that my interpretation of the roles of sections 5/6 are correct? If so, could you comment on whether you were hoping to achieve something specific by structuring the paper this way?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We appreciate the reviewer’s thoughtful comments and expertise. The reviewer’s main question is about their interpretation of Sections 5 and 6, which we address in the following. In Section 5, we first introduce novel theoretical results for the price of JR for arbitrary score functions, and then evaluate these results in section 6. Please note that the aspect of arbitrary score functions is key here for the theoretical results and connects both sections.
Our main contribution is to introduce JR into the problem of facilitating deliberation online, particularly on social media platforms. In the social media context, JR is unlikely to be adopted if it also comes at a substantial decrease in user engagement or a substantial increase in the toxicity of comments. Therefore, we analyzed the price of JR, not only with respect to engagement (like Elkind et al did), but also with respect to arbitrary score functions.
Our theoretical results in Section 5 hold for arbitrary score functions, which is why it logically follows to present them before our experiments where we evaluate the price of JR not just for engagement but also for diverse approval and the content-based bridging classifiers. In this way, our experiments also go beyond Elkind et al who only studied engagement. Although the worst-case price for arbitrary score functions can be arbitrarily high (as we showed in Sec 4), the observed price for all three score functions is remarkably low. As the reviewer points out, our theoretical results in Section 5 may explain these findings—a connection we intended to highlight and will clarify in our revision.
Our empirical results also contribute to the literature on prosocial interventions in recommender systems, such as bridging-based ranking. The most common way to operationalize “bridging” is via diverse approval. However, surprisingly, we found that the content-based bridging classifiers provided much better representation than diverse approval. Indeed, all the Perspective API bridging feeds always satisfied JR by default. This is surprising as there is a line of literature showing that *toxicity* classifiers (including Perspective API’s) can be biased against various groups (e.g. Sap et al 2019, Lee et al 2024). Yet, it appears that the newer *bridging* classifiers target attributes with broad appeal, suggesting that these content-based classifiers may be a promising direction for future research in prosocial ranking.
We will also make clear that the bound in Theorem 5.4 is not about any particular algorithmic strategy.
Thank you again to the reviewer for your careful review of our paper.
---
Rebuttal Comment 1.1:
Comment: Thanks, this is useful clarification and I hope some discussion to this end can be added to the final version of the paper! | null | null | null | null | null | null |
Explanatory Instructions: Towards Unified Vision Tasks Understanding and Zero-shot Generalization | Accept (poster) | Summary: This work proposed a large-scale explanatory instruction dataset to unify multiple CV tasks for AR VLM understanding and then generation. It uses VQ-VAE style tokens for vision and then an AR model to merge the 2 modality. It provides qualitative results on various tasks, showing the zero-shot capabilities.
Claims And Evidence: Yes.
Methods And Evaluation Criteria: Yes.
Theoretical Claims: None in this work.
Experimental Designs Or Analyses: 1. The model is trained for 2 epcohs. My impression is that most VLM or AR model either during pre-training or fine-tuning train for 1 epoch. Does the author justify the setup?
Supplementary Material: Dataset construction and quantitative results.
Relation To Broader Scientific Literature: This work contributes to the areas of VLM understanding and generation, more specifically, showing a unified AR model can do multiple CV tasks and zero-shot generalization.
Essential References Not Discussed: I think the VideoPoet work bears resemblance to what the authors want to achieve, using AR VLM to do some zero-shot tasks, but there was no mention of it.
Other Strengths And Weaknesses: Weakness:
1. It is common knowledge that an instruction method such as this paper proposed would be helpful to in the proposed task. So, I'm not sure if the novelty is not already understood or practiced.
2. There are not many quantitative results to objectively compare with others as a whole. (I know there are a few in the appendix.)
Strength:
1. The paper provided a large-scale synthetic dataset that integrates multiple CV tasks.
Other Comments Or Suggestions: I think the captions of the images can be more explanatory for reading flow, but that is optional.
Questions For Authors: So given the dataset is a bit like generated from GPT-4o, wouldn't it be like distilling ability from GPT? and resulting in a chicken-n-egg problem? What if there is no ChatGPT?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your feedback. We realize there may be some misunderstandings regarding both the dataset and idea presented in our paper. We hope the following responses will help clarify these points.
**Experimental Designs**: *The model is trained for 2 epcohs.*
**Response**: Thank you for your comments. Most large-scale VLM or AR models typically adopt only 1 epoch during pre-training, primarily due to the sheer volume of data available, which is usually sufficient for the model to generalize effectively. However, for SFT, it is reasonable to employ more than 1 epoch, since the dataset size is typically smaller and involves more complex tasks. Specifically, our dataset includes rich explanatory instructions covering diverse vision tasks, necessitating multiple exposures for the model to effectively learn and generalize. Empirically, we observed improved performance and better instruction comprehension when training for 2 epochs compared to just 1. We will clarify this reasoning to avoid confusion.
**Weakness 1**: *It is common knowledge that an instruction method would be helpful to in the proposed task.*
**Response**: We have to clarify that the vision task-level zero-shot generalization has not been clearly addressed by any prior work. Indeed, prior sota vision-language models do not demonstrate this capability to generalize across multiple distinct vision tasks. The idea is also considered highly innovative by Reviewers #v7hm, #Mwwt, and #yk8P. We notice that the reviewer might misunderstand the type of generalization we target. Specifically, we distinguish clearly between **task-level zero-shot generalization** and **data-level zero-shot generalization**, the latter of which has indeed been extensively studied in prior works.
Data-level zero-shot generalization, exemplified by models like VideoPoet that the reviewer mentioned, refers to generating diverse outputs (e.g., images or videos) conditioned on various textual prompts within a single predefined vision task, such as text-to-image or text-to-video generation. Although VideoPoet achieves impressive zero-shot performance in video generation tasks, it still remains constrained to the single task of video generation and does not exhibit cross-task generalization capabilities. In contrast, our paper explicitly addresses the fundamentally different challenge of task-level zero-shot generalization, where the model is expected to understand and execute completely novel and diverse vision tasks solely based on explanatory instructions, without task-specific fine-tuning.
Moreover, to facilitate and validate this task-level generalization, we have constructed a dataset consisting of approximately 12 million individual "input image → explanatory instruction → output" triplets. Unlike existing datasets, which typically contain predefined task-specific annotations, our dataset uniquely provides rich explanatory instructions that describe the objectives of diverse vision tasks explicitly. To the best of our knowledge, this dataset is the first and currently the only dataset specifically designed for studying and enabling unified task-level zero-shot generalization in vision tasks.
**Weakness 2**: *There are not many quantitative results.*
**Response**: We appreciate the reviewer raising this concern. To clarify, we have indeed provided extensive quantitative evaluations in the supplementary materials, covering 12 different tasks in total. For each task, representative visual examples are also included in Appendix Section C for further transparency.
It is important to note that all baseline methods we compared against, with the exception of Lumina-mGPT, do not utilize instruction-level or task-level zero-shot settings. While Lumina-mGPT is closer to our method in principle, it still requires rigid and fixed-format prompts for each specific task, as explicitly discussed in lines 1546\~1551 of the paper, and it did not provide any quantitative results for both instruction-level or task-level zero-shot experiments. Thus, it does not truly operate in a fully zero-shot, instruction-driven manner as proposed by our method. Additionally, to the best of our knowledge, this paper is the first work to provide quantitative analyses under both instruction-level and task-level zero-shot settings.
**Question**: *The dataset is like distilling ability from GPT?*
**Response**: The reviewer seems misunderstood the construction of the dataset. Before the submission of this paper, the three GPT-4o models officially released by OpenAI, i.e., gpt-4o-2024-05-13, gpt-4o-2024-08-06, and chatgpt-4o-latest, did not possess image generation or image editing capabilities, let alone the vision task-level generalization capability to be addressed by our work. In the construction of this dataset, we only adopt gpt-4o to generate part of the explanatory instructions, while other explanatory instructions for terminological-based vision tasks are manually annotated. | Summary: This paper proposes a concept called “Explanatory Instructions” to move beyond the conventional limitations of computer vision (CV) tasks. The authors argue that the currently common terminological definitions (e.g., “semantic segmentation”) oversimplify the expression of CV objectives, limiting the model’s ability to achieve generalized zero-shot performance across tasks. To address this, they propose using detailed natural language instructions to describe transformations between input and output images in a large-scale dataset. The idea is that by exposing the model to these more expressive and fine-grained task descriptions, it learns to “understand” the underlying objectives and changes for each visual task. Built on an autoregressive vision-language model their experiments show that the method not only generalizes in zero-shot fashion to previously seen tasks but also demonstrates some ability to handle unseen tasks.
Claims And Evidence: The primary claim of the paper is, by introducing Explanatory Instructions and constructing a corresponding large-scale dataset, the authors claim to achieve zero-shot generalization for both seen and unseen vision tasks.
The authors have presented numerous qualitative examples—such as generating reasonable outputs for previously unseen image-to-image transformation tasks—and some initial tests to illustrate zero-shot performance.
While the qualitative results are intuitive, more thorough quantitative evaluations or systematic comparisons with existing baselines would bolster the credibility of their claims about task-level zero-shot generalization.
Methods And Evaluation Criteria: I think the proposed methods and evaluation criteria in this paper are appropriate for addressing zero-shot generalization in vision tasks. The intuitive that define CV task objectives through detailed linguistic transformations from input images to outputs also sounds great.
-Methods: The authors adopt a standard autoregressive Transformer as the backbone for their vision-language generative model, converting both image and text inputs into discrete token sequences, and training via next-token prediction.
-Datasets and Evaluations: The authors constructed a large dataset, separating some tasks to remain unseen for zero-shot testing. This design helps assess whether the model can generalize to tasks not included in its training set.
From an application perspective, replacing fixed “task-name” categories with more flexible, instructive natural language is a promising approach. It also aligns with current instruction tuning trends in NLP. However, it seems that the evaluations make sense are primarily qualitative visualizations.
Theoretical Claims: The paper does not include formal theoretical claims or proofs, so there was nothing to verify in this regard.
Experimental Designs Or Analyses: The key experimental setup is distinguishing between tasks included in the training set and tasks that remain unseen, testing for zero-shot performance on the latter. Most analyses focus on sample outputs and visual demonstrations of how the model handles various image editing and transformation tasks. While these examples highlight the model’s adaptability, a more fine-grained quantitative analysis, such as performance under different instruction styles or varied input modalities would provide additional insight into robustness and failure modes.
Supplementary Material: The supplementary material includes additional examples and descriptions of dataset construction and model details. Specifically, the appendix includes more detailed visual examples and descriptions of data construction, helping clarify how the dataset and model perform in different scenarios. While training details and hyperparameters are briefly mentioned, the main paper still relies heavily on qualitative outcomes.
Relation To Broader Scientific Literature: This work is building on vision-language models and closely tied to the current trend of creating generalist models for vision tasks. Recent methods, such as Lumina-mGPT and OmniGen, rely on the notion of “task tag + input-output” to unify tasks such as image generation, segmentation, depth estimation, etc. In contrast, this paper introduces more descriptive natural language explanations to capture the goal behind each task, potentially enlarging the task space and improving zero-shot feasibility.
Essential References Not Discussed: While the paper covers recent VLM-related literature well, it would benefit from discussing more explicitly related previous work on task-level generalization in vision-language domains, such as [1] and [2].
[1] Bachmann R, Kar O F, Mizrahi D, et al. 4M-21: An any-to-any vision model for tens of tasks and modalities. NeurIPS, 2024: 61872-61911.
[2] Xiao B, Wu H, Xu W, et al. Florence-2: Advancing a unified representation for a variety of vision tasks. CVPR, 2024: 4818-4829.
Other Strengths And Weaknesses: Other Strengths:
1.Substantial scale of dataset (12 million triplets) facilitating robust training.
2.Promising demonstration of task-level zero-shot generalization beyond conventional terminological boundaries.
3.Clearly articulated ideas and methodological innovations.
Other Weaknesses:
1.It seems that this paper could benefit from stronger baselines or comparative studies with existing methods.
2.This paper also lacks some in-depth analysis for the proposed Explanatory Instructions, details can refer to “Questions for authors” part.
Other Comments Or Suggestions: Authors can consider providing quantitative evaluation metrics (FID, CLIP scores, etc.) in the main paper.
Questions For Authors: As mentioned in the weaknesses, I am more focused on some analytical issues regarding Explanatory Instructions.
1. Could Explanatory Instructions potentially exhibit clustering patterns? For instance, short editing instructions and fixed task-specific instructions (e.g., “Semantic Segmentation”) used in some VLMs might cluster around a few points when their features are extracted and visualized. I wonder whether different descriptions of the same task, when expressed via Explanatory Instructions, would demonstrate similar properties. If even for the same task, the representations via Explanatory Instructions in the evaluation dataset show significant bias. For example, wide dispersion in feature space. This could provide stronger evidence for the feasibility of task-level zero-shot generalization.
2. As real-world instructions can be vague or ambiguous. So if the instruction phrasing, length, style, or ordering changes, does this result in notable performance differences for image generation or understanding tasks?
If Explanatory Instructions show higher intra-task diversity and clear inter-task separation, it would empirically validate their ability to capture task objectives beyond rigid terminological definitions.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for your positive evaluation of our paper. Below are our responses to the concerns you raised.
**Essential References Not Discussed**: *While the paper covers recent VLM-related literature well, it would benefit from discussing more explicitly related previous work on task-level generalization in vision-language domains.*
**Response**: Thank you for your suggestions. We will discuss these works in our paper.
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**Question 1**: *Could Explanatory Instructions potentially exhibit clustering patterns?*
**Response**: Thank you for your insightful comment. Based on your suggestion, we analyzed 14 different **Terminological-based Vision Tasks** (including *Image Restoration*, *Deraining*, *Dehazing*, *Desnowing*, *Object Detection*, *Style Transfer*, *Depth Estimation*, *Surface Normal Estimation*, *Pose Estimation*, *Semantic Segmentation*, *HED Boundary to Image*, *Pose-to-Image*, *Depth-to-Image*, *Segmentation-to-Image*) to explore whether Explanatory Instructions exhibit clustering patterns.
We extracted the text features of Explanatory Instructions for each task using the BERT model, and then applied PCA to reduce the high-dimensional features to two dimensions. For better visualization, we randomly sampled 100 features per task and plotted them in a scatter plot.
Results can be found in the following anonymous link: https://anonymous.4open.science/r/ICML_Re-C752/instruction_features_pca_bert_all_tasks.png .Our findings show that **the Explanatory Instructions, when used to express vision tasks, do not exhibit the same clustering patterns as fixed task-specific instructions** (e.g., "Semantic Segmentation"). Fixed task-specific instructions tend to be highly discrete in nature, which may hinder the model’s generalization capability. On the other hand, Explanatory Instructions display a greater degree of continuity, which enhances the model’s ability to generalize across different vision tasks.
Additionally, we further investigated the zero-shot performance of specific vision tasks during testing. Specifically, we plotted the Explanatory Instructions used during both the training and testing phases in the same manner. For instruction-level zero-shot, we focused on the Explanatory Instructions for the same task in both the training and testing phases. We provide 3 examples in the following anonymous link: https://anonymous.4open.science/r/ICML_Re-C752/Instruction_level_zero_shot_bert_pca_3_samples.pdf . For task-level zero-shot, we visualized all the Explanatory Instructions across the training and testing tasks. For the selected zero-shot vision task, we random sample 500 features. We also provide 3 examples in the following anonymous link: https://anonymous.4open.science/r/ICML_Re-C752/task_level_zero_shot_bert_pca_3_samples.pdf . The above results demonstrate that in both instruction-level zero-shot and task-level zero-shot scenarios, there is almost no overlap between the training set and the test set.
We hope this analysis helps clarify the potential of Explanatory Instructions for enhancing task-level zero-shot generalization, and we appreciate your suggestion for further exploring clustering patterns.
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**Question 2**: *As real-world instructions can be vague or ambiguous. So if the instruction phrasing, length, style, or ordering changes, does this result in notable performance differences for image generation or understanding tasks?*
**Response**: We thank the reviewer for raising this important question. Indeed, real-world instructions can vary significantly in phrasing, length, style, and ordering, and such variations can impact model performance. To thoroughly address this concern, we have provided numerous examples of real-world instructions in Appendix C, explicitly illustrating a wide diversity in phrasing, length, style, and structure.
In our validation experiments, the unseen explanatory instructions indeed include substantial variations in linguistic expression. We acknowledge that different descriptive language choices can lead to noticeable differences in the model's generation or interpretation outcomes. However, it is precisely this linguistic diversity that facilitates stronger generalization capabilities of our model. For instance, as discussed explicitly in Appendix B.1.4 (Fig. 32), when encountering categories not included in the training set (e.g., "broad-winged damselfly"), the model struggles to recognize the category name alone. Yet, it significantly benefits from alternative descriptive expressions (e.g., "the creature on the leaf"), highlighting the model’s improved interpretability under instruction diversity.
To further illustrate this behavior, we provide additional examples at the following anonymous link: https://anonymous.4open.science/r/ICML_Re-C752/More_Examples.pdf .
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Rebuttal Comment 1.1:
Comment: After reading the review, I am satisfied with the author's response, therefore I maintain my decision of giving a score of four.
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Reply to Comment 1.1.1:
Comment: Thank you for your feedback! We sincerely appreciate the time and expertise you've dedicated to evaluating our work. We will implement all suggested improvements to enhance the academic rigor and presentation clarity in the final version. | Summary: This paper proposes Explanatory Instructions to address the challenge of task-level zero-shot generalization in computer vision, inspired by the success of instruction-driven models in NLP. The authors hypothesize that conventional terminological task definitions (e.g., "semantic segmentation") limit models' ability to generalize, as they fail to convey task objectives intuitively. To overcome this, they introduce Explanatory Instructions—natural language descriptions of image-to-output transformations—and construct a Dataset of Explanatory CV Tasks (DECVT) with 12M "image-input → instruction → output" triplets. A token-based autoregressive vision-language model is fine-tuned on DECVT, demonstrating instruction-level (unseen instructions for seen tasks) and task-level (unseen tasks like Canny-to-Image) zero-shot capabilities. Experiments show improvements over baselines in image editing, generation, and low-level tasks, though performance gaps remain compared to task-specific models.
Claims And Evidence: Most claims made in the submission are supported by clear and convincing evidence, e.g.,
1) Explanatory Instructions improve instruction-level and task-level zero-shot generalization.
2) DECVT enables models to handle diverse vision tasks via linguistic instructions.
3) The AR-VLM achieves competitive results on unseen tasks (e.g., Depth-to-Image) compared to vision generalist models.
Methods And Evaluation Criteria: As the unified token-based AR-VLM architecture aligns with recent trends in multimodal modeling, this paper further constructed a systematic dataset of explanatory CV tasks, combining manual annotation and GPT-4o-generated instructions. Although the results in Table 5 ~ 7 still show significant gaps compared to state-of-the-art task-specific models, both the task-level and instruction-level zero-shot generalization for CV tasks shown in this paper are exciting.
Theoretical Claims: The paper does not introduce formal theorems or rigorous mathematical proofs, so there is no specific need for verification of theoretical correctness. Its principal contribution lies more in method design and dataset construction than in theoretical innovation.
Experimental Designs Or Analyses: The authors make comprehensive experiments across 10+ tasks in Appendix B. During the evaluation for task-level zero-shot tasks, it seems that authors have excluded specific tasks during training, which make the zero-shot scores convincing. However, I think there need some discussions for failure cases.
Supplementary Material: I review the appendix part. The appendix details dataset construction (e.g., GPT-4o prompts, manual annotation processes) and provides additional examples (e.g., Figs. 9 ~ 56).
Relation To Broader Scientific Literature: The paper clearly situates its contributions within the broader scientific literature. It identifies a clear gap between NLP and CV regarding zero-shot generalization capabilities, acknowledging previous approaches such as Lumina-mGPT, OmniGen, and PixWizard. The paper builds convincingly upon prior NLP-inspired vision-language paradigms and emphasizes the uniqueness of explanatory-based instruction as a conceptual advance beyond existing terminological frameworks.
Essential References Not Discussed: Overall, the authors cite most of the major and emerging literature on multi-task vision models and multimodal pretraining.
Other Strengths And Weaknesses: I just brief summarize some other strengths and weakness.
Strengths:
1) Novel idea of Explanatory Instructions for both task-level and instruction-level generalization in computer vision.
2) The proposed large-scale dataset is meaningful to the community, the dataset also encompasses various transformations and task types.
3) Authors provide various discussions in the appendix.
4) If validated further, this approach could be an important training paradigm for general-purpose multimodal models.
Weaknesses:
1) Overreliance on GPT-4o for instruction generation introduces potential noise and biases.
2) There lacks an explanation regarding the distribution of data across different tasks in the dataset.
3) Zero-shot experiments can address a subset of unseen tasks, while the authors have also discussed in Section 5. More diverse or challenging tasks need exploration to confirm broader scalability.
Other Comments Or Suggestions: None
Questions For Authors: 1) The authors used GPT-4o for training data generation, especially the instructions. From my experience, although GPT-4o seems better than other VLMs as discussed in Appendix A, there still remains potential noise and biases in the generated instructions. How the authors deal with these noises, biases, and even inaccuracies?
2) Section 2 provides a detailed account of the dataset composition, and the supplementary materials explain how the dataset was constructed. However, certain details remain unspecified. For instance, in the task-level zero-shot experiments, what proportion of the data is allocated to each task? And in the complete dataset, what is the ratio of each task pair?
3) The examples in Figure 32 are quite helpful in illustrating the effectiveness of explanatory instructions. However, the authors only provided pair of examples, and it would be beneficial if they included more convincing samples.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for your positive feedback on our paper. In the following responses, we have addressed the concerns you raised during the review process, and we hope these answers will resolve your questions.
**Question 1 / Weakness 1**: *The authors used GPT-4o for training data generation, especially the instructions. From my experience, although GPT-4o seems better than other VLMs as discussed in Appendix A, there still remains potential noise and biases in the generated instructions. How the authors deal with these noises, biases, and even inaccuracies?*
**Response**: We appreciate the reviewer highlighting this important issue. Although GPT-4o indeed provides superior capability compared to other VLMs (as detailed in Appendix A), the instructions it generates still contain noise, biases, or inaccuracies. To address these potential issues, we have implemented a data quality control procedure.
To be specific, we noticed that GPT-4o can occasionally produce unstable or inaccurate explanatory instructions if it misunderstood the input images. To mitigate this, we simultaneously asked GPT-4o to generate captions corresponding to the images. We then employed CLIP to measure the semantic similarity between these captions and their associated images. Any generated data pair with a similarity score below 0.5 was automatically filtered out from the final dataset. Otherwise, we maintained the explanatory instructions. In addition, a portion of our dataset was manually annotated as described in Section A.1 (Ln, 718\~719), ensuring high-quality and bias-free explanatory instructions.
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**Question 2 / Weakness 2**: *Section 2 provides a detailed account of the dataset composition, and the supplementary materials explain how the dataset was constructed. However, certain details remain unspecified. For instance, in the task-level zero-shot experiments, what proportion of the data is allocated to each task? And in the complete dataset, what is the ratio of each task pair?*
**Response**: Thank you for your suggestions. We clarify these details as follows:
**Complete Dataset Composition**: Our full dataset consists of two components: Terminological-based Vision Tasks and Explanatory-based Vision Tasks. Specifically, the Terminological-based Vision Tasks component includes approximately 4M individual “input image → explanatory instruction → output” triplets for image editing tasks. For the other vision tasks within this component, each task has a varying number of triplets, ranging from a minimum of 0.05M to a maximum of 2M. In contrast, the Explanatory-based Vision Tasks component contains approximately 2M individual “input image → explanatory instruction → output” triplets.
**Task-Level Zero-Shot Experiment Allocation**: As detailed in Section 4.2 (Ln. 320\~329), to **rigorously test task-level zero-shot generalization**, we deliberately removed data corresponding to the following tasks from the Terminological-based Vision Tasks component: *Image Restoration*, *Depth Estimation*, *Depth-to-Image*, *Surface Normal Estimation*, *Surface Normal-to-Image*, *HED Boundary Detection* and *HED-to-Image*. From the remaining tasks, we then constructed the training dataset for zero-shot experiments by randomly selecting 1M triplets from the Explanatory-based Vision Tasks component, 1M triplets specifically for image editing tasks, and another 1M triplets from other remaining vision tasks.
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**Question 3 / Weakness 3**: *The examples in Figure 32 are quite helpful in illustrating the effectiveness of explanatory instructions. However, the authors only provided pair of examples, and it would be beneficial if they included more convincing samples.*
**Response**: Thank you for your suggestions. We have provided additional examples at the following anonymous link: https://anonymous.4open.science/r/ICML_Re-C752/More_Examples.pdf . | Summary: This work proposes a new method for fine-tuning visual tasks, explanatory Instructions. Inspired by the work on text instruction fine-tuning, the authors aim to explore whether there is a generalization phenomenon in instruction fine-tuning for visual tasks. Therefore, they construct pure-text instructions for different visual tasks and use a large vision model, specifically Lumina-mGPT-7B-768-Omni, to verify the effectiveness of the constructed instruction dataset. The authors observe both intra-task generalization ability and cross-task generalization ability. Meanwhile, this article proposes an Explanatory Instructions dataset.
Claims And Evidence: NA
Methods And Evaluation Criteria: NA
Theoretical Claims: NA
Experimental Designs Or Analyses: NA
Supplementary Material: NA
Relation To Broader Scientific Literature: NA
Essential References Not Discussed: NA
Other Strengths And Weaknesses: I really really like the idea proposed in this paper. However, the discussion on zero-shot task generalization in this paper is clearly insufficient. If my concerns can be addressed and the paper can be further improved, I will raise my score. Otherwise, I will lower my score after the rebuttal stage.
Strengths:
The idea put forward in this paper, namely that zero-shot generalization can be observed across different vision tasks, is an important finding. The publicly available dataset Explanatory Instructions will also make a significant contribution to the research community and accelerate the process of achieving true unification in visual tasks.
Weaknesses:
1. There are only relatively subjective case analyses as experimental results. It is unclear whether they have been cherry-picked, and there is no quantitative measurement of the true capability of solving tasks generalized in the zero-shot setting.
2. I am not sure if a well-trained stable diffusion model for image generation can also solve these problems.
3. I am curious about the cross-task generalization ability of the initial VLM model, Lumina-mGPT-7B-768-Omni, without any training. Does task generalization come from the base model or from instruction fine-tuning?
Other Comments Or Suggestions: NA
Questions For Authors: 1. I am curious about the cross-task generalization ability of the initial VLM model, Lumina-mGPT-7B-768-Omni, without any training. Does task generalization come from the base model or from instruction fine-tuning?
2. What if the base model is a text + image-to-image model, such as Stable Diffusion (SD)?
3. Are there any quantitative results? Case-level arguments are hardly convincing enough for me to determine whether the theory you proposed is truly reliable.
4. It is necessary to further demonstrate whether this cross-task generalization ability is inherent in the base model itself or is stimulated by the task fine-tuning method. It is recommended to use multiple base models for proof.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We greatly appreciate your recognition of the idea presented in our paper. Below are our responses to the concerns you raised.
**Question 1 & 4 / Weakness 3**: *I am curious about the cross-task generalization ability of the initial VLM model, Lumina-mGPT-7B-768-Omni, without any training. Does task generalization come from the base model or from instruction fine-tuning? It is necessary to further demonstrate whether this cross-task generalization ability is inherent in the base model itself or is stimulated by the task fine-tuning method. It is recommended to use multiple base models for proof.*
**Response**: Thank you for your valuable suggestions. We would like to clarify that, in our experiments on analysing the **zero-shot capabilities on unseen vision tasks**, the base model used for initialization was **Lumina-mGPT-7B-768** (cf. 300~301 of the paper, it is a text-to-image generator). This base model **has no multi-task capabilities beyond text to image generation**, so it cannot perform other vision tasks on its own.
Thus, any cross-task generalization observed comes from our instruction fine-tuning, not from an inherent ability of the pre-trained model. We explicitly discuss this in Appendix B.2 (lines 1546–1551), confirming that Lumina-mGPT-7B-768-Omni by itself does not generalize to unseen tasks – the generalization emerges only after training with our explanatory instructions.
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**Question 2 / Weakness 2**: *What if the base model is a text + image-to-image model, such as Stable Diffusion (SD)?*
**Response**: Thank you for your suggestions. Using a stronger or more flexible foundation model (e.g. more advanced DiT model) could indeed further improve the overall performance. Our primary goal, however, was to validate the methodology of unified vision task-level generalization rather than to chase state-of-the-art results on any single base model. Furthermore, traditional stable diffusion model can only generate images but can not generate text. Although directly using stable diffusion (text + image-to-image) can also adopt such vision task-level zero-shot capability (following settings in Section 4.2 of the paper), to enhance the scalability of the model, i.e., enabling the model to simultaneously generate text, images, and other multimodal data, we therefore adopted the vanilla AR-based VLM introduced in Chameleon and Lumina-mGPT.
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**Question 3 / Weakness 1**: *Are there any quantitative results? Case-level arguments are hardly convincing enough for me to determine whether the theory you proposed is truly reliable.*
**Response**: Thank you for your suggestions. Actually, we have provided **quantitative results in Appendix B (Ln. 1375\~1510)** of the paper. In particular, Table 6 and Table 7 in Appendix B reports results on 5 instruction-level zero-shot tasks (the instructions are not seen during training) and 5 task-level zero-shot tasks (both the task and instructions are not seen during training). **Notably, all methods used for comparison do not use instruction-level or task-level zero-shot settings except Lumina-mGPT.** However, Lumina-mGPT requires rigid and fixed format prompts as input, as we had discussed in Ln. 1546\~1551 of the paper:
In the evaluation process for Lumina-mGPT in Table 6, all instructions follow this format: "``Generate an image according to the provided image, and according to the following caption: {Image Caption},<|image|>``". For the experiments in Appendix B.1, the instructions are "``Depth estimation. <|image|>``'' for the *Depth Estimation* task, "``Semantic segmentation. <|image|>``'' for the *Semantic Segmentation* task and "``Surface normal estimation. <|image|>``'' for the *Surface Normal Estimation* task. Any alteration to the format of these instructions leads to model failure or significantly degraded its performance.
In addition, following the suggestions from Reviewer #yk8P (Question 1), we further demonstrate that under both the instruction-level and task-level zero-shot settings, there is a significant divergence between the training and test samples (visualizations for instruction-level zero-shot can be found in the following anonymous link: https://anonymous.4open.science/r/ICML_Re-C752/Instruction_level_zero_shot_bert_pca_3_samples.pdf , visualizations for task-level zero-shot can be found in the following anonymous link: https://anonymous.4open.science/r/ICML_Re-C752/task_level_zero_shot_bert_pca_3_samples.pdf). This provides additional evidence for the model’s generalization capability.
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Rebuttal Comment 1.1:
Comment: Thanks for the author's response. Some of my concerns have been addressed and clarified, yet others persist. The matter that concerns me is whether the method presented in the paper possesses sufficient generalization ability to be applied across other base models. For example, when considering the Supervised Fine-Tuning (SFT) for large language models, it is applicable to all such LLMs. Making a claim of zero-shot generalization is a significant assertion. The authors need to conduct more in-depth investigations to determine whether the instruct data is the crucial factor or if a powerful base model is the key determinant. Otherwise, misleading conclusions may ensue. Consequently, I will maintain my score unchanged.
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Reply to Comment 1.1.1:
Comment: Thank you for your additional response. We are concerned that some details may not have been clearly expressed, so please allow us to provide a brief supplementary explanation:
**1. Baseline Model Setup:**
In our paper, we employ a fundamental AR-based vision-language model for experiments, which is built upon a basic large language model (LLM) augmented with a VQ-GAN for image encoding and decoding.
**2. Lumina-mGPT-7B-768:**
This model is trained under the aforementioned architecture and exhibits text-to-image generation capabilities. However, it does not inherently possess the ability to perform complex visual tasks. We use this model to directly demonstrate that Explanatory Instructions can enable vision task-level zero-shot generalization (as shown in Section 4.2).
**3. Lumina-mGPT-7B-768-Omni:**
This model, based on the same foundational architecture, can handle some visual tasks but remains limited (as discussed in Ln. 1546\~1551). Specifically, it only performs fixed visual tasks when provided with rigid, fixed-format language prompts. We conducted Supervised Fine-Tuning (SFT) on this model and showed that even a simple SFT can endow the model with both instruction-level and task-level zero-shot capabilities. Quantitative results demonstrating these abilities are provided in Appendix B.1, while Appendix C contains qualitative examples based on this SFT model.
**4. Controlled Experiments and Contributions:**
Through these controlled experiments, we have demonstrated that Explanatory Instructions are instrumental in eliciting both instruction-level and task-level zero-shot generalization. We also acknowledge that these zero-shot capabilities are partly influenced by the pre-trained visual encoder/decoder, an aspect we discuss further in Section 5.
We understand your concerns regarding the claim of zero-shot generalization. Precisely because we were concerned that a powerful pre-trained model might obscure our assessment of zero-shot capability, we deliberately chose the aforementioned basic model for our validation experiments. We hope these clarifications can address your concerns. Once again, thank you for your valuable feedback and your positive comments on our idea. | null | null | null | null | null | null |
De-coupled NeuroGF for Shortest Path Distance Approximations on Large Terrain Graphs | Accept (poster) | Summary: This paper proposes a new learning-based approach for answering shortest path distances on large-scale terrain DEMs. Overall, the proposed method extends the prior work of NeuroGF while providing a comprehensive and in-depth analyses on the training mechanisms and design choices of neural components. Extensive experiments demonstrate that the proposed method brings obvious improvement in terms of both accuracy, efficiency, and scalability.
Claims And Evidence: Well supported.
Methods And Evaluation Criteria: Comprehensive experimental evaluations.
Theoretical Claims: Technically sound.
Experimental Designs Or Analyses: Well-organized experimental setup.
Supplementary Material: I have broadly skimmed all parts of the Appendix.
Relation To Broader Scientific Literature: Closely related to geometry processing and downstream applications of geospatial data processing.
Essential References Not Discussed: Reference adequate.
Other Strengths And Weaknesses: In general, this paper deals with an essential and highly valuable problem of developing efficient geodesics answering frameworks, which are not fully investigated in the current community, especially for "neuralized" design paradigms. The ways of analyzing the working mechanisms and restrictions of existing baselines and further exploring more effective structural designs are solid and inspiring.
Particularly, the decoupled training of embedding and distance adjustment modules are technically sound. Since the first stage is performed on coarsen graphs, the overall training efficiency can be greatly improved when facing large-scale data. More importantly, we can circumvent the cumbersome re-training process by only fine-tuning the second stage.
In summary, I tend to think the proposed method is an insightful work to the problem of neural geodesics learning.
Other Comments Or Suggestions: N/A
Questions For Authors: In the right column of page 1, the authors mentioned "Throughout this paper we assume that a terrain is represented as a xy-monotone triangulated surface Σ in R^3". What does it mean specifically?
Code Of Conduct: Affirmed.
Overall Recommendation: 5 | Rebuttal 1:
Rebuttal: Thank you for your review! We are glad that you appreciate our proposed advancement in the problem of neural data structures for SP queries on terrains.
**Regarding your question about $xy$-monotone surfaces**, a continuous surface in $\mathbb{R}^3$ is called $xy$-monotone if every line parallel to the $z$-axis only intersects the surface at a single point.
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Rebuttal Comment 1.1:
Comment: Thanks for the authors' explanations. I have no further concerns.
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Reply to Comment 1.1.1:
Comment: Thank you for your thoughtful evaluation of our paper! | Summary: This paper proposes a De-coupled NeuroGF for efficiently approximating SPD queries on large-scale DEMs. The key contribution authors decouples the Siamese embedding module and the distance calculation module in NeuroGF. By combining an efficient two-stage hybrid training strategy, the method significantly reduces computational bottlenecks, making training on large-scale terrain DEMs (up to 16 million nodes) feasible. Experimental results demonstrate that the method performs excellently on both synthetic and real datasets.
Claims And Evidence: The main claim is the decoupled training framework, combined with a two-stage hybrid training strategy, provides an efficient solution for SPD queries on large-scale terrain DEMs. This claim is supported by clear by experiments.
Methods And Evaluation Criteria: The evaluation criteria include mean relative error and accuracy, which are commonly used metrics for SPD approximation problems and are both reasonable and standard. The datasets including synthetic and real-world terrains, fully test method performance.
Theoretical Claims: I think this paper focus on the practical implementation. Therefore, there are no theoretical claims or proofs that need to be verified.
Experimental Designs Or Analyses: I have read the experimental section and believe that it provides sufficient evidence to support the paper's claims.
Supplementary Material: I have read the supplementary material and gained some additional implementation details
Relation To Broader Scientific Literature: This paper refers to NeuroGF, and extend this idea to large-scale terrain DEMs, addressing the scalability challenges
Essential References Not Discussed: The comparison methods in the paper are only up to 2023, which may be somewhat outdated for ICML 2025. Are there any updated methods from 2024?
Other Strengths And Weaknesses: Strength:
1. The paper is generally well-written, well-structured, and easy to read and understand.
2. The proposed method achieves training on large-scale terrain DEMs and accelerates the training stage. This is the main advantage of the proposed method and is a good improvement.
3. Extensive experiments on both synthetic and real datasets provide strong evidence.
Weakness:
1. The paper does not provide detailed information on hyperparameter tuning or sensitivity analysis, which could affect the understanding of reproducibility and robustness. For example, in M-CTR, increasing the value of k reduces training time, but what impact does this have on accuracy? Does each dataset require separately designed parameters?
2. The comparison methods are only up to 2023. Are there any methods from 2024 or more recent ones?
Other Comments Or Suggestions: 1. It is recommended to include a sensitivity discussion or ablation study on key hyperparameters (such as embedding dimension, number of GNN layers, and coarsening factor) to improve reproducibility.
2. compare with more recent methods.
Questions For Authors: Dividing the network into two parts to accelerate training is a common approach in the computer vision (CV) field, such as in ACE[1]. What are the advantages and differences of the method proposed by the authors?
[1] Brachmann E, Cavallari T, Prisacariu V A. Accelerated coordinate encoding: Learning to relocalize in minutes using rgb and poses[C]//Proceedings of the IEEE/CVF Conference on Computer Vision and Pattern Recognition. 2023: 5044-5053.
Ethics Expertise Needed: ['Other expertise']
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We thank you for your time and constructive feedback. We are glad the reviewer appreciates our de-coupled and mixed coarse-to-refined training strategy for efficiently processing large terrain graphs at scales previously which were not able to be considered. As you point out, our de-coupled training strategy is particularly useful for dynamically updating neural data structures efficiently.
**Hyperparameter tuning:** Thank you for these comments. We should have included such information in the paper. In fact, we do deploy hyperparameter tuning in the paper. For our experiments, we perform all hyperparameter tuning on smaller-scale synthetic terrains, selecting the best-performing hyperparameters based on these trials. These optimized hyperparameters are then applied across all subsequent experiments on large-scale terrain graphs. We will include detailed hyperparameter tuning in the revision. An example of how the model accuracy changes with different embedding dimensions for the latent space is shown in Figure 1 (https://shorturl.at/SXyB2). In general, we observe that model performance stabilizes after a while.
**Comparisons with other work:** The primary goal of our paper is to develop a lightweight neural data structure to answer shortest-path (SP) distance queries for extremely large terrain graphs. We see three relevant areas of work for comparison:
(1) Metric learning: Siamese networks are the SoTA architecture in the field of metric learning and we already compare with state-of-the-art Siamese network, denoted by $\mathsf{X}$+$L_p$ in our paper. Furthermore, we explored the design space of Siamese learning approaches by using different SoTA GNN architectures and transformers used as the network backbone. (See C.3 in the Supplement.)
(2) Neural models specific for geodesic distance queries: GeGNN and NeuroGF are the current SoTA architectures for processing geodesic distance queries (i.e. shortest path distance) on graphs induced by meshes. In our paper, we provide direct comparisons to both GeGNN and NeuroGF.
(3) General graph learning: While SPD approximation is a commonly considered problem in the graph learning community, our goals are different as we seek a lightweight and efficient neural data structure. The setting here is that once we preprocess the data (i.e. trained the model), the users might have many future SP queries, each of which consists of two points, and the model should return the SP distance between them quickly. (This is a fundamental primitive in GIS applications.)
Current GNNs are not directly suitable as a neural data structure for answering many future SP queries. For example, there are several existing recurrent GNN methods which imitates algorithmic control flows in order to generalize all graph instances (Tang, et al. 2020, Luca, et al. 2024). However, such iterative approaches are computationally expensive during the inference time for each SP distance query, as it requires many iterations of the models to essentially explore the entire graph. In contrast, our latent embedding can capture hidden patterns in the SP distance function, while MLP can effectively retrieve the final distance. As an example, we trained a lightweight GNN model trained to learn two steps of single-source shortest paths. The inference time for approximating the SPD between a pair of nodes with 100 iterations of our lightweight model is 307 seconds on Norway as such a model is essentially forced to compute all shortest paths on the graph from a single source even though we are **only** interested the SP distance between a single pair. In contrast, our M-CTR method, after computing all initial embeddings, achieves an inference time of merely $7 \times 10^{-6}$ seconds. We would be happy to add such a comparison to the revised paper.
In short, we have compared our method with all relevant neural approaches; but we would be happy to add additional comparisons with iterative GNNs. Note that all neural approaches are orders of magnitude more efficient than SoTA classical algorithmic approaches (as we described in paper).
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Rebuttal Comment 1.1:
Comment: Thank you to the author for the detailed response, which has addressed my concerns. I agree with reviewer j9PW's assessment that this is a meaningful piece of work, and I have decided to increase my score.
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Reply to Comment 1.1.1:
Comment: Thank you for your thoughtful evaluation of our paper! | Summary: This paper presents decoupled-NeuroGF framework for efficient approximate SPD queries on large terrain DEMs, based on the NeuroGF framework. This paper appropriately abstracts high-resolution terrain datasets as weighted graphs. The proposed decoupled-NeuroGF with a two-stage mixed-training strategy significantly improves computational efficiency and model performance, making the method suitable for large scale terrain. It reduces training time from days to hours for million-scale terrains and maintains high SPD approximation accuracy. The method also supports efficient updates for terrain changes through retraining only the distance-adjustment module. Experiments on real-world terrains with up to 16 million nodes demonstrate its scalability and superiority over previous approaches.
Claims And Evidence: The paper's claims are well - supported by evidence:
[1] The significant reduction in training time is evidenced by experiments showing the method cuts training from days to hours for large terrains.
[2] Model performance improvement is proven by data indicating the method maintains high SPD approximation accuracy and enables efficient updates for terrain changes.
[3] The two - stage mixed - training strategy's benefits are experimentally validated, proving its effectiveness in enhancing computational efficiency and model performance.
To strengthen the evidence:
More comparative data on terrains of different scales could be provided to better demonstrate the method's versatility and efficiency across various terrains.
Methods And Evaluation Criteria: The methods and evaluation criteria presented in the paper are reasonable for the problem of efficient SPD queries on large-scale terrain DEMs. The decoupled-NeuroGF data structure and the two-stage mixed-training strategy address computational bottlenecks and enable efficient training on large terrains. The evaluation focuses on key aspects like training time reduction, approximation accuracy, and efficient updates for terrain changes, which are appropriate for assessing the method's effectiveness in real-world applications.
Theoretical Claims: The theoretical claims regarding complexity in the paper are correctly proven.
Experimental Designs Or Analyses: The paper's experimental design for SPD queries on large-scale terrain DEMs is reasonable. It uses synthetic terrains with varying complexity but the same size, generated via 2D Gaussian mixtures, to evaluate different model designs. However, evolving more datasets with more vertices and corresponding complexity is recommended, as this paper aims to solve SPD question on high-resolution terrain datasets.
Supplementary Material: I have reviewed the supplementary material, specifically sections ABC. The theoretical explanations provided are logical and well-reasoned. Additionally, the supplementary experiments are fairly comprehensive and reinforce the validity of the study.
Relation To Broader Scientific Literature: The key contributions of this paper are closely related to the broader scientific literature in several ways:
[1] Extension of NeuroGF Framework: This paper builds upon the existing NeuroGF framework, which is already a significant contribution to the field of geodesic distance estimation. By proposing a decoupled-NeuroGF data structure, the authors extend the applicability and efficiency of the original framework, addressing its limitations in handling large-scale terrain DEMs.
[2] Innovative Training Strategy: The two-stage mixed-training strategy is an advancement in training neural data structures for terrain analysis. This approach not only reduces computational bottlenecks but also allows for efficient training on large terrains, which was previously challenging. This strategy can be seen as a progression from traditional training methods, incorporating insights from model optimization and efficient learning techniques.
Essential References Not Discussed: No essential references appear to be missing from the paper's discussion.
Other Strengths And Weaknesses: Strengths.:
1. The proposed decoupled-NeuroGF framework represents a creative advancement in the field. By separating the training process into two stages, it effectively reduces computational demands and enhances training efficiency on large-scale terrains, which is a significant improvement for practical applications.
2. The method's ability to handle dynamic terrains by updating only the distance-adjustment module is also a valuable contribution, as it addresses the realistic challenge of terrain changes.
Weaknesses:
1. The experimental section could be strengthened by including more diverse and large-scale datasets to better showcase the method's generalizability.
2. While the paper presents a novel approach, a more detailed comparison with other existing methods would help better position its contributions within the broader literature.
3. The scope of the work appears to be somewhat limited. The paper could benefit from a more extensive exploration of the framework's capabilities and potential applications, which would provide a more comprehensive understanding of its value and impact.
Other Comments Or Suggestions: No additional comments.
Questions For Authors: High-resolution terrain data set is a fundamental assumption in this paper.
[1] How to determine whether a data set belongs to this category?
[2] Could some indicators like vertex density be used for quantification? The paper seems to lack relevant analysis.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank the reviewer for your time and constructive feedback. We are happy that the reviewer appreciated our innovative training strategy: with our de-coupled and mixed coarse-to-refined training strategy, we introduce a lightweight neural data structures that can efficiently answer many shortest path distance (SPD) queries over massive terrain graphs orders of magnitude faster than classic algorithmic approaches. Note that this is a fundamental problem in GIS (see also our discussion in “Scope of work”). Below we provide responses for main questions/comments.
**High-resolution terrain datasets:** In our experiments, we use high-resolution terrain graphs because the shortest paths on these graphs provide more accurate approximations of the true geodesic on the terrain surface (and as a result, these are the most common data available). However, our technique is applicable to any terrain graph, including lower resolution ones where the geodesic approximation is coarser.
We think that the resolution of the terrain graph does not directly affect the quality of the approximation; rather, the ``complexity" of the metric induced over the terrain graph would. As an example, we measure complexity by the _doubling dimension_ of the terrain graph. This is theoretically motivated by Theorem 1.2 of (Naor et al. 2012), which states that every metric space can be approximately embedded into $R^N$ with distortion dependent on the _doubling dimension_ of the original metric space. We conduct new experiments on synthetic terrains (see Table 1). We observe that: (1) as the doubling dimension increases, the relative error incurred by the Siamese embedding approach (i.e, GAT+$L_1$) also increases. (2) Our de-coupled training approach can help to adjust the errors from the Siamese approach (via the distance-computation module) and further improve the SPD approximation. Also the relative error by our de-coupled approach increases at a slower rate as doubling dimension increases, compared to that of the Siamese approach (GAT+L1).
Theoretically, it could be interesting to provide sample complexity bounds w.r.t. doubling dimension but we leave this to future work.
| Doubling Dimension| De-coupled| GAT + L |
|-|-|-|
| 4.1| **0.0052**| 0.0061|
| 4.4| **0.0132**| 0.0166|
| 4.7| **0.0186**| 0.0329|
*Table: Approximate doubling dimension, and average relative error of each model.*
**Comparisons to other methods:** Please see our response to Reviewer 2aDC.
**Experiments with more diverse and large-scale datasets:** Thank you for the suggestion. First, we note that we focus on Norway and Los Angeles in our experiments as are they are both complex and large-scale. Both Norway (4M nodes) and Los Angeles (16M nodes) are far larger than any terrain graphs considered in previous work. They both represent highly complex terrains: The Norway terrain graph is taken from a highly mountainous region and the Los Angeles dataset spans all of LA county and has both flat and mountainous regions with elevations varying between 3000m and 0m.
We will include more large-scale datasets in the revision. We have already obtained results for two additional datasets: Holland and Philadelphia, both of which contain 1M nodes. Results are shown in Table 2. For both datasets, our new M-CTR approach outperforms just simply using the Siamese network trained on a coarse 2500 node version of the terrain (Coarse GAT+L1). We will update our paper with these results, as well as additional results from larger datasets (e.g. a 25M node Norway dataset which covers a different region of Norway than our current Norway dataset).
| Dataset| Model| Relative Error (%) ↓ | Accuracy (%) ↑ |
|-|-|-|-|
|**Holland, IN**| Coarse GAT + L1| 2.06 ± 1.54| 65.1|
| | M-CTR| **0.86 ± 2.29** | **90.8**|
| **Philadelphia, PA**| Coarse GAT + L1| 2.07 ± 1.47| 30.1|
| | M-CTR| **0.51 ± 0.71** | **94.4** |
**Scope of the work:** First, we would like to emphasize that the development of succinct data structures to support efficient SP distance queries on massive terrain graphs is important in its own right: it is a fundamental problem in geospatial data analysis and GIS database systems with a wide range of applications, as SPD queries is a key primitive operation from terrain-navigation, to point of interest search problems, to flood simulations. Thus a scalable, practical data structure for SP-distance queries on terrains will have a huge impact. This explains the huge literature on this problem both in GIS and computational geometry. We also show that our two-stage mixed training strategy leads to an easy-to-update neural data structure when there are dynamic changes in the terrain (e.g. in time-sensitive natural disaster relief scenarios). Furthermore, while not explored in this paper, our de-coupled training framework could also be applicable to other general metric learning setups, when the input metric space is massive, and a large number of future SP queries are expected. | null | null | null | null | null | null | null | null |
How Much Can We Forget about Data Contamination? | Accept (poster) | Summary: - the paper studies the effect of data contamination during the pre-training of language models, through a series of *controlled* contamination experiments
- the paper studies the effect by considering: (1) scaling the amount of contamination (i.e. repetitions), (2) scaling the model size, (3) scaling the (unrelated) pre-training data size, (4) scaling data and model jointly (Chinchilla), and (5) if and how weight decay plays a role
- the paper reports multiple findings, for example:
- small-scale contamination may or may not be "forgotten" (i.e. the contamination stops contributing to benchmark gains), depending on how much (unrelated) pre-training data there are (as relative to Chinchilla optimal)
- more repetitions of contamination uniformly increases benchmark performance, but the increase depends on both model scale and data scale
- exposing to *novel* pre-training data is more effective at forgetting contamination than to old pre-training data
- repetition is an important factor, perhaps arguably more so than seeing them later in training
## update after rebuttal
I appreciate the authors' rebuttal and will keep my score and my assessment that the paper should be accepted.
Claims And Evidence: Yes, the claims in the paper are supported by extensive experiments to my understanding
Methods And Evaluation Criteria: Yes, the proposed research question, methods, and evaluation data make sense overall.
- One minor weakness is that for some of the experiments, the authors used the 124M model, which is perhaps too small for meaningful performance on some of the benchmark datasets (e.g. MMLU).
- Another minor weakness is that FineWeb-Edu contains only text and largely no math or code; this means the models may be biased towards being a text model as opposed to a general purpose model like GPT-4. Though I understand that this could be an artifact of using LLM.c which primarily uses FineWeb-Edu.
Theoretical Claims: The paper is mostly empirical. The analysis component for weight decay (sec 5.1) seems to make sense.
Experimental Designs Or Analyses: Overall, the experiments of the paper are well-designed to comprehensively answer the proposed research question. The findings are well supported by the experiment results.
Comments:
- (minor) deduplicating the contamination benchmark data (e.g. HellaSwag) from the pre-training tokens (e.g. FineWeb) is also recommended for a truly unbiased evaluation. Since the authors report accuracy gaps between holdout and contaminated, this is perhaps OK.
- (minor, mentioned earlier) depending on the model size (small vs big), pre-training data (FineWeb vs other pre-training mix), or even architecture (GPT-3 vs newer ones), the pre-trained model may not perform meaningfully on some of the benchmark data (e.g. the 124M model trained on 1x Chinchilla can be basically random guessing at MMLU). This could affect the takeaways, but on a macroscopic level the results are consistent and make sense.
Supplementary Material: Yes, particularly A.3 near-duplicate data filtering (as deduplication is very important)
Relation To Broader Scientific Literature: - this paper can be viewed as a more systematic, comprehensive, and rigorous execution of Jiang et al. (2024) [2] to understand the effect of data contamination in the pre-training stage
- related work like [1] discussed the effect of gradual forgetting of past training data over the course of training, which is related to this paper's finding that benchmark data can be forgotten (e.g. in abstract "Lllama 3 405B, have forgotten the data seen at the beginning of training.").
- this paper can be viewed as an intersection of several parts of the relevant literature: contamination analysis (many references in paper), memorization analysis (e.g. [1]), optimization analysis, data selection (e.g. use stale vs fresh pre-training data [3])
[1] https://arxiv.org/abs/2207.00099
[2] https://arxiv.org/abs/2401.06059
[3] https://arxiv.org/abs/2305.16264
Essential References Not Discussed: N/A to my understanding. Key references are cited and discussed in the paper, although prior work's contributions can be highlighted a bit more.
Other Strengths And Weaknesses: Strength
- the paper is well-written and a pleasure to read!
Weaknesses: see prior sections
Other Comments Or Suggestions: - Section 4: "We being in" --> "We begin in"
Questions For Authors: - Fig 1, 2: when you scale more pre-training data ("Chinchilla Tokens"), are the extra tokens *fresh* tokens, or repetitions of the same set of 1x Chinchilla tokens (e.g. same 20B tokens for an 1B model)? My understanding is fresh tokens, but since Fig 2 (b, c) says "Epochs", I'm not too sure
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for the detailed review of our paper. We are happy to hear that our paper is “a pleasure to read”! Below, we respond to your questions/comments.
*“deduplicating the contamination benchmark data (e.g. HellaSwag) from the pre-training tokens (e.g. FineWeb) is also recommended for a truly unbiased evaluation.”*
While it will not be possible to re-run the experiments with de-duplicated pre-training data, we commit to adding a Supplement Section that reports the overlap between the pre-training data and the benchmark questions that we contaminate with.
Preliminary experiments with a random subset of benchmark questions and a random subset of the pre-training data indicate that the overlap between the benchmark questions and FineWeb-edu is small (as measured by the fuzzy string metric used to de-duplicate the benchmark questions).
*“Key references are cited and discussed in the paper, although prior work's contributions can be highlighted a bit more.”*
Thank you for the additional reference [3]; we will incorporate it. We think that the reviewer's positioning of our contribution in the literature is quite fitting! We will revise the relevant parts of the paper to highlight the contributions of prior work better.
*“Fig 1, 2: when you scale more pre-training data ("Chinchilla Tokens"), are the extra tokens fresh tokens,”*
Yes, they are fresh tokens. We will replace or qualify the usage of the term “epoch,” which can indeed be confusing in our setting.
Thank you again for providing such a high-quality review. We would be happy to answer any additional questions.
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Rebuttal Comment 1.1:
Comment: I appreciate the authors' rebuttal and will keep my score and my assessment that the paper should be accepted. | Summary: The paper investigates the impact of data contamination in LLMs, specifically addressing whether small-scale contamination significantly affects benchmark evaluations. The authors analyze contamination effects along three dimensions: model size, number of training tokens, and repetition of contaminated examples. They find that while contamination can lead to overfitting under certain conditions, large-scale training beyond Chinchilla-optimal regimes can mitigate or even eliminate its impact. Empirical experiments demonstrate that continual pre-training can effectively erase contamination effects, with weight decay playing a key role in forgetting.
Claims And Evidence: The experimental results support the paper’s main conclusions regarding the impact of data contamination and forgetting dynamics in large-scale training. However, the section on weight decay raises some questions, which will be discussed below.
Methods And Evaluation Criteria: The methods and evaluation criteria are reasonable for the problem. The main limitation is the relatively small scale of experiments, though this is understandable given computational constraints.
Theoretical Claims: I checked Proposition 1, and it appears to be correct. No issues were found.
Experimental Designs Or Analyses: The experimental conclusions are sound and align well with expectations. No issues were found.
Supplementary Material: A.1, A.2 and A.5.
Relation To Broader Scientific Literature: The paper provides findings on LLM forgetting through controlled experiments, contributing to the understanding of data contamination and memory dynamics. However, it is unclear how these conclusions translate into actionable insights, which I would like to ask the authors about.
Essential References Not Discussed: The paper does not strongly rely on prior literature, so additional references are not essential.
Other Strengths And Weaknesses: **Strengths:**
1. The paper includes a large number of experiments with well-designed and solid methodologies, leading to conclusions that align with expectations.
2. This paper is well-written.
**Weaknesses:**
1. The practical actionable insights of these empirical findings are unclear.
2. The experiments are limited in scale (model size), though this is understandable given computational constraints.
3. The analysis of weight decay is relatively shallow. While the perspective is interesting, the analysis mainly focuses on gradient decay, ignoring how earlier gradients influence the optimization trajectory. Simply showing that gradients decay to zero may not be sufficient. Additionally, the paper states that weight decay is not necessary for forgetting, making the core insights of Section 5 unclear. Does this section propose a possible explanation? If so, it is presented in a shallow way and is not clearly necessary, raising questions about its contribution.
Another point of confusion is the mention of data attribution. While the paper references it, neither the experimental results nor the theoretical analysis provide any direct connection to data attribution methods. This is not necessarily a weakness, but it raises questions about why data attribution is discussed if it does not play a role in the findings.
Other Comments Or Suggestions: First line of Section 4: "We being" -> "We begin"
Questions For Authors: 1. Your experiments provide insights into LLM forgetting, but it is unclear what **actionable** takeaways arise from these findings. How do you envision these results informing model training or evaluation practices?
2. Section 5 suggests weight decay contributes to forgetting, but the analysis is mainly based on gradient decay without considering how earlier gradients influence the optimization trajectory. Given that the paper also states weight decay is not necessary for forgetting, what is the key insight of this section? Are you proposing weight decay as a primary mechanism, or just one possible factor?
3. The paper references data attribution, but the experiments and theoretical analysis do not directly connect to it. What role does data attribution play in your findings, and how does it relate to the core contributions of the paper?
Overall, I really appreciate the experimental design of this paper. If Questions 1 and 2 are addressed convincingly, I would be happy to increase my score.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for the detailed review of our paper and insightful questions. Below, we give detailed answers to your questions/comments.
*“The main limitation is the relatively small scale of experiments, though this is understandable given computational constraints.”*
Running experiments with a 7B parameter model is the largest we can afford on an academic compute budget. We hope that, inspired by our work, future work will study forgetting and contamination as part of a large-scale training run.
*“Your experiments provide insights into LLM forgetting, but it is unclear what actionable takeaways arise from these findings. How do you envision these results informing model training or evaluation practices?”*
A key insight of our work is that the causal effect of a small number of data points in the LLM pre-training data on final model behavior can be zero. If model training is in this large-data regime, this has several important practical implications:
- Our work questions the common practice of grouping benchmark questions into “clean” and “contaminated” questions based on the maximum found overlap between a question and the training data (for example, n-gram overlap) to reason about benchmark overfitting (Brown et al. 2020, Touvron et al., 2023, Dubey et al., 2024). Specifically, our work shows that the mere existence of an evaluation data point in the LLM pre-training data is not necessarily an indicator of benchmark overfitting. We show that it is necessary to consider other factors, such as the frequency of the contamination.
- Our work highlights the importance of when a contaminated sample is seen. If the samples are seen early during pre-training, overfitting is mitigated due to the forgetting phenomenon. This is directly **actionable**: If we suspect benchmark overfitting during an early pre-training stage on relatively unfiltered internet data, the practitioner can consider continual pre-training (“mid-training”) on clean data to mitigate the overfitting.
- Our work suggests that filtering benchmark questions from the mid-training and post-training data is much more critical than filtering the pre-training data (additional factors like the learning rate schedule come into play). This has immediate and direct implications for the design of training datasets.
We would be happy to further elaborate on these points.
*“Section 5 suggests weight decay contributes to forgetting, but the analysis is mainly based on gradient decay without considering how earlier gradients influence the optimization trajectory. [...] what is the key insight of this section? Are you proposing weight decay as a primary mechanism, or just one possible factor?”*
Let us outline the motivation for Section 5 in the paper and our interpretation of the experimental results.
Given that forgetting is a key empirical property of LLM pre-training, it is natural to ask: Is there a simple factor in the pre-training pipeline that explains the forgetting? Asking this question, it seemed straighforward to consider the weight decay parameter: After all, weight decay is a mechanistic process that gradually removes the influence of earlier gradient updates on the model weights (this is what we formally describe in Proposition 1).
In our experiments, it turned out that the weight decay parameter does indeed influence forgetting in the sense that increasing the weight decay parameter leads to faster forgetting (Figure 4). The experiments also revealed that the empirical rate of forgetting occurs faster than the cumulative weight decay. This makes a lot of sense to us, given how weight decay works mechanistically. At the same time, the experiments also demonstrated that weight decay is not necessary for forgetting (Supplement Figure 8) – though forgetting without weight decay occurs at a slower rate. We don’t see this as a problem for our analysis—it simply means that forgetting is a multifaceted phenomenon not exclusively driven by weight decay.
Section 5.3 suggests that the mechanism of forgetting via weight decay is likely relevant in large-scale LLM pre-training.
To summarize, the key insight in Section 5 is that the weight decay parameter has a causal effect on forgetting that is likely relevant in large-scale LLM pre-training.
*“What role does data attribution play in your findings, and how does it relate to the core contributions of the paper?”*
Our paper's controlled experiments resemble the “leave-one-out” (LOO) procedure in data attribution. Concretely, our experiments directly “leave-out” entire groups of benchmark questions, thus simulating a kind of “group” LOO procedure.
Moreover, our result that the (average) causal effect of inserting individual benchmark questions into the pre-training data can be zero suggests that we might not be able to attribute “importance” to individual data points in the LLM pre-training regime.
We would be happy to answer any additional questions.
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Rebuttal Comment 1.1:
Comment: Thank you for the detailed and thoughtful response. I’d like to follow up on a few points:
**Regarding Q1**: I think the points you raised—such as the effect of contamination frequency—are certainly valid, but also somewhat expected. I’m curious whether your findings offer any implications for the design of **benchmark contamination detection** methods. For instance, could frequency- or position-aware strategies improve beyond simple overlap-based heuristics? I understand this may be future work, but hearing your thoughts would strengthen the **practical** relevance of your conclusions.
As for the role of when a contaminated sample appears in training: while the result aligns with intuition, I understand this is exactly the kind of effect that controlled experiments like yours can rigorously isolate and quantify. I do see value in that.
**Regarding Q2**: I now better understand the intention behind Section 5 and appreciate the mechanistic perspective on weight decay and forgetting. However, as a standalone section, I still feel the analysis is relatively shallow—the theoretical side does not go very deep, and the practical takeaway remains somewhat limited. I wonder if this section could benefit from a clearer articulation of how one might use these findings to **predict or control** forgetting in large-scale training.
To be clear, I am not nitpicking—I genuinely like this paper a lot. The experimental design and metrics are elegant and thoughtfully constructed, and I find the section on weight decay particularly interesting. It’s precisely because the paper covers so much ground that I find myself thinking harder about what the key **practical takeaways** might be. In fact, because the content is quite rich, I would suggest explicitly summarizing your takeaways—perhaps in a dedicated section, even in the appendix—so that readers can more easily understand the implications for practice. I want to emphasize that I recommend acceptance; my comments are offered in the spirit of exploring how to make an already strong paper even more impactful.
One additional limitation, which is perhaps unavoidable for this type of controlled study, is that real-world LLM training involves a wide range of model architectures, scales, and benchmark types (e.g., question formats, domains). While your experiments already cover multiple models and datasets, they inevitably cannot represent the full diversity of practical settings. As a result, findings such as “the causal effect of a single data point can be zero” may not universally hold. I would suggest adding a short discussion of this limitation to clarify the boundaries of the conclusions and avoid overgeneralization.
I have increased my score to a 3. While some aspects could be further clarified or expanded (e.g., practical takeaways and the weight decay analysis), I see these as opportunities for refinement rather than fundamental flaws. I welcome any further discussions.
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Reply to Comment 1.1.1:
Comment: Thank you for the thoughtful comment and for increasing your score.
To us, the most important takeaway from the paper is the negative result: If the scale of the data is large in comparison to the scale of the model, contamination can be completely forgotten.
Now, it is true that this insight does not boil down to a single recommendation of the form “do X” (as in, “add qk-norm to increase training stability”). However, we would argue that it is highly relevant to several practices in pre-training (as outlined in our original rebuttal comment) and also to how we think about LLMs more generally.
One example is contamination detection methods, where our paper primarily provides arguments to be critical of these methods. Consider, for example, the widely used n-gram overlap. In our experiments, if we were to compute the n-gram overlap between the pre-training data and the benchmark questions used for evaluation, we would find a large n-gram overlap for the questions we contaminate with (by construction) and a much smaller overlap for the holdout questions (see our response to Reviewer F1rX). Now, at least in the setting that we study in our paper, the n-gram overlap does not determine overfitting. Instead, what is relevant is the joint scale of model, data, and contamination. By modifying the scale of the model, the data, and the number of repetitions of benchmark questions, we can get any possible result from no overfitting to complete overfitting while the n-gram overlap between the pre-training data and the contaminated benchmark questions is consistently large.
Concerning Section 5, we completely agree with the reviewer that more research is needed on how cumulative weight decay can predict forgetting in large-scale training. We decided to include Section 5 in the paper, even if it is relatively brief, since it provides a valuable backdrop to the experiments in the previous Sections.
Perhaps one final observation: When we write, “We hope that, inspired by our work, future work will study forgetting and contamination as part of a large-scale training run.” we actually think it would be important to do this. Among others, this is because of the point raised by the reviewer, namley it would be desirable to corroborate our results with evidence from “real-world” LLM training.
*“I would suggest explicitly summarizing your takeaways—perhaps in a dedicated section, even in the appendix [...] I would suggest adding a short discussion of this limitation to clarify the boundaries of the conclusions and avoid overgeneralization.”*
This is a great idea. We commit to adding two new sections to the appendix, one to discuss the takeaways and one to discuss the limitations of our work.
Thank you again for the interesting comment! We appreciate that this kind of discussion helps us to clarify the contribution of the paper and and make it more impactful. | Summary: This paper investigates the impact of data contamination in large language models (LLMs), challenging the assumption that minor contamination invalidates benchmark evaluations. Through controlled experiments, the authors study how contamination effects scale with model size (up to 1.6B parameters), training tokens (up to 40B), and example repetitions (up to 144x).
Claims And Evidence: The claims are supported by systematic experiments and theoretical analysis. Evidence includes:
1. Controlled scaling experiments showing monotonic trends in contamination effects.
2. Weight decay analysis linking optimization hyperparameters to forgetting.
3. Validation via OLMo-7B continual training However, extrapolation to larger models (e.g., Llama 3 405B) relies on theoretical weight decay bounds rather than direct empirical validation.
Methods And Evaluation Criteria: Benchmarks (ARC-Easy, HellaSwag, etc.) are filtered for duplicates to isolate contamination effects. Contamination is inserted randomly, mimicking real-world leakage. Evaluation via accuracy gaps between contaminated and holdout data is appropriate. A limitation is the focus on smaller models (≤7B), which may not fully capture dynamics in larger LLMs.
Theoretical Claims: Proposition 1 (cumulative weight decay bounds forgetting) is proven in the appendix. The proof assumes constant learning rates, which may not hold in practice, but the core intuition—weight decay reduces past gradient influence—is valid.
Experimental Designs Or Analyses: Experiments are methodical but limited to smaller models due to computational constraints. The extrapolation to larger models is plausible but unverified empirically. The OLMo-7B experiments add credibility, but testing on >10B parameter models would strengthen conclusions.
Supplementary Material: All good.
Relation To Broader Scientific Literature: None
Essential References Not Discussed: None
Other Strengths And Weaknesses: None
Other Comments Or Suggestions: I recommend that the authors open-source the code and experimental data logging of this work in order to verify reproducibility and increase the transparency of the work.
Questions For Authors: Could paraphrased or semantically similar contamination (vs. exact matches) alter the conclusions, especially for larger models?
For example the "Semantic Level" and "Information Level" contamination in the Xu et al. 2024 (Benchmark data contamination of large language models: A survey)
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for the detailed review of our paper. We are happy to hear that you appreciate our experimental design. Below, we give answers to your questions/comments.
*“The proof assumes constant learning rates”*
To clarify, the proof does not assume constant learning rates (in the proof, the learning rate is denoted $\gamma_i$ and depends on the gradient step). We conjecture that the reviewer observed that $\lambda$ in the proof is constant - this is the weight decay (which is usually constant, but the algebra in the proof does not require this).
*“I recommend that the authors open-source the code and experimental data logging of this work in order to verify reproducibility and increase the transparency of the work.”*
The code is available at https://github.com/icml9771/code (the link is currently in the supplement; we will move it to the first page). We additionally commit to open-source our Weights & Biases logs and model checkpoints.
*“Could paraphrased or semantically similar contamination (vs. exact matches) alter the conclusions, especially for larger models?”*
This is an interesting question. The reviewer is correct in observing that we decided to consider only exact contamination because non-exact contamination might behave qualitatively differently for larger models (see also Supplement A.1. Additional Discussion of Data Contamination Assumptions and Setting). For example, larger models might observe a kind of ``emergence’’ phenomenon where they can suddenly make efficient use of rephrased samples.
That being said, we agree with the provided reference Xu et al. (2024), which states that exact contamination is more severe than other forms of contamination (e.g. the last paragraph on page 4 in Xu et al. (2024)). This means that the results in our paper should provide a heuristic upper bound for what would happen with paraphrased or semantically similar contamination.
Of course, ultimately experimental evidence would be required for other forms of contamination, too.
We would be happy to answer any additional questions.
---
Rebuttal Comment 1.1:
Comment: Thanks for the author's response, which addressed my concerns. | Summary: This paper provides a very important perspective in data contamination of LLM and show that not all data leakage will lead to false evaluation in benchmarks.
Claims And Evidence: Strengths:
1. This paper question the severity mentioned in the previous paper. The assumption or the settings of data contamination might not be practical or not common in LLM.
2. Besides the problem, this paper gives a comprehensive evaluation on the property of forgetting.
3. The paper is well-written and the problem is interesting.
Question:
1. Although the paper point out this problem, people still have the question when would the benchmark be totally safe. And is there any method to improve or gaurantee the fairness of the benchmark?
Methods And Evaluation Criteria: Yes. Their evaluation is more practical than the previous paper.
Theoretical Claims: N/A
Experimental Designs Or Analyses: The experiments are comprehensive.
Supplementary Material: Yes. The Reproducibility section
Relation To Broader Scientific Literature: It questions the reaonability in previous settings of data containation paper.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: See above
Other Comments Or Suggestions: N/A
Questions For Authors: N/A
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for reviewing our paper and for your positive assessment.
It seems that you ask under what conditions we can be confident that a benchmark evaluation is not contaminated. This is an interesting question that lies somewhat beyond the scope of our paper. In our paper, we demonstrate that moderate amounts of exact contamination do not necessarily lead to benchmark overfitting. This implies that minor mistakes in data pre-processing and filtering might not lead to benchmark overfitting. To provide stronger guarantees that a benchmark evaluation is "totally safe", we would require a much deeper understanding of the learning dynamics of LLMs.
We would be happy to answer any additional questions. | null | null | null | null | null | null |
e-GAI: e-value-based Generalized $\alpha$-Investing for Online False Discovery Rate Control | Accept (poster) | Summary: The paper proposed the e-GAI framework which can control the FDR under arbitrary dependence structures by defining a conservative e-value-based FDP estimator and adopting a risk-averse strategy.
Claims And Evidence: yes
Methods And Evaluation Criteria: yes
Theoretical Claims: no
Experimental Designs Or Analyses: 1. In financial bubble detection, ω1 is set to 0.0001 without justification.
2. The paper does not evaluate runtime or memory consumption for ultra-long sequences. I noticed that recursive updates in Eq 8 (where αt depends on all historical Rj ) may lead to linear computational complexity, which might be inefficient in real-world scenarios.
Supplementary Material: no
Relation To Broader Scientific Literature: The paper’s contributions build upon and extend prior work in online false discovery rate control and e-value theory.
Essential References Not Discussed: no
Other Strengths And Weaknesses: Strength: Unlike some traditional methods, the proposed e-GAI framework does not need prior knowledge of dependency patterns, which could be more flexible in real-world scenarios.
Weaknesses: 1. The user is required to set the initial parameters (e.g., ω₁, λ), which may rely on experience or a large number of experiments in practical applications.
2. The long-term performance of the algorithm has not been analyzed. For example, if the dynamic allocation strategy (Eq 9) consume too much α-wealth with high rejection rates in the early stages, will the late test sacrifice overall efficacy due to lack of budget, and does it have cumulative errors, etc.?
Other Comments Or Suggestions: Please see above comments.
Questions For Authors: Q1. The covariance matrix assumes equal correlation coefficients (ρ) across all time points, what if there are some time-varying correlations (e.g., increasing ρ) or nonlinear dependencies?
Q2: How to consider the long-term performance of the algorithm?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your helpful comments and suggestions. We would like to part-wisely respond to your comments.
> In financial bubble detection, ω1 is set to 0.0001 without justification.
This application can be seen as a long-term time series (i.e., $T=10000$). As response to your W1&W2, we suggest choosing $\omega_1$ as $1/T$ approximately to avoid spending too much wealth in the early stages and resulting in $\alpha$-death.
> The paper does not evaluate runtime or memory consumption...
We would like to make the following clarification.
+ The update of $\omega_t$ and $\alpha_t$ can be expressed in a recursive form, so computation is highly efficient and memory-friendly. Specifically, updating $\omega_t$ is shown in (9) (line 195). To compute $\alpha_{t}$ for e-LORD (lines 165-177), we define remaining wealth $r_t^{\text{e-LORD}}=\alpha-\sum_{j=1}^{t}\frac{\alpha_j}{R_{j-1}+1}$ and update $\alpha_t=\omega_t r_t^{\operatorname{e-LORD}}(R_{t-1}+1)$. Similar recursive $\alpha_t$ for e-SAFFRON can be obtained.
+ We also evaluated runtimes of various algorithms in Table 2 below. It shows that e-LORD and e-SAFFRON are computationally fast. We will add the recursive update form and present results in final version.
> W1: The user is required to set the initial parameters (e.g., ω₁, λ)...
Thank you for your insightful comments! We would provide some suggestions about $\omega_1$ and $\lambda$.
+ In general, a larger $\omega_1$ means more wealth will be assigned to each hypothesis testing, making it easier to discover alternatives, and meanwhile, it will be more possible to exhaust entile wealth at an early stage. Hence, we recommend a relatively small $\omega_1$ for a long period, e.g., $\omega_1\approx 1/T$ empirically.
+ $\lambda$ affects initial wealth and the proportion of hypotheses counted into FDP's estimator. We recommend $\lambda=0.1$ to preserve wealth as discussed in _Remark 3.5_.
+ We have simulation results with different ($\omega_1$,$\lambda$) in Appendix C.1. Additional results of powers of e-LORD and e-SAFFRON ($\lambda>0$) under an $\operatorname{AR}(1)$ model are shown in Table 1 below. All FDRs are controlled and omitted due to the space limit. We can see the choices of ($\omega_1,\lambda$) do not affect results too much. So, it enables users to integrate domain knowledge in real applications.
Table 1: Power (%) with different ($\omega_1,\lambda$) and $\alpha=5$%.
| | e-LORD | $\lambda=0.1$ | $\lambda=0.2$ | $\lambda=0.3$ | $\lambda=0.4$ | $\lambda=0.5$ |
| --- | --- | --- | --- | --- | --- | --- |
| $\omega_1=0.001$ | 69.92 | 70.53 | 69.36 | 68.04 | 66.46 | 64.56 |
| $\omega_1=0.005$ | 67.16 | 75.03 | 74.19 | 72.99 | 71.53 | 69.79 |
| $\omega_1=0.01$ | 49.41 | 66.47 | 65.69 | 64.54 | 63.19 | 61.48 |
> W2: Long-term performance of algorithm has not been analyzed. ...
As noted, excessive early-stage wealth consumption leads to "$\alpha$-death", halting rejections once $\alpha$-wealth is zero. It is a common phenomenon within GAI framework. So, we recommend using a small $\omega_1$ to preserve wealth as response to your W1.
This issue warrants further research, such as considering "activation" after reaching a certain condition or exploring scenarios where online sequence inherently exhibits block structure, among other possibilities. In addition, this work focuses on measuring the cumulative error by FDR. Exploring other metrics is also a valuable future direction.
> Q1: ...what if there are some time-varying correlations...
We design a new time-varying $\text{AR}(1)$ model: $X_t=\rho_t X_{t-1}+\epsilon_t$ for $H_0$ and $X_t=4+\rho_t X_{t-1}+\epsilon_t$ for $H_1$ with $\rho_t=\frac{2}{1+\operatorname{exp}(-0.01(t-T/2))}-1$. The table below shows that e-LORD and e-SAFFRON control FDR while leading to relatively high power.
Table 2: FDR, power, and runtime with $\alpha=1$%. SupLORD is referenced by **Reviewer k3m9**.
| | e-LORD | e-SAFFRON | e-LOND | LORD | SAFFRON | SupLORD |
| --- | --- | --- | --- | --- | --- | --- |
| FDR (%) | 0.01 | 0.03 | 0.00 | 0.15 | 1.07 | 0.00 |
| Power (%) | 54.29 | 58.03 | 15.42 | 78.05 | 91.06 | 10.22 |
| Runtime ($\times 10^{-4}$s) | 11.7 | 17.8 | 17.0 | 11.0 | 5.0 | 77.6 |
> Q2: How to consider long-term performance?
Here we focus on controlling online FDR, a common criterion in online multiple testing. To alleviate "$\alpha$-death" over a long period (potentially infinite), Ramdas et al. (2017) discussed controlling decaying memory FDR under independence. But, how to control it under dependence remains challenging due to additional complexity introduced by these dependencies. As response to your W1, another potential way is to consider other strategies or specific structures. We will include a careful discussion of long-term issues in a future revision per your suggestions. Thank you!
---
Rebuttal Comment 1.1:
Comment: Thanks for the detailed responses and your new simulation results and clarifications.
1. While the authors recommend setting $ω_1 \approx 1/T$, I could not find any theoretical justification for this choice in the paper. If such justification exists, I would appreciate it if the authors could point it out. From my perspective, the proposed update strategy appears to be heuristic. Moreover, It seems no analysis is provided regarding how the choice of $ω_1$ interacts with $T$, nor are there experimental results across varying T to assess robustness.
2. Regarding Q2 (long-term performance and $\alpha$-death), the authors acknowledge the issue but do not provide any experimental evidence/figures (e.g., α-wealth over time), or even suggested strategies/analysis to address the problem. While referencing Ramdas et al. (2017) for the independence case is useful background, the paper’s setting includes general dependence, where the issue remains unaddressed. I look forward to seeing this discussion later.
---
Reply to Comment 1.1.1:
Comment: Thank you for your helpful suggestions! We would like to part-wisely respond to your comments.
> Q1: choices of $\omega_1$...
+ In e-GAI, we update $\omega_t$ from a **risk aversion** perspective in (9), _dynamically_ allocating the testing levels and enabling _data-driven_ updates to achieve higher power; see lines 188-193 of right column. In contrast, $\alpha_t$ in e-LOND is derived from a _pre-specified_ decay sequence that sums to 1.
+ A simplified version is to set $\omega_t=\omega_1$ for all $t$, and a natural choice is $\omega_1=1/T$, motivating the choice of initial value for our dynamic updates.
+ Empirical results support this analysis. Table 1 shows power for different $\omega_1$ across $T$ under the same AR(1) model in previous response. It shows that e-GAI with $\omega_1=1/T$ achieves the highest power, latest last rejection, and largest tail testing level, supporting long-term testing. Moreover, its updates are data-driven: remaining wealth remains robust as $T$ varies. In contrast, $\alpha_T$ of e-LOND diminishes as $T$ increases. Table 2 shows discoveries in real data example in Section 5.2. From Table 2, we observe that allocating an excessively small or large initial wealth results in few rejections.
Table 1: Results under AR(1) model with $\alpha=0.05$.
||Method|$\omega_1$|Power (%)|Time of the last rejection|$\alpha_T/\alpha(\times 10^{-4})$|
|-|-|-|-|-|-|
|$T=500$|e-LORD|$1/T$|70.0|498|1031.0|
|||$1/\sqrt{T}$|22.2|275|0.0|
|||$1/T^2$|8.6|483|0.7|
||e-SAFFRON|$1/T$|70.5|498|1368.1|
|||$1/\sqrt{T}$|38.7|441|0.0|
|||$1/T^2$|8.0|483|0.6|
||e-LOND|-|30.9|491|2.5|
|$T=1000$|e-LORD|$1/T$|70.1|998|1029.0|
|||$1/\sqrt{T}$|16.2|406|0.0|
|||$1/T^2$|4.5|962|0.2|
||e-SAFFRON|$1/T$|70.9|998|1366.7|
|||$1/\sqrt{T}$|28.0|706|0.0|
|||$1/T^2$|4.2|958|0.2|
||e-LOND|-|23.9|983|1.0|
Table 2: Number of discoveries with different $\omega_1 (T=8320)$.
|$\omega_1$|e-LORD|e-SAFFRON|e-LOND|
|-|-|-|-|
|$10^{-4}(O(1/T))$|47|46|33|
|$10^{-8}(O(1/T^2))$|33|33||
|$10^{-2}(O(1/\sqrt{T}))$|3|3||
> Q2: long-term performance...
+ The e-LORD and e-SAFFRON algorithms dynamically adjust the ratio to allocate _remaining_ wealth (of a fixed budget $\alpha$), thus theoretically leading to the $\alpha$-death when the sequence is infinite. We added experiments to investigate the long-term performance of e-GAI algorithms; see Table 1 in the above response for more settings. Table 3 shows e-GAI outperforms e-LOND in wealth retention and sustained rejections. $\alpha$-death occurs slowly (not yet observed), likely benefitting from data-driven $\omega_t$ update.
Table 3: Results under AR(1) model with $\alpha=0.05$ and $\omega_1=1/T$.
||Method|Power (%)|Time of the last rejection|$\alpha_T/\alpha(\times 10^{-4})$|
|-|-|-|-|-|
|$T=10000$|e-LORD|69.5|9998|1021.1|
||e-SAFFRON|70.1|9998|1344.6|
||e-LOND|7.4|9898|0.0|
+ To alleviate $\alpha$-death over a long period, Ramdas et al. (2017) defined decaying memory FDR (mem-FDR) by introducing a user-defined discount factor $d\in (0,1] $ and proposed mem-LORD++ that controls mem-FDR instead under independence.
+ To address the issue, we design **mem-e-GAI** to control mem-FDR in our setting as follows. The technique used here is similar to e-GAI framework in the main text. Denote the denominator of mem-FDP as $R_t^m$ for simplicity. A natural choice that is $(j-1)$-measurable for _predicting_ $R_t^m$ is $d^{t-j}[dR_{j-1}^m+1]$. It holds $d^{t-j}[dR_{j-1}^m+1]\leq (R_t^m\vee1)$ for each $\delta_j=1$. Therefore, we propose an **oracle estimate of mem-FDP** as $\sum_{j\in H_0(t)}\frac{\alpha_j}{dR_{j-1}^m+1}$ and design mem-e-LORD by overestimators $\sum_{j=1}^t\frac{\alpha_j}{dR_{j-1}^m+1}$. Thus the testing levels of mem-e-LORD are $\alpha_t=\omega_t(\alpha-\sum_{j=1}^t\frac{\alpha_j}{dR_{j-1}^m+1})(dR_{j-1}^m+1)$ with updating $\omega_t$ in (9) in the main text. Similar results for mem-e-SAFFRON can be obtained, and we omit them due to space limitation. Using the same proof technique as in Appendix A, it can be shown that **both mem-e-LORD and mem-e-SAFFRON achieve mem-FDR control**.
+ Table 4 presents the revelant results under AR(1) model. **All mem-FDRs are controlled** and omitted due to the space limit. The mem-Power is the decaying memory power in (Ramdas et al., 2017). From Table 4, mem-e-GAI performs well over long-time testing periods, especially with sparse alternatives, outperforming mem-LORD++ in mem-Power.
Table 4: Results under AR(1) model with $\alpha=0.05,d=0.99$, and $\omega_1=1/T$.
||Proportion of alternatives $\pi_1$|Method|mem-Power (%)|Time of the last rejection| $\alpha_T/\alpha(\times 10^{-4})$|
|-|-|-|-|-|-|
|$T=10000$|0.01|mem-e-LORD|10.3|8939|0.4|
|||mem-e-SAFFRON|10.3|8939|0.3|
|||mem-LORD++|0.0|1171|0.0|
||0.05|mem-e-LORD|11.0|9787|0.6|
|||mem-e-SAFFRON|10.6|9782|0.5|
|||mem-LORD++|56.0|9650|55.7|
We greatly appreciate your comments, which have significantly improved our paper, and we will incorporate them into the revision. | Summary: The paper proposes a framework for online multiple testing with false discovery rate (FDR) control that utilizes e-values with generalized alpha-investing methods to improve power for e-values that satisfy conditional validity. This paper then establishes connections between these methods and existing generalized alpha-investing methods based on p-values, and provide numerical simulations and real data experiments demonstrating the performance of their new methods.
Claims And Evidence: > "The proposed e-GAI can ensure provable online FDR control under arbitrary dependence while improving the power by dynamically allocating the testing levels." (in abstract)
This claim (and variants) are the central thrust of the paper and repeated throughout, though it is incorrect. All FDR controlling results require condition (2), which enforce that the e-values are conditionally valid on past rejection decisions. This is a special case of the conditional superuniformity assumption for p-values that has been repeated throughout the existing literature, and indeed the authors themselves acknowledge it in Appendix B. Prior literature in both online and offline multiple testing have consistently referred to the term "arbitrary dependence" as allowing any kind of dependence structure among p-values/e-values (test statistics) for each hypothesis. Notably, positive dependence among all test statistics (e.g., jointly Gaussian with only positive correlations) *do not* satisfy conditional validity, but fall under the umbrella of arbitrary dependence. The inaccuracy of this claim becomes relevant in the setup choice in numerical simulations (see later point in "Experimental Design and Analyses")
> Theorem 4.1 + "applying LORD++ to $\\{1/e_t\\}$ is equivalent to applying e-LORD to $\\{e_t\\}$" in Appendix B.
I don't believe LORD++ and e-LORD have any equivalence (nor SAFFRON and e-SAFFRON). The $FDP_e^*(t)$ estimator introduced in this paper is much more conservative than the typical $\widehat{FDP}^{\text{LORD}}(t)$ from prior work, since the denominator is smaller in the former. This smaller denominator is a key part of the proof. This discrepancy is noted in the intro by the authors, so it seems that the intro and Appendix B are incoherent. Further, in Theorem 4.1 they require $\mathbb{E}[FDP_e^*(t)] = \mathbb{E}[\sum_{j = 1}^t \alpha_j / (R_t \vee 1)]$, which also is incorrect, since $\mathbb{E}[FDP_e^*(t)]$ is conservative (though this seems like a typo).
Methods And Evaluation Criteria: The methods and evaluation criteria (FDR + power) make sense.
Theoretical Claims: The errors with the theoretical claims are discussed in the prior section.
Experimental Designs Or Analyses: - As referred to before, the design of the numerical simulation is unclear --- is the covariance positive for all alternatives or all hypotheses? If it is for all hypotheses (as suggested by "The $\Sigma > 0$ is with all diagonal elements being 1 and off-diagonal elements being \rho$"), then the data simulation is does not provide e-values that satisfy condition (2) that is necessary for all proofs of FDR validity for all methods presented in the paper. This setting is then a bit odd for a paper which focuses on methods with provable control of the FDR. Could the authors confirm whether the covariance is positive for just the alternatives (and independent for the nulls) or across all hypotheses?
- The real data experiments are lacking critical details --- in particular, what are the assumptions on the data generating process under the null in each setting, and how are the e-values/p-values explicitly constructed? This is particularly relevant for Section 5.3 since the choice of p-value and e-value seem to be quite different, and it's unclear whether the gap can be explained by that difference.
Supplementary Material: I reviewed all of the supplementary material.
Relation To Broader Scientific Literature: Although the presentation of the paper has somewhat obfuscated what the contributions are, I believe there is an interesting contribution here where the authors have designed a new FDP estimator that allows for online multiple testing with FDR control under conditional validity, at the cost of some power compared to when independence is assumed. This then allows them to use generalized alpha-investing to design procedures valid in that specific setting.
Essential References Not Discussed: - Aaron Fisher. Online false discovery rate control for LORD++ and SAFFRON under positive, local dependence. *The Biometrical Journal*, 2024.
This paper shows that LORD++ and SAFFRON have valid FDR control under conditional superuniformity (a more general condition that is implied by the conditional validity in the paper), and an additional positive dependence assumption on the test statistics. This should at least be cited in the context of existing work with FDR control under conditional superuniformity.
- Ziyu Xu and Aaditya Ramdas. Dynamic Algorithms for Online Multiple Testing. *Mathematical and Scientific Machine Learning*, 2022.
The SupLORD algorithm in this paper (to my knowledge) is the only algorithm that has valid FDR control under (just) conditional superuniformity (apart from algorithms valid under arbitrary dependence) and should be compared to in experiments.
Other Strengths And Weaknesses: The real data experiments in this paper are seem quite comprehensive, and the authors did a great job presenting visualizations for the analysis.
Other Comments Or Suggestions: Looking at the proof in Appendix A.1, is there anything in particular that is specific to e-values? It seems like it would hold for p-values that satisfy conditional superuniformity --- that would be a solid result if it were the case.
Questions For Authors: No questions/concerns outside ones stated. The paper generally seems unclear about what its actual contributions are, and missing comparisons to key prior work/comparisons.
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: We appreciate your careful reading and constructive suggestions. Per your comments, we would like to clarify key **contributions** of our work as follows:
1. We **propose the e-GAI framework** for online testing with using e-values, which **achieves FDR control under arbitrary dependence among valid e-values** (i.e., satisfying condition (2)).
2. We designed **a new e-value-based FDP estimator** and **provided theoretical guarantees for online FDR control** building on it under the relevant conditions.
3. Within the e-GAI framework, we **developed a new updating approach for allocating testing levels from a risk aversion perspective,** aiming to save budget while achieving high power. Along this line, we proposed two new algorithms (**e-LORD and e-SAFFRON**) for implementation.
Thanks for your comments on our paper. We would like to part-wisely respond to your comments.
> This claim (and variants) are central thrust of the paper and repeated throughout...
We sincerely apologize for any confusion. As you have pointed out, by "arbitrary dependence", we mean allowing any dependence structure among test statistics for each hypothesis, i.e., online conditionally valid p-values/e-values. In the revision, we will refine descriptions to minimize confusion. Further details on the experimental design will be clarified in the following. Thank you!
> I don't believe LORD++ and e-LORD have any equivalence (nor SAFFRON and e-SAFFRON). ...
Thank you for your insightful comments. We agree with you that e-GAI is a different framework from GAI. The "equivalence" in Section 4 was to explore the connection between LORD++ and e-LORD when _independent_ p-values are available. In such cases, we can design testing algorithms using a less conservative FDP estimator, i.e., $\sum_{j = 1}^t \alpha_j / (R_t \vee 1)$ such as the one in Theorem 4.1, which will coincide LORD++ and e-LORD. Previously, for notational simplicity, Theorem 4.1 did not explicitly highlight the change in the FDP estimator. The final version will revise the discussion in Section 4 for clarity and precision. Hope these interpretations can ease your doubts!
> As referred to before, the design of the numerical simulation is unclear. ...
Thank you for pointing this out! We apologize for the unclear setup description. The covariance matrix assumes positive correlations between all elements, including nulls and alternatives. In simulations, we assessed our methods using oracle p-values/e-values, calculated from the known conditional distributions derived from the normal distribution. Furthermore, we conducted additional experiments by designing other dependence structures, and these results will be added into the future revision. For details, please see our response to **Reviewer kFoC**'s Q1 due to the space limitation.
> The real data experiments are lacking critical details. ...
We appreciate your feedback and offer the following clarification. In Section 5.2, the data is assumed to be independent and normally distributed under $H_0$ as discussed in (Ahmad et al., 2017), using p-values derived from the normal distribution. We employed KDE to estimate $f_t(x)$ and $f_0(x)$, taking their ratio as the e-value. Due to the independence assumption, these e-values are valid.
In Section 5.3, following [1] modeling framework for financial bubbles, we characterized the problem as a right-tailed unit root test in an $\text{AR}(1)$ model. We built valid e-values on normalized likelihood ratios by dividing its conditional expectation under $H_0$. Both this likelihood ratio and p-values are proposed by Dickey & Fuller's series works. We will clarify these details in the future revision.
> Two References Not Discussed
Thank you for your recommendation! We have introduced and cited Fisher (2024) in Section 2.2 (lines 126-129 of right column) in the main text. Additionally, we include a comparison with the SupLORD algorithm (Xu & Ramdas, 2022) in Table 2 of our response to **Reviewer kFoC**'s Q1 due to space constraints. In the new setting, SupLORD controls FDR but has low power, whereas our methods achieve FDR control with higher power. In future revisions, we will incorporate Xu & Ramdas (2022) and add comparative experiments.
> Looking at the proof in Appendix A.1, is there anything in particular that is specific to e-values? ...
The proof in Appendix A.1 does indeed rely on a unique property of e-values: the larger the e-value, the more significant the evidence against the null. Note that $\delta_t=\mathbb{I}[e_t\geq 1/\alpha_t]\leq e_t\alpha_t$ deterministicly in the numerator of inequality (ii) of the proof. This, however, does _not hold_ for p-values. Hence, e-GAI cannot theoretically guarantee FDR control when directly applied to p-values satisfying condition (1).
Ref:
[1] Phillips, P. C., & Yu, J. Dating the timeline of financial bubbles during the subprime crisis. Quantitative Economics, 2(3), 455-491, 2011.
---
Rebuttal Comment 1.1:
Comment: > We propose the e-GAI framework for online testing with using e-values, which achieves FDR control under arbitrary dependence among valid e-values (i.e., satisfying condition (2)).
I'd like to re-iterate that *arbitrary dependence* is explicitly used to describe unknown dependence, and condition (2) has been explicitly characterized as *conditional superuniformity*. Conditional superuniformity is a well-studied notion in online multiple testing --- indeed this condition already appears in the origins of the problem in the foundational papers of Foster and Stine (2007) and Saharoni and Rosset (2014). Both papers showed that alpha-investing and GAI provide valid online marginal FDR control at stopping times (a stronger guarantee for the marginal variant of FDR). A characterization that is more accurate may be to say that a known dependence/distribution structure implies conditional superuniformity (vs. online multiple testing methods that control FDR even when the FDR is unknown). This is not simply a semantic difference --- even when the dependence is known, the online multiple testing methods that have validity under unknown arbitrary dependence (reshaped LOND of Zrnic et al. (2021) and e-LOND) also control FDR at stopping times (and not just fixed times) [1].
I apologize if the above comment was redundant wrt my original review, but I think method comparison in Table 1 somewhat omits key details about the state of existing work, and consequently the description of condition (2) as "arbitrary dependence" muddies the water wrt the precise contribution made by this work.
> This, however, does not hold for p-values.
I don't think that part of the proof is critical --- you can accomplish the same thing w/ conditionally superuniform p-values
$$\mathbb{E}[\mathbf{1}\\{p_j \leq \alpha_j\\}/ (R_{j - 1} + 1)] = \mathbb{E}[\mathbb{E}[\mathbf{1}\\{p_j \leq \alpha_j\\} \mid \mathcal{F}\_{j - 1}] / (R_{j - 1} + 1)]\leq \mathbb{E}[\alpha_j / (R_{j - 1} + 1]$$
where the 2nd step + last step is by conditional superuniformity of $p_j$ and the fact that $\alpha_j, R_{j - 1}$ are measurable wrt $\mathcal{F}_{j - 1}$.
[1] Lasse Fischer and Aaditya Ramdas. An online generalization of the e-BH procedure. arXiv:2407.20683, 2024.
---
Reply to Comment 1.1.1:
Comment: Thank you for your helpful comments and suggestions. We would like to part-wisely respond to your comments.
> Q1: I'd like to re-iterate that arbitrary dependence is explicitly used to describe unknown dependence, and condition (2) has been explicitly characterized as conditional superuniformity. ...
Thanks for your comments. We sincerely apologize for the confusion caused by the ambiguous expression here. In the revised version, we will modify the description to accurately state that our e-GAI algorithm achieves FDR control under conditional superuniformity, revise the comparison of algorithms in Table 1 in the main text, and supplement the relevant and necessary references mentioned in your comment.
> Q2: I don't think that part of the proof is critical. ...
We sincerely apologize for overlooking this property and greatly appreciate your insightful observation. The existence of this property will enrich and elevate the contributions and applicability of our methodology framework, making the theory more comprehensive and complete. We would like to add a discussion of this part in the revised version. Thank you very much for your suggestion! | Summary: This paper proposes a framework for generalized $\alpha$-investing (GAI) with e-values, an approach for online multiple hypothesis testing. While prior work had considered GAI with p-values, this paper contributes two things: First (Section 3.1) they derive bounds on the false discovery proportion (FDP) for the setting of arbitrarily dependent e-values, and second (Section 3.2) they design a schedule for "spending" alpha that depends on previous costs. While the theory speaks to the false positive rate control, experiments on simulated and real-world data demonstrate that the proposed schedule yields greater power than existing approaches. There are several baselines considered: SAFFRON and LORD++ are both based on an assumption of independent p-values (or p-values satisfying the PRDS condition), and so do not have guarantees in the setting of arbitrary dependence, while e-LOND does allow for arbitrary dependence, but uses a spending schedule that does not incorporate prior costs, and empirically has lower power as a result.
**Post rebuttal update**: See my comments in the chain below.
> After reading the response and the other reviews, I will maintain my score, though I have somewhat lower confidence in my assessment after reading the review of k3m9. Nonetheless, I'm still in favor of the paper being accepted, assuming that these clarifications (and those made to other reviewers) are incorporated.
Claims And Evidence: Yes, the claims are supported by clear and convincing evidence.
Methods And Evaluation Criteria: Yes, the evaluation criteria make sense to me. The theoretical claims demonstrate control over the FDR, and experiments are used to assess power in real-world situations, both of which I would expect to see in a paper like this one.
Theoretical Claims: I checked the proofs in Appendix A for the main results, which appear correct to me.
Experimental Designs Or Analyses: Yes, I found both the synthetic (Section 5.1) and the real-data experiments (Sections 5.2, 5.3) to be sound and valid. Both experiments demonstrate control of the real (in 5.1) and estimated (in 5.2,5.3) false discovery rates based on known anomalies. I found both real-world experiments easy to follow and compelling.
Supplementary Material: I reviewed the proofs in Appendix A, but did not review in detail Appendix B (which describes relationships to other approaches in more detail) or Appendix C (which describes additional simulation results)
Relation To Broader Scientific Literature: The key contributions appear a little incremental to me, but are summarized well in introduction (Table 1 and "Related Works"). Both prior approaches to GAI with p-values do not allow for arbitrary dependence between p-values, and the existing approach with e-values (e-LOND) does not consider scheduling based on prior costs, and empirically (as shown in experiments) has lower power as a result.
Essential References Not Discussed: I did not notice any essential references not discussed, though I am less familiar with this literature, so I may be missing something.
Other Strengths And Weaknesses: First, the empirical argument would have been stronger in Section 5.1 with a simulated scenario that caused LORD++ to exceed the desired FDR bounds.
Second, these are all very minor, but my main critiques of this paper would be related to clarity of presentation, with a few examples where more context would have been helpful:
* Section 2.2, it is stated that the "key idea in GAI...is that each rejection gains some extra $\alpha$-wealth", shouldn't this be the opposite, that accepting the null gains wealth, and rejections spend it?
* I get the math, but had trouble following the conceptual explanation below Theorem 3.1, that $R_{j-1} + 1$ "predicts" the number of possible future rejections, since it obviously under-predicts the total number of rejections. As I understand it, the key is to observe that the "right" denominator is something like $R_t \lor 1$, and that by under-predicting this quantity, we get an upper bound (since we're in the denominator). A little more explanation would have been helpful here.
* The PRDS condition is mentioned in several places in the introduction / Section 2 (see page 1, "p-values with...positive regression dependence on a subset") but is not formally defined, might have been nice to at least include in the appendix for completeness.
Other Comments Or Suggestions: It may be worth taking an editing pass for grammar, e.g., Line 092, left-hand column "though this operation only achieves a smaller improvement in power while introduces additional" sounds off, should perhaps be something like "though this operation only achieves...while **introducing** additional" or "though this operation only achieves a smaller improvement in power, **and introduces** additional"
Questions For Authors: There is one area where I wasn't as clear on the contribution: Could the authors clarify how their results in Theorem 3.1 differ from those in the e-LOND paper? I didn't see this exact result anywhere in that paper on a very brief skim, but I imagine they need to have used some similar result to also achieve FDR control with arbitrary dependence?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thanks for your comments on our paper. We would like to part-wisely respond to your comments.
> First, the empirical argument would have been stronger in Section 5.1 with a simulated scenario that caused LORD++ to exceed the desired FDR bounds.
Thank you for your valuable suggestion! We have to acknowledge that we explored various simulation settings and did not get the results that LORD++ exceeds the target FDR level for now. This is mainly because the LORD++ algorithm itself is inherently conservative. However, we found that LORD++ does not perform well with $\widehat{\text{FDP}}=0.189$ in the real data analysis in Section 5.2. As we know, LORD++ lacks reliable theoretical guarantees with the dependence of p-values, which may compromise its safety and reliability in practical applications.
> Section 2.2, it is stated that the "key idea in GAI...is that each rejection gains some extra $\alpha$-wealth", shouldn't this be the opposite, that accepting the null gains wealth, and rejections spend it?
We would like to make the following clarifications.
+ The GAI algorithm is designed from an investment perspective: each hypothesis test is treated as an investment, where the significance level $\alpha_t$ is drawn from a wealth pool $W_t$. Thus, each test consumes a certain amount of "wealth", and if the test results in a rejection, it is considered a successful investment, thereby gaining additional "wealth" and increasing the cumulative wealth.
+ In contrast, our e-GAI framework adopts a different design philosophy: e-GAI views the entire testing process as a risky investment and the whole wealth does not increase; instead, each test consumes a fixed proportion of the remaining wealth (e.g., $\omega_t$ in e-LORD). Therefore, each rejection introduces risk, and from a risk-averse perspective, it is necessary to reduce the investment proportion in subsequent tests to ensure long-term sustainability.
+ The difference in design philosophy between e-GAI and GAI stems from the distinct estimators used for the FDP. For the GAI method, which allows for wealth accumulation, increased investment is advantageous. In contrast, for the e-GAI method, where total wealth cannot increase, each investment inherently entails risk.
> I get the math, but had trouble following the conceptual explanation below Theorem 3.1, ... A little more explanation would have been helpful here.
Thank you for your suggestion! As you noted, the key role of $R_{j-1}+1$ here is that it serves as a $(j-1)$-measurable lower bound for $R_t\vee1$. Since $R_{j-1}+1\leq R_t\vee 1$ and it is placed in the denominator, it results in an overestimation of the oracle FDP. As the true $R_t\vee1$ is _unobservable_ at time $j-1$, we use $R_{j-1}+1$ as a substitute, effectively "_predicting_" the value at time $t$ from the perspective of time $j-1$. This is why we used the verb "predict" in this context. Per your comment, we will provide a more detailed explanation in the final version to make this point clear.
> The PRDS condition is mentioned in several places in the introduction / Section 2 (see page 1, "p-values with...positive regression dependence on a subset") but is not formally defined, might have been nice to at least include in the appendix for completeness.
We appreciate your attention to detail and your valuable feedback. We will include a formal definition of PRDS and relevant references in the appendix of the final version.
> It may be worth taking an editing pass for grammar, e.g., Line 092, left-hand column ...
Thank you for pointing this out! We will carefully review the grammar throughout the paper and make the necessary corrections, including the sentence you highlighted.
> Could the authors clarify how their results in Theorem 3.1 differ from those in the e-LOND paper? I didn't see this exact result anywhere in that paper on a very brief skim, but I imagine they need to have used some similar result to also achieve FDR control with arbitrary dependence?
Theorem 3.1 introduces an estimator for the FDP and proves that FDR control can be achieved when the expectation of this estimator does not exceed $\alpha$. Based on this key estimator, we subsequently propose algorithms for designing testing levels (e-LORD and e-SAFFRON). In contrast, the e-LOND algorithm follows a different approach. Specifically, e-LOND does not introduce an FDP estimator; instead, inspired by the LOND algorithm [1], it defines the testing levels $\alpha_t$ by directly leveraging a decay sequence that sums to 1 and the number of rejections. This approach allows for the cancellation of a common term in the numerator and denominator of the FDP, thereby achieving FDR control.
Ref:
[1] Zrnic, T., Ramdas, A., and Jordan, M. I. Asynchronous online testing of multiple hypotheses. Journal of Machine Learning Research, 22(33), 1-39, 2021.
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Rebuttal Comment 1.1:
Comment: Thank you for these clarifications. After reading the response and the other reviews, I will maintain my score, though I have somewhat lower confidence in my assessment after reading the review of k3m9. Nonetheless, I'm still in favor of the paper being accepted, assuming that these clarifications (and those made to other reviewers) are incorporated.
---
Reply to Comment 1.1.1:
Comment: We sincerely appreciate your helpful comments and continued support for our work. Addressing your thoughtful concerns has helped us improve the presentation of our paper. We will incorporate all clarifications, including responses to all reviewers, into the revised version of the paper to enhance its clarity and quality. Thank you again for your valuable suggestions and your participation in reviewing our work! | Summary: The paper extends the generalized $\alpha$-investing (GAI) framework for online testing by allowing it to be based on e-values as well (hence the name e-GAI). This allows for online false discovery rate control under arbitrary dependencies of the hypotheses and can lead to improved power under good dynamic allocation of the test levels. More concretely, they do this by defining an oracle estimate of the false discovery proportion at each time that is based on e-values. Then, they employ existing methods of bounding it from the literature, leading to the corresponding methods e-LORD and e-SAFFRON. They supplement their proposal by numerical experiments (including a simulation, taxi anomaly detection, and financial bubble detection).
Claims And Evidence: Yes.
Methods And Evaluation Criteria: Yes.
Theoretical Claims: I skimmed through the proofs and they appear correct.
Experimental Designs Or Analyses: I found the experimental analyses to be thorough and well-done. I appreciated the inclusion of different types of data (simulated and real). One small note is that maybe Figure 2 could benefit from some improvements in its display as currently the squares and dots are quite small and subtle (the latter could be fixed by different coloring I think).
Supplementary Material: I skimmed the proofs in Appendix A.
Relation To Broader Scientific Literature: This paper is connected to the broader scientific literatures of sequential hypothesis testing via betting and, especially, the line of work in online testing with FDR control. The authors do a good job of discussing and comparing to prior methods.
Essential References Not Discussed: Not to my knowledge.
Other Strengths And Weaknesses: Beyond the explicit contributions, an additional strength is that the proposed framework unifies multiple existing approaches. A potential weakness is that the paper doesn't go into too much depth on devising new methods, and mainly instantiates LORD and SAFFRON in their own framework.
Other Comments Or Suggestions: One general small personal suggestion would be to not center the A/B testing for tech companies applications so much in the abstract and introduction, and instead showcase more exciting (possibly for social good) applications.
Typos:
- add “The” before “e-LOND” in line 19, left column
- add “the" before “GAI” in line 70 right column
- “guarantee” should be “guarantees” in line 417 right hand side
Questions For Authors: N/A
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thanks for your comments on our paper. We would like to part-wisely respond to your comments.
> One small note is that maybe Figure 2 could benefit from some improvements in its display as currently the squares and dots are quite small and subtle (the latter could be fixed by different coloring I think).
Thank you for your advice! We have improved Figure 2 by increasing the size of the squares and dots and adjusting the coloring for better contrast. These changes will present in the future revision.
> A potential weakness is that the paper doesn't go into too much depth on devising new methods, and mainly instantiates LORD and SAFFRON in their own framework.
Thank you for your comments! Our work aims to address the challenge of online FDR control under arbitrary dependence. To overcome the limitations of p-values in this context, we propose a novel framework leveraging e-values for hypothesis testing, along with two concrete and implementable algorithms, i.e., e-LORD and e-SAFFRON. Furthermore, under the independence assumption, we establish connections between our framework and existing methods, such as LORD++ and SAFFRON from the GAI framework. We have named our approach _e-GAI_, which reflects the key method is to build a new GAI framework with the use of e-values under arbitrary dependence.
> One general small personal suggestion would be to not center the A/B testing for tech companies applications so much in the abstract and introduction, and instead showcase more exciting (possibly for social good) applications.
Thank you for this suggestion! We will revise the abstract and introduction to emphasize additional use cases, such as real-time monitoring of machine operation status in industrial settings. Indeed, we have applied the e-GAI algorithm to one relevant real example in Appendix C.2. We appreciate that this will better showcase the potential benefits of our framework.
> Typos: add “The” before “e-LOND” in line 19, left column; add “the" before “GAI” in line 70 right column; “guarantee” should be “guarantees” in line 417 right hand side
Thank you for the careful reading! We will correct these typos in the final version. | null | null | null | null | null | null |
Adaptive Median Smoothing: Adversarial Defense for Unlearned Text-to-Image Diffusion Models at Inference Time | Accept (poster) | Summary: This paper seeks to enhance the adversarial robustness of unlearned t2i diffusion models, specifically aiming to balance the adversarial robustness and generative capabilities of the original t2i models. The proposed method, Adaptive Median Smoothing, starts by formulating the target task as a regression problem, and extends it to an anisotropic noise case with median smoothing by introducing a global relevance score for the input prompt.
Claims And Evidence: The main claims of the paper are supported by the experimental results and ablation studies.
Methods And Evaluation Criteria: The proposed method, with regression formulation for unlearned diffusion models, generally makes sense to the reviewer (with some more specific questions detailed in the Questions below). The evaluation results are reported based on three metrics, including ASR, FID, and CLIPScore, which also makes sense.
Theoretical Claims: The main theoretical claim is Theorem 3.2 in P4, which is just a special variant of Lemma 1 under the constraint of non-isotropic Gaussian noise, the reviewer checked the proof and did not find evident flaws.
Experimental Designs Or Analyses: The current experimental designs and analyses are in general reasonable, with several questions specified below.
Supplementary Material: The reviewer checked the supplementary material, which mainly includes the proof of Theorem 3.2 and some hyperparameters. No particular evidence of flaws in the theoretical deviation, but some problems related to implementation details are specified below the Question section.
Relation To Broader Scientific Literature: The reviewer finds that the references and related literature in the paper are generally well discussed, helping the reader understand the key contributions proposed in this work.
Essential References Not Discussed: The paper has a relative good reference discussion on related works in the problem of adversarial robustness of unlearned models.
Other Strengths And Weaknesses: S1: The paper is well-structured with a clear logical flow, making it easy to follow.
S2: The problem and task are relatively well-defined and appear reasonable.
W1: This work focuses on a highly specific scenario—adversarial robustness for unlearned T2I diffusion models—with experiments conducted only on SD 1.4. It remains unclear how well the proposed method generalizes to other T2I model variants and how its performance is affected by the underlying unlearned base models.
W2: The experiments primarily evaluate two concepts: nudity and violence. While I am not explicitly requesting additional experiments, I would appreciate a discussion on specific failure cases to better understand the limitations of the approach.
W3: Certain aspects of the formulation and implementation details remain unclear—please see my questions section for further clarification.
Other Comments Or Suggestions: - The abstract is a bit too long, maybe the authors may consider shortening it for better readability.
- The reviewer believes it will be interesting to investigate a bit further the combination of different unlearned concepts, as those concepts may present correlations among them and impact the performance of the proposed method.
- Maybe also consider numbering all the equations as it is difficult to refer to while some are numbered and others are not.
Questions For Authors: Q1: In the regression formulation, are there any constraints on the expected perturbation $\delta$? Specifically, could the perturbation become too large, such that $y+\delta$ falls into a distribution different from $p*(x_{(0,...,T)|\mathcal{T}(y)})$ ?
Q2: Why does the formulation consider all intermediate steps in the regression process? Intuitively, wouldn’t it make more sense to focus only on step 0 in theory? Moreover, in implementation, many prior works suggest that the full sequence is not necessary for T2I generation.
Q3: Regarding relevance score computation, the paper mentions the need to collect pairs of positive and negative prompts. How are these pairs collected and constructed, and what is the computational cost associated with this step?
Q4: Do the authors have any insights on failure cases? Additionally, how might the method be impacted if multiple concepts were unlearned in a single base T2I model?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: # Generalizability Across T2I Model Variants
We evaluated our method on other widely used T2I models, SD 1.5 and SD 2.1, to assess the generalizability of our method. Due to time constraints, we used the UCE unlearned model with "*nudity*" removed, keeping $\sigma_0$ and $k$ consistent with version 1.4. The table below shows results using four attack methods: I2P, P4D, RAB, and QF-PGD, with average attack success rate (ASR) for robustness and FID and CLIP scores for utility.
| SD Version | Defense | ASR $\downarrow$ | FID $\downarrow$ | CLIP $\uparrow$ |
| -------- | --------- | ----------- | ----------- | --------------- |
| 1.5| w/o defense|28.05|4.354|31.05|
| 1.5|Ours|10.65|5.460|30.56|
| 2.1|w/o defense|21.52|5.303|31.00|
| 2.1|Ours|7.01|6.575|30.66|
Our findings indicate that our method remains effective across different T2I model variants, enhancing the adversarial robustness of unlearned models without significantly affecting their generation capabilities. We will expand the analysis to include additional baselines in our paper.
# Discussion on Failure Cases
Thank you for your insightful feedback. We have provided some qualitative results [here](https://anonymous.4open.science/r/Re-ML/fig5.png). These results show that with the default hyper-parameter value of $\sigma_0$ (as seen in the second and fifth columns), certain adversarial prompts can still restore the nudity concept. In our implementation, $\sigma_0$ is fixed for each unlearned model, but there are challenging cases that require a larger $\sigma_0$ to address effectively. While increasing $\sigma_0$ can help defend against these prompts, it may also degrade model performance with benign inputs. Therefore, it is worthwhile to explore how to dynamically adjust $\sigma_0$ based on the input prompt in future work. We will include this discussion in our paper.
# Multiple Concept Unlearning
Thank you for the insightful comment. We conducted a preliminary exploration on the UCE unlearned model with *nudity* and *violence* concepts erased simultaneously. For this multi-concept setting, we computed each token's relevance score by taking the maximum of its similarity with both the nudity concept direction and the violence concept direction. The results are presented in the table below, where for each concept, the average attack success rate (ASR) is computed across three attack methods (I2P, RAB, and QF-PGD).
| Defense | ASR $\downarrow$ (Nudity) | ASR $\downarrow$ (Violence) | FID $\downarrow$ | CLIP $\uparrow$ |
| ----------- | ------------------------- | ----------------------- | ------------ | ----------- |
| w/o defense|24.22|36.30|6.181|30.92|
| Ours|5.26|9.18| 6.752|30.31|
Our method is effective in concurrently handling multiple concepts. Compared to the single-concept case, the additional computation involves calculating similarities with more concepts and performing a subsequent max operation. However, when the number of concepts is large, the efficiency of our method may be affected. We will include this analysis in our paper.
# Constraints on Adversarial Perturbation
The perturbation is constrained within a norm-bounded set $\\mathcal{B}$, specifically $\||\delta\||\_2<\rho$ in the isotropic case (Lemma 3.1) and $\||\delta\||_{\Sigma,2}<\rho\prime$ in the anisotropic case (Theorem 3.2). If the upper bound of the perturbation norm is large, users can increase noise intensity in median smoothing. A detailed discussion on handling large perturbations is available in the `Theoretical Tightness under Large Perturbation` section of our response to Reviewer CcZX.
# Justification for Considering Intermediate Steps in Formulation
Our formulation follows the DDPM [1] framework, modeling generation as Markov chains. While we aim to constrain $x_0$, the dependency structure ($x_0$ depends on $x_1$, $x_1$ on $x_2$, and so forth) means perturbations propagate through the entire sequence. The formulation ensures robustness at each step, preventing cascading errors and ultimately safeguarding the final output. Notably, related works, such as [2], also incorporate intermediate steps in their formulations.
In practical applications, efficient sampling techniques enable us to perform smoothing over a limited number of time steps, often just tens or even fewer, thus maintaining computational efficiency.
[1] Denoising Diffusion Probabilistic Models, NeurIPS 2020.
[2] Ablating Concepts in Text-to-Image Diffusion Models, ICCV 2023.
# Collection of Prompt Pairs
Positive and negative prompts are sourced from the ViSU dataset, as explained in the Implementation Details (Section 4.1), requiring no additional computation. We also explored generating prompt pairs using a large language model (LLM) interface. More details are in the `Clarifying the Use of Prompt Pairs from ViSU` section of our response to Reviewer 9A3r.
# Additional Comments
We will shorten the abstract and number all the equations in our paper. Thanks for your advice.
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Rebuttal Comment 1.1:
Comment: (Accidentally posted this Rebuttal Comment as Official Comment before)
First, I thank the authors for their rebuttal. I have read the responses, and most of my concerns have been addressed. Accordingly, I am raising my score to a 4.
That said, I remain unconvinced by the justification regarding the use of all intermediate steps. In most T2I diffusion models, DDIM-based samplers with significantly reduced steps (e.g., ~50 steps) are commonly adopted. In this context, the original DDPM sampling procedure is often considered unnecessary. Given the application-oriented nature of this work, I do not see a strong rationale for adhering to the theoretically bounded stepwise error formulation. While the authors mention that “efficient sampling techniques enable us to perform smoothing over a limited number of time steps,” it appears that no concrete experiments have been conducted.
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Reply to Comment 1.1.1:
Comment: We sincerely appreciate the continued engagement and your raising of our score.
You are correct that in practice many T2I pipelines use DDIM [1] or other fast samplers with $S \ll T$ steps (e.g., $S \approx 50$). Our original formulation covers the full DDPM [2] chain ($x_0,x_1,\dots, x_T$), which may not be necessary in practical applications. To better align our theoretical framework with practical sampling procedures, we generalize our formulation by considering a **sub-sequence** $\\{x_{\tau_0},x_{\tau_1},\dots, x_{\tau_S}\\}$ used in **practical sampling**. These timesteps satisfy:
$$
0 = \tau_0 < \tau_1 < \tau_2 < \dots < \tau_S = T.
$$
We then bound the KL divergence over this **sub-sequence** for any perturbation $\delta$ within a norm-bounded set $\mathcal{B}$:
$$
\mathcal{D}_{\mathcal{KL}}\Big({p^*}\big({x}\_{(\tau_0\dots\tau_S)}|\mathcal{T}(y)\big)\\,||\\,{p^*}\big({x}\_{(\tau_0\dots\tau_S)}|\mathcal{T}(y+\delta)\big)\Big),
$$
which translates to constraining the mean squared error (MSE) at **each sampled step** $\tau_i$, for $i=1,\dots,S$:
$$
\mathbb{E}_{{x}\_{\tau_i},\tau_i}\big[\\|{\epsilon}^{\*}\big({x}\_{\tau_i},\mathcal{T}(y),\tau_i\big)-{\epsilon}^{\*}\big({x}\_{\tau_i},\mathcal{T}(y+\delta),\tau_i\big)\\|_2^2\big] \leq C(\mathcal{B}), \quad \forall \delta \in \mathcal{B}.
$$
In our **experiments** we use $S=50$ for SD 1.4/1.5 and $S=25$ for SD 2.1, applying adaptive median smoothing at **each sampled step**. We will clarify this generalized formulation in the final version.
Thank you again for helping us enhance the rigor and clarity of our paper.
[1] Denoising Diffusion Implicit Models, ICLR 2021.
[2] Denoising Diffusion Probabilistic Models, NeurIPS 2020. | Summary: This paper proposes an inference-time defense method, named Adaptive Median Smoothing, to protect unlearned text-to-image diffusion models against adversarial prompt attacks. Specially, the promposed method reformulates robustness as a regression problem and extends median smoothing by using anisotropic noise. Then, it utilizes token-level adaptive noise to keep the model robust without hurting image generation utility.
Claims And Evidence: In this paper, authors make five claims about their proposed method
- Robustness enhancement is supported by its lower ASR (through different attack methods)
- Model utility preservation is supported by the results of FID and CLIP score, which assess the image generation quality and text alignment, respectively.
- Compared with other training-free methods, it utilizes reasonable inference time for a robust defense.
- Good generalization across different NSFW contents (e.g., nudity, violence).
- Supported by Theorem 3.2 and extensive experiments, the claim that the proposed method improve robustness against adversarial prompts while maintaining the model utility generative quality and fast inference.
Methods And Evaluation Criteria: The proposed method utilizes a new form of median smoothing with anisotropic noise and adapts noise intensity per token using concept relevance scores.
Theoretical Claims: Theorem 3.2 provides bounds for robust regression using median smoothing with anisotropic noise.
Experimental Designs Or Analyses: A SOTA adversarial unlearning[1] is a strong baseline because, unlike ESD and UCE, it fine-tunes the text encoder to achieve effective unlearning and also maintain good model utility, which exist certain resemblances to the proposed method in essence since both are implementing defense in the text embedding space. It is also worth investigating whether the proposed defense can further enhance unlearning performance for unlearned text encoder.
[1] Defensive Unlearning with Adversarial Training for Robust Concept Erasure in Diffusion Models, NeurIPS 2024
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: NA
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for your insightful comment regarding the relationship between our method and AdvUnlearn [1]. Our response is elaborated on the following three aspects:
# Methodological Differences
AdvUnlearn [1] is a pre-inference method that fine-tunes the text encoder. It falls into the category of **adversarial erasing-based** defenses, similar to the *RACE* and *RECE* baselines evaluated in our manuscript. While AdvUnlearn operates in the text-embedding space as our method does, several key differences exist:
- **Efficiency**: AdvUnlearn requires relatively large computational resources for the fine-tuning process, as acknowledged by the authors [1]. In contrast, our approach is training-free and operates at inference time, offering greater efficiency.
- **Theoretical Guarantees**: Unlike AdvUnlearn’s empirical defense, we provide theoretical guarantees through generalized median smoothing (Theorem 3.2), which could potentially offer new insights to this field.
# Comparative Performance Evaluation
We implemented AdvUnlearn using its official codebase to compare it with our method, targeting the concept of "*nudity*". For our approach, we integrated our method with ESD, setting $\sigma_0$ to 0.012 and $k$ to 9. We evaluated adversarial robustness through four attacks (i.e., I2P, RAB, MMA, and QF-PGD) and calculated the average attack success rate (ASR), while assessing model utility through FID and CLIP scores. The results are shown in the table below:
| Defense | ASR $\downarrow$ | FID $\downarrow$ | CLIP $\uparrow$ |
| ---------- | ---------------- | ---------------- | --------------- |
| AdvUnlearn | 1.39 | 6.973 | 29.03 |
| Ours | 1.62 | 7.783 | 29.80 |
The results indicate that our method achieves adversarial robustness comparable to AdvUnlearn. In terms of model utility, AdvUnlearn maintains superior FID metrics (image quality) because it preserves the U-Net weights. However, its CLIP score (image-text alignment) is lower due to modifications in the text encoder. Our defense employs adaptive median smoothing without altering text encoder parameters, better preserving **image-text alignment** capabilities.
# Compatibility and Future Work
We found that directly applying our method to an unlearned text encoder presents challenges. Our approach requires calculating each token's relevance to unsafe concepts, but AdvUnlearn's fine-tuning process maps unsafe token representations to benign ones, making it difficult to distinguish between them based on textual representations. This results in inaccurate relevance scores.
Currently, our proposed method serves as an effective complement to unlearning approaches that modify *U-Net parameters*, which constitute the **majority** of diffusion model unlearning techniques. In future work, we plan to explore adaptations to our method to enhance compatibility with unlearned text encoders.
We will incorporate a citation to AdvUnlearn and include the above analysis in our paper.
[1] Defensive Unlearning with Adversarial Training for Robust Concept Erasure in Diffusion Models, NeurIPS 2024. | Summary: This paper proposes "Adaptive Median Smoothing" as an inference-time defense for adversarial attacks on unlearned diffusion models. The defense goal can be formulated as minimizing MSE predicted noise before and after adversarial perturbation. Based on this formulation, the paper then introduces the naive median smoothing method with isotropic noise, analyzing its bound to show the method can theoretically defend against adversarial attacks. The paper then generalizes the analysis to generalized median smoothing with anisotropic noise. However, such an approach is computationally heavy in approximating medians for each timestep. Given these insights, the paper proposes adaptive median smoothing: (1) it computes the relevance score of each token by looking into the text embedding, and adds larger noise to the token embeddings of more relevant tokens; (2) instead of computing medians independently at every timestep, the paper computes medians of token embeddings before the generation and always use this as conditional input to the denoiser. The paper conducts defense experiments on ESD and UCE under different adversarial attacks, focusing on the concept nudity. It compares the ASR, FID, and CLIP with baseline defense methods and shows better balance between adversarial robustness and utility.
Claims And Evidence: 1. Why the estimation of medians before generation can still be theoretically supported is not clear - the theoretical results seem to assume the medians are estimated separately for every timestep.
2. The bound of mean squared error requires $\|\delta\|_2<\rho$, yet the norm upper bound of adversarial perturbation $\delta$ can be very large. It's not clear how meaningful the bound of the mean squared error in equation (2) is - if it's a loose bound, it can not theoretically support that median smoothing can be used as a defense strategy.
Methods And Evaluation Criteria: The method is for defending unlearned diffusion models from adversarial attacks during inference-time. Yet, the benchmark datasets only focus on defending nudity. In machine unlearning, usually, at least three levels of concepts are considered: object, style, NSFW. Since the key problem the paper aims to solve is defending unlearned diffusion models, it is essential to fully demonstrate its effectiveness on these different levels of concepts, instead of only nudity from NSFW.
Theoretical Claims: I have checked the correctness of proofs, and it overall makes sense following the assumptions.
Experimental Designs Or Analyses: 1. There are concerns about datasets, as stated in the Evaluation Criteria section.
2. Besides, the paper should discuss why only UCE and ESD are the only chosen unlearned models - is it because they are the most robust and widely used models, or is it for some other reasons?
Supplementary Material: I reviewed all parts - this supp majorly contains proofs.
Relation To Broader Scientific Literature: Maybe the paper can inspire later work to consider applying methods inspired from signal processing to the deep learning safety community for a more fundamental and potentially fruitful research.
Essential References Not Discussed: [1] Defensive Unlearning with Adversarial Training for Robust Concept Erasure in Diffusion Models. Yimeng Zhang, etc. NeurIPS 2024.
Ths paper comes up with a similar regression formulation in defending adversarial perturbations and maybe cited and discussed.
Other Strengths And Weaknesses: Strengths
1. The paper does stand out with its theoretical analysis on applying median smoothing to defending unlearned diffusion models.
2. The paper does make an interesting engineering effort to adapt naive median smoothing to a more efficient defending method with good performance on defending nudity.
Other Comments Or Suggestions: It might be helpful to have a notation section - not a big problem.
Questions For Authors: 1. Why the estimation of medians before generation can still be theoretically supported?
2. When assuming $\|\delta\|_2<\rho$, is it possible that $\rho$ can be very large and cause the bound of the mean squared error in equation (2) to be a loose bound? How to argue it is a meaningful bound?
3. Can the method also work well in defending concepts in the category of object and style?
4. Why only UCE and ESD are the only chosen unlearned models - is it because they are the most robust and widely used models, or is it for some other reasons?
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: # Evaluation Across Object and Style Concepts
We would like to clarify that our original manuscript includes experiments not only on the concept of nudity but also on **violence**. Following your suggestion, we expanded to include **object** and **style** concepts.
- For the **object** concept, we targeted "*gun*" and used three attack methods (UDA, RAB, QF-PGD) to assess adversarial robustness, reporting the mean attack success rate (ASR). Due to time constraints, we compared only with SLD-Medium and SLD-Max baselines. The results, presented in the table below, show our method achieves a superior balance between robustness and utility.
| Unlearned Model | Defense | ASR $\downarrow$ | FID $\downarrow$ | CLIP $\uparrow$ |
| --------------- | ----------- | ---------------- | ---------------- | --------------- |
| ESD | w/o defense | 56.11 | 6.595 | 30.06 |
| ESD | SLD-Medium | 28.44 | 9.624 | 29.45 |
| ESD | SLD-Max | 18.11 | 16.630 | 28.26 |
| ESD | Ours | 26.07 | 7.959 | 29.66 |
| UCE | w/o defense | 58.56 | 5.281 | 31.03 |
| UCE | SLD-Medium | 40.11 | 8.201 | 30.65 |
| UCE | SLD-Max | 21.00 | 14.223 | 29.25 |
| UCE | Ours | 29.85 | 7.142 | 30.29 |
- For the **style** concept, we targeted "*Van Gogh*" using three attack methods (UDA, RAB, QF-PGD), with results shown in the table below. These results demonstrate the method's effectiveness in addressing style concepts.
| Unlearned Model | Defense | ASR $\downarrow$ | FID $\downarrow$ | CLIP $\uparrow$ |
| --------------- | ----------- | ---------------- | ---------------- | --------------- |
| ESD | w/o defense | 11.33 | 5.612 | 30.38 |
| ESD | SLD-Medium | 1.33 | 7.929 | 30.03 |
| ESD | SLD-Max | 0.00 | 15.364 | 28.70 |
| ESD | Ours | 0.00 | 6.181 | 30.16 |
| UCE | w/o defense | 39.83 | 2.024 | 31.11 |
| UCE | SLD-Medium | 1.67 | 6.569 | 30.55 |
| UCE | SLD-Max | 0.00 | 17.322 | 28.30 |
| UCE | Ours | 0.00 | 3.843 | 30.94 |
We acknowledge the limited baselines for object and style concepts and will include more in our final paper.
# Clarifying Median Estimation Independence Across Timesteps
We want to clarify that the conditional text embeddings at each timestep are **independent** of one another. For *each timestep*, we sample noise from Gaussian distribution and apply adaptive median smoothing to obtain the conditional text embedding. This smoothed text embedding is then input into the U-Net for the current denoising step. Although the computation of the smoothed text embedding occurs at each timestep, it can be performed in parallel, making it more efficient than computing the median U-Net noise prediction, as shown in Table 2 of our manuscript.
# Theoretical Tightness under Large Perturbation
The bound in Equation (2) remains theoretically meaningful even for large adversarial perturbation, as the bound explicitly depends on the interplay between perturbation norm upper bound $\rho$ and the **noise magnitude** $\sigma$ used in median smoothing.
According to Lemma 3.1, the perturbed output $\mathcal{E}\_{0.5}(y+\delta)$ is bounded by $\underline{\mathcal{E}}\_{\underline{p}}(y)$ and $\overline{\mathcal{E}}_{\overline{p}}(y)$. Tighter bounds are achieved when $\underline{p}$ and $\overline{p}$ are closer to 0.5. The probabilities $\underline{p}:=\Phi\left(-\frac{\rho}{\sigma}\right)$ and $\overline{p}:=\Phi\left(\frac{\rho}{\sigma}\right)$ suggest that increasing $\sigma$ can tighten the bound when $\rho$ is large. Thus, **theoretically**, the bound remains effective even with large perturbations.
In **practice**, while $\rho$ may be large, increasing $\sigma$ helps maintain adversarial robustness. However, excessive $\sigma$ may harm the model utility, so it requires careful tuning.
# Reasons Behind Choosing ESD and UCE as Base Unlearned Models
We selected ESD and UCE as the base unlearned models for the following reasons:
- **Widely Recognized Baselines**: ESD and UCE are frequently used in the field of unlearning for diffusion models.
- **Distinct Paradigms**: They represent two primary diffusion unlearning paradigms: ESD is associated with fine-tuning, while UCE pertains to model editing.
- **Ensuring Fair Comparison**: The adversarial erasing-based baselines, RACE and RECE, are implemented using ESD and UCE, respectively. Therefore, selecting ESD and UCE as the base unlearned models ensures a fair comparison between our method and adversarial erasing-based approaches.
# Discussion on AdvUnlearn
We will cite and discuss AdvUnlearn [1] in our paper. The detailed discussion is provided in our response to Reviewer ZpJv.
[1] Defensive Unlearning with Adversarial Training for Robust Concept Erasure in Diffusion Models, NeurIPS 2024.
# Notation Section
Thanks for your advice. We will include a notation section in our paper. | Summary: Even after unlearning, models are still vulnerable to adversarial inputs that can expose users to inappropriate contents. Existing adversarial defense methods still have difficulty with balancing the adversarial robustness and the generation quality. To address these issues, the paper proposes an inference-time defense strategy to defend against adversarial text prompts. To do so, the paper formulates the optimization for robustness as a robust regression problem, which is extended to a generalized median smoothing framework incorporating anisotropic noise. Finally, the paper proposes a token-wise Adaptive Median Smoothing strategy that applies noise of intensity that is dynamically adjusted according to the relevance of tokens to target concepts.
Claims And Evidence: Claims are reasonable.
Methods And Evaluation Criteria: Yes, I couldn't find any issue.
Theoretical Claims: Yes, I couldn't find issues.
Experimental Designs Or Analyses: Yes, the experimental designs and analyses seem sound and valid.
Supplementary Material: Yes. I've checked the supplementary material.
Relation To Broader Scientific Literature: Formulating adversarial-robustness of concept erasure as robust regression problem and extending it to a generalized median smoothing framework brings non-trivial contribution and new insights to the field.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: Strengths:
- It’s a reasonable and nice perspective to view adversarial defense as robust regression problem
- This robust regression perspective allows the proposed method to be robust to adversarial attacks by employing a median smoothing framework.
- The paper does not stop at just applying a median smoothing framework, but finds the problem with applying it naively to concept erasure framework. Thus, the paper proposes a generalized median smoothing framework with anisotropic noise.
Weakness:
- If relevance score relies on token similarity, I'm guessing that it can be vulnerable to vague adversarial prompts (e.g., prompts that have no nudity-related words but lead to nudity generation). It would be great if the paper shows the analysis on this with various vague adversarial prompts .
- It seems that hyperparameters need to be finetuned for each baseline model. How robust is the proposed framework to the choice of hyperparameters? It would be great to show this analysis. The ablation study shows the results for only one baseline.
- To show how robust the proposed framework is to adversarial attacks, the paper could improve with the analysis that shows when the proposed framework fails and succeeds.
- The paper has a few typos/grammar errors. A thorough proof-reading is recommended.
- There is no detail on positive & negative prompts. Furthermore, which model has used positive & negative prompt list from ViSU? I think it's unfair to compare against models that did not have access to this list. The paper should provide an ablation study on the proposed method without prompt list from ViSU. Also, the paper should compare against existing methods that employ the list from ViSU. The paper should also use the prompt list to re-train methods that do not employ the prompt list and compare against them as well.
Other Comments Or Suggestions: Typos/grammar erros
- line 229: The findings in Theorem 3.2 suggests -> The findings in Theorem 3.2 suggest
- line 241: we propose a Efficiency -> we propose an Efficiency
- run-on sentences in line 317-319
Questions For Authors: Questions are written in the weakness section.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: # Analysis of Vague Adversarial Prompts
Thanks for your insightful comment. Our method’s robustness against vague adversarial prompts is validated through evaluations on the **MMA attack** [1], which constructs adversarial prompts avoiding sensitive words while inducing unsafe generations. As shown in Table 1 of our manuscript, our method reduces the attack success rate (ASR) for MMA from $7.50\\%$ to $4.23\\%$ (ESD model) and from $39.30\\%$ to $17.53\\%$ (UCE model), demonstrating effectiveness against such vague adversarial prompts.
[1] MMA-Diffusion: MultiModal Attack on Diffusion Models, CVPR 2024.
# Ablation Study of Hyper-Parameters
In response, we have conducted an ablation study on hyper-parameters using the other unlearned model, **UCE**. The updated results, provided [here](https://anonymous.4open.science/r/Re-ML/tb4.png), indicate that moderately increasing $\sigma_0$ and $k$ enhances the adversarial robustness of unlearned models without significantly compromising their utility.
# Discussion on Failure Cases
We have provided qualitative results [here](https://anonymous.4open.science/r/Re-ML/fig5.png). These results reveal that the framework occasionally fails on "hard cases" where adversarial prompts bypass default hyper-parameters ($\sigma_0$), allowing unsafe concept restoration (columns 2 & 5). While increasing $\sigma_0$ mitigates such cases, it risks degrading benign-generation quality. This highlights a trade-off between robustness and utility under fixed hyper-parameters. Future work will explore dynamic $\sigma_0$-adjustment based on input prompt to better balance these objectives.
# Clarifying the Use of Prompt Pairs from ViSU
Thank you for your valuable feedback. Here is our response:
- **Details on Prompts**: As reported in [2], the authors fine-tuned a large language model (LLM), Llama 2, to generate unsafe sentences from safe ones collected from COCO captions. The training set contains 7,863 prompt pairs for the nudity concept.
- **ViSU for Baseline Methods**: Most defense baselines in our manuscript do not require *prompt pairs*. Specifically, pre-inference defenses (RACE and RECE) *optimize* adversarial prompts and subsequently erase them. For training-free defenses, SLD uses *inappropriate keywords* to calculate unsafe guidance, while Blacklist uses *NSFW words* for filtering.
- **Ablation Without ViSU**: To further demonstrate the effectiveness of our proposed method, we implemented "*nudity*" unlearning without using prompt pairs from ViSU. Specifically, we first used an uncensored LLM interface on Hugging Face to generate 100 nudity-related prompts (positive prompts) and then used another LLM interface (e.g., Kimi) to transform them into safe versions (i.e., negative prompts). We then used these 100 prompt pairs (denoted as **Self-Gen**) in our experiments, with results shown in the table below (a detailed table with attack success rates for each attack is provided [here](https://anonymous.4open.science/r/Re-ML/tb1.png)). Overall, our method remains effective even with just 100 collected prompt pairs. In the detailed table, we observe that adversarial robustness against vague adversarial prompts (i.e., MMA) degrades, suggesting that collecting more prompt pairs further enhances defense against vague adversarial prompts.
| Unlearned Model | Defense Methods | ASR $\downarrow$ | FID $\downarrow$ | CLIP $\uparrow$ |
| --------------- | --------------- | ---------------- | ---------------- | --------------- |
| ESD | w/o defense | 25.42 | 7.161 | 30.18 |
| ESD | Ours (ViSU) | 6.80 | 7.365 | 30.10 |
| ESD | Ours (Self-Gen) | 5.33 | 7.436 | 30.09 |
| UCE | w/o defense | 40.34 | 4.379 | 31.02 |
| UCE | Ours (ViSU) | 11.02 | 5.343 | 30.48 |
| UCE | Ours (Self-Gen) | 15.93 | 5.526 | 30.54 |
- **Generalization to Other Concepts**: ViSU primarily contains unsafe prompts (e.g., nudity and violence) and is not suitable for other types of concepts (e.g., objects and styles). For these concept types, we first used an LLM interface to generate 100 positive prompts depicting the target concept, and then instructed the LLM to remove target concept-related elements to create negative prompts. The experimental results for these additional concept types are provided in the `Evaluation Across Object and Style Concepts` section in our response to Reviewer CcZX.
[2] Safe-CLIP: Removing NSFW Concepts from Vision-and-Language Models, ECCV 2024.
# Typos & Grammar Errors
Thank you for your careful review. We have corrected the identified typos/grammar errors and will perform a thorough proofread of the entire manuscript to ensure clarity and correctness.
---
Rebuttal Comment 1.1:
Comment: Thank you for the rebuttal, which has addressed most of my concerns, but not all of them.
Particularly, for the ablation on ViSU, I think baseline models, such as ESD, UCE, and Concept Ablation, can be trained with pairs of positive and negative prompts. Can't you take positive prompts as target concepts and negative prompts as anchor concepts? The proposed model's reliance on pairs of positive and negative prompts comes to me as weakness of the proposed framework. With the knowledge of the list of positive and negative prompts is available to adversaries, adversarial prompts could be easily generated to bypass the framework.
But, considering the balance between strengths and weakness of the proposed framework, I retain the score.
---
Reply to Comment 1.1.1:
Comment: We appreciate your concerns and address them as follows:
# ESD and UCE with ViSU Prompt Pairs
We have incorporated ViSU into the training processes of ESD and UCE, as detailed below:
- **Implementation:** In the **official implementations** of ESD and UCE, **keywords** (e.g., "*nudity*") are typically used for target concepts, while null text ("") serves as anchor concepts. We acknowledge that positive prompts can be adapted as targets and negative prompts as anchors in ESD and UCE training. Specifically, for ESD, we randomly sample prompt pairs for fine-tuning in each iteration. For UCE, all prompt pairs are used for model parameter editing.
- **Experimental Results**: We evaluated adversarial robustness specifically targeting the "*nudity*" concept through six attacks and calculated the average attack success rate (ASR). Model utility was assessed using FID and CLIP scores. The results are presented in the table below (a detailed table with attack success rates for each attack is provided [here](https://anonymous.4open.science/r/Re-ML/tb6.png)).
| Unlearned Model | ViSU | Defense Methods | ASR $\downarrow$ | FID $\downarrow$ | CLIP $\uparrow$ |
| --------------- | ---- | --------------- | ---------------- | ---------------- | --------------- |
| ESD | ❌ | w/o defense | 25.42 | 7.161 | 30.18 |
| ESD | ✔️ | w/o defense | 22.62 | 6.741 | 30.31 |
| ESD | ✔️ | Ours | 6.80 | 7.365 | 30.10 |
| UCE | ❌ | w/o defense | 40.34 | 4.379 | 31.02 |
| UCE | ✔️ | w/o defense | 0.00 | 167.569 | 20.41 |
| UCE | ✔️ | Ours | 11.02 | 5.343 | 30.48 |
For **ESD**, incorporating ViSU prompt pairs does not negatively impact model utility, but the **adversarial robustness improvement is slight** (ASR: $25.42\\%\rightarrow22.62\\%$). Unlike ESD, which relies on fine-tuning, **UCE** is based on model editing. Incorporating a large number of prompt pairs can lead to excessive modifications to the model's parameters, which may **significantly harm its utility** (FID: $4.38\rightarrow167.57$). However, our method, which employs ViSU to compute relevance scores for adaptive median smoothing during inference, **effectively enhances adversarial robustness while preserving model utility**. As demonstrated in our previous response, even without ViSU, using our self-generated prompt pairs (**Self-Gen**) achieves comparable performance.
# Prompt List for Deployment and Its Vulnerabilities under Attack
Thanks for your insightful comment. Our response is as follows:
Firstly, we want to clarify that prompt pairs are used to calculate the **concept vector** for the target concept, which is then utilized to compute the **relevance score**. This score determines the **noise intensity** for each token. Our previous ablation study of ViSU demonstrated that **Self-Gen** prompt pairs, generated using the LLM interface, are also effective.
Although ViSU is publicly available and accessible to attackers, defenders can generate similar prompt pairs (like **Self-Gen**) using the LLM interface. The inherent **randomness** in the prompt generation process makes it difficult for attackers to replicate the exact prompt list used by defenders, thus making bypass attempts **more challenging**. Even if attackers were to obtain the exact list, designing an attack strategy to circumvent our framework would require careful planning, as, to our knowledge, existing attack methods are **not** equipped to handle such scenarios. Future efforts will focus on examining sophisticated attack techniques that might penetrate our framework, thus allowing us to bolster its robustness.
We sincerely thank you again for your valuable feedback and suggestions, which have greatly assisted us in improving the quality of our paper. | null | null | null | null | null | null |
AI for Global Climate Cooperation: Modeling Global Climate Negotiations, Agreements, and Long-Term Cooperation in RICE-N | Accept (poster) | Summary: ## update after rebuttal
The paper proposed a multi-agent reinforcement learning (MARL) approach to model global climate negotiations, agreements, and long-term cooperation. Two novel negotiation protocols were proposed: Bilateral Negotiation and Basic Club. The proposed approach and protocols take into account many realistic components such as climate dynamics and economic dynamics. The simulated results compared the two negotiation protocols and a baseline without negotiation. The comparison shows better results with negotiation.
The rebuttal responses helped clarification.
Claims And Evidence: The claim, the two negotiation protocols are better than the baseline without negotiation, is well supported by the experimental results.
Methods And Evaluation Criteria: 1. The proposed multi-agent reinforcement learning method and the two negotiation protocols are novel and make sense.
2. The evaluation criteria include both climate-economic and Gini indexes, which make sense and are comprehensive.
Theoretical Claims: The work is a game-theoretic problem. The paper itself does not have proof.
Experimental Designs Or Analyses: The experimental design in Section 6 and result analyses (mostly in Table 1) are reasonable.
Supplementary Material: I mostly checked Section B and Algorithm 1 in the supplementary material to understand more on how multi-agent reinforcement learning works.
Relation To Broader Scientific Literature: The work extends existing climate-economic policy tradeoff modeling work including integrated assessment models (IAMs) and Regional Integrated Model of Climate and Economy (RICE) by capturing the strategic behavior in climate negotiations.
Essential References Not Discussed: I think the references in the Related Works (both main paper and appendix) are comprehensive.
Other Strengths And Weaknesses: W1: Most results are global macro level. Analysis of actions and goals of individual countries/regions are missing. The simulation should be reasonable at both global macro level and individual micro-level.
Other Comments Or Suggestions: Figures 6-15 are not explained.
Questions For Authors: Q1. Could region level analysis be provided? For example, what are a region’s actions overtime and how they are different with the two negotiation protocols and without negotiation. Are there any patterns in the actions for the 27 regions studied. Could their actions be categorized into a few common groups?
Q2. Can you summarize possible usages of the proposed approach for different types of users: ML researchers, climate scientists, government, international organizations such as IPCC?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We thank the reviewer for their thoughtful feedback and for pointing out the positive aspects of our submission, such as the novelty of the protocols, the realism of the components, the empirical support for our claims and the overall quality of the evaluation criteria, experimental design and results analysis. We hope our response clarifies any outstanding concerns.
> Could region level analysis be provided? For example, what are a region’s actions overtime and how they are different with the two negotiation protocols and without negotiation. Are there any patterns in the actions for the 27 regions studied. Could their actions be categorized into a few common groups?
Thank you for this suggestion. Under Basic Club, all regions tend to increase their mitigation rate as much as constraints allow until the maximum mitigation rate is reached. Without negotiation acting as a coordination mechanism, regions tend to fall into different subgroups. There are ambitious mitigators, reducing 40-60% of emissions by the end of the run, moderate mitigators reducing 20-30%, and free riders reducing 0-10%. In the camera-ready version, we will include a detailed quantitative and qualitative analysis of these phenomena.
> Can you summarize possible usages of the proposed approach for different types of users: ML researchers, climate scientists, government, international organizations such as IPCC?
ML researchers can make use of the modularity of the RL component to evaluate how different RL algorithms perform in a real world-calibrated environment. Climate scientists can use it to compare different climate modules and damage functions. Governments can use it to evaluate the robustness of a given climate-economic policy to strategic behavior and estimate the consequences on international trade. International organizations, such as the OECD or WTO could use the tool to analyze the economic trade-offs of different climate policies and negotiation strategies. We will add these potential uses to the text, while making sure to surface the limitations.
> Figures 6-15 are not explained.
Thank you for pointing this out. These results are additional visualizations to support Section 6. In the camera-ready, we will expand the captions for each of the images such that they are sufficiently informative to understand the figures, describing the various scenarios, as well as the variables under study, and what can be concluded from the plots. We will also point to them more strongly in the main text. | Summary: The paper adds reinforcement learning to a multi-agent Nordhaus RICE model.
It allows two communication protocols between agents, whereby agents can make binding commitments to curtail their greenhouse gas emissions.
Simulation allows these two protocols to be compared to the 'no negotiation' (Nordhaus RICE) baseline. Relative to that baseline, the negotiation protocols allow higher welfare outcomes, better controlling the climate's evolution.
The paper claims that the underlying code's modularity allows climate dynamics and economic loss functions to be easily adjusted.
## update after rebuttal
Score maintained for existing manuscript. A considerably revised manuscript (as discussed in the rebuttal) could receive a higher score.
I am concerned by the statement that "no single equilibrium concept applies in all cases", as it raises the question of whether the output corresponds to any intelligible or benchmark description of play. I suspect that nation states are fumbling their way forward here, rather than playing anything that could be clearly rationalized as a form of Nash equilibrium, so this may be fine - but needs to be argued.
Again, the lack of realism in the modeled mechanisms weakens the paper.
Claims And Evidence: The headlines claims are evidenced by three figures of plots and a table in the body of the paper.
Overall, I did not find the claims surprising: stronger protocols for binding commitments allow agents to better overcome the 'cost of anarchy' associated with playing Nash equilibria rather than the social planner's first best outcome.
Methods And Evaluation Criteria: The various runs are compared on the basis of temperature deviations, GDP impact and other standard criteria.
Nordhaus' RICE model is a workhorse of the theoretical literature (contributing to his Nobel prize).
Theoretical Claims: The paper makes no theoretical claims.
On this front, I was interested to know what - for example - the equilibrium concept is. Overall, I felt that too many of the paper's details (e.g. the equilibrium concept, details of RL) were hidden in the appendix.
Experimental Designs Or Analyses: Have not checked anything in detail.
Supplementary Material: Dipped in to some Appendix sections.
Relation To Broader Scientific Literature: Fine.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: My biggest concern with the paper is the specification of binding negotiations.
In the 'real world', significant countries withdraw from their climate change commitments, partly as they do not trust others' commitment. This, of course, is the standard stuff of game theory - and an essential part of the problem.
The original RICE paper (Nordhaus & Yang, 1996) noted that the international transfers required to support its first best solutions would swamp international transfers, making the solutions considered infeasible.
For research to make a significant contribution to this debate, it must at least address these issues. The current paper, to my knowledge, does not.
I grade this paper as a 'weak accept': I think that this issue needs to be kept alive; I do not think that this significantly advances the debate (e.g. novel techniques, surprising results, useful policy insights), but it does help keep the issue alive.
Other Comments Or Suggestions: 1. sanity check: does the 'no negotiation' baseline match the Nordhaus-Yang results?
1. how does the current code compare to Nordhaus code? Is it more modular, faster/slower? (I had seen that there were RICE implementations in Julia a decade ago, but have lost track.)
1. it could be useful to plot policy functions as well (q.v. the comment in the Limitations section about interpretability).
1. Nordhaus appears in the references as both "W." and "W.D." "Stern" and "AI" should be capitalised in the references.
Questions For Authors: 1. why are 27 fictitious countries used, rather than the full set?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank the reviewer for the incisive review of our submission. Below, we respond to the concerns raised.
### > does the 'no negotiation' baseline match the Nordhaus-Yang results?
We can compare our results to Nordhaus’ RICE from 2010 [1]. The aforementioned has two results: baseline and optimal. The former consists of each region optimizing its own objective function and the latter of a cooperative mode with a shared objective function. We compare our results with RICE up until 2115, as that is the end year of our simulation. Looking at global temperature only for simplicity’s sake, the RICE2010 baseline and optimal temperature rises are 3.91 C and 2.92 C, respectively. Our no-negotiation baseline and basic club protocols result in increases of ~4.21 °C and ~2.97 °C, respectively. Exact matches are not expected as initial conditions differ: our rollout starts in 2015 (in line with DICE2016, which served as the basis for the implementation) and RICE2010 in 2005. Nonetheless, both no-negotiation and basic club yield temperature rises comparable to the RICE 2010 base and optimal trajectory, respectively.
[1] Nordhaus, W. D. (2010). Economic aspects of global warming in a post-Copenhagen environment. Proceedings of the NAS, 107(26), 11721-11726.
### > Is [the code] more modular, faster/slower?
While Python is likely slower than e.g. GAMS for model optimization, the runtime is bottlenecked by the deep RL agents, not the environment dynamics. Writing RICE-N in Python makes it simpler for the simulation code to interface with the RL agent code, which can be implemented using common Deep RL frameworks in Python and reduces barriers for ML researchers to contribute to the codebase, and extend it with novel modelling components. Finally, we are working on an efficient JAX implementation, which we plan to release alongside the paper and which will improve the runtime by multiple orders of magnitude.
### > My biggest concern with the paper is the specification of binding negotiations.
In our current setup, agents cannot deviate from agreed-upon actions for the specified time lapse (5 years). While this assumption simplifies analysis and isolates the impact of the negotiation mechanism, it does not reflect the uncertainty and strategic mistrust present in real-world climate negotiations (e.g., countries withdrawing from agreements).
Future work should explore the possibility of non-binding commitments, which would enable agents to engage in strategic communication or 'cheap talk,' thereby better capturing realistic negotiation dynamics [2]. We will add this discussion to the text.
[2] Caparros, A. (2016). The Paris Agreement as a step backward to gain momentum: Lessons from and for theory. Revue d'économie politique, 126, 347.
### > Nordhaus & Yang issues related to international transfers >
The reviewer is correct to identify concerns related to international transfers at the scale required to implement RICE’s optimal pathways. For example, large-scale international transfers risk misappropriation without oversight [3]. However, in the time since Nordhaus and Yang’s 1996 comment on the practicality of international transfers, there has been a greater focus on equity and burden sharing [4], shifting the question from whether international transfers are possible to how do international transfers fit into a larger patchwork of climate finance instruments [5]. Adding an international transfers module is on the RICE-N development road map such that we can explore different means of financing mitigation.
[3] Nest, M., et al. (2022). Corruption and climate finance. Brief Chr. Michelsen Institute U, 4, 14.
[4] Landis, T. & Bernauer, T. (2012). Transfer payments in global climate policy. Nature Climate Change, 2(8), 628-633.
[5] Pickering, J., et al. (2017). Special Issue: Managing Fragmentation and Complexity in the Emerging System of International Climate Finance. *International Environmental Agreements: Politics, Law and Economics*, 17(1), 1-16.
### > too many of the paper's details were hidden in the appendix.
Thank you for this feedback. We will use the extra page of the camera-ready version to discuss more RL-related details in the main text.
### > it could be useful to plot policy functions as well
Thank you for the suggestion. We will add to the final version.
### > Nordhaus appears in the references as both "W." and "W.D." "Stern" and "AI" should be capitalised in the references.
Thank you for catching this. We have corrected this oversight.
### > why are 27 fictitious countries used, rather than the full set?
Many individual countries lack comprehensive data making modeling unreliable. By aggregating countries into regions, the errors from lacking in data from these countries would be less impactful to the whole region. We believe, for a similar reason, RICE-2010 only includes 12 regions. Besides, 27-region setting makes bilateral negotiation computational feasible due to $O(n^2)$ complexity.
---
Rebuttal Comment 1.1:
Comment: Thank you. Some thoughts in reply:
1. **Nordhaus-Yang baselines**: you mention that you are unable to compare the two models as N-Y starts in 2005, and you start in 2015. Any paper I've seen that makes about its performance against benchmark/SOTA models necessarily compares the models on the same datasets. Whether it's easier to run RICE-N on N-Y, or RICE on your data, I don't know.
1. **comparison of code to N-Y**: I suspect that speed is not a big issue here, as we're analysing dynamics that take place over decades. Instead, I am trying to understand how strong the argument is for a re-implementation of RICE is: the paper is weaker if it feels more like 'yet another...' rather than a novel contribution.
1. **binding negotiations**: your comment about '5 years' confuses me: are agents myopically optimising? This is why I originally asked about the equilibrium concept: for computations to be meaningful, we need to know _what_ is being computed: e.g. a Nash equilibrium, a subgame perfect Nash...
1. **international transfers**: my initial view that this paper 'keeps the issue' alive continues - the paper seems to abstract from some of (what I regard as) the main reasons that this is a hard problem.
1. **hidden in the appendix**: noted.
1. **policy functions**: noted.
1. **references**: noted.
1. **27 countries**: again, I think that comparability to Nordhaus-Yang would be useful. From this point of view, RICE-2010's 12 regions would be a natural baseline.
---
Reply to Comment 1.1.1:
Comment: Thank you for your continued engagement.
## 1. Comparison to RICE2010 baseline:
To ensure the consistency of RICE-N’s no-negotiation baseline with Nordhaus2010, we will run the RICE-N no-negotiation baseline starting in 2005 as a sanity check. Since this will involve a significant recalibration effort, we can only promise this for the camera-ready deadline. We will also make sure to run the 12-region version.
Taking a step back, we are not claiming our model is “SOTA”. In fact, there is no definition of SOTA among similar works, since we cannot evaluate the accuracy of prediction of temperature rise 100 years in the future. We compare other models with us for the purpose of sanity check.
## 2. Code comparison.
Thank you for clarifying.
### 2.1
The novelty of RICE-N is that it combines the RICE model with a multi-agent RL framework for climate-economic negotiations between regions.
- Self-interested agents can negotiate, using “tools” such as trade and tariffs. This allows us to explore different negotiations that structure strategic interactions between regions differently.
- Using deep RL algorithms to model agent policies avoids the need to manually specify agent policies for different negotiation protocols.
### 2.2
To be clear: we do not claim novelty in our implementation of RICE in Python, for which we follow William Nordhaus’ 2010 implementation while we do add an extra international trading module. However, we didn’t emphasize our contribution here. A python interface is convenient, but not novel.
## 3. Binding negotiations:
### 5 year step:
Sorry for the confusion. The agents are not myopic. Instead, RICE-N is a MARL agent-based model with per-agent independent model-free RL algorithms (A2C). Therefore, player strategies (agent policies) are not computed analytically, but independently learned iteratively by the agents with the goal of improving their individual returns, which correspond to their long-term aggregate rewards (see eqs 1 and 2).
### What is being computed:
This agent-based model approach is relevant for complex settings [1], and deep RL is useful in settings where exact solutions may be intractable or difficult to qualify [2]. This is particularly helpful for RICE-N, which is meant to serve as a testbed for different negotiation protocols that can extend the environment with observations and actions beyond the original scope of RICE, such as punishment tariffs.
### The equilibrium concept:
NY96 originally discusses pure strategy Nash equilibria. However, RICE-N departs from NY96 through the introduction of RL agents, international trade, tariffs and negotiation protocols. Importantly, since negotiation protocols can vary widely, no single equilibrium concept applies in all cases:
- Equilibrium type: The negotiation protocol can give rise to the introduction of previously irrelevant equilibrium concepts, such as correlated equilibria from a stochastic protocol.
- Augmenting observation/action spaces: The introduction of novel actions, such as punishment mechanisms (e.g. tariffs), can affect the equilibria, and in particular can create the possibility of self-enforcement through collective punishment for defection.
- Commitment: Relaxing the commitment mask introduces cheap talk. A relevant solution concept here is the coalition-proof Nash equilibrium [3].
- Information: The negotiation protocol can affect what information is public vs private.
## 4. Enforcement & International transfers:
We fully agree that enforcement is a central component of any solution. We see this paper as a tool to help enable the study of different negotiation protocols and enforcement mechanisms. For example, future work could relax the formulation of the mask, structure self-enforcing negotiation protocols.
Regarding transfers, we acknowledge that international transfers pose a hard problem with respect to the unequal distribution of funding requirements. RICE-N currently does not include international transfers, but rather opts for tariffs as a mechanism to incentivise mitigation. We are interested in including a climate finance module to explore potential avenues for climate finance, such as green bonds, technology sharing, and carbon pricing.
[1] Bertsekas, Dimitri, and John N. Tsitsiklis. Neuro-dynamic programming. Athena Scientific, 1996.
[2] Farmer, J. Doyne, et al. "A third wave in the economics of climate change." Environmental and Resource Economics 62 (2015): 329-357.
[3] Bernheim, B. Douglas, Bezalel Peleg, and Michael D. Whinston. "Coalition-proof nash equilibria i. concepts." Journal of economic theory 42.1 (1987): 1-12. | Summary: The paper introduces and analyses a climate policy modelling framework for assessing the effect of different international agreemtns on future climate. It introduces RICE-N, a multi-region integrated assessment model that simulates global climate negotiations and agreements using multi-agent reinforcement learning to model strategic decision-making in climate policies. It develops and evaluates two negotiation protocols, Bilateral Negotiation and Basic Club which encourage cooperation among regions to mitigate climate change while balancing economic growth. The results indicate that these protocols have the potential to reduce global temperature rise give the particular simulation environment.
Claims And Evidence: The claims in the submission are generally supported by the evidence, particularly through comparisons of negotiation protocols using multi-agent simulations and integrated assessment modelling. As the claims are made within the context of the RICE-N model, they are supported. Naturally, their applicability to real-world scenarios may be questioned but the paper does not claim to provide policy advice and outlines some possible unintended consequences in the Impact Statement.
Methods And Evaluation Criteria: The proposed methods -- the use of MARL within the RICE-N integrated assessment model -- are suitable for studying strategic climate negotiations, as they allow agents to learn dynamic policies in a multi-region setting.
Theoretical Claims: There are no theoretical claims in the paper apart from the set up of the model that relates back to theoretical understanding of world economy, trade and international negotiations.
Experimental Designs Or Analyses: The experimental results provide some illustrative results for different policies though are not very extensive (e.g. in terms of comparing the effect of different variables, different assignment of regions, the computational considerations in the multi-agent RL inference). The authors mention that a more extensive sensitivity study would require a more efficient implementation of the methodology (e.g. in JAX).
Supplementary Material: I have reviewed parts of the supplement (Parts C and E) to better understand the setup of the model.
Relation To Broader Scientific Literature: The paper includes an extensive literature review on different aspects of the paper, including climate negotiations, climate negotiations and economic actions that affect climate outcomes, as well as some relevant RL literature.
Essential References Not Discussed: I cannot comment on this.
Other Strengths And Weaknesses: The paper is well-written and includes an explanations of different aspects of climate negotiations, reinforcement learning methods, and integrated assessment modelling, making it accessible to a broad audience. Its originality lies in combining multi-agent reinforcement learning with climate-economic modelling, allowing for a more dynamic exploration of international climate agreements compared to static game-theoretic approaches. The availability of the implementation and the modularity of the it should make it easy for other users to try out their own approaches.
While the paper presents an interesting application of multi-agent reinforcement learning, its primary focus on climate economics and policy modelling may make it less suitable for a machine learning venue. To the best of my understanding, the technical ML contributions, such as improvements to MARL methods or novel learning dynamics, are limited, and the paper leans more toward applying existing ML techniques rather than advancing them. While it may be of interest to an ML audience due to potential future directions (improving scalability with JAX or more advanced RL methodology), I would suggest that the extensions are suitable for ML audience while this paper may be better received at a climate venue.
Other Comments Or Suggestions: 208, column 2: clarify that the link is to **Section** 6.
Questions For Authors: Could you clarify what you mean by, the climate, economic and trade components are **loosely** coupled?
Most of the results contain some uncertainty estimates but I could not find the exact explanation of its origin. Could you explain or reference the specific part of the paper that details the source the stochasticity? Could you then give some intuition of why the uncertainty seems so small for most models and what changes to the model or the inference is likely to have a significant effect on the uncertainty?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for the thoughtful review and for highlighting the positive aspects, such as RICE-N’s suitability for studying strategic climate negotiations, the evidence-based claims, and the originality of our MARL application. We are pleased that you consider both the paper and the code accessible, and we hope that our response clarifies any outstanding concerns.
### > Suitability for ICML.
Thank you for voicing your concerns. We believe that the application of MARL to a climate economic negotiation integrated assessment model provides a relevant methodological contribution to the Application-Driven Machine Learning track of ICML. Beyond its contribution to topics mentioned in the call for papers such as social sciences, and sustainability and climate for which the ML community demonstrates interest through concurrent work on climate investment [1], as well as the many potential extensions that are interesting to the ML community, such as the integration of LLMs into negotiation [2], this work also provides a useful testbed for topics of interest to MARL researchers, such as studying multi-party cooperation between AI agents in sequential social dilemmas [3].
[1] Hou, X., et al. (2025). InvestESG: A multi-agent reinforcement learning benchmark for studying climate investment as a social dilemma. In ICLR 2025.
[2] Vaccaro, M., et al. (2025). Advancing AI negotiations: New theory and evidence from a large-scale autonomous negotiations competition. arXiv preprint arXiv:2503.06416.
[3] Leibo, J. Z., et al. (2017). Multi-agent reinforcement learning in sequential social dilemmas. In Proceedings of the 16th AAMAS. ACM.
### > Additional experimental analysis on effects of variables.
Since the space of possible configurations is large, we perform a sensitivity analysis over a subset of economically relevant parameters, namely the discount factor, welfare loss weight, consumption substitution rate and relative preference for domestic goods. This analysis showcases the robustness of our findings. We will add it to the appendix and reference it in the main text. We plot heatmaps of the analysis here: https://imgur.com/a/W0194Ej . We show the percentage change in outcome variables of interest across different scenarios when critical model parameters are perturbed by a multiplication factor ranging from 0.96 to 1.04. The max percentage change is 3.16% while mean is -0.22% and medium is -0.36%. We thus conclude the dynamics are stable, corresponding to changes in critical model parameters.
We will also include a discussion on the computational complexity of RICE-N (please see our response to QTAV).
### > 208, column 2: clarify that the link is to Section 6
Thank you for spotting this.
### > possible unintended consequences
We wish to highlight the importance of qualifying these claims by discussing the potential unintended consequences of climate clubs being implemented without redistributive financing and technology sharing. Uniform tariffs on developing countries with lower mitigation rates would effectively serve as a tax on less developing countries, which we do not advocate for [4,5]. Our goal is to create a simulation framework where these dynamics and alternative policies can be explored and cross compared. We will give an account of these points in the main text of the camera-ready version.
[4] Goldthau, A., & Tagliapietra, S. (2022). How an open climate club can generate carbon dividends for the poor. Bruegel-Blogs.
[5] Perdana, S., & Vielle, M. (2022). Making the EU Carbon Border Adjustment Mechanism acceptable and climate friendly for least developed countries. Energy Policy, 170, 113245.
### > loosely coupled
To clarify: this comment refers to the structure of the code, not any functional difference. We mean that we try to reduce as much as possible the number of assumptions that each component must make about the other components, and make the necessary dependencies between dynamics both explicit and local [6]. This makes extensions to the existing codebase much easier to implement, which makes testing new ideas, such as novel negotiation protocols, much easier.
[6] Leymann, F. (2016, September 5–7). Loose coupling and architectural implications. Keynote address presented at the ESOCC, Vienna, Austria.
### > uncertainty estimates
The uncertainties arise from the stochasticity of the learned policy as we sample actions from the policy's distribution during evaluation. We estimate uncertainty across 50 rollouts with varying seeds (see Section 6, paragraph “Experimental Setup”). The relatively small uncertainty shows that the agents have learned robust policies. An increase could indicate that the learned policy is less reliable, potentially due to insufficient training or the model's inability to generalize effectively. Adding uncertainty to the environment (e.g., the climate component) or relevant parameters (see sensitivity analysis) would likely result in an increase of the uncertainty.
---
Rebuttal Comment 1.1:
Comment: Thank you for your responses. I particularly appreciate the clarification regarding the suitability for the venue and I'm happy to update my recommendation.
I would suggest adding a more careful discussion of uncertainty estimates and sensitivity analysis as pointed out by other reviewers to the final version of the paper.
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Reply to Comment 1.1.1:
Comment: Thank you for your kind feedback and for updating your recommendation. We appreciate your constructive suggestion and will incorporate a more detailed discussion on uncertainty estimates and sensitivity analysis in the final version of the paper, as recommended. | Summary: The paper introduces RICE-N, a multi-region integrated assessment model designed to simulate global climate negotiations, agreements, and long-term cooperation using multi-agent reinforcement learning (MARL). The model extends the Regional Integrated Model of Climate and Economy (RICE) by incorporating negotiation protocols and international trade dynamics. The authors propose two negotiation protocols: Bilateral Negotiation and Basic Club, inspired by real-world climate policy mechanisms like Climate Clubs and the Carbon Border Adjustment Mechanism (CBAM). The main findings are that both negotiation protocols significantly reduce temperature growth and carbon emissions compared to a no-negotiation baseline, with only a minor drop in production. The Basic Club protocol, in particular, achieves a balance between emissions reduction and economic growth, outperforming the no-negotiation baseline in the long term. The paper also highlights the importance of equitable burden-sharing in climate agreements, as measured by the Gini Index.
Claims And Evidence: The claims made in the paper are generally supported by clear and convincing evidence. The authors provide detailed simulations and comparisons between different negotiation protocols and baselines, showing the impact on global temperature, carbon emissions, and economic output. The use of MARL to model strategic behavior in climate negotiations is well-justified, and the results are presented with appropriate statistical measures (e.g., mean ± 1.96 standard error). However, the paper could benefit from more detailed sensitivity analyses to demonstrate the robustness of the results to different parameter settings or model assumptions.
Methods And Evaluation Criteria: The proposed methods and evaluation criteria are appropriate for the problem at hand. The use of MARL to model strategic interactions in climate negotiations is innovative and well-suited to the complex, dynamic nature of global climate cooperation. The evaluation criteria, including global temperature anomaly, carbon emissions, and economic output, are standard metrics in climate-economic modeling. The inclusion of the Gini Index to measure inequality in emission reduction costs and consumption adds a valuable dimension to the analysis, addressing the equity concerns often raised in climate negotiations.
Theoretical Claims: The paper does not present any formal theoretical claims or proofs, so there are no theoretical issues to evaluate. The focus is on empirical results from simulations, which are well-documented and supported by the data.
Experimental Designs Or Analyses: The experimental design is sound, with clear comparisons between different negotiation protocols and baselines. The authors train five models (Basic Club, Bilateral Negotiation, no negotiation, maximum mitigation, and minimum mitigation) and evaluate them over 50 rollouts to ensure statistical robustness. The results are presented with appropriate confidence intervals, and the authors discuss the implications of their findings in detail. One potential limitation is the lack of sensitivity analysis to different parameter settings, which could strengthen the robustness of the results.
Supplementary Material: The supplementary material includes detailed descriptions of the model parameters, variables, and calibration procedures. It also provides additional figures and tables that support the main findings of the paper. The supplementary material is well-organized and complements the main text effectively.
Relation To Broader Scientific Literature: The paper is well-situated within the broader scientific literature on climate-economic modeling and game-theoretic approaches to climate negotiations. The authors draw on prior work in integrated assessment models (IAMs) like DICE and RICE, as well as recent advances in MARL. The paper extends this literature by incorporating negotiation protocols and international trade dynamics, which are critical for modeling real-world climate agreements. The use of MARL to model strategic behavior in climate negotiations is a novel contribution that bridges the gap between climate economics and machine learning.
Essential References Not Discussed: The paper adequately covers the relevant literature, but it could benefit from a more detailed discussion of recent work on MARL in climate-related applications. For example, recent papers on MARL for energy systems optimization or climate policy design could provide additional context for the use of MARL in this domain. Additionally, the paper could discuss more recent developments in climate clubs and carbon border adjustment mechanisms, which have been the subject of ongoing policy debates.
Other Strengths And Weaknesses: Strengths:
1. The paper addresses a critical and timely issue in climate policy, namely the challenge of achieving global cooperation on climate change mitigation.
2. The use of MARL to model strategic behavior in climate negotiations is innovative and well-executed.
3. The inclusion of international trade dynamics and negotiation protocols adds realism to the model and provides valuable insights into the design of effective climate agreements.
4. The paper provides a comprehensive analysis of the equity implications of different negotiation protocols, which is often overlooked in climate-economic modeling.
Weaknesses:
1. The paper could benefit from a more detailed sensitivity analysis to demonstrate the robustness of the results to different parameter settings or model assumptions.
2. The discussion of the real-world applicability of the Basic Club protocol could be expanded, particularly in light of ongoing policy debates on carbon border adjustment mechanisms.
3. The paper could provide more details on the computational requirements of the MARL approach, particularly for large-scale simulations with many regions.
Other Comments Or Suggestions: 1. The paper is well-written and clearly organized, but it could benefit from a more detailed discussion of the limitations of the model, particularly in terms of its assumptions about agent behavior and the real-world applicability of the negotiation protocols.
2. The authors should consider adding a discussion of the potential policy implications of their findings, particularly in light of ongoing international climate negotiations.
Questions For Authors: ## Sensitivity Analysis
**Question:** Have the authors conducted a sensitivity analysis to test the robustness of the results to different parameter settings or model assumptions? If so, could they provide more details on the findings?
**How this affects my evaluation:** If the authors can demonstrate that the results are robust to different parameter settings, it would strengthen the validity of their conclusions.
## Real-World Applicability
**Question:** How do the authors see the Basic Club protocol being implemented in real-world climate negotiations, particularly in light of ongoing debates on carbon border adjustment mechanisms?
**How this affects my evaluation:** A more detailed discussion of the real-world applicability of the Basic Club protocol would enhance the practical relevance of the paper.
## Computational Requirements
**Question:** What are the computational requirements of the MARL approach, particularly for large-scale simulations with many regions?
**How this affects my evaluation:** Understanding the computational requirements would help assess the scalability of the approach and its potential for real-world applications.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We thank the reviewer for their favorable assessment regarding the innovativeness and suitability of our chosen approach, as well as the constructive feedback. Below, we carefully address any outstanding concerns:
### > detailed sensitivity analysis
Thank you for this suggestion. We select parameters based on economic theory, which are the discount factor, welfare loss weight, consumption substitution rate and relative preference for domestic goods. This analysis showcases the robustness of our findings. We will add it to the appendix and reference it in the main text. We plot heatmaps of the analysis here: https://imgur.com/a/W0194Ej . In the heatmap, we show the percentage change in variables of interest (including Temperature, Carbon Emissions, GDP) across different scenarios when critical model parameters are perturbed by a multiplication factor ranging from 0.96 to 1.04. The max percentage change is 3.16% while mean is -0.22% and medium is -0.36%. We thus conclude the dynamics are stable, corresponding to changes in critical model parameters.
### > real-world applicability of the Basic Club protocol
Basic Club and carbon border adjustment mechanisms (CBAM) fight carbon leakage by setting the strength of the tariff proportionally to the difference in the cost of carbon between the exporting and importing countries. Basic Club relies on a uniform tariff [1]. In contrast, CBAM targets specific goods, which can exacerbate carbon leakage by leaving large swaths of emissions unaccounted for, such as those produced for non-EU exports. Climate clubs can go further than what is modeled in RICE-N at the moment, hence the term “Basic”. Uniform tariffs, coupled with technology sharing and redistribution, are theorized to be more effective at curtailing carbon leakage [2]. Future work should implement CBAM in RICE-N, which requires disaggregating production and trade by sector to allow for targeted tariffs. This is currently a work in progress and high on our agenda.
[1] Overland, I., & Huda, M. S. (2022). Climate clubs and carbon border adjustments: A review. *Environmental Research Letters*, 17(9), 093005.
[2] Tarr, D. G., Kuznetsov, D. E., Overland, I., & Vakulchuk, R. (2023). Why carbon border adjustment mechanisms will not save the planet but a climate club and subsidies for transformative green technologies may. *Energy Economics*, 122, 1066
### > What are the computational requirements of the MARL approach, particularly for large-scale simulations with many regions?
The computational complexity of our MARL approach is driven by the number of regions N (i.e., agents). Since each agent’s action space scales linearly with N, the total action space across all agents grows quadratically (O(N²)). However, the number of agents in our setting is naturally bounded by the number of countries on the planet. Currently, training 27 agents for 100 thousand episodes takes approximately 3 hours on a 30 CPU cluster. To improve runtime, we are exploring more efficient implementations using JAX-based acceleration and model parallelism, which would enable large-scale sensitivity analyses and experiments.
### > more detailed discussion of recent work on MARL in climate-related applications.
We extend the section on MARL in the appendix with some more references on MARL applied to real-world problems such as:
Hou, X., et al. (2025). InvestESG: A multi-agent reinforcement learning benchmark for studying climate investment as a social dilemma. In *Proceedings of the Thirteenth International Conference on Learning Representations (ICLR)*.
May, R., & Huang, P. (2023). A multi-agent reinforcement learning approach for investigating and optimising peer-to-peer prosumer energy markets. *Applied Energy*, 334, 120705.
Wang, X., et al. (2020). Large-scale traffic signal control using a novel multiagent reinforcement learning. *IEEE Transactions on Cybernetics*, 51(1), 174–187.
### > discussion of the potential policy implications
The policy impacts of climate clubs (and border adjustment mechanisms for that matter) depends on their implementation. Without some degree of redistribution and technology sharing, they risk acting as a tax on carbon locked developing countries [3; 4]. A Loss and damage fund can mitigate that risk [5].
[3] Goldthau, A., & Tagliapietra, S. (2022). How an open climate club can generate carbon dividends for the poor. Bruegel-Blogs.
[4] Perdana, S., & Vielle, M. (2022). Making the EU Carbon Border Adjustment Mechanism acceptable and climate friendly for least developed countries. *Energy Policy*, 170, 113245.
[5] Boyd, E., et al. (2021). Loss and damage from climate change: A new climate justice agenda. *One Earth*, 4(10), 1365–1370.
### > more detailed discussion of the limitations of the model.
Thank you for this suggestion. We will add a clarifying paragraph to the main text describing key assumptions around binding commitments, region preferences, and power imbalances. | null | null | null | null | null | null |
Efficient First-Order Optimization on the Pareto Set for Multi-Objective Learning under Preference Guidance | Accept (spotlight poster) | Summary: This paper considers the problem of preference-guided multi-objective optimization. The authors first formulate it as a semivectorial bilevel optimization problem, which optimizes the upper-level preference objective, subject to the constraint that the model parameters are weakly Pareto optimal or Pareto stationary for the lower-level multi-objective optimization problem. The authors further propose an algorithm to solve this semivectorial bilevel optimization problem, which first converts the lower-level constraint to a single-objective constraint through a merit function, then solves the transformed problem by a penalty-based reformulation. Theoretically, the authors analyze the relations of solutions for different formulations and the convergence of the proposed method. Empirical results on various synthetic and real-world problems demonstrate the effectiveness of the proposed method.
Claims And Evidence: There are two key claims in this work:
- The preference-guided multi-objective optimization problem can be solved through a semivectorial bilevel optimization problem
- The proposed method FOOPS can effectively solved the obtained semivectorial bilevel optimization problem
While the second claim is supported by sound theoretical analysis and empirical results, the first claim seems not sufficiently supported from my perspective. I am a bit confused on how the original formulation for preference-guided multi-objective optimization:
$\min_x F(x), s.t., G(x) \le 0, H(x)=0$
can be re-formulated as
$\min_x f_0(x), s.t., x \in \arg\min F(x)$
I suppose $F(x)$ remains the same, while how are $G(x)$ and $H(x)$ related to $f_0(x)$? Some more explanations are necessary here. Without such explanations, it is even unclear how existing preference-guided multi-objective optimization methods are implemented and if they are solving the same problem.
Methods And Evaluation Criteria: While the proposed method is easy to understand and the evaluation is sufficient, I am a bit curious on whether the proposed method can be combined with other bi-level optimization methods, as is also mentioned in Appendix A.1. Specifically, after converting the lower-level constraint to a single-objective constraint, I suppose the converted problem can be also solved by some bi-level optimization methods other than the penalty-based formulation? Some empirical comparisons can be useful here.
Theoretical Claims: Theoretical analysis in this work is sound and interesting. I have checked the proofs in Appendix B-E and found they are clearly organized and easy to understand without significant errors.
Experimental Designs Or Analyses: Generally the experiments are sufficient with sound analysis.
Supplementary Material: This paper does not have supplementary material.
Relation To Broader Scientific Literature: This paper proposes a novel formulation of preference-guided multi-objective optimization as well as a novel method (based on smoothed merit functions and existing gradient-based bi-level optimization methods) to solve the optimization problem under this formulation.
Essential References Not Discussed: The references are generally complete, and I do not have any works that are strongly recommended to be included.
Other Strengths And Weaknesses: All mentioned in previous parts
Other Comments Or Suggestions: The authors seem to have modified margins in some places, e.g., line 110-116 and line 432-439. This should be strictly forbidden and some reasonable explanation is necessary here.
Questions For Authors: Please see the mentioned points of weakness in the **Claims And Evidence** and **Methods And Evaluation Criteria** part, as well as the possible violation of paper format template.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thanks for acknowledging that **we propose a novel formulation and an easy-to-understand novel method for preference-guided multi-objective optimization, our proof is sound and interesting, and the experiments are sufficient with sound analysis**.
Below we address your concerns point by point. The link to additional results is https://anonymous.4open.science/r/FOOPS-F746/ICML3045_rebuttal.pdf
>**Claims And Evidence:** "The preference-guided multi-objective optimization problem can be solved through a semivectorial bilevel optimization problem" is unclear... How are $G(x)$ and $H(x)$ related to $f_0(x)$? Whether they are solving the same problem?
Yes, $F(x)$ remains the same. The relation of $G,H$ to $f_0$ is that $f_0$ can be chosen as $f_0(x) = ||H(x)||^2 + ||[G(x)]_+||^2$. $f_0$ is minimized when $H(x)=0$ and $G(x)\leq 0$. In our experiments, we show the example for equality-constrained problems without $G$ and with $f_0(x) = ||H(x)||^2$. See Section 6, and Eq. (16) for the speech experiment.
The two formulations are not equivalent mathematically. But both can be applied to preference-guided multi-objective learning with different emphasis on either satisfying preference or achieving weak Pareto optimality. As discussed in Section 3.3 and Section 6 in our paper, the constrained formulation in e.g., PMTL and FERERO with preference modeled by constraints $G$ and $H$ puts more emphasis on satisfying the preference, while the FOOPS formulation with preference modeled by $f_0$ puts more emphasis on achieving weak Pareto optimality.
>**Methods And Evaluation Criteria:** While the proposed method is easy to understand and the evaluation is sufficient, I am a bit curious on whether the proposed method can be combined with other bi-level optimization methods, as is also mentioned in Appendix A.1. Specifically, after converting the lower-level constraint to a single-objective constraint, I suppose the converted problem can be also solved by some bi-level optimization methods other than the penalty-based formulation? Some empirical comparisons can be useful here.
- *Other bilevel methods.*
Thanks for the suggestion. Indeed, the penalty method used in this paper is not the only way to solve a bilevel problem. However, the existing methods listed in Appendix A.1, Table 5 require **different assumptions** which cannot be satisfied by our converted problem. Therefore, the methods in Table 5 cannot be directly applied to our converted problem.
However, we provide a discussion on how some other methods could be applied under certain additional assumptions.
For example, the recent concurrent AGILS (Bai et al., 2024) method can be applied when the merit function $v_{l,\tau}$ has HEB with $\eta \geq 1$.
- *Empirical comparisons.*
Since other existing bilevel methods require different assumptions, they cannot be directly applied to our converted problem. Further investigation is needed to check whether the methods still work under weaker assumptions. The concurrent AGILS (Bai et al., 2024) method may be applied to specific problems satisfying the assumptions therein, which we leave for future work. We provide a comparison to other OPS methods such as PNG in Figure A and Table B in the link.
>**Other Comments Or Suggestions:** The authors seem to have modified margins in some places, e.g., lines 110-116 and lines 432-439. This should be strictly forbidden and some reasonable explanation is necessary here.
Thanks for spotting this. We would like to clarify that **we did not intentionally or explicitly alter the margins**. Instead, we used the {\small } environment in LaTeX to reduce the size of Equations (5) and (16) so they would better fit the space. This inadvertently caused the line spacing for lines 110-116 and 432-439, immediately before the equations, to appear smaller, despite our attempt to limit the {\small } environment to the equations themselves.
In response to the reviewer’s feedback, we will modify the paper to remove this unintended spacing issue.
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We hope our rebuttal resolves the reviewer's concerns and the reviewer can reconsider the rating of our paper. Thanks!
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Rebuttal Comment 1.1:
Comment: I would like to first thank the authors for their detailed reply. Most of my previous concerns are addressed and the authors are encouraged to add the additional clarification in the revised version, as well as fixing the formatting issue. I have also increased my score.
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Reply to Comment 1.1.1:
Comment: Thank you very much for acknowledging our response, engaging in the discussion, and updating your score. Yes, we will incorporate the promised revisions and fix the formatting issue.
Sincerely, authors. | Summary: This paper studies multi-objective optimization with user-specified preferences. The authors formulate the problem as a bilevel optimization problem, where the upper-level is a preference function, and the lower-level problem is the minimization of a smoothed version of merit function. Merit function usually serves as an objective whose solutions are a set of weak Pareto optimal points. The authors provide a comprehensive analysis for the proposed problem. In particular, they first provide some properties of the smoothed merit functions under the assumption that f_m is quasar-convex function. Then, they consider a penalized reformulation of the original bilevel problem. And then they characterize the equivalence between the two problems in terms of global or local solutions, based on the assumption on the global subanalyticity, Holderian error bound and KL inequality. Experiments validate the effectiveness of the proposed method.
Claims And Evidence: Yes.
Methods And Evaluation Criteria: A running time comparison and confidence intervals could be provided.
Theoretical Claims: Check some proofs and did not find main problems.
Experimental Designs Or Analyses: A running time comparison and confidence intervals could be provided. More details
Supplementary Material: Yes, mainly the theoretical proofs. But I did not go through all details.
Relation To Broader Scientific Literature: The idea of using bilevel optimization for preference-based multi-objective optimization is new to the literature.
Essential References Not Discussed: Yes. it includes the most important works on preference-based MOO. However, more related works on differentiable MOO in ML could be provided. For example, PCGrad, CAGrad, NashMTL, MoCo, SDMGrad, where CAGrad and SDMGrad also introduce preference-based regularization or constraints. They should be discussed.
Other Strengths And Weaknesses: Strengths:
1. The studied problem is very important in multi-objective optimization, because we often tend to find a preferred point on the Pareto front. The bilevel optimization perspective seems to be new.
2. The authors analyze the smoothed merit function and the equivalence between the bilevel problem and the panelized problem under some assumptions. Experiments seem to support that the proposed method can get higher accuracy.
Weakness:
1. The paper is not well written. The analysis part makes multiple assumptions. Some theorem requires the convexity-like assumptions, some needs HEB assumption, and later a KL inequality is needed to guarantee the penalty function is less than \epsilon. I suggest explicitly point out all assumptions in before the theorems.
2. The motivation of smoothing the merit function is not very clear to me. I understand that the original merit function could be non-differentiable. It may not be a problem in real-world problems. Can the authors validate this in the experiments to see if smoothing is necessary?
3. Another issue for this smoothing is that it introduces two more hyperparameters \tau and l. Can the authors explain how they select these hyperparameters in practice? Ablation studies should be provided.
4. The assumptions could be quite strong. The point strong quasar-convexity assumption is hard to be satisfied in practical problems. Although the authors mention some examples such as linear models with leaky ReLU, for general setups, it may be hard to validate this assumption. In addition, the subanalyticity and the KL inequality assumptions further make the analysis less applicable to the practical cases. It would be great if the authors could provide some justification that the problems in the experiments could satisfy these assumptions (it is ok if just partially)?
5. In lemma 3.4, what does it mean by X_v^* \cap X_C is globally subanalytic. The assumption 2 is made on the function rather than the set. Perhaps a definition on subanalyticity should be provided.
6. In theorem 3.5, what is the definition of $(\epsilon,\delta)$-global solution for (CP)?
7. The algorithm is complex, containing multiple hyperparameters like $\tau, l, \gamma_t, K_t, \alpha_t,\beta_t$, as well as two projections in steps 5 and 8. Compared to previous methods like EPO, FERERO, this is less appealing.
8. Experiments results are not convincing. In table 4, it is very close to FERERO-FT. Then, multiple seeds with confidence interval should be provided. A running time comparison could be provided to further justify the efficiency compared to FERERO.
Other Comments Or Suggestions: see the strengths and weaknesses.
Questions For Authors: see the strengths and weaknesses.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thanks for acknowledging that the problem is important and the bilevel perspective is new. We would like to emphasize that the bilevel problem in this paper with *non-convex vector-valued lower-level objective* is much more challenging and nontrivial, as pointed out by Reviewer XkmK.
Below we address your concerns. The link to additional results is https://anonymous.4open.science/r/FOOPS-F746/ICML3045_rebuttal.pdf
>W1.Writing&assumptions not clear... Explicitly point out all assumptions before the theorems.
It might be a misunderstanding that the HEB and KL conditions are assumed. Instead of directly assuming them, **we prove them** based on the properties of $F$.
In our theorems, we list all the required assumptions in the beginning and then discuss other conditions that can be proved. We will clarify this.
>W2.Motivation of smoothing the merit function ...Validate this in the experiments?
Smoothing is commonly used for nonsmooth optimization problems, whose motivation is well-studied in prior works, e.g. [R1] and references therein. [R1] shows that smoothing is necessary for finite-time convergence of nonconvex nonsmooth problems using any algorithm. Therefore, we use LSE to smooth the max-min nonsmooth $\bar{u}$ to ensure finite-time convergence, which is widely used in prior works, e.g. [R2]. In our experiments, we find that without smoothing, it could return NaN (not a number) errors and the algorithm could diverge.
[R1] Deterministic Nonsmooth Nonconvex Optimization. M.I. Jordan, et. al. COLT 2023.
[R2] An alternative softmax operator for reinforcement learning. Kavosh Asadi, et. al. ICML 2017.
>W3.Smoothing introduces hyperparams. \tau and l. How to select them? Provide ablation studies.
We choose $\tau,l$ to be small and to ensure differentiability. We use grid search to tune them. See more details in Appendix F. We provide an ablation study in Table C in the link.
>W4.The assumptions could be strong...The subanalyticity&KL assumptions make the analysis less applicable...Justification of problems in the experiments satisfying these assumptions (ok if partially)?
Note that compared to existing works for OPS (Table 2) and bilevel optimization (Table 5), which usually require convexity or PL assumptions, our assumptions are actually much weaker. The subanalylticity and KL conditions are weaker than PL, see more discussions in Appendix C with examples justifying the assumptions.
>W5.In lemma 3.4, meaning of global subanalyticity?...A definition should be provided.
We have mentioned in the main paper, lines 204-216 that, the definition of (global) subanalyticity, including both subanalytic functions and sets is provided in Appendix C, Definitions C.1 and C.2.
>W6.In theorem 3.5, what is the definition of $(\epsilon,\delta)$-global solution for (CP)?
The $(\epsilon,\delta)$-global solution for (CP) is that, $f_0(x) - \min_{x\in {\cal X}_{\delta}} f_0(x) \leq \epsilon, x\in {\cal X}_{\delta} = \{x \in {\cal X} \mid v_{l,\tau}(x) + \tau\ln M \leq \delta \}.$ This is a widely used definition for constrained optimization.
>W7.The algorithm is complex, containing multiple hyperparameters like $\tau, l, \gamma_t, K_t, \alpha_t,\beta_t$, as well as two projections in steps 5 and 8. Compared to previous methods like EPO, FERERO, this is less appealing.
This might be a misunderstanding. The algorithm is general such that it can be applied to both the cases when $\cal X$ is compact and when ${\cal X} = R^q$.
When ${\cal X} = R^q$, the two projections are not needed, which is the case in our experiments. $K_t$ can be chosen to be small like 1 or 2. As a comparison, FERERO also requires choosing hyperparameters such as $\alpha_t,\gamma_t,K,c_g,c_h$. So the number of hyperparameters is similar. They do not make FOOPS more complex or inefficient.
We do provide a run time in Appendix F, Table 10 in the paper, and Table A in the link to show FOOPS is comparable or more efficient than FERERO.
>W8&**Methods&Evaluation&Experiment**: Experiments are not convincing. In Table 4, it is very close to FERERO-FT ...confidence interval... A running time comparison could be provided to further justify the efficiency compared to FERERO.
We respectively disagree. We show in Table 3 that FOOPS achieves much better hypervolume compared to FERERO and other baselines. In Table 4, it achieves comparable average performance as FOOPS. So we believe our result demonstrates FOOPS is effective, as *acknowledged by all other reviewers*. This experiment takes much longer time. We will run additional experiments add the confidence in the revision.
Running time comparison is given in Appendix F, Table 10 in the paper, and Table A in the linked PDF. Results show FOOPS can be faster than FERERO.
>**References:** More works on differentiable MOO could be discussed.
Thanks, we will include a discussion in the revision.
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We hope we have addressed your concerns and you can reconsider the rating of our paper. Thanks!
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Rebuttal Comment 1.1:
Comment: Apologize for the late response. I thank the authors for the detailed response. My concerns have been resolved and I increase my score accordingly. I highly suggest the authors add the related works and the discussion I mentioned in the final revision.
Best,
Reviewer
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Reply to Comment 1.1.1:
Comment: Thank you very much for acknowledging our response, engaging in the discussion, and updating your score. Yes, we will incorporate the promised revisions and other related works.
Sincerely, authors. | Summary: In this work, the authors frame preference-guided multi-objective learning as an optimization problem on the Pareto set and propose a first-order penalty method to address it, where the penalty function is a polynomial of a smoothed merit function. They begin by establishing key properties of the merit function, including its connection to weak Pareto optimality and the Hölderian error bound. Next, they examine the relationship between solutions of the penalty reformulation and those of the original problem. Finally, they present algorithms for solving the penalty problem and analyze their convergence guarantees.
Claims And Evidence: I find it unclear how the authors incorporate Preference Guidance in this paper. If Preference Guidance were replaced with another objective function, the overall formulation would remain largely unchanged, raising questions about its specific role and impact.
Methods And Evaluation Criteria: I believe there is still a missing component in the problem reformulation. The authors only establish the connection between CP and PP, but it would be helpful if they could also provide insights into the relationship between (1) and CP.
Theoretical Claims: In Proposition 3.2, where $\epsilon = \tau \ln M$, $\epsilon$ can become quite large as $M$ increases. Would it be better to choose $\tau$ as a function of $M$ rather than a constant, ensuring that $\epsilon$ remains sufficiently small?
Experimental Designs Or Analyses: The baselines used in the experimental section are incomplete. I suggest that the authors compare their algorithms with those listed in Table 2 for a more comprehensive evaluation.
Supplementary Material: I have reviewed Appendices D and E.
Relation To Broader Scientific Literature: The experimental results appear promising. After incorporating comparisons with additional baselines, it would be beneficial to scale up the approach and explore its potential applications in larger models.
Essential References Not Discussed: I did not find any essential references that are missing.
Other Strengths And Weaknesses: Strengths:
1. This paper improves the theoretical results of optimization on the Pareto set by removing the strong convexity assumption in (Roy, 2023) and provides stronger convergence guarantees compared to (Ye, 2022).
2. The applications of this type of optimization problem are broad. The paper presents an algorithm to solve such problems, which has the potential to be scaled up to some large-scale applications.
Weaknesses:
1. How should $\tau$ and $l$ be chosen both theoretically and in practice for the merit function?
2. Theorem 3.6, 3.7, and 3.9 appear to be direct adaptations from (Shen, 2023) with only minor modifications.
3. The convergence analysis is relatively trivial, as it primarily leverages results from well-known optimization algorithms.
References:
[1] Roy, A., So, G., and Ma, Y.-A. Optimization on Pareto sets: On a theory of multi-objective optimization. arXiv preprint arXiv:2308.02145, 2023.
[2] Ye, M. and Liu, Q. Pareto navigation gradient descent: a first-order algorithm for optimization in Pareto set. In Uncertainty in Artificial Intelligence, pp. 2246–2255, 2022.
[3] Shen, H., Xiao, Q., and Chen, T. On penalty-based bilevel gradient descent method. arXiv preprint arXiv:2302.05185, 2023.
Other Comments Or Suggestions: No
Questions For Authors: See Theoretical Claims, Experimental Designs Or Analyses, and Other Strengths And Weaknesses.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thanks for acknowledging that we consider BLO with *non-convex vector-valued lower-level objective* with stronger guarantees, which is different from prior works, and the experiment results are promising.
We would like to emphasize that the *non-convex vector-valued lower-level objective* is much more challenging and nontrivial, as also pointed out by Reviewer XkmK.
Below we address all your concerns. The link to additional results is
https://anonymous.4open.science/r/FOOPS-F746/ICML3045_rebuttal.pdf
>**Claims:** How to incorporate Preference Guidance...
This might be a misunderstanding. In our paper, the preference guidance was not replaced with another objective from $F$, but was enforced via a new upper-level preference objective $f_0$.
Our experiments include the preference vector guided problems with $f_0(x) = ||H(x)||^2$, and $H(x)=0$ describing the preference vector; see Section 6. See also the response to **Reviewer SqKr-Claims**. We will clarify this.
>**Broader Literature:** ...scale up to applications in larger models.
We have experiments for larger models for speech recognition. See Section 6, Table 4. The model size is around 64.5M, with more details provided in Appendix F.
>**Methods&Evaluation:** Relationship between (1) and CP.
In our paper, below Eq. (CP), we have discussed that as $l,\tau \downarrow 0$, (1) and (CP) are equivalent. For $\tau \downarrow 0, l>0$, (1) and (CP) are equivalent under conditions in Proposition 3.2-2-b). Moreover, by Proposition 3.2, the approximate solutions to (CP) with $v_{l,\tau}(x) + \tau \ln M \leq \epsilon$ are $\epsilon'$-weak Pareto optimal. Therefore, an $\epsilon$-global/local solution $x$ to (CP) satisfies that it is global/local $\epsilon'$-weakly Pareto optimal, and that $f_0(x)\leq f_0(x^*)$, with $x^*$ being the global/local solution to (1). We will add this discussion in the modified paper.
>**Theoretical Claims:** In Proposition 3.2, $\epsilon=\tau\ln M$,... choose $\tau$ as a function of $M$...?
Yes. In our experiments, $M$ is fixed for a problem, and $\tau$ is chosen according to $M$, so we can ensure $\epsilon$ to be sufficiently small.
>**Experimental Designs/Analyses:** ...Compare with methods listed in Table 2.
It is hard to compare with the methods since they do not provide open-source code. Furthermore, these methods require different assumptions that cannot be satisfied in our case. For example, for the lower-level objective, PMM and TAWT require strong convexity or invertible Hessian, which does not hold in our problems. So these methods cannot be applied.
As per the reviewer's request, we implement PB-PDO and PNG. Figure A and Table B in the linked PDF summarize the results, which show they sometimes cannot converge to the Pareto front, and they achieve worse hypervolumes compared to FOOPS.
>W1.How should $\tau$ and $l$ be chosen theoretically and in practice?
As discussed in Section 3.1, theoretically, smaller $\tau$ approximates $\bar{u}$ better, but also increases the smoothness constant. We need to choose $l \geq \ell_{f,1}$ to ensure $\nabla v_{l,\tau}$ exists and can be computed. In practice, we choose relatively smaller $\tau$ and $l$ but not smaller such that $v_{l,\tau}$ is not differentiable. Detailed choices are provided in Appendix F.
>W2.Thm 3.6, 3.7, and 3.9 appear to be direct adaptations from (Shen, 2023)...
We respectively disagree. The theorems compared to (Shen, 2023) are not minor. In (Shen, 2023), the focus is on a scalar lower-level objective satisfying the QG condition (a special case of HEB with $\eta=2$). Directly applying the results from (Shen, 2023) is impossible as we can only make assumptions on objective $F$, but not on $v_{l,\tau}$, and $v_{l,\tau}$ does not satisfy this condition even if $F$ satisfies. In comparison, our theories require much weaker assumptions, as discussed in Appendix A.1, lines 749-756. In addition, (Shen, 2023) assumes the QG holds on the entire domain. However, the exponential function in our case is not globally subanalytic on the whole domain (Remark C.9). Instead, we can prove that $v_{l,\tau}$ is globally subanalytic on any bounded subanalytic set given that the objective $F$ is subanalytic. Thus, the HEB holds on the bounded subanalytic set, which is the base of the proof for Thm 3.6, 3.7, and 3.9.
>W3.Convergence analysis is relatively trivial...
We respectively disagree. Our main contribution is to **convert the challenging semivectorial bilevel optimization problem to a simpler penalty problem** with guarantees on their relations, and easy-to-evaluate gradients for the penalty problem. Building upon this, the convergence of the penalty problem can be analyzed using existing tools.
By converting challenging problems to simpler ones, we have a simple convergence analysis. This actually shows the *strength rather than weakness* of our method.
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We hope the concerns are addressed and the reviewer can reconsider the rating of our paper. Thanks!
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Rebuttal Comment 1.1:
Comment: Thanks to the authors for the rebuttal. I have a follow-up question regarding "Relationship between (1) and CP".
I am wondering why you do not have a definition of $\epsilon$-stationary solution for CP. Why is the gradient-based formula (10) needed here? It seems like (10) is only needed for the definition of an $\epsilon$-stationary solution. The relation between CP and (10) is also not clear to me.
Since the authors have addressed most of my concerns, I’ve updated my score accordingly.
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Reply to Comment 1.1.1:
Comment: Thank you very much for engaging in the discussion and the follow-up questions. Indeed, a proper definition of a stationary condition of CP is a delicate issue in our studied problem and one of our contributions. We will answer your questions point by point as follows.
**1. Why not use $\epsilon$-stationary solution for CP.** A commonly used stationarity condition is the $(\epsilon,\epsilon')$-KKT condition for the constrained problem CP, which is defined as $v_{l,\tau}(x)\leq \epsilon, ||\nabla f_0(x) + \nabla v_{l,\tau}(x) w || \leq \epsilon'$, with $w$ being a bounded scalar. However, it has been proved in prior works [Liu et al. 2022, Section 4.1; Xiao et al. 2023, Example 1] that for the bilevel problem, the KKT condition of CP is not a necessary optimality condition when the KL exponent of $v_{l,\tau}$ is in a certain range, e.g. exponent $\alpha_v=2$, which reduces to the PL condition. Therefore, it is not suitable to directly use the KKT condition of CP as a stationarity measure.
**2. The need of formula (10).** The above discussion shows KKT condition for CP cannot be used. Nevertheless, when the lower-level objective satisfies certain conditions such as the KL condition, then the KKT condition of the reformulated problem (10) is a necessary optimality condition. This is proved in our paper in Appendix D.4, Lemma D.7, which shows that the calmness constraint qualification in Definition D.6 holds under the KL condition, justifying that the KKT condition of the reformulated problem (10) is a necessary optimality condition to (10). This type of reformulation exists and has been justified in prior works [Liu et al. 2022, Eq(3); Xiao et al. 2023, Eq(3)], but only for PL lower-level objective. And (10) is equivalent to CP under the KL condition as detailed in the next point.
**3. Relation between CP and (10).** (10) is an equivalent reformulation of CP when the lower-level objective $v_{l,\tau}(x)$ or $p(x)$ satisfies the KL condition. This is because under the KL condition, $\nabla p(x)=0$ is equivalent to $p(x)=0$, and thus equivalent to $v_{l,\tau}(x) + \tau\ln M=0$. Similar discussions exist in prior works [Liu et al. 2022, Section 4.1; Xiao et al. 2023, Section 2.1], but only under the PL condition (i.e. exponent $\alpha_p=2$).
Due to limited space, a brief discussion is provided below Theorem 3.9, and a detailed discussion is provided in Appendix D.4 in the paper. We will further clarify these questions in the revision. We hope our answers address your questions and that you will reconsider the rating of our paper. We are willing to address any follow-up questions the reviewer may have.
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Thank you very much for acknowledging our response, engaging in the discussion, and updating your score. We will incorporate the promised revisions to improve our paper.
Sincerely, authors
>References
>Liu, B., Ye, M., Wright, S., Stone, P., and Liu, Q. "BOME! Bilevel optimization made easy: A simple first-order approach." NeurIPS, 2022.
>Xiao, Q., Lu, S., and Chen, T. "An alternating optimization method for bilevel problems under the Polyak Łojasiewicz condition." NeurIPS, 2023. | Summary: This paper proposes a new method for solving the semivector bilevel optimization problem. The authors first reformulate the multi-objective subproblem as a single objective constraint and then use a penalty-based method to solve the reformulated optimization problem. The results demonstrate the effectiveness of the proposed method in finding preference-guided optimal solutions to the multi-objective problem.
Claims And Evidence: I think all the claims have been well supported by clear and convincing evidence.
Methods And Evaluation Criteria: I think the proposed methods are well-evaluated.
Theoretical Claims: I have checked the proof.
Experimental Designs Or Analyses: I have checked the experimental designs.
Supplementary Material: I have reviewed Appendix A.
Relation To Broader Scientific Literature: The key contribution of this paper is proposing a new method for solving the challenging semivector bilevel optimization problem.
Essential References Not Discussed: I think the author should discuss some related work. (See Comments 2)
Other Strengths And Weaknesses: Strengths:
1. I think this paper is clearly written and easy to understand.
2. The solved semivector bilevel optimization is very challenging. This paper proposes an efficient method to solve it with a strong theoretical guarantee.
3. The experimental result is intuitive and demonstrates the authors' claims.
Other Comments Or Suggestions: 1. Lacking analysis on computational cost. The authors should provide the order of computational cost and memory cost per iteration, and provide the table of real running time for each method.
2. In Appendix A, the authors discuss several works on bi-level optimization (BLO). However, I suggest they also provide a discussion on multi-objective bi-level optimization (MOBLO) problems, as explored in [1-5]. The key difference between semivector bi-level optimization and multi-objective bi-level optimization is that the former involves solving multiple objectives at the lower level, making it significantly more challenging.
3. Typo: The author should pay attention to the consistency of the punctuation at the end of the formulas; some formulas end with a period, while others do not.
4. The experiment on the multi-patch image classification problem (using Multi-Fashion+MNIST) is relatively simple and may not fully demonstrate the capabilities of the proposed method. Could the authors conduct experiments on more challenging and widely used datasets, such as Office-31 or Office-Home?
5. It seems the number of objectives in the LL subproblem is small in the experiments. Could the authors conduct experiments on more challenging settings, $M>20$ ?
[1] Gu et al. Min-max multi-objective bilevel optimization with applications in robust machine learning. ICLR, 2023.
[2] Ye et al. AFirst-Order Multi-Gradient Algorithm for Multi-Objective Bi-Level Optimization, ECAI 2024.
[3] Ye et al. Multi-Objective Meta-Learning, AIJ 2024.
[4] Yang et al. Gradient-based algorithms for multi-objective bi-level optimization, Science China Mathematics, 2024
[5] Fernando et al. Mitigating gradient bias in multi-objective learning: A provably convergent approach. ICLR, 2023.
Questions For Authors: No other questions.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thanks for supporting our work, acknowledging that **we propose a new efficient method to solve a very challenging semivectorial bilevel optimization problem, with a strong theoretical guarantee, and with intuitive experimental result demonstrating the authors' claims**.
We address your other comments below. The link to the additional results is
https://anonymous.4open.science/r/FOOPS-F746/ICML3045_rebuttal.pdf
>1.Lacking analysis on computational cost. Provide the order of computational cost and memory cost per iteration, and the real running time for each method.
Thanks for the suggestion. In Appendix F, Table 10, we have provided the real running time for each method. We add the memory cost per-iteration in Table A in the link.
>2.In Appendix A, the authors discuss several works on bi-level optimization (BLO). I suggest they also provide a discussion on multi-objective bi-level optimization (MOBLO) problems, as explored in [1-5]...
Thanks for the suggestion. We will incorporate these works in our paper.
>3.Typo: consistency of the punctuation at the end of the formulas.
Thanks for the suggestion. We will check to ensure the consistency of the punctuation.
>4.The experiment on the multi-patch image classification problem (using Multi-Fashion+MNIST) is relatively simple and may not fully demonstrate the capabilities of the proposed method. Could the authors conduct experiments on more challenging and widely used datasets, such as Office-31 or Office-Home?
We have included the experiment for larger models in our paper for speech recognition; see e.g., Table 4 in Section 6. The model size is around 64.5M, much larger than the image classification problem. More details are provided in Appendix F. The benchmarks Office-31 and Office-Home suggested by the reviewer are designed for multi-task learning, but not for preference-guided multi-objective learning studied in this paper, thus not very suitable for our problem. To do such experiments, we need to first define a preference objective $f_0$, then conduct the experiments using our method. We will include the results in the revision.
>5.It seems the number of objectives in the LL subproblem is small in the experiments. Could the authors conduct experiments on more challenging settings, $M>20$?
Theoretically, our method can be used for a larger $M$ without significantly increasing complexity. We test this on a toy problem with $M=25$ and report the running time till convergence in Table A in the linked PDF, the last row, which shows the run time can be much shorter compared to FERERO. The problem is defined as
$f_m(x) = (x - m)^2, m\in [M]$, $H(x) = f_1(x) - f_2(x)$, and $f_0(x) = ||H(x)||^2$. $x$ is initialized to be $100$. We will find some other real-world problems with more objectives and include the experiments in the revised paper.
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We hope the concerns are addressed and the reviewer can continue to support our paper. Thanks!
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Rebuttal Comment 1.1:
Comment: Thanks for the authors' responses. My concerns have been solved, and I will keep my positive score.
Here are some other suggestions.
In some BLO papers, such as "A Generic Descent Aggregation Framework for Gradient-Based Bi-Level Optimization," they call this kind of BLO a simple BLO where there is only one variable. I wonder whether we can call this problem (Problem 1) semivector bilevel optimization, because naturally, we will have UL variables and LL variables, but the solved problem only has one variable.
The authors should write the convergence metric in a separate section and include the discussion of theoretical analysis challenges in the paper.
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Reply to Comment 1.1.1:
Comment: Thank you for the follow-up reply and the consistent support!
Thank you for the suggestions.
1. Yes, it would be more accurate to call (Problem 1) a semivector simple bilevel optimization problem. We will revise the paper accordingly.
2. We have highlighted some theoretical analysis challenges in the introduction and remarks. Following your suggestion, we will write the convergence metric in a separate section and include a more detailed discussion of theoretical analysis challenges in the main paper.
Since you are an expert in the field, it would be great if you could champion our paper! Much appreciated!
Sincerely, Authors | null | null | null | null | null | null |
QEM-Bench: Benchmarking Learning-based Quantum Error Mitigation and QEMFormer as a Multi-ranged Context Learning Baseline | Accept (poster) | Summary: This paper presents QEM-Bench, a benchmarking suite for machine learning-based quantum error mitigation (ML-QEM), addressing the lack of standardized datasets in the field. The benchmark includes twenty datasets spanning different circuit types and noise models to enable consistent evaluation of ML-QEM techniques. The authors also propose QEMFormer, a two-branch architecture incorporating MLPs for short-range dependencies and Graph Transformers for long-range dependencies, leveraging directed acyclic graph (DAG) representations of quantum circuits. Empirical evaluations show QEMFormer outperforms other ML-QEM baselines across diverse settings, reinforcing the claim that a structured representation enhances mitigation performance.
Claims And Evidence: 5/10
While the paper makes strong claims about the benefits of QEM-Bench and QEMFormer, the supporting evidence is limited in some areas. The benchmark provides a well-structured dataset, but its generalizability to real-world quantum hardware is not thoroughly demonstrated. The experimental results highlight improvements over prior ML-based approaches, but the paper does not compare against traditional QEM techniques like Zero-Noise Extrapolation (ZNE) in real-device settings. The justification for QEMFormer’s performance lacks ablation studies isolating the contributions of different architectural components.
Methods And Evaluation Criteria: 6/10
The proposed evaluation framework is well-motivated, and QEM-Bench is a meaningful contribution. However, there are inconsistencies in evaluation settings—while the benchmark includes diverse noise models and circuit types, real hardware evaluations are limited to IBM Kyiv, raising concerns about applicability to other quantum architectures. The choice of Root Mean Squared Error (RMSE) as the primary evaluation metric is standard but insufficient, as the robustness of the mitigation method under varying noise intensities remains unexplored.
Theoretical Claims: 4/10
The paper lacks formal theoretical analysis of QEMFormer’s effectiveness beyond empirical results. The use of DAG representations and multi-range feature extraction is intuitively justified but not rigorously analyzed. Claims regarding the preservation of circuit topology and feature locality should be accompanied by theoretical bounds or complexity analyses. The paper cites relevant works on graph-based representations, but it does not explicitly demonstrate why QEMFormer outperforms existing methods from a theoretical standpoint.
Experimental Designs Or Analyses: 6/10
The experiments are comprehensive in terms of dataset coverage. The results confirm QEMFormer’s superiority over prior ML-QEM methods. While the authors benchmark across multiple noise models, hyperparameter tuning details are unclear, and there is no discussion on whether the performance gains hold for circuits larger than those evaluated. Furthermore, real-device evaluations are minimal, limiting the reliability of the reported findings.
Supplementary Material: 4/10
The supplementary material is not explicitly discussed in the main paper, making it difficult to assess its relevance. The utility of the supplementary material is unclear.
Relation To Broader Scientific Literature: 7/10
The paper is well-positioned within the ML-QEM literature, citing relevant works on machine learning for quantum error mitigation, benchmarking efforts, and graph-based circuit representations. However, there is no engagement with broader ML-based circuit optimization techniques, which could provide useful insights.
Essential References Not Discussed: 6/10
Most of the relevant references are cited. However, works on hardware-specific noise mitigation techniques and hybrid classical-quantum optimization strategies are not discussed comprehensively.
Other Strengths And Weaknesses: Strengths:
1. QEM-Bench provides a standardized evaluation suite, which is a valuable asset for the field.
2. QEMFormer’s hybrid approach to short- and long-range dependency modeling is innovative.
3. The inclusion of different noise models and circuit types enhances the credibility of QEM-Bench.
4. The experiments cover multiple baselines, demonstrating QEMFormer’s competitive performance.
5. The paper is well-organized and presents technical details in a clear manner.
Weaknesses:
1. Lack of real-hardware validation beyond IBM Kyiv: Generalizability to other quantum platforms is not demonstrated.
2. Limited ablation studies: The contribution of each architectural component in QEMFormer is not isolated.
3. Minimal theoretical justification: Claims about circuit topology preservation and information retention are not rigorously analyzed.
4. Unclear evaluation criteria: The choice of RMSE as the sole metric does not provide a full picture of mitigation effectiveness.
5. Limited engagement with non-ML QEM methods: The paper does not sufficiently compare QEMFormer with traditional mitigation techniques.
Other Comments Or Suggestions: 1. Include additional real-device evaluations beyond IBM Kyiv for broader applicability.
2. Provide detailed ablation studies on QEMFormer’s feature encoding and architecture.
3. Compare against non-ML-based QEM techniques more rigorously.
4. Offer hyperparameter tuning details to improve reproducibility.
Questions For Authors: 1. How does QEMFormer perform on hardware other than IBM Kyiv?
2. Can you provide ablation studies showing the contribution of each component of QEMFormer?
3. Why was RMSE chosen as the primary evaluation metric, and how does it compare to alternative metrics?
4. How does QEM-Bench compare to prior QEM benchmarks, if any exist?
5. Can you clarify the dataset curation process and whether it reflects real-world noise characteristics?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We would like to thank the reviewer for the insightful comments and inquiries, and the positive evaluation of our work. **We have summarized the newly added Figs and Tabs at [this link](https://anonymous.4open.science/r/Rebuttal-iomM-B8AB/rebuttal_iomM.pdf).**
Below are our responses.
> **1. Real devices other than IBM Kyiv and traditional QEM techniques like ZNE on real devices.**
We apologize for the earlier oversight. We have now incorporated the following enhancements:
- Two datasets derived from 63-qubit Trotter circuits executed on **IBM Brisbane** have been included—one with extreme outlier filtering (Brisbane Pre) and one without (Brisbane Raw).
- Dataset statistics are detailed in **Tab. 1**.
- The performance of various QEM techniques is provided in **Tab. 2** and **Fig. 1**.
- We have evaluated ZNE across the datasets from Kyiv (Pre and Raw) and Brisbane (Pre and Raw), as detailed in **Fig. 1-2** and **Tab. 2-3**.
We would like to note that the CDR approach entails significant time costs due to the need to construct training sets for each circuit individually. Consequently, we plan to include its results in future revisions.
> **2. Ablation studies of QEMFormer**
We now conduct two sets of analyses.
- **Tab. 4** compares the performance impact of the MLP and Graph Transformer modules.
- **Tab. 5** evaluates our multi-ranged feature extractor.
> **3. RMSE as the sole evaluation metric?**
We apologize for any potential confusion. **In the original manuscript, we report RMSE (Tabs. 1 & 2), MAE (Tabs. 5 & 6), and standard deviation (Tabs. 1 & 2)** to provide a comprehensive evaluation. RMSE emphasizes larger deviations and is sensitive to outliers, while MAE directly measures the average error magnitude. Additionally, violin plots (**Figs. 3 & 6 of the original manuscript**) depict the full error distribution along with the STD.
> **4. About prior QEM benchmarks.**
**To the best of our knowledge, there are currently no standardized benchmarks for the ML-QEM task.** This gap, as also noted by reviewers Qjn1 and 6Drn, has been a primary motivation for this work.
> **5. Dataset curation process and whether it reflects real-world noise**
We detail the dataset curation process in **Tab. 6**. Our design intentionally reflects real-world noise characteristics in two key ways:
- **Diverse Circuits:** A single type of noise impacts various circuits differently. By including types of structured circuits and random unstructured circuits, QEM-Bench aims to gather a comprehensive depiction of real-world conditions.
- **Broad Noise Modeling:** We incorporate multiple realistic noise sources, including data from real devices (Kyiv), fake providers (published by IBM) resembling the real devices, and manually set configurations based on statistics from representative real devices (e.g., Sycamore [1] for incoherent settings).
This design aims to let the QEM-Bench effectively mirror the diverse noise characteristics encountered in practice and bridge the current gap for further research.
> **6. Hyperparameter tuning details.**
We include an analysis of how the number of layers and hidden dimensions in the MLP and Graph Transformer modules affect QEMFormer's performance (see **Fig. 3**). Our findings indicate that increasing the model size initially enhances model capability; however, excessively large models can lead to overfitting and degraded performance. We also politely noted that hyperparameter settings are provided in **Tab. 7 of the original manuscript**.
> **7. Formal theoretical analysis.**
We appreciate the reviewer's suggestion. Our primary focus in this work is to introduce a comprehensive benchmark dataset that spans a variety of circuits and noise configurations, addressing a significant gap in ML-QEM studies.
On the method side, we specifically design a 2-branch neural network architecture in QEM tasks. The idea is that the multi-range context and dependency as frequently occurred in the quantum system can be better captured, and the effectiveness is also verified by our extensive empirical results. We plan to incorporate further qualitative analysis in the revised manuscript.
Due to the inherent complexity of quantum systems and noise profiles, we leave a rigorous theoretical analysis of QEMFormer’s effectiveness for future work.
> **8. Discussion about hardware-specific noise mitigation and circuit optimization techniques.**
We will expand the related works section to include discussions on hardware-specific noise mitigation techniques, hybrid classical-quantum optimization strategies, and ML-based circuit optimization methods. We will clarify the differences and relationships between these approaches and ML-QEM techniques, especially QEMFormer.
We hope the reply eases your concern. If you have any further questions, we would be pleased to respond.
**References:**
[1] Quantum supremacy using a programmable superconducting processor, *Nature volume 574, 2019.*
---
Rebuttal Comment 1.1:
Comment: In light of all the reviews and authors' rebuttal, my score is confirmed.
---
Reply to Comment 1.1.1:
Comment: We appreciate your valuable time and insightful feedback. We will revise the manuscript in accordance with your suggestions and our discussion. Thank you again for your positive evaluation of our work! | Summary: This paper introduces a dataset for benchmarking quantum error mitigation techniques, as well as a graph-transformer model to serve as baseline. The dataset consists of three evaluation settings - each with different levels of added noise; Standard (general purpose testing with Trotterized TFIM Circuits, Random Circuits and MaxCut QAOA Circuits), advanced (testing aspects of generalization capabilities) and two large-circuit datasets, executed on real quantum hardware. The circuit data-samples are encoded directed acyclic graph representations and are provided with statistical information about the circuit itself (e.g. nr-gates, nr-parameters etc.), as well as the noisy and ideal measurement expectation values. To leverage the graph-representations and the informational feature vectors, a graph-transformer (QEMFormer) is introduced and compared on the proposed benchmark against a set of QEM algorithms from the literature.
Claims And Evidence: Since the paper is mostly focused on introducing and specifying the benchmark dataset, I’d say the claims are rather on the neutral side. The QEMFormer is compared against other algorithms from the literature, where it performs consistently strong across most of the dataset settings. The evaluation is thorough, with a good selection of comparable algorithms of both ml-based and non-ml-based error mitigators.
Methods And Evaluation Criteria: Both the proposed dataset as well as the QEMFormer are well motivated. The evaluation criteria of (root, mean) absolute errors mitigated is ultimately the logical metric, although a more critical discussion on other factors such as run-time or complexity of the compared algorithms would have been beneficial.
Theoretical Claims: No theoretical claims are made in this paper.
Experimental Designs Or Analyses: The experimental comparison in Ch.5 is in itself quite simple, a direct comparison of the final absolute errors mitigated across different circuit-type and noise settings. All results are reported with mean and std.div. and appear to be sound.
Supplementary Material: I have skimmed the appendix, which mostly contains additional explanations of the metrics and some additional experiments. All relevant information is in the main paper.
Relation To Broader Scientific Literature: The benchmark should be helpful for a more standardized quantum evaluation, which is currently indeed rather lacking. A comprehensive, maintained dataset as proposed here would certainly help the field. The QEMFormer seems to be a performant, but on this data specialized baseline (i.e., the graph structure).
Ultimately, quantum error correction is a technical problem that needs to be solved to make QC in itself a technically sound computing device. As an intermediary solution ML-based mitigators may have their merits, but on a practical level QEM is a problem that will (need to) be solved on the hardware side, which is why I would not expect learning based QEM methods to stay around for too long.
Essential References Not Discussed: None that I am aware of. The discussion on related work covers the field decently well.
Other Strengths And Weaknesses: I generally have very little to critique on this paper, it is well written, formalized and visualized. While the contribution is generally rather “short-term”, as mentioned above, until QC hardware handles QEM natively, I find this benchmark a good current contribution to a current problem.
Other Comments Or Suggestions: The colors in Fig.1 could be stronger, and Fig. 4 is too small to read.
Questions For Authors: No questions.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We appreciate your constructive feedback and positive evaluation of our work. We acknowledge that quantum error correction is aimed to be solved on the hardware side ultimately. However, the significant qubit overhead associated with QEC renders it less feasible in the near term, especially for large-scale circuits, as illustrated in [1] and [2]. Therefore, during the NISQ era, ML-QEM methods offer an effective and efficient interim approach, and we hope our work lays a foundation for future studies.
We will revise the manuscript to clearly reflect this nuanced perspective and incorporate your valuable suggestions.
**References:**
[1] Quantum Error Mitigation, *Reviews of Modern Physics, American Physical Society, 2022*
[2] Near-term quantum computing techniques: Variational quantum algorithms, error mitigation, circuit compilation, benchmarking and classical simulation, *Science China Physics, Mechanics & Astronomy, 2023.* | Summary: The paper introduces QEM-Bench, a benchmarking suite designed to evaluate machine learning-based Quantum Error Mitigation (QEM) techniques.
The benchmark includes 20 datasets covering various circuit types and noise models to standardize QEM evaluation.
Furthermore, the paper proposes QEMFormer, a novel learning-based QEM method that improves quantum error mitigation by leveraging both short-range and long-range dependencies with quantum circuits.
The paper evaluates QEMFormer against various baselines, showing its superior performance across different circuit families, noise configurations, and real quantum devices (IBM Kyiv 50-qubit experiments).
Claims And Evidence: - QEM-Bench provides a comprehensive and standardized benchmarking suite for machine learning-based QEM techniques.
- Based on experimental results, QEMFormer outperforms other machine learning-based and traditional QEM methods.
- The two datasets with 50-qubit circuits executed on IBM Kyiv might not be flexible. This is because, in practice, the real quantum systems can have higher than 50 qubits. The benchmark on real quantum systems should show the scalability.
Methods And Evaluation Criteria: - The proposed benchmarking is well-motivated since prior QEM methods might have different evaluation protocols, which could make the evaluation unfair in some perspectives or unable to be compared because of a lack of reproducibility.
- The proposed QEMFormer utilizing the long-range and short-range dependencies in Graph Transformer is well-aligned with quantum circuit structure, which can be represented as Directed Acyclic Graphs (DAGs).
Theoretical Claims: The paper does not have any explicit theoretical claim.
Experimental Designs Or Analyses: The proposed QEM-Bench shows the diversity of circuit designs and scenarios to evaluate the QEM methods.
Besides, as mentioned in "Claims And Evidence", the evaluation on the IBM Kyiv system should be considered since it does not convince that the QEM methods can work in multiple systems.
Supplementary Material: I have reviewed the supplementary material, including experiment configuration, backgrounds, evaluation metrics, and additional experimental results.
Relation To Broader Scientific Literature: The paper can potentially standardize the evaluation of the QEM methods, making the comparisons fair and transparent.
Essential References Not Discussed: There are no additional related works that are essential to understanding the key contributions of the paper.
Other Strengths And Weaknesses: I don't have any comments on other strengths and weaknesses of the paper.
Other Comments Or Suggestions: No other comments or suggestions.
Questions For Authors: I think the paper is solid in terms of the benchmark and proposed model.
What I am concerned about is the evaluation on the real quantum devices:
- Why does the paper evaluate on IBM Kyiv only? There are other quantum computers in the IBM Quantum system.
- Is the evaluation on a 50-qubit system good enough? Why? If the circuits are deployed on a 127-qubit system, will the performance stay the same?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We would like to thank the reviewer for the insightful questions and positive evaluation of our work. **We summarize the Tabs. and Figs. for newly added experiments at [this link](https://anonymous.4open.science/r/Rebuttal-6Drn-C2D8/rebuttal_%206Drn.pdf).**
Below are our responses to each question.
> **Q1: Why does the paper evaluate IBM Kyiv only? There are other quantum computers in the IBM Quantum system.**
Initially, we evaluated only IBM Kyiv due to the significant financial and time costs associated with executing large-scale quantum circuits on real quantum devices. Although multiple IBM devices are available, these constraints still limited our testing.
To improve the diversity of QEM-Bench and strengthen your confidence in our work, we have expanded our evaluation to include two datasets from the **IBM Brisbane** device: one with extreme outlier filtering (Brisbane Pre) and another with raw, unfiltered data (Brisbane Raw).
- Detailed statistics for the two datasets are provided in **Tab. 1**
- The performance of various QEM techniques is shown in **Tab. 2 and Fig. 1**.
Notably, even with the more severe noise effects on the Brisbane device (compared to Kyiv), QEMFormer consistently outperforms the baseline methods.
We shall include these datasets and results in the revised manuscript.
> **Q2: Is the evaluation on a 50-qubit system good enough? Why? If the circuits are deployed on a 127-qubit system, will the performance stay the same?**
We would like to clarify that the construction of our datasets on 50-qubit systems is limited by **the prohibitive computational cost of obtaining ideal EVs for circuits with over 100 qubits.** Although devices like Kyiv and Brisbane support up to 127 qubits, their outputs are inherently noisy. Hence, ideal EVs, which serve as the dataset labels, have to be obtained through classical simulation. Yet, to the best of our knowledge, the IBM simulators that do not restrict circuit structure to provide ideal simulation are limited to 63 qubits (namely, Aer matrix_product_state simulator), making 100-qubit simulations difficult under the current implementation structure of QEM-Bench.
Furthermore, to the best of our knowledge, the only ML-QEM method exploring circuits beyond 100 qubits, [1], also demonstrates such difficulty in ideal EV obtaining in their work and thus **uses ZNE-mitigated results as training labels.** However, our experiments applying IBM’s built-in ZNE to both 50-qubit and 63-qubit circuits (on the Kyiv and Brisbane devices) show only marginal improvements over noisy outcomes, with significant residual errors (see **Fig. 1–2 and Tab. 2–3**). This suggests that using ZNE outcomes as labels may not provide a fair or reliable benchmark for larger systems.
Accordingly, due to the current time constraint, we plan to extend the inclusion of systems exceeding 100 qubits to future work. Nevertheless, to enhance your confidence and further evaluate the scalability of various ML-QEM methods, we have developed the Brisbane Pre and Brisbane Raw datasets on **63-qubit systems** (results summarized in **Tab. 2 and Fig. 1**).
We hope the reply eases your concern. If you have any additional questions, we would be pleased to provide further responses.
**References:**
[1] Machine learning for practical quantum error mitigation, *Nature Machine Intelligence, 2024*
---
Rebuttal Comment 1.1:
Comment: The authors have addressed my questions. I will maintain the score.
---
Reply to Comment 1.1.1:
Comment: We sincerely appreciate your time and thoughtful feedback. We will revise the manuscript in accordance with your suggestions and integrate the newly added datasets. We are glad that these modifications address your concerns and thank you once again for your positive evaluation of our work! | Summary: The authors make two primary contributions in their manuscript. First, they compile QEM-Bench, a set of twenty datasets that the community can use to benchmark ML-based approaches to quantum error mitigation (QEM). Second, they introduce a new ML-based approach to QEM called QEMFormer, which combines multi-layered perceptrons (MLPs) and graph transformers to predict the true expectation value of a quantum circuit based on the noisy measurement statistics. Comparisons between QEMFormer and other ML-based QEM methods are made on QEM-Bench. The authors claim that these results show that QEMFormer is generally superior to existing methods across QEM-Bench.
## update after rebuttal
Most of my concerns were addressed with post-review edits. I’ve raised my score.
Claims And Evidence: The authors provide modest evidence for their claim that QEMFormer outperforms the other ML-based QEM methods that they tested. QEMFormer routinely achieves the lowest or second lowest root mean squared error on the various datasets in QEM-Bench. However, the large error bars make it difficult to ascertain if this performance is statistically significant. I would like to see more rigorous analysis to support their claim.
The authors also overlook several competing ML-based QEM methods that have shown good performance. They chose not to include the random forest model from [1] in their paper, despite the random forest model routinely beating the MLP and GNN in [1] (which are both included). The authors also do not compare their method to the graph transformer approach in [2].
Methods And Evaluation Criteria: The overall method of comparing several competing models on multiple datasets is sound. The use of RMSE, absolute error (AE), and mean absolute error (MAE) is also typical, as is reporting error bars. However, the large error bars mean that you need to perform additional statistical analyses to show that QEMFormer truly outperforms the other models.
Theoretical Claims: N/A
Experimental Designs Or Analyses: I greatly appreciated that the authors included data simulated using both incoherent (i.e., stochastic) and coherent error models. A lot of papers overlook coherent errors, despite evidence that they are much harder for ML approaches to model. Nonetheless, I question the value of benchmark sets simulated under fixed noise parameters. By not varying the noise strengths across error models it is hard to get a good sense for how models perform in a variety of noise regimes, and the community risks training to the standard rather than truly probing their models.
It is also hard to judge how hard these benchmarks are from the data presented. For instance, no analysis is presented showing how far the noisy expectation values differ from the true expectation values in each dataset.
Supplementary Material: I read the appendices.
Relation To Broader Scientific Literature: See my comments in the “Claims and evidence” and “Other comments or suggestions” section about missing models and less-than-ideal descriptions of other works.
Also, it isn’t really explained how they came up with these benchmarks. For instance, both one-dimensional transverse field Ising model circuits and mitigating unseen observables were used in [1]. You should credit that work!
Essential References Not Discussed: [1] H. Liao, D. Wang, I. Sitdikov, C. Salcedo, A. Seif, and Z. Minev. Machine learning for practical quantum error mitigation. Nature Machine Intelligence, 6(12), December 2024.
[2] T. Bao, X. Ye, H. Ruan, C. Liu, W. Wu, J. Yan. Beyond circuit connections: a non-message passing graph transformer approach for quantum error mitigation. ICLR 2025.
Other Strengths And Weaknesses: N/A
Other Comments Or Suggestions: The description of the GNN modelled on [1] fails to convey how similar it is to the GNN branch of QEMFormer. Yes, they use an undirected acyclic graph instead of a direct acyclic graph and a slightly different architecture, but when phrased this way QEMFormer doesn’t seem like that big of an advancement.
Questions For Authors: 1. How does the random forest model in [1] perform on QEM-Bench?
2. How does the graph transformer model in [2] perform on QEM-Bench?
3. How did you get the true expectation values for the one-dimensional TFIM circuits run on ibm_kyiv? Are exact solutions known?
4. Given the large error bars, how do you know if the benchmarks have enough resolving power to meaningfully distinguish between different approaches?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your thoughtful comments and inquiries. **We summarized all Tabs. and Figs. of the newly added experiments at [this link](https://anonymous.4open.science/r/Rebuttal-fTJA-433C/rebuttal_%20fTJA.pdf).**
Below are our responses.
> **1: RF [1] and GTraQEM [2] on QEM-Bench.**
We apologize for the oversight and now implement the RF in [1] and GTraQEM in [2] and evaluate them on 20 datasets from QEM-Bench (**Figs. 1&2, Tabs. 1-3**).
Although [1] reported that the RF outperformed the MLP and GNN on a simple 4-qubit random circuits dataset, we consider it not convincing to state that "the RF routinely beats the MLP and GNN in [1]" as no further comparisons are conducted in other settings in [1]. Our comprehensive evaluation shows that RF's performance degrades in advanced settings such as trotter zero-shot.
Also, though GTraQEM shows competitive performance in certain settings, its non-message passing aggregation incurs high computational costs with increasing circuit depth, as constructing its structural matrix has an $O(n^3)$ complexity.
> **2. How to obtain the ideal EV on the Kyiv device.**
**The ideal EVs were computed solely based on the circuit, independent of any quantum device.** For 50-qubit circuits, we use the IBM Aer simulator for ideal simulation, specifically with:
simulator_ideal = AerSimulator(method='matrix_product_state')
estimator = Estimator(mode=simulator_ideal)
job = estimator.run([(circs, observables)])
> **3. Large Error Bars?**
There may be confusion in our previous writing. To clarify, the reported error bars (**in Tab. 2 & 3 of the original manuscript**) refer to
$$
\sigma_{\text{dataset}} = \sqrt{\frac{1}{N} \sum_{i=1}^{N} \left(y^{\text{miti}}_i - y^{\text{ideal}}_i\right)^2},
$$
where $N$ is the number of test data points. This metric quantifies the deviations of noisy (or mitigated) results from the ideal values across the dataset. **It is not a measure of model reproducibility across different random seed runs**, computed by:
$$
\sigma_{\text{stability}} = \sqrt{\frac{1}{K} \sum_{k=1}^{K} \left(\text{MAE}_k\right)^2} \quad \text{(or similarly for RMSE)},
$$
with $K$ representing the number of runs.
To show this distinction, we executed QEMFormer under five different random seeds, summarized in **Tab. 4**.
We will clarify it in our main paper:
1. The models show a small $\sigma_{\text{stability}}$, indicating that the mean performance is reliable for comparison.
2. The relatively large $\sigma_{\text{dataset}}$ reflects the variable impact of noise on different circuits, leading to diverse deviations from the ideal outcomes.
> **4. Difference between GNN in [1] and QEMFormer**
We would like to note that **QEMFormer is an integrated architecture rather than a mere refinement of the GNN in [1]**. A comparison is shown in **Tab. 5**. Importantly, **QEMFormer experimentally outperforms the GNN in [1] among most settings**, demonstrating its two-branch design's inherent well-suitedness for the quantum system.
> **5. How QEM-Bench came up with?**
We apologize for the unclear expression. Regarding the design of the QEM-Bench:
1. QEM-Bench is built on insights from existing QEM and quantum computing research **to ensure it includes the key concerns of the community**.
2. **Key Enhancements:**
- **Structural Diversity:** Incorporates representative QAOA circuits.
- **Circuit Complexity:** Enriches gate types and parameter selection in random circuits.
- **Noise Characterization:** Include coherent noise.
- **Evaluation Scope:** Expands zero-shot settings to test generalization ability.
- **Real-World Data:** Construct large-scale circuit datasets executed on quantum devices with ideal EVs as labels.
By integrating these enhancements with established research, QEM-Bench aims to address the need for a standardized benchmark evaluation dataset for ML-QEM techniques.
> **6. Are noise parameters fixed across error models?**
We politely clarify that **QEM-Bench does incorporate different noise strengths across error models.** Incoherent noise parameters are derived from the real device, the Sycamore [3], and the parameters of real devices and simulators provided by IBM are **not manually set**, thereby capturing a realistic and diverse range of noise regimes.
> **7. How far do the noisy EVs differ from the ideal EVs?**
We respectfully note that **the error distributions, MAE, and RMSE of raw data are detailed in Tabs 2-4 and Figs 3, 4 & 6 of the original manuscript**.
We hope the reply eases your concern. Should you have any further inquiries, we would be pleased to offer responses.
**References:**
- [1] Machine learning for practical quantum error mitigation. *Nature Machine Intelligence, 2024*
- [2] Beyond circuit connections: a non-message passing graph transformer approach for quantum error mitigation. *ICLR 2025*.
- [3] Quantum supremacy using a programmable superconducting processor, *Nature 574, 2019*
---
Rebuttal Comment 1.1:
Comment: Thank you for taking the time to respond to my report. I especially appreciate the inclusion of the random forest and GTraQEM. Here are a few additional comments.
1. Large error bars: Thank you for including results on $\sigma_{\text{stability}}$ along with the original values of $\sigma_{\text{dataset}}$. Reporting both is a good idea. However, doing so does not address my original concern, which is that it is very difficult to assess if any of your results are statistically significant. You are comparing many different models across many different datasets. You can’t just report mean performance and error bars on each dataset and then say that “our model performed better than most of the other models more often than not, so it is better.” With so many possible pairwise comparisons, it is very hard to determine the significance of the results just by looking at the error bars. I would really appreciate the addition of appropriate significance tests.
2. Error models: Thanks for clarifying that the error parameters are fixed. By “fixed” I mean that only a single instance of error model was generated for the five devices that you considered. My follow-up question is “why should an error mitigation benchmark use simulations from static error models?” Quantum computers are improving every day. Shouldn’t benchmark datasets reflect that improvement? Otherwise, we risk testing QEM approaches on outdated data. For instance, are you using Sycamore calibration data from 2019?
---
Reply to Comment 1.1.1:
Comment: Thank you for the follow-up questions. **The experimental results are summarized in [this link](https://anonymous.4open.science/r/Rebuttal-fTJA-433C/rebuttal_fTJA_r2.pdf).**
Please find our response below.
> **Q1: About the Significance Test**
Our initial evaluation metrics align with prior work [1, 2]. To further address your concerns and substantiate our findings, we now provide a statistical analysis using paired t-tests.
Namely, we use
t_stat, p_value = stats.ttest_rel(baseline_err_array, ours_err_array, alternative='greater'),
to demonstrate that EVs mitigated by a baseline show larger errors than those mitigated by a QEMFormer for most data points in a test set. We consider a positive $t$ and $p < 0.05$ as the demonstration for the claim.
The results in **Tabs. 1–3** generally aligns with our previous findings, that QEMFormer attains the best or second-best performance in most datasets.
> **Q2: About the error model setups.**
We appreciate the opportunity to clarify this point, which was not fully addressed in round 1 due to space limitations.
> "Only a single instance of error model was generated for the five devices that you considered."
We respectfully disagree with this claim. Our work does not rely on a single error model instance for the five devices. Instead, for **each** of the four distinct error settings, **multiple instances are incorporated**. Specifically,
- Non-Manually Constructed Noise Settings:
- **Real Devices:** Noisy outcomes are obtained directly from circuit executions on IBM's quantum devices.
- **Fake Providers:** Noisy outcomes are generated by directly executing circuits over IBM's fake provider backends, each emulating a specific quantum device. For example, the noise profile of FakeWashington differs from that of FakeHanoiV2.
**For these settings, randomness is naturally built-in, and no modifications are performed**. The usage of fake providers is in line with [1, 2].
- Manually Constructed Noise Settings:
- **Coherent:** Over-rotation rates are set at $0.02\pi$ with an additional random fluctuation (approximately $0.001$).
- **Incoherent:** Two gate subsets are randomly constructed: one for gates with depolarizing errors and another for gates with Pauli errors. The error rates for each gate, as well as the readout errors, are sampled **from a normal distribution whose mean is derived from Sycamore error rates correspondingly**.
**For each circuit set and for each random seed, the noise models are different due to the randomness**. Consequently, QEM-Bench constructs multiple instances in the incoherent and coherent noise settings.
*We are unsure which **five devices** are referred to; this may be due to typos in the column names of Tab. 2 & 3 in our round-1 rebuttal. We have corrected them and apologize for any confusion.*
> "Why should a QEM benchmark use simulations from static error models?"
Based on the diverse noise types, multiple instances per type, and the inherent randomness in error rate sampling and gate type assignments, we respectfully disagree that our error models are static. Yet, to further ease this concern, we include two additional types of datasets:
- **Varying Incoherent:** To assess mitigators under largely varying noise, an individual incoherent noise model is constructed **for each circuit** using random gate selection and error rate sampling in this setting. The results are detailed in **Tab. 4**.
- **Brisbane Pre & Raw:** To evaluate mitigators using data from more actual devices, we include two datasets of 63-qubit Trotter circuits executed on the IBM Brisbane device. The results are detailed in **Tab. 5**.
Overall, QEMFormer exhibits a strong performance compared to the baselines.
> Usage of Sycamore Error Rates
As QEM-Bench comprises multiple datasets derived from real IBM quantum computers or simulated providers emulating specific IBM devices, incorporating rates from Google devices could further enrich noise diversity. This approach aims to capture a broader range of quantum device profiles. **Importantly, the Sycamore statistics are used only as references to set the mean of the error rate in the incoherent setting, with no calibration performed. We do not fix any error rates.**
> Benchmarks in QEM
With error model setups aligned with recent studies and data from real devices on IBM platforms, we respectfully argue that our benchmark does not rely on outdated data. We would like to argue that a single benchmark may not be able to capture all the daily updates in a field. Our objective is to address the need for standardized benchmarks under the current situation.
We genuinely appreciate your time and feedback and hope this response addresses your concerns.
**References**
- [1] Machine learning for practical quantum error mitigation. *Nature Machine Intelligence*.
- [2] Beyond circuit connections: a non-message passing graph transformer approach for quantum error mitigation. *ICLR 2025*. | null | null | null | null | null | null |
FlexControl: Computation-Aware Conditional Control with Differentiable Router for Text-to-Image Generation | Accept (poster) | Summary: This paper proposes FlexControl, a framework that introduces a novel gating mechanism for dynamically selecting blocks to activate in the control network, reducing computational overhead while preserving or improving image quality. The authors have conducted experiments on both UNet-based (SD1.5) and DiT-based (SD3.0) architecture across three tasks (depth, canny, seg.), demonstrating the effectiveness of the proposed method.
Claims And Evidence: The claims in the submission are well-supported by the experiments.
Methods And Evaluation Criteria: Yes, the proposed methods make sense for the problem. The evaluation metrics (FID, CLIP score, depth RMSE, canny SSIM, seg mIoU) are all common criteria in the area of controllable image generation.
Theoretical Claims: This papar does not contain any theoretical claims or proofs.
Experimental Designs Or Analyses: Yes, I've checked all the experiments. Some issues are listed as follows:
1. Quantitative comparison: As one of the main contributions of this paper is to reduce the computational overhead, it lacks comparison on the image quality (Table 1) and controllability (Table 2) with efficient control models mentioned in the Related Work section, such as ControlNeXt[1].
2. Ablation study: Similar to the first issue, this paper lacks computational complexity comparison (Table 3) with efficient methods. Adding these comparisons could help the readers understand the computational efficiency of the proposed method better.
3. The paper lacks explanation or ablation study on how to determine the hyperparameter $\lambda_{\mathbf C}$ in equation (18).
[1] Peng, Bohao, et al. "Controlnext: Powerful and efficient control for image and video generation." *arXiv preprint arXiv:2408.06070* (2024).
Supplementary Material: Yes, I've reviewed all parts of the supplementary material.
Relation To Broader Scientific Literature: This paper falls into the area of controllable image generation. It addresses a key problem in this area that previous methods heavily rely on heuristic network design, and proposes a novel dynamic gating mechanism to solve this problem. This paper is also related to efficient control models, proposing a novel cost loss that controls the sparsity of the network.
Essential References Not Discussed: The essential related works are well-discussed and cited.
Other Strengths And Weaknesses: Strengths:
1. The dynamic gating mechanism is novel in the area of controllable image generation.
2. The paper is well-written, the presentation is clear and easy to follow.
Weaknesses:
1. The desired sparsity $\gamma$ needs to be specified before training. It would be better if a single model can handle all possible $\gamma$, further increasing the flexibility of the proposed method.
2. Compared to other efficient control models, FlexControl only reduces computational overhead but does not decrease the number of parameters (actually doubles the parameters of the original ControlNet), which increases the burden of distributing and deploying the model.
Other Comments Or Suggestions: I do not have other comments or suggestions.
Questions For Authors: 1. How is the FLOPs in the cost loss $\mathcal L_\mathbf{C}$ computed, such that the gradients can be back-propagated to the parameters of the network?
2. During inference, is it possible to manually adjust the number of activated blocks to achieve a efficiency-performance trade-off?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We sincerely thank the reviewer for acknowledging the novelty and performance of our paper. We hope the following answers reflect your questions.
> Quantitative comparison and ablation on ControlNeXt..
We appreciate the reviewer’s concern regarding the need for additional comparisons with efficient control models. In response, we have conducted further experiments on ControlNext and Omini-Control[1], as mentioned in our reply to Reviewer eHec.
It is important to highlight that while optimizing control block efficiency is valuable, our focus is different: we propose a dynamic routing strategy that adaptively determines the most efficient control strategy across different time steps and samples. This approach complements existing efficient control methods rather than solely aiming to reduce the cost of control blocks.
Our experiments confirm that integrating our method with these efficient control models further enhances their performance while improving efficiency.
-[1] Tan, Z., Liu, S., Yang, X., Xue, Q. and Wang, X., 2024. OminiControl: Minimal and Universal Control for Diffusion Transformer. arXiv e-prints, pp.arXiv-2411.
> The paper lacks explanation or ablation study on how to determine the hyperparameter $\lambda_C$
We appreciate the reviewer’s request for further clarification on determining the hyperparameter $\lambda_C$ in Equation (18).
$\lambda_C$ serves as a scaling factor to balance different objectives: the diffusion loss optimizes image quality, while $L_C$ regulates and enforces control block sparsity. To ensure the trained gating mechanism achieves the desired sparsity while maintaining generation quality, $\lambda_C$ needs to be tuned empirically. While the optimal value may vary slightly across models, our experiments indicate that setting $\lambda_C$ = 0.5 provides the best trade-off in practice.
To compute $L_C$, we utilize a precomputed block-wise FLOPs lookup table, following methodologies from prior work ([a], [b], [c]). This approach ensures an efficient and structured way to regulate computational cost while preserving performance.
-[a] Meng, L., Li, H., Chen, B. C., Lan, S., Wu, Z., Jiang, Y. G., & Lim, S. N. (2022). Adavit: Adaptive vision transformers for efficient image recognition. In Proceedings of the IEEE/CVF conference on computer vision and pattern recognition (pp. 12309-12318).
-[b] Rao, Y., Liu, Z., Zhao, W., Zhou, J., & Lu, J. (2023). Dynamic spatial sparsification for efficient vision transformers and convolutional neural networks. IEEE Transactions on Pattern Analysis and Machine Intelligence, 45(9), 10883-10897.
-[c] Han, Y., Liu, Z., Yuan, Z., Pu, Y., Wang, C., Song, S., & Huang, G. (2024). Latency-aware unified dynamic networks for efficient image recognition. IEEE Transactions on Pattern Analysis and Machine Intelligence.
>The desired sparsity γ needs to be specified before training. During inference, is it possible to manually adjust the number of activated blocks to achieve an efficiency-performance trade-off?
We appreciate the reviewer’s suggestion regarding an inference-time scaling mechanism. To explore this, we conducted additional experiments where a ControlNet-Large model was trained with all blocks activated on a segmentation mask control task. During inference, we dynamically adjusted the gating threshold to control the number of activated blocks.
Our results confirm that scaling activation blocks at inference is feasible, leading to better performance than the ControlNet baseline while maintaining comparable FLOPs and inference speed. However, the performance does not fully match that of the $\gamma$-aware trained version as we proposed in the paper, indicating that explicit training with sparsity constraints remains crucial for achieving the optimal efficiency-performance trade-off. Detailed results are presented below.
| Method | Base Model | FID | CLIP_score | mIoU | Speed |
|----------------------------|:----------:|:-----:|:----------:|:------:|:--------------:|
| FlexControl(γ=0.5) | SD1.5 | 14.80 | 0.2842 | 0.3751 | 5.21±0.12 it/s |
| FlexControl(w.o. training) | SD1.5 | 19.86 | 0.2732 | 0.3295 | 5.24±0.11 it/s |
| FlexControl(γ=0.7) | SD1.5 | 14.71 | 0.2840 | 0.3775 | 4.94±0.07 it/s |
| FlexControl(w.o. training) | SD1.5 | 16.56 | 0.2778 | 0.3665 | 4.86±0.09 it/s |
> Issue of parameters
We acknowledge the reviewer’s concern about parameter count. Our goal is not just to reduce control block cost but to develop a dynamic routing strategy that optimally adapts efficiency across time steps and samples. As shown in our experiments and discussed in our response to Reviewer eHec, integrating our method with efficient control models further improves both performance and efficiency, reinforcing its broad applicability of our methods. | Summary: This paper proposes FlexControl, a novel method aimed at improving the computational efficiency of ControlNet, an important model for adding controllability in text-to-image generation tasks. Unlike the original ControlNet, which utilizes half of the diffusion architecture as its encoder, FlexControl introduces an additional, fully trainable encoder as a separate copy of the entire diffusion architecture. A differentiable router is trained alongside this encoder to dynamically activate only the necessary blocks required for each specific task.
To train this router, authors propose a computation-aware loss function that regularizes the model by matching a predetermined target ratio for reducing Floating Point Operations (FLOPs). The chosen ratio significantly influences both the performance and efficiency of FlexControl. The proposed method demonstrates improved results in terms of both performance and computational efficiency across various conditions, including depth maps, Canny edges, and segmentation masks.
## Update after rebuttal
Through the rebuttal and discussion, I’ve come to understand that FlexControl can indeed achieve improved computational efficiency compared to baselines when gamma is properly selected. However, the method still requires careful hyperparameter tuning, which may present practical challenges.
I am raising my score to a weak accept, though I still believe this paper sits on the borderline and could reasonably be rejected.
Claims And Evidence: The claims presented in the paper regarding computational efficiency and performance gains through FlexControl require additional evidence. Specifically, a comparative analysis with the open-source community's LoRA baseline [A], which modifies only the input layer's channel count and trains only LoRA parameters, without additional models, should be included. Such baseline may be more efficient in parameter count, FLOPs, and inference speed. Moreover, comparisons with ControlNeXt are essential.
The authors note that FlexControl with Gamma values of 0.5 and 0.7 performs well and maintains similar speed to ControlNet at Gamma=0.5. However, Table 4 reveals that at Gamma=0.3, FlexControl underperforms relative to ControlNet, indicating that performance gains only occur when computational efficiency is equivalent to or less than ControlNet. This raises questions regarding the actual advantage of FlexControl over ControlNet, particularly when improved efficiency corresponds to reduced performance. Further exploration of the lower bound of the gamma value and its impact on model performance is also necessary for a comprehensive evaluation.
[A] Black Forest Labs, https://github.com/black-forest-labs/flux/blob/main/docs/structural-conditioning.md
Methods And Evaluation Criteria: The evaluation used in this paper appropriately assess quality and fidelity across various tasks.
Theoretical Claims: There are no theoretical claims.
Experimental Designs Or Analyses: A deeper exploration into the effects of varying gamma values, especially their lower limits, would strengthen the experiments.
Supplementary Material: The supplementary material includes the implementation details and the distribution of activated control blocks. The implementation details provided are sufficient to allow reproducibility of the experiments. The distribution figures offer valuable insights to readers, showing the interesting observation that most blocks, except for the initial ones, tend to be predominantly activated during later inference steps.
Relation To Broader Scientific Literature: Adding controllability to text-to-image generation models is a critical research topic within visual generative modeling. In this context, computational efficiency emerges as an essential aspect.
Essential References Not Discussed: No issues found.
Other Strengths And Weaknesses: A notable strength of FlexControl is its ability to maintain strong performance, comparable to ControlNet, particularly at gamma values around 0.5. However, its key weakness is evident when aiming for higher computational efficiency (gamma=0.3), where its performance significantly drops below ControlNet's baseline.
Other Comments Or Suggestions: No issues found.
Questions For Authors: Regarding the SD3 adaptation, which part of the dual-stream block was specifically trained using a trainable copy in FlexControl? Parameters of both modalities? Or only the image modality?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We sincerely thank the reviewer for the detailed and constructive feedback.
> ControlNext.. LoRA-based…
We appreciate the reviewer’s feedback regarding the comparison with other methods. While a direct comparison is not applicable (as our work focuses on control block integration rather than parameter fine-tuning), we have instead integrated our methods with two representative approaches: ControlNeXt and Omini-Control [1] (a recent popular LoRA-based control method). Specifically, for Omni-Control, instead of following Flux’s approach of concatenating control tokens into new tokens, it appends condition image tokens with noisy image tokens as a longer sequence and leverages LoRA to jointly process them.
Our results show that, unlike methods that control all blocks by default, our approach achieves superior performance with fewer activated blocks, demonstrating its adaptability and broader applicability. Detailed comparisons follow below.
*[1] Tan, Z., et,al. OminiControl: Minimal and Universal Control for Diffusion Transformer. arXiv e-prints, pp.arXiv-2411.*
**On segmentation mask**
| Method | Base Model | FID | CLIP_score | mIoU | FLOPs | Speed |
|------------------------|:----------:|:---------:|:----------:|:----------:|:-------:|:--------------:|
| ControlNeXt | SD1.5 | 24.16 | 0.2659 | _0.2825_ | 51.72 G | 5.34±0.02 it/s |
| FlexControlNeXt(γ=0.3) | SD1.5 | 25.22 | 0.2531 | 0.2644 | / | / |
| FlexControlNeXt(γ=0.5) | SD1.5 | **23.74** | _0.2664_ | 0.2819 | / | / |
| FlexControlNeXt(γ=0.7) | SD1.5 | **23.71** | **0.2674** | **0.2841** | / | / |
| FlexControlNeXt(γ=0.8) | SD1.5 | _23.84_ | _0.2662_ | **0.2841** | / | / |
**On Canny**
| Method | Base Model | FID | CLIP_score | SSIM | FLOPs | Speed |
|-------------------------|:----------:|:---------:|:----------:|:----------:|:-----------:|:------------------:|
| OminiControl | FLUX.1 | 22.84 | 0.2830 | 0.4125 | 16.89 T | 2.36±0.00 it/s |
| FlexOminiControl(γ=0.2) | FLUX.1 | 36.62 | 0.2712 | 0.3122 | **10.76 T** | **3.42±0.09 it/s** |
| FlexOminiControl(γ=0.3) | FLUX.1 | 26.65 | 0.2791 | 0.3668 | _11.45 T_ | _3.28±0.07 it/s_ |
| FlexOminiControl(γ=0.5) | FLUX.1 | 22.61 | **0.2886** | 0.4123 | 13.08 T | 3.08±0.10 it/s |
| FlexOminiControl(γ=0.7) | FLUX.1 | _22.39_ | 0.2855 | _0.4146_ | 14.57 T | 2.80±0.09 it/s |
| FlexOminiControl(γ=0.8) | FLUX.1 | **22.27** | _0.2861_ | **0.4153** | 15.40 T | 2.69±0.07 it/s |
> Table 4.. Gamma=0.3…Further exploration..gamma value…
We appreciate the reviewer’s observations on FlexControl’s performance across $\gamma$ values. Even at $\gamma$ = 0.3 our method surpasses standard ControlNet while being significantly more efficient. Though slightly behind the more computationally expensive ControlNet-Large, it achieves over three times the efficiency, highlighting its effectiveness. To provide further insights, we conducted additional ablation studies on segmentation and Canny tasks, analyzing $\gamma$ values from 0.2 to 0.8. The results, detailed below, illustrate the trade-offs between efficiency and performance:
**On segmentation mask**
| Method | Base Model | FID | CLIP_score | mIoU | FLOPs | Speed |
|--------------------|:----------:|:-----:|:----------:|:------:|:-----:|:--------------:|
| ControlNet | SD1.5 | 21.33 | 0.2531 | 0.2764 | 233 G | 5.23±0.07 it/s |
| FlexControl(γ=0.2) | SD1.5 | 21.52 | 0.2584 | 0.2995 | 112 G | 5.98±0.09 it/s |
| FlexControl(γ=0.3) | SD1.5 | 17.21 | 0.2713 | 0.3572 | 168 G | 5.64±0.12 it/s |
| FlexControl(γ=0.8) | SD1.5 | 15.59 | 0.2804 | 0.3695 | 448 G | 4.82±0.06 it/s |
**On Canny**
| Method | Base Model | FID | CLIP_score | SSIM | FLOPs | Speed |
|--------------------|:----------:|:-----:|:----------:|:------:|:------:|:---------------:|
| ControlNet | SD3.0 | 27.21 | 0.2512 | 0.3749 | 3.25 T | 48.34±1.78 s/it|
| FlexControl(γ=0.2) | SD3.0 | 28.11 | 0.2524 | 0.3577 | 1.25 T | 38.21±2.97 s/it |
| FlexControl(γ=0.3) | SD3.0 | 23.39 | 0.2581 | 0.4286 | 1.86 T | 40.83±3.09 s/it |
| FlexControl(γ=0.8) | SD3.0 | 20.72 | 0.2719 | 0.4816 | 4.97 T | 54.05±2.53 s/it |
We apologize for any confusion caused by our text and table presentation that may have led to misunderstandings. We will refine our wording to ensure greater clarity in the camera-ready version.
> SD3 adaptation
In SD3 tasks, we select **all** transformer blocks as candidates and use our dynamic routing strategy to flexibly decide which transformer block to add control to. We copy all parameters in a block for both modalities.
---
Rebuttal Comment 1.1:
Comment: I appreciate the authors’ detailed rebuttal and the additional results provided.
I’m curious why the ControlNeXt table does not report FLOPs or speed metrics, and why the SD3.0 table reports speed in seconds per iteration (s/it), which differs from other tables.
---
Reply to Comment 1.1.1:
Comment: We appreciate the reviewer's thoughtful consideration of our detailed rebuttal and additional experimental results. Below, we clarify the points raised concerning the reporting of FLOPs and speed metrics:
>1. Regarding the absence of FLOPs and speed metrics in the ControlNeXt table:
ControlNeXt processes control features using a lightweight module, subsequently normalizing these features and applying them across each block. Our method introduces router units solely to determine the applicability of features to these blocks, without incorporating mechanisms for skipping control blocks. Consequently, our proposed approach does not alter inference speed or FLOPs relative to the baseline ControlNeXt model. Therefore, we have reported only the performance metrics for ControlNeXt, omitting unchanged FLOPs and speed metrics for clarity and conciseness.
>2. Rationale for reporting SD3.0 speed metrics in seconds per iteration (s/it):
As detailed in our manuscript (line 377), inference experiments for both SD1.5 and SD3.0 models were conducted on a single RTX2080Ti GPU (22GB memory). However, the computational complexity significantly varies between these two model versions: SD1.5 FLOPs range approximately between 168G and 561G, whereas SD3.0 FLOPs span from 1.86T to 3.25T. Consequently, inference speed for SD3.0 is substantially slower than SD1.5. To clearly and effectively illustrate speed differences across various experimental configurations in SD3.0, we have reported inference speeds in seconds per iteration (s/it), diverging from the units (it/s) used for other tables. We previously believed this choice enhances readability and comprehension of the substantial computational cost differences involved. We thank the reviewer for raising this, and let us know that it might confuse. We have now updated the table format as follows:
| Method | Base Model | Param. | FLOPs | Speed |
|:------------------:|:----------:|:----------:|:----------:|:------------------------:|
| ControlNet | SD1.5 | **0.36 G** | _233 G_ | _5.23±0.07 it/s_ |
| ControlNet-Large | SD1.5 | 0.72 G | 561 G | 4.02±0.05 it/s |
| FlexControl(γ=0.7) | SD1.5 | 0.73 G | 393 G | 4.94±0.07 it/s |
| FlexControl(γ=0.5) | SD1.5 | 0.73 G | 280 G | _5.21±0.12 it/s_ |
| FlexControl(γ=0.3) | SD1.5 | 0.73 G | **168 G** | **5.64±0.12 it/s** |
| ControlNet | SD3.0 | **1.06 G** | 3.25 T | (20.68±0.56)E-3 it/s |
| ControlNet-Large | SD3.0 | 2.02 G | 6.22 T | (16.82±0.51)E-3 it/s |
| FlexControl(γ=0.7) | SD3.0 | 2.03 G | 4.35 T | (19.18±0.78)E-3 it/s |
| FlexControl(γ=0.5) | SD3.0 | 2.03 G | _3.11 T_ | _(21.86±0.86)E-3 it/s_ |
| FlexControl(γ=0.3) | SD3.0 | 2.03 G | **1.86 T** | **(24.49±0.82)E-3 it/s** |
We will apply this update in the next version of the manuscripts. | Summary: This paper studies the Computation-Aware ControlNet by proposing a dynamic routing strategy which dynamically selects blocks to activate at each denoising step. It aims at adjusting control blocks based on timestep and
conditional information while maintaining (or even improving) generation quality. The experimental results show its effectiveness (higher score).
### update after rebuttal
The response addressed my concerns partially. I would like to increase my initial rating, but I am also not against Rejection, as other reviewers an I both have some concerns on the performance (such as FLOPs, compuatational cost, the impact caused by hyperparameters.).
Claims And Evidence: Yes.
Methods And Evaluation Criteria: Yes.
Theoretical Claims: N/A
Experimental Designs Or Analyses: No issues.
Supplementary Material: All parts.
Relation To Broader Scientific Literature: It is helpful for designing an efficient controlnet for the image generation community.
Essential References Not Discussed: This paper proposes the dynamic routing strategy, which have been widely studied in computer vision community, like [1,2,3], even in text2image [4], while it does not discuss them.
[1] Cai et al., Dynamic Routing Networks
[2] Wang et al., SkipNet: Learning Dynamic Routing in Convolutional
Networks
[3] Ma et al., DiT: Efficient Vision Transformers with Dynamic
Token Routing
[4] Xue et al., RAPHAEL: Text-to-Image Generation via Large Mixture of Diffusion Paths
Other Strengths And Weaknesses: Strengths:
The proposed method is efficient, achieving better performance with lower FLOPs.
Weaknesses:
- The proposed method requires more parameters than the typical controlnet.
- In Tab.3, why do not compare with controlnet++. ControlNext should also be compared w.r.t. performance and parameters and flops.
- In Tab.5, what is the control signal? Why do not provide the relevant results in Tab.1 for clear comparison?
- How to optimize the cost loss (Eq. 17).
- There are many previous works for dynamic routing strategy. The authors do not review them, and the proposed implementation also does not contain new thing.
Other Comments Or Suggestions: -
Questions For Authors: See Weaknesses.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We hope the answer below solves all the clarity issues.
> The proposed method requires more parameters than the typical controller.
Yes, our method requires more parameters than standard ControlNet. However, compared to ControlNet-Large, **it achieves better generation quality and controllability while halving inference FLOPs and improving inference speed**. As discussed in Remark (page 4), the additional parameters have a negligible impact on GPU memory and inference performance.
Importantly, **our focus is not on parameter efficiency within control blocks but on dynamic routing for adaptive efficiency. Our approach is also compatible with recent parameter-efficient control methods, such as ControlNext and OmniControl, as noted in our response to Reviewer eHec.**
> not compare with ControlNet++ and controlnext on flops and parameters
We would like to clarify that our research does not focus on designing more efficient control block structures but rather on investigating how to integrate control blocks effectively and efficiently into pre-trained diffusion models. In this sense, our work is orthogonal to ControlNeXt methods, which is why we initially excluded it from Table 1 and Table 2. However, our approach can potentially be adopted by ControlNeXt to further enhance its performance.
We appreciate the reviewer's suggestion for additional experiments. To evaluate our method in the context of ControlNeXt, we refer the reviewer to our response to Reviewer eHec. Briefly, since ControlNeXt applies control to all blocks by default, our method achieves comparable performance to ControlNeXt at $\gamma$ = 0.3 and outperforms it at $\gamma$ = 0.5.
Regarding ControlNet++, it primarily focuses on improving training strategies while maintaining the same inference cost as the standard ControlNet. In contrast, our work explicitly targets inference efficiency. Thus, a direct comparison is not applicable. Nevertheless, we acknowledge the relevance of these methods and will consider discussing them in future versions of our paper.
> In Tab.5, what is the control signal? Why do not provide …
Table 5 presents an ablation study on different control strategies under the "Canny edge" control signals.
We agree with the reviewer's suggestion and will reorganise the table in a camera-ready version to improve the clarity.
> How to optimize the cost loss (Eq. 17).
The FLOPs loss is computed by referencing pre-computed FLOPs values from a lookup table, which are then combined with the diffusion loss using a scaling factor. This approach aligns with prior research[a,b,c] **(as referred to in response to reviewer eKoB)**, on dynamic and efficient neural network architectures that optimize computational cost while maintaining performance. We will add those parts in the related works.
>There are many previous works for dynamic routing strategy…
We appreciate the reviewer’s suggestion to discuss prior work on dynamic routing strategies. While our method shares some conceptual similarities with existing approaches, its goal and implementation are fundamentally different. Below, we clarify these distinctions concisely:
- [1] (Dynamic Routing Networks): Introduces a model with multiple branches, where a learned router selects the best path for each input to improve efficiency. Their method is trained from scratch for classification and focuses on reducing FLOPs. In contrast, our approach dynamically adjusts the influence of a fine-tuned ControlNet within a pre-trained diffusion model, aiming for controlled generation rather than computational savings.
- [2] (SkipNet): Uses a gating mechanism to decide whether to skip certain convolutional layers, reducing computation for easier inputs. Unlike SkipNet, which skips layers within a single network, our method balances contributions between a fixed diffusion backbone and a fine-tuned control module. We modulate control strength from ControlNet to a pre-trained diffusion model for better adaptation.
- [3] (DiT: Dynamic Token Routing): Dynamically routes image tokens within a Vision Transformer, deciding which tokens to process at each layer for efficiency. While DiT optimizes computation by selectively processing tokens, our method adjusts how much control blocks the ControlNet influences the final output, without altering token flow within the transformer.
- [4] (RAPHAEL): A large-scale diffusion model using a mixture-of-experts (MoE) to assign different paths for different styles or concepts. RAPHAEL is trained from scratch on massive datasets, while our approach efficiently adapts a pre-trained diffusion model using dynamic routing, making it suitable for low-data settings.
**These prior works focus on optimizing efficiency or designing new architectures, while our method adapts an existing pre-trained model for more flexible and controlled generation**. We appreciate the reviewer’s suggestion and will incorporate this discussion into the final version of our paper. | Summary: The paper addresses the limitations of existing ControlNet implementations in diffusion-based generative models, which often rely on ad-hoc heuristics for selecting control blocks. The authors employs a trainable gating mechanism to dynamically select which blocks to activate at each denosing step.
Claims And Evidence: Yes
Methods And Evaluation Criteria: Yes
Theoretical Claims: no theoretical claims.
Experimental Designs Or Analyses: Yes, the paper uses various metrics and baselines to support the effectiveness of the proposed method.
Supplementary Material: I have check the appendix and there is no other supplementary material.
Relation To Broader Scientific Literature: The introduction of a computation-aware training loss aligns with prior research on optimizing computational efficiency in generative models.
Essential References Not Discussed: No
Other Strengths And Weaknesses: Strengths:
1. The paper is well-written and organized.
2. The paper introduces a novel dynamic control mechanism that enhances the adaptability of diffusion models, moving away from static, heuristic methods.
3. The paper includes extensive experiments across multiple architectures (UNet and DiT) and various tasks, providing robust evidence of FlexControl's effectiveness.
Weaknesses:
1. The ablation study presented in the paper lacks rigor and comprehensiveness. The authors should investigate how the performance of FlexControl is affected by replacing the proposed gating mechanism with simpler alternatives, such as random selection of control blocks.
2. At the optimal performance setting (\lambda=0.5), both the number of parameters and the FLOPs (Floating Point Operations) are worse than those of ControlNet. This raises concerns about the validity of their claims regarding efficiency.
3. Also no code provided here make it harder to evaluate the method.
Other Comments Or Suggestions: None
Questions For Authors: 1. In Table 3, why does the speed decrease when \(\lambda\) changes from 0.3 to 0.5 with SD1.5?
2. How should \(\lambda_C\) be chosen, and does its value affect performance?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank the reviewer for the positive feedback and support of our work. We hope to have answered all of your questions satisfactorily below. Please let us know if you see any further issues in the paper that must be clarified or addressed.
> The ablation study … with simpler alternatives, such as random selection of control blocks…
We sincerely thank the reviewer for their suggestion to conduct ablation studies on simpler alternatives to the random selection of control blocks. In response, we have considered the following alternative sampling strategies.
As suggested, we first evaluate the simplest strategy—uniform sampling—where 50% of the control blocks are randomly selected, denoted as Uniform.
The experimental results corresponding to these sampling strategies are presented below.
| Method | Base Model | FID | CLIP_score | mIoU | FLOPs | Speed |
|--------------------|:----------:|:---------:|:----------:|:----------:|:---------:|:------------------:|
| Uniform | SD1.5 | 19.14 | 0.2600 | 0.3024 | 323 G | 4.95±0.07 it/s |
| FlexControl(γ=0.3) | SD1.5 | _17.21_ | _0.2713_ | _0.3572_ | **168 G** | **5.64±0.12 it/s** |
| FlexControl(γ=0.5) | SD1.5 | **14.80** | **0.2842** | **0.3751** | _280 G_ | _5.21±0.12 it/s_ |
Notably, compared to all random sampling strategies, our approach with $\gamma$ = 0.3 achieved superior performance and higher inference speed. Moreover, the FID score improves from 17.21 to 14.80 when $\gamma$ is increased from 0.3 to 0.5. This ablation study further demonstrates the effectiveness of our method, and we will incorporate these findings into the camera-ready version of our paper.
>At the optimal performance setting ($\lambda$=0.5)... regarding efficiency…
We would like to clarify that our method with $\gamma$ = 0.3 has already outperformed the ControlNet baseline in both SD1.5 and SD3.0 experiments, as demonstrated in Table 4 and Table 5 of the original paper, while also achieving significantly lower FLOPs, as shown in Table 3.
Our choice of $\gamma$ = 0.5 for comparison in Table 1 and Table 2 is not because it represents the optimal value, but rather because it provides a more direct comparison with the ControlNet baseline in terms of computational cost (280G FLOPs vs. 233G FLOPs). In contrast, when $\gamma$ = 0.3, the FLOPs are substantially lower at just 168G. We decide to add all $\gamma$ value experiment results in Table 1 and Table 2 to increasing the clarity in camera ready version.
> code links
We provided anonymous links for comparison and reproduction:【https://github.com/Anonym916/Anonymity】
> In Table 3. why does the speed decrease from 0.3 to 0.5
Since $\gamma$ represents the expected overall number of activated blocks, increasing $\gamma$ results in a higher number of active blocks, leading to increased computational cost (FLOPs) and consequently lower inference speed. This explains the observed decrease in speed from $\gamma$ = 0.3 to $\gamma$ = 0.5 in Table 3. We will refine our text in the camera-ready version to improve clarity.
> How should ($\lambda_C$) be chosen, and does its value affect performance?
$\lambda_C$ is a scaling factor that balances the diffusion objective and the FLOPs constraint objective. Since these two loss functions operate on different scales, $\lambda_C$ is necessary to ensure proper weighting between them. We tune this value to achieve the target activation percentage while maintaining overall performance. Proper selection of $\lambda_C$ ensures that the model activates the desired number of blocks without significantly degrading generation quality. We proposed to use $\lambda_C$ = 0.5 in all our experiments as an experience value. | null | null | null | null | null | null |
SToFM: a Multi-scale Foundation Model for Spatial Transcriptomics | Accept (poster) | Summary: The authors introduce SToFM, a single-cell foundation model that incorporates not only the single-cell expression data but also their spatial locations. They propose SToCorpus-88M, one of the largest single-cell pretraining datasets curated to date, and also pretrain their model on the large pretraining dataset. It is demonstrated that SToFM is able to outperform a lot of recent SOTA ST FM such as Geneformer, Nicheformer, and scGPT.
Claims And Evidence: Most are well-supported - However, I think the claim that SToCorpus-88M is the largest high-resolution ST pretraining corpus to date needs to be thoroughly validated.
Methods And Evaluation Criteria: Yes, the authors validate SToFM on diverse tasks such as ST imputation, morphological segmentation, and etc. and show universally better performance.
Theoretical Claims: No theoretical claims are made.
Experimental Designs Or Analyses: I think the explanations on each experiment is quite lacking. For instance, for morphological segmentation, it is unclear how many regions are being segmented. For imputation, it's unclear how SToFM is being used to infer the ST for certain cells. In short, I have doubts that the readers can "reproduce" the experimental results just based on what is provided in the paper.
Supplementary Material: Yes, all of them. It contains additional ablation experiments and details about SToFM training and architecture.
Relation To Broader Scientific Literature: I think it is well-placed in terms of broad literature, especially with encouraging results against the SOTA baselines.
Essential References Not Discussed: I think maybe recently-published public ST benchmarks (although they are predominantly Visium-based) deserve some references.
[1] Jaume, Guillaume, et al. "Hest-1k: A dataset for spatial transcriptomics and histology image analysis." Advances in Neural Information Processing Systems 37 (2024): 53798-53833.
[2] Chen, Jiawen, et al. "STimage-1K4M: A histopathology image-gene expression dataset for spatial transcriptomics." ArXiv (2024): arXiv-2406.
Other Strengths And Weaknesses: While there are many strengths in this work, as demonstrated with diverse evaluation tasks against many SOTA baselines, there are several factors in this study that prevents me from giving higher score.
**Lack of clarity & details**: The technical details behind SToFM and the experiment details are quite lacking, to the point that it is a bit hard to understand and replicate what the authors have proposed. For instance, in domain-adaptation phase, there are at least 7 different platforms from which the data comes from - Is the domain-adaptation performed on all 88M points? In what sequence? Does each batch randomly sample from 88M point each time? Why only one epoch?
How are the sub-slice generated exactly? The authors only mention that it roughly contains 1,000 genes per sub-slice and it's probably hard for readers to replicate.
For the experiments, it's unclear what number of morphological classes the segmentation is done on - Is it binary, due to the use of F1 and acc? But DLPFC typically has at least 5~6 morphological classes. How are the ST imputation done? How are the 327 inputs used to impute for 50 outputs?
In short, I would cut down verbose explanations on the architecture and paradigm and focus on providing more technical/experimental details.
**Lack of ablations**: Right now, it feels like SToFM is a combination of existing parts (geneformer & SE(2) encoder & masking loss) put together. While I think that is fine and how the field advances, I feel like there is lack of motivation/explanation behind each of the component design choices. To really make strong claims about SToFM, I think the authors need to perform more extensive ablations (other than just cell/micro/macro ablations)
- Data efficiency: That 88M is very big size is good, but is this really what drives the performance? Especially if the authors are only performing one epoch of pretraining. I would like the authors to try pretraining SToFM with only fractions of data (e.g., 12.5%, 25%, 50%) to see whether SToFM really follows the scaling law and that all 88 M datapoints are needed.
- SE(2) Transformer: Can we try with different architecture (e.g., without spatial distance) to really show that the distance information is really required? I feel like expression reconstruction alone could be sufficient, but I might be wrong.
- Masking ratio: The masking ratio is universally 10%. Given that typical use of Masked Image Modeling use higher masking ratio than 10%, I would like the authors to show the effect of this.
- Geneformer initialization: What if it is randomly-initialized? What if other pretraining weights are used?
Other Comments Or Suggestions: - How are the authors dealing with batch effect that arises from integrating 7 different sequencing platforms? There wasn't a reference to any efforts for batch effect correction, so I think it's very important.
- Continual training can easily lead to catastrophic forgetting - Have the authors observed this + What have authors done to prevent any form of collapse?
- scGPT in Table 1 says it doesn't use expression values - but scGPT uses expression values as well. What did the authors mean to say here?
- Leiden clustering cannot control for exact number of clusters, i.e., virtual cells in each sub-slice. How do authors control for this?
- Are the authors planning to release SToCorpus-88M publicly?
Questions For Authors: Please see above
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Dear Reviewer tnYZ:
Thanks for your appreciation and detailed review! We try our best to response your questions. Due to space limitations, we include **tables and references in the anonymous link** https://anonymous.4open.science/api/repo/stofm-rebuttal/file/rebuttal-tnYZ.pdf?v=af96a9f5, and refer to them in the following as *Rebuttal-Table X* and [X], separately.
>Q1: About SToCorpus-88M.
- **Is it the largest?** To our best knowledge, it is the cell-resolution ST pretraining corpus that contains the largest number of both slices and data points.
- **Will it be released?** Yes, it will be publicly released.
- **Recently-published ST datasets.** Thank you! We will add citations to the revised manuscript.
>Q2: Lack of clarity and details.
Apologies for the lack of clarity. We promise to **add details to the revised version and release detailed code**.
- **Domain-adaptation**
Domain adaptation performs an epoch in random order on all 88M data points. The loss had converged at the late stage of the first epoch.
- **How are the sub-slice generated exactly?**
First, we divide the slice into rectangles of the same size. Then, for each rectangle, we merge or split it according to the number of cells it contains. The code will be released for reproducing.
- **Number of morphological classes?**
They are multi-classifacation tasks. We have provided experimental details in the *Rebuttal-Table 1*.
- **How is the ST imputation done?**
We trained a fully connected neural network with cell representations from SToFM to obtain 50 outputs, as a multi-target regression task.
>Q3: Lack of ablations
We will **add more ablation studies in the revised version**.
- **Data efficiency**
Due to the high computational cost, we pretrain the multi-scale ST representation learning phase using 12.5% and 50% of the data during rebuttal, as shown in *Rebuttal-Table 2*. The results show that reduction in data volume led to a significant decrease in model performance. Considering that the SToCorpus-88M consists of approximately 2,000 ST slices, we believe that reducing the amount of data may reduce data diversity and limit the model's transferability. Additionally, we would like to clarify that, as mentioned in Section 4.1, we conducted 1 epoch and 3 epochs in each of the two training stages.
- **SE(2) Transformer**
We conduct ablation studies on the PDR loss and the spatial distance matrix, as shown in *Rebuttal-Table 3*. For more analysis, please refer to the response Q1 to Reviewer LBxH. In addition, the effectiveness and efficiency of the SE(2) Transformer are discussed in detail in Uni-Mol[1]. And when incorporating spatial information in ST data, we primarily focus on the interactions between neighboring cells. Therefore, using the distance-based architecture is in line with the data characteristics.
- **Masking ratio**
Masking ratios are set according to the specific data. Each point in ST data contains high-dimensional features, which increase the data complexity. We had attempted to mask 20% of the cell expressions and perturb another 20% of the cell positions, but found training difficult to converge. In addition, [2] has demonstrated that models are usually robust to mask probabilities when they can converge properly.
- **Geneformer initialization**
If randomly initialized, it will incur expensive computational overhead to train a cell encoder from scratch. And due to the lower quality of gene expressions in ST data compared to scRNA-seq data, our pre-experiments indicate that it is difficult to converge in early training. Considering that Geneformer is one of the SOTA models, and domain adaptation was performed using a large amount of data, we believe there will not be a significant difference if using other SOTA models such as scGPT [3].
>Q4: Batch effect correction.
Please refer to the response Q5 to Reviewer Rgcj.
>Q5: Catastrophic forgetting.
Catastrophic forgetting may cause the model's suitability for scRNA-seq data to decrease while becoming more suitable for ST data.
- SToFM is a model specialized for ST data, and we do not recommend users to apply SToFM on scRNA-seq data scenarios.
- We conduct an experiment on scRNA-seq data. As shown in *Rebuttal-Table 4*, there is almost no drop in performance. This may be because the distribution of gene expressions in ST data and scRNA-seq data is similar.
>Q6: scGPT in Table 1.
Apologies for the confusion. The table header is "ST Pretraining", and what we want to express is that scGPT did not use gene expressions from ST data during pretraining.
>Q7: Leiden cannot control the number of clusters.
After clustering, the number of clusters will be checked. If it does not fall within 20-100, the resolution of Leiden will be adjusted to re-cluster until the cluster number meets the requirement.
___
Thank you again for your insights which are invaluable in solidifying our work. Should our responses address your queries, we would deeply appreciate your support.
---
Rebuttal Comment 1.1:
Comment: The response by the authors look thorough and satisfactory. Before I contemplate about changing the scores, I want authors to provide additional numbers & details if possible. I have noticed that most of the rebuttal experiments have been reported with F1.
- Can authors provide details behind F1 score, which I think is important, in the context of multiclass settings.
- Can authors provide **balanced accuracy** score (or macro-averaged AUC) as well, so we have different views of the same experiment.
---
Reply to Comment 1.1.1:
Comment: Thank you for your appreciation! We do our best to provide more detailed information below:
>Comment Q1: Details behind F1 score
- Line 331 of the paper states that we use macro F1-score for multi-class classification problems, which means calculating the F1-score for each class and then taking the average. As follows:
$F1_i=\frac{2P_iR_i}{P_i+R_i}$,
macro-$F1=\frac{1}{N}\sum_iF1_i$,
Where $P_i$, $R_i$, and $F1_i$ are the precision, recall, and F1 score of class $i$, respectively. N is the number of classes.
- Below, as an example, we provide the intermediate results of calculating the macro F1-score of SToFM on Embryo2. As shown in *Rebuttal-Table 1*, there are 16 classes. (The results reported in the paper are average of three repeated experiments, and the results below are from one of them.)
|Class|Number|Precision|Recall|F1-score|
|-|-|:-:|:-:|:-:|
|Brain|153|0.899|0.758|0.823|
|Branchial Arch|45|0.714|0.333|0.455|
|Cloaca|71|0.922|0.831|0.874|
|Ganglion|131|0.782|0.519|0.624|
|Heart|243|0.956|0.979|0.967|
|Hepatic Diverticulum|44|0.740|0.841|0.787|
|Limb Ectoderm|187|0.843|0.888|0.865|
|Lung Primordium|96|0.738|0.823|0.778|
|Meninges|181|0.727|0.796|0.760|
|Mesonephron|51|0.864|0.745|0.800|
|Pancreas Bud|54|0.920|0.852|0.885|
|Pharyngeal|64|0.714|0.781|0.746|
|Primitive Gut|92|0.784|0.870|0.825|
|Somite|463|0.842|0.842|0.842|
|Spinal Cord|422|0.877|0.943|0.909|
|Surface Ectoderm|246|0.864|0.907|0.885|
|**Macro F1-score**||||**0.802**|
>Comment Q2: Balanced accuracy and macro-averaged AUC-ROC
For experiments of Rebuttal-Table 2-4, we additionally calculate the balanced accuracy and macro-averaged AUC-ROC, which are reported below:
- Rebuttal-Table 2
|Data volume|Macro F1|Balanced accuracy|Macro AUC-ROC|
|-|:-:|:-:|:-:|
|**Embryo2**||||
|12.5%|0.758|0.764|0.968|
|50%|0.782|0.790|0.968|
|100%|0.801|0.799|0.972|
|**EmbryoCross**||||
|12.5%|0.423|0.518|0.927|
|50%|0.450|0.546|0.930|
|100%|0.459|0.551|0.933|
- Rebuttal-Table3
|Model|Macro F1|Balanced accuracy|Macro AUC-ROC|
|-|:-:|:-:|:-:|
|**Embryo2**||||
|w/o $\mathcal{L}_{PDR}$|0.749|0.756|0.965|
|w/o spatial distance matrix|0.721|0.704|0.957|
|SToFM|0.801|0.799|0.972|
|**EmbryoCross**||||
|w/o $\mathcal{L}_{PDR}$|0.437|0.520|0.929|
|w/o spatial distance matrix|0.413|0.525|0.920|
|SToFM|0.459|0.551|0.933|
- Rebuttal-Table 4
|Model|Macro F1|Balanced accuracy|Macro AUC-ROC|
|-|:-:|:-:|:-:|
|scBERT|0.905|0.906|0.988|
|Geneformer|0.957|0.949|0.995|
|SToFM-CellEncoder|0.944|0.949|0.993|
We will also add more details and evaluation results in the revised edition of the paper.
___
Thank you again for your help in solidifying our work! | Summary: This paper introduces a foundation model for cell spot representation of spatial transcriptomics. It fine-tunes the pretrained cell embedding (from existing scRNA foundation models) by incorporating the location information via masked feature prediction and noised distance information recovery, as well as involving the proposed virtual macro cells. A series of down-stream tasks are performed with the pretrained spot embeddings to demonstrate the effectiveness of them.
Claims And Evidence: The ablation study is not sufficient to support the effectiveness of the fine-tuning with the incorporation of distance information.
Methods And Evaluation Criteria: For the Pairwise Distance Recovery (PDR), it is not sure that the cell embedding contains sufficient distance information to make the distance recovery mechanism feasible.
Theoretical Claims: No theoretical contribution is introduced in this work.
Experimental Designs Or Analyses: The experiments are extensive and relatively comprehensive.
Supplementary Material: Supplementary material show the details of the adopted network architectures, as well as more results. Codes are also provided with supplementary material.
Relation To Broader Scientific Literature: It is an important direction to develop sing-cell rna expression, and there emerge a large body of pretrained foundation model for this purpose. This paper extend to incorporate location information of ST for better spot embedding learning.
Essential References Not Discussed: Most essential references are mentioned.
Other Strengths And Weaknesses: It is an important direction to pretrain spot representation with the consideration of location information.
This paper is well written and easy to follow.
The proposed model only trained on cell resolution spatial transcriptomics data, and the feasibility of extending to low resolution ST remains unknown.
Other Comments Or Suggestions: N/A
Questions For Authors: Not very sure the effectiveness of the way to formulate the virtual cell, i.e., simple by averaging of the representation and location.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Dear Reviewer LBxH:
Thanks for your appreciation and detailed review. We try our best to response the questions below:
>Q1: The ablation study is not sufficient to support the effectiveness of the fine-tuning with the incorporation of distance information.
Thank you for your suggestions! We conduct an ablation study on the spatial distance matrix. As shown in the Table below, the results demonstrate that removing the spatial distance matrix significantly decreases model performance. Essentially, the SE(2) Transformer relies on the spatial distance matrix to establish relationships between cells. If spatial distance matrix is removed, the ability of the model to perform intercellular information interactions will be compromised.
|Model|Embryo2-F1| EmbryoCross-F1|
|-|:-:|:-:|
|w/o distance matrix|0.721|0.413|
|SToFM|0.801|0.459|
>Q2: For the Pairwise Distance Recovery (PDR), it is not sure that the cell embedding contains sufficient distance information to make the distance recovery mechanism feasible.
- **Intuitively**, the spatial autocorrelation of cellular expression profiles [1], as well as the ligand-receptor intercellular signaling pathways of neighboring cells can help to recover the original distances from the noisy data.
- **Experimentally**, the PDR loss can be converged well during our pre-training process. Moreover, following the discussion in Uni-Mol [2] about recoverability of distances, we only add limited noise to the cell coordinates, which does not obscure all spatial location information. This makes this pre-training task more feasible.
>Q3: The proposed model only trained on cell resolution spatial transcriptomics data, and the feasibility of extending to low resolution ST remains unknown.
- **SToFM can be applied to low-resolution ST data without domain adaptation.** In the DLPFC experiment of Section 4.2, we specifically chose the low-resolution 10x Visium data, and SToFM performed exceptionally well in this task, demonstrating that the model can be scaled to low-resolution ST data.
- Advancements in biotechnology in recent years have continuously improved the resolution of ST data, making the analysis of high-resolution ST data a more valuable direction in the field of bioinformatics [3].
>Q4: Not very sure the effectiveness of the way to formulate the virtual cell, i.e., simple by averaging of the representation and location.
- **Intuitively**, the main purpose of constructing virtual cells is to provide a summary of information from global tissue sections. After clustering by combining expression embedding and location information, each cluster should contain a set of cells that are close in location and have similar expression. Thus, by averaging the embedding and position of the cells within a cluster, it is possible to say "there is a cluster of cells with similar expression at this location". We believe this is methodologically sound. The use of average or sum for simple yet effective pooling is also widely applied in fields such as graph representation learning [4].
- **Experimentally**, our ablation experiments demonstrate that incorporating macro-scale information through virtual cells can effectively improve model performance. In addition, we calculate the similarity of expression embeddings and spatial positions of some virtual cells with each cell in the cluster, as shown in the Table below.
|Sample ID|Pearson correlation of expression embeddings|Cosine Similarity of positions|
|-|:-:|:-:|
|1|0.863|0.804|
|2|0.871|0.833|
|3|0.893|0.853|
The results indicate a high similarity between the expression embeddings and positions of the virtual cell and individual cells within the cluster.
___
Thank you again for your detailed review! Your insights have been invaluable in aiding us to enhance and solidify our work. Should our responses satisfactorily address your queries, we would deeply appreciate your support for our work.
Refs:
[1] Mapping the transcriptome: Realizing the full potential of spatial data analysis
[2] Uni-Mol: a universal 3D molecular representation learning framework
[3] Methods and applications for single-cell and spatial multi-omics
[4] Graph pooling in graph neural networks: methods and their applications in omics studies | Summary: The paper proposes a multi-scale foundation model to integrate macro-scale tissue morphology, micro-scale cellular microenvironment and gene-scale gene expression profile of spatial transcriptomics. The author constructs a large-scale spatial transcriptomics corpus containing approximately 2,000 tissue slices and 88 million cells for pretraining, which is claimed to be released. Various downstream tasks are validated to prove the performance.
Claims And Evidence: The paper claims to propose a multi-scale foundation model that captures and integrates information from macro, micro and gene scale of spatial transcriptomics. The ablation on the three scale is conducted in Table 5. Large performance improvement is shown at the second and fourth row in Tabel 5. However, performance improvement involving micro scale by adding the SE(2) Transformer is relatively limited. The author should include an ablation experiment evaluating the model’s performance when using only macro- and gene-scale features without micro-scale components. Besides, the author requires isolating the effect of the spatial distance matrix through experiments comparing performance with and without this component. The sensitivity of sample rate on the second-time cell encoding mentioned in Sec. 3.2 should be explored. And the effect of incorporating spatial information should also be evaluated in ablation study.
Methods And Evaluation Criteria: The evaluation criteria makes sense for the analysis of spatial transcriptomics representation. The downstream tasks about human embryonic structure segmentation, DLPFC layer segmentation, cell type annotation in spatial transcriptomics are validated in the experiments. Accuracy and F1 are reported to evaluate the segmentation and cell type annotation performance. Besides, the performance in Zero-shot Clustering and Visualization and Spatial Deconvolution illustrates the model’s ability to produce high-quality cell embeddings.
Theoretical Claims: No
Experimental Designs Or Analyses: The experimental designs evaluates the model’s performance in various downstream tasks. The experiments on tissue region semantic segmentation evaluate the model’s ability to understand the functional specialization of cells. The author claims the experiments on cell type annotation in spatial transcriptomics confirm that incorporating spatial information can help improve cell type annotation. But the effect of incorporating spatial information should be evaluated in ablation study. Experiments on zero-shot clustering and visualization illustrate the ability of the model to produce high-quality cell embeddings.The model is also is evaluated to be a effective tool for spatial deconvolution. Experiments on spatial transcriptomics imputation shows the model’s ability to infer the uncaptured gene expression levels. The paper claims to propose a multi-scale foundation model that captures and integrates information from macro, micro and gene scale of spatial transcriptomics. The ablation on the three scale is conducted in Table 5. Large performance improvement is shown at the sencond and fourth row in Tabel 5. However, performance improvement involving micro scale by adding the SE(2) Transformer is relatively limited. It’s needed to evaluate what’s the performance when the model involve both Gene and Macro, except for Micro. Besides, the ablation on the effect of the spatial distance matrix is also needed to be evaluated. Also, ablation on the second-time cell encoding mentioned in Sec. 3.2 is needed to be explored. How does the sample rate influence the performance? The effect of incorporating spatial information should also be evaluated in ablation study.
Supplementary Material: I reviewed the supplementary material, including Architecture of the Model Components, More Experimental Result, Experiment Settings for Pretraining and Downstream Tasks and Dataset.
Relation To Broader Scientific Literature: First, the author we construct SToCorpus-88M, the largest high-resolution ST pretraining corpus to date, which contains approximately 2,000 tissue slices and 88 million cells and is claimed to be released. This contribution will provide a large dataset for further ST analysis. Second, the author proposes a multi-scale foundation model to integrate macro-scale tissue morphology, micro-scale cellular microenvironment and gene-scale gene expression profile of spatial transcriptomics, which provides a idea for integrate multi-scale information from ST.
Essential References Not Discussed: No
Other Strengths And Weaknesses: This paper is clearly written and easy to read. In terms of spatial transcriptome characterization methods, this thesis incorporates macro-, micro-, and gene-scale information and adds positional information, for which the largest spatial transcriptome dataset to date has been created. And the downstream task experiments in this paper are very rich. But the ablation experiment needs to be improved.
Other Comments Or Suggestions: No
Questions For Authors: 1. The author should include an ablation experiment evaluating the model’s performance when using only macro- and gene-scale features without micro-scale components.
2. The author requires isolating the effect of the spatial distance matrix through experiments comparing performance with and without this component.
3. The details on the second-time cell encoding mentioned in Sec. 3.2 should be written. If a sample rate is involved in the second-time cell encoding, the sensitivity of sample rate should be explored.
4. The effect of incorporating spatial information should also be evaluated in ablation study.
5. This paper migrates the single-cell model through a domain adaptation strategy. However, there may be relatively large differences between different ST datasets, such as different technical platforms. How should we further improve adaptability?
Ethical Review Concerns: No
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Dear Reviewer Rgcj:
Thanks for your appreciation and detailed review. We try our best to response the questions below:
>Q1: Ablation experiment on micro-scale components. **&** Q2: The effect of the spatial distance matrix. **&** Q4: The effect of incorporating spatial information.
Thank you for your suggestions for refining the ablation experiments!
- For Q1, We ablate the micro-scale by limiting the scale of sub-slices to 1, to ensure that the cells could only interact informationally with the virtual cells that represent macro-scale information, but not with other cells in the micro-environment. Experimental results are shown in the Table below. A significant decrease in performance is observed, which demonstrates the effectiveness of incorporating the micro-scale information.
- For Q2, we conducted an ablation study on the spatial distance matrix. The spatial information is very underutilized in this case, only used to construct virtual cells and divide sub-slices. As shown in the Table below, the results demonstrate that removing the spatial distance matrix significantly decreases model performance.
- For Q4, we had presented the results of completely ablating spatial information in the second row "Cell Encoder w/ DA" of Table 5 of our paper. We repeat the results in the Table below. Essentially, we rely on spatial information to establish relationships between multiple cells, with both micro- and macro-scale information being part of spatial information. If spatial information is removed, the model will not be able to interact between cells at all, essentially degrading to independently encoding each single cell.
|Model|Embryo2-F1| EmbryoCross-F1|
|-|:-:|:-:|
|Q1: w/o micro|0.721|0.425|
|Q2: w/o spatial matrix|0.721|0.413|
|Q4: w/o spatial information (i.e. Cell Encoder w/ DA)|0.718|0.415|
|SToFM|0.801|0.459|
>Q3: The details on the second-time cell encoding mentioned in Sec. 3.2 should be written. If a sample rate is involved in the second-time cell encoding, the sensitivity of sample rate should be explored.
- We will present more details in the revised paper, and will release detailed code to help readers better understand and reproduce our approach.
- We will add experiments and discussion on the sample rate. The purpose of the second time cell encoding is to enable L_MCM and L_PDR to optimize the cell encoder through backpropagation. To balance the training cost and model performance, we use only a small number of cells for this computation, which is similar to selecting a smaller batch size to update the cell encoder. For the selection of the sampling number, we determined the number of samples to be 12, given that the original Geneformer paper gave a training batch size of 12.
- Considering the computational cost, we test the impact of the sample number on a small amount of data (1/8 of the SToCorpus-88M), as shown in the Table below. The results show that the model has some robustness to this hyperparameter, just as the batch size often only affects the convergence speed rather than the model performance. However, setting the sample size to 0, i.e. freezing the cell encoder, will lead to a decrease in model performance.
|Sample number|Embryo2-F1| EmbryoCross-F1|
|-|:-:|:-:|
|0|0.722|0.417|
|4|0.754|0.424|
|12|0.758|0.423|
>Q5: This paper migrates the single-cell model through a domain adaptation strategy. However, there may be relatively large differences between different ST datasets, such as different technical platforms. How should we further improve adaptability?
- Research such as scGPT [1] and LangCell [2] has already proven that large-scale pretraining is one of the best ways to remove batch effects in scRNA-seq data. Nicheformer [3] has also demonstrated that by pretraining, the model can gain modeling capabilities across different ST technology platforms. Indeed, despite the gap between different datasets, the underlying gene co-expression, intercellular signaling pathways, and other information should be largely uniform, which makes them have similar distributions that can be captured by the pre-trained model.
- In the DLPFC experiments in Section 4.2, we purposely chose 10x Visium data that was not used in the pretraining. The excellent performance of SToFM on this task also proves that the model has gained the ability to transfer across technology platforms from the pretraining. We believe that our model and dataset can be of great help for future research in the application scenario of batch integration.
___
Thank you again for your detailed review! Your insights have been invaluable in aiding us to solidify our work. Should our responses address your queries, we would deeply appreciate your support for our work.
Refs:
[1] scGPT: toward building a foundation model for single-cell multi-omics using generative AI
[2] LangCell: language-cell pre-training for cell identity understanding
[3] Nicheformer: a foundation model for single-cell and spatial omics
---
Rebuttal Comment 1.1:
Comment: In the author's "Ablation Study", it states, "we ablate the model’s ability to jointly model multiple cells at the micro-scale by removing the SE(2) Transformer." This implies that the SE(2) Transformer is responsible for capturing micro-scale features. Given this, for Q1, wouldn't it be more appropriate to remove the SE(2) Transformer while retaining the virtual cell to assess the model’s performance using only macro- and gene-scale features, without micro-scale components? However, in the current ablation, the author limits the sub-slice scale to 1 to remove micro-scale modeling. In this case, wouldn’t the SE(2) Transformer still capture interactions among micro-scale cells within the sub-slice?
---
Reply to Comment 1.1.1:
Comment: Apologies for the confusion. We try our best to clarify as follows:
1. First of all, we would like to clarify that "*the SE(2) Transformer is only responsible for capturing micro-scale features*" is a misunderstanding. The SE(2) Transformer is used for encoding **both macro-scale and micro-scale** information. It captures micro-scale information by modeling intercellular relationships in the microenvironment, and captures macro-scale information by modeling relationships between cells and virtual cells. Removing SE(2) Transformer will remove both macro-scale and micro-scale information simultaneously.
2. The context of this sentence in the "Ablation Study" is: "*We **first ablate the macro-scale** information by removing the virtual cells. **Then, we ablate ... micro scale** by removing the SE(2) Transformer.*" What we want to express is that in the case of **already ablating the macro scale**, removing the SE(2) Transformer can **further ablate the micro scale**, i.e., ablate both macro- and micro-scale, as shown in Table 5. We will use a clearer statement in the revised paper.
3. **Q:** Wouldn't it be more appropriate to remove the SE(2) Transformer while retaining the virtual cell?
**A:** We use SE(2) Transformer to integrate information from cells and virtual cells. Therefore, it is unreasonable to conduct an ablation study that remove SE(2) Transformer but retain virtual cells.
4. **Q:** The author limits the sub-slice scale to 1 to remove micro-scale modeling. In this case, wouldn’t the SE(2) Transformer still capture interactions among micro-scale cells within the sub-slice?
**A:** SE(2) Transformer captures micro-scale information by modeling cells in the microenvironment, and captures macro-scale information by modeling virtual cells. Therefore, we remove the cellular microenvironment by setting the sub-slice size to 1 in rebuttal Q1. In this case, only one cell and some virtual cells are input to the SE(2) Transformer. **Since there is only one cell in the sub-slice, the microscale information is de facto absent, and the SE(2) Transformer is naturally unable to capture the micro-scale cell-cell interactions.**
5. More intuitively, We summarize the relationship between modules and scales as follows:
**Virtual Cells + SE(2) Transformer -> macro-scale**
**Microenvironment + SE(2) Transformer -> micro-scale**
|Ablation|gene scale|micro scale|macro scale|
|-|:-:|:-:|:-:|
|w/o SE(2) Transformer (*CellEncoder w/ DA* in **Table 5**)|$\checkmark$|$\times$|$\times$|
|w/o virtual cells (*SToFM w/o VCs* in **Table 5**)|$\checkmark$|$\checkmark$|$\times$|
|w/o microenvironment (*w/o micro* in **Rebuttal Q1**)|$\checkmark$|$\times$|$\checkmark$|
___
Thank you again for your help in solidifying our work! | Summary: The paper proposes SToFM, a multi-scale Spatial Transcriptomics foundation model, to effectively integrate macro-, micro-, and gene-scale information from Spatial Transcriptomics (ST) data. SToFM uses a combination of gene expression profiles, cell coordinates, and spatial relationships to learn representations of cells in their tissue context. It employs domain adaptation for gene expression embeddings, integrates spatial information using an SE(2) Transformer, and introduces novel pretraining tasks like masked cell modeling and pairwise distance recovery. The model outperforms existing methods on several biological tasks, demonstrating its ability to capture complex multi-scale biological information.
Claims And Evidence: There may be a domain gap between ST data and scRNA-seq data. While ST data contains spatial information, scRNA-seq data only includes gene expression values. Therefore, the justification for bridging the significant gap between these two data types through transfer learning is insufficient.
Methods And Evaluation Criteria: Since this model requires pretraining of the cell encoder, its scalability is limited. Additionally, training both the cell encoder and the SE(2) Transformer can result in significant computational costs. However, the paper lacks running time experiments and time complexity analysis.
Theoretical Claims: This paper does not present theoretical analysis.
Experimental Designs Or Analyses: The alpha value in Algorithm 1 represents the combination ratio of cell embeddings and cell positions. However, the paper lacks an analysis of the model's sensitivity to different alpha values. It is necessary to examine how varying alpha values impact the integration of multi-scale information.
The impact of the combination ratio of the two loss functions, L_MCM and L_PDR, on the model's performance should be analyzed.
Supplementary Material: The provided code does not run. The supplementary material includes only two Python files. To demonstrate the model’s reliability and applicability, executable code should be uploaded. All necessary files for running the model should be provided along with a README file explaining how to execute them.
Relation To Broader Scientific Literature: The main contribution of this paper is the integration of multi-scale information from Spatial Transcriptomics (ST) data, including gene expression, cellular interactions, and tissue morphology. Unlike prior models, SToFM effectively combines micro-scale (cellular) and macro-scale (tissue) information using a multi-scale approach and SE(2) Transformer. This approach captures richer, more comprehensive biological insights from ST data.
Essential References Not Discussed: No
Other Strengths And Weaknesses: No other Strengths And Weaknesses
Other Comments Or Suggestions: No other Comments
Questions For Authors: Please refer to the above contents.
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: Dear Reviewer TZDp:
Thanks for your appreciation and detailed review. We try our best to response the questions below:
>Q1: Bridging the gap between ST and scRNA-seq data through transfer learning.
ST data consists of two parts: **spatial location** and **gene expression values**. As SToFM is a model for ST data, the purpose of domain adaptation is to utilize well-trained scRNA-seq model to better encode the **gene expression values** of ST data. The gene expression values of ST data have a similar distribution to scRNA-seq data and follow the same underlying gene co-expression patterns. Many well-established bioinformatics methods have also proven the effectiveness of transferring knowledge between scRNA-seq and ST data, such as Tangram[1]. Therefore, we believe it is reasonable to apply transfer learning between scRNA-seq data and the **gene expression values** of ST data.
>Q2: Since this model requires pretraining of the cell encoder, its scalability is limited.
Research like scGPT[2] has already shown that Transformer-based cell encoder models have good scalability. We believe that a well-pretrained cell encoder can help improve the model's scalability.
>Q3: Computational costs. Lack of running time experiments and time complexity analysis.
- The cell encoder is based on the Transformer architecture. And the time complexity of the SE(2) Transformer is similar to that of a standard Transformer [3]. Therefore, the time complexity of both parts of SToFM is **the same as the standard Transformer**. Specifically, the time complexity is $O(N *n^2+M *m^2)$, where $N$ and $n$ are the number of cells and genes, and $M$ and $m$ are the number and the scale of the sub-slices, respectively.
- Section 4.2 of our paper provides details on the pretraining time cost. We have also added runtime experiments for inference, as shown in the Table. Specifically, running inference on an ST slice containing tens of thousands of cells typically takes 1–5 minutes, which we consider acceptable for practical applications.
|Slice|Gene number|Cell number|Sub-slice number|Cell encoder time (s)|SE(2) Transformer time (s) | Total time (s)
|-|-|-|-|:-:|:-:|:-:|
|Allen1(Sec. 4.4)|355|21002|23|28.6|21.1|49.7|
|Embryo2(Sec.4.2)|17552|12865|14|211.5|15.9|217.4|
>Q4: Model's sensitivity to different alpha values.
Thank you for your suggestion! We have added experiments to show how different alpha values affect the model’s performance, as shown in the Table below:
|alpha|Embryo2-F1| EmbryoCross-F1|
|-|:-:|:-:|
|0|0.751|0.435|
|0.2|0.767|0.458|
|0.4|0.778|0.440|
|0.6|0.796|0.436|
|0.8|**0.801**|**0.459**|
|1.0|0.769|0.448|
The model has a certain robustness in alpha, and we believe this may be because cells that are closer in location are more likely to have similar gene expressions [4]. The alpha=0.8 that we chose is essentially the optimal setting.
>Q5: The impact of the combination ratio of the two loss functions.
We will introduce further analysis on the loss ratio in the revised version of the paper. These two loss are relatively close in scale, and in our experiments, combining them in a 1:1 ratio allows both to converge normally. Considering the computational cost, we test the impact of the ratio of the two losses on the speed of convergence and the performance of the model on a small amount of data (1/8 of the SToCorpus-88M), as shown in Rebuttal-Fig.1 (https://anonymous.4open.science/api/repo/stofm-rebuttal/file/rebuttal-TZDp.pdf?v=5b2ab9f4) and the Table below. ($\gamma$ is the loss ratio in $L=\gamma*L_{MCM} + (1- \gamma) * L_{PDR}$)
|$\gamma$|Embryo2-F1| EmbryoCross-F1|
|-|:-:|:-:|
|0|0.683|0.409|
|0.2|0.729|0.423|
|0.5|**0.758**|0.423|
|0.8|0.753|**0.429**|
|1.0|0.701|0.415|
The results show that the model's performance is robust to the ratio of loss functions. However, removing one of the loss functions will lead to a decrease in model performance. The $\gamma$=0.5 that we chose is essentially the optimal setting.
>Q6: The provided code does not run.
We had uploaded the code of the model and core algorithms along with the paper to help better understand the method. The executable code has been organized now, but anonymous links containing code are not allowed during rebuttal. We promise to release the executable code on github after the paper is published.
___
Thank you again for your detailed review! Your insights are invaluable in aiding us to solidify our work. Should our responses satisfactorily address your queries, we would deeply appreciate your support for our work.
Refs:
[1] Deep learning and alignment of spatially resolved single-cell transcriptomes with Tangram
[2] scGPT: toward building a foundation model for single-cell multi-omics using generative AI
[3] Uni-Mol: a universal 3D molecular representation learning framework
[4] Mapping the transcriptome: Realizing the full potential of spatial data analysis
---
Rebuttal Comment 1.1:
Comment: 1. It is necessary to specifically justify how the gap between spatial information and gene expression can be bridged. Additional experiments, such as visualization, are required to demonstrate the validity of the transfer learning approach.
2. To prove the efficiency regarding the pre-training time cost, it is essential to compare the running time with various other baselines. However, the authors have only presented the running time of the proposed method.
3. As the complete code is not available, I was unable to attempt reproduction of the provided experimental results. This poses a problem in validating the reliability of the model.
I will maintain my current score.
---
Reply to Comment 1.1.1:
Comment: Dear Reviewer TZDp,
Thanks for your detailed comments. We try our best to address any further concerns:
> 1. It is necessary to specifically justify how the gap between spatial information and gene expression can be bridged. Additional experiments, such as visualization, are required to demonstrate the validity of the transfer learning approach.
- We would like to clarify that, as mentioned in line 182-205 of the paper and Rebuttal Q1, our method does not perform transfer learning between spatial information and gene expression. Instead, we focus on transfer learning between gene expression data from ST and scRNA-seq.
- It is widely accepted in the bioinformatics community that gene expression profiles in ST and scRNA-seq data tend to have similar distributions. For example, when deconvolution is performed on ST data, the scRNA-seq dataset is often used as the reference dataset, as detailed in the benchmark paper [1].
- We have added a visualization experiment, as shown in the anonymous link https://anonymous.4open.science/api/repo/icml-reply-2256/file/reply-TZDp.pdf?v=9b10dd35. In this experiment, we use three types of cells from the mouse brain, which were obtained from an ST slice (Allen1 in Sec. 4.4) and a scRNA-seq dataset [2]. We demonstrate the UMAP visualization of both the original expression levels and the cell embeddings obtained using the cell encoder of SToFM. The results shows that the gene expression of different cell types followed a similar relative distribution between the ST data and the scRNA-seq data (*Reply-Figure 1*). Furthermore, through domain adaptation, the cell encoder of SToFM is able to further bridge the data gap (*Reply-Figure 2*).
> 2. To prove the efficiency regarding the pre-training time cost, it is essential to compare the running time with various other baselines. However, the authors have only presented the running time of the proposed method.
Thank you for your suggestion. We have provided the running times of different models using two slices in Rebuttal Q3 as examples, in the table below. All experiments, except PCA, were conducted on a single NVIDIA Tesla A100 GPU. We found that most models are able to complete the calculation for an ST slice in a few minutes, which we believe is a reasonable processing time for practical applications in single-cell analysis. The computational efficiency of SToFM is similar to that of other Transformer-based models for processing gene sequences (Geneformer, Nicheformer) when dealing with large slices like Embryo2.
|Slice|Allen1(Sec. 4.4)|Embryo2(Sec. 4.2)|
|-|:-:|:-:|
|Gene number|355|17552|
|Cell number|21002|12865|
|PCA (s)|16.3|229.6|
|Geneformer (s)|29.3|208.0|
|Nicheformer (s)|326.9|344.45|
|CellPLM (s)|41.9|76.0|
|SToFM (s)|49.7|217.4|
> 3. As the complete code is not available, I was unable to attempt reproduction of the provided experimental results. This poses a problem in validating the reliability of the model.
We understand the importance of code availability for reproducibility and are committed to ensuring that all necessary resources are accessible after the anonymous review. Additionally, our supplementary materials contain detailed code implementations of all the core methods in the paper. The addition of checkpoint, data and simple script files would be sufficient for execution. We kindly request that this be taken into account.
___
Thank you again for your help in solidifying our work! If you have further concerns, please let us know by editing the Rebuttal Comment.
Refs:
[1] Benchmarking spatial and single-cell transcriptomics integration methods for transcript distribution prediction and cell type deconvolution
[2] Thyroid hormone remodels cortex to coordinate body-wide metabolism and exploration | null | null | null | null | null | null |
MiraGe: Editable 2D Images using Gaussian Splatting | Accept (poster) | Summary: This paper presents approaches to editing 2D images represented by Gaussian Splatting. The authors propose to use 3D flat Gaussians optimized with mirrored cameras from two opposite sides to represent 2D images, with quality better than other prior works. With the GS-represented images, this paper demonstrates different ways to do image editing with the assistance of various geometry processing tools.
## update after rebuttal
I appreciate the efforts made by the authors during the rebuttal. The authors’ responses addressed some of my concerns. The proposed method to fit Gaussians for representing and editing 2D images is somewhat effective. Regarding the editing capability, editing the image by manipulating augmented Gaussians is interesting, but I don’t think that manipulating Gaussians can make image editing simpler or more efficient. The authors should clearly state such limitations or tradeoffs in the paper. I will keep my borderline rating ("weak reject") on this submission, however, I won't have objections if other reviewers agree to accept this work.
Claims And Evidence: In the following 3 questions, I assume the method and evaluation in this paper refer to the proposed approach to representing 2D images with 3D Gaussians.
The claims about their new approach to better fitting 3D Gaussians to represent 2D images are somewhat supported by their evaluations. However, the authors fail to give a clear reason why amorphous-MiraGe gives better editing quality, and how it resolves the artifacts shown in other variants.
Methods And Evaluation Criteria: The evaluation makes sense.
Theoretical Claims: There’s no proof for theoretical claims.
Experimental Designs Or Analyses: The comparisons with DragGAN (Fig. 8 & 10) and PhysGen (Fig. 12) are not sound to me. Although the proposed method may give better visual quality from those figures, the manual efforts to achieve MiraGe’s results are way more than DragGAN and PhysGen. This comparison is like classical PhotoShop vs. Generative image editing, which does not mean anything.
Supplementary Material: I reviewed all the parts.
Relation To Broader Scientific Literature: This work is somewhat related to implicit neural representation (just a bit “neural” and “implicit”) and 2D/3D geometry processing.
Essential References Not Discussed: References are sufficient.I reviewed all the parts.
Other Strengths And Weaknesses: Strengths:
* Utilizing two opposite cameras to fit 3D Gaussians to represent 2D images is an interesting idea, and evaluation also shows the effectiveness of this idea.
* I appreciate the authors’ manual efforts in making all these image edits/animations.
Weaknesses:
* Once an image is represented as Gaussians, editing those Gaussians is quite trivial, since Gaussians here are just discrete 3D points that can be freely moved. The real difficulty is how to easily edit the 2D image with 3D Gaussians. When I read the title of this paper, I was expecting to see some novel ways to ease the Gaussian editing for 2D images. However, the editing part still relies on existing tools, which usually require a lot of manual effort to bind the Gaussian points and to precisely define deformation or motions. Moreover, regular images represented by pixels can also do these 2D editings with more mature tools/pipelines. Finally, I acknowledge the proposed improvement from amorphous-MiraGe with artifacts after editing compared to other variants. However, this comparison is only shown in a small figure (Fig. 6), which makes it hard to extensively evaluate the proposed improvements.
Other Comments Or Suggestions: This paper is fundamentally an image processing paper. There are a few machine learning contents inside (e.g., new ways to fit 3DGS for 2D images) but not too many. I am concerned whether ICML is a good fit for this work, as opposed to other computer vision/graphics or image processing conferences.
Questions For Authors: None
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: We appreciate the Reviewer’s feedback. We also thank Reviewer for appreciating the concept and work: “utilizing two opposite cameras to fit 3D Gaussians to represent 2D images is an interesting idea, and evaluation also shows the effectiveness of this idea”. Since the section for questions directed to us is empty, we have opted to refer to other sketches. We have made every effort to resolve any ambiguities. We hope the additional clarifications provide further clarity. We remain open and keen to provide further explanations if needed.
EDOA: The comparisons with DragGAN and PhysGen are not sound to me...
We would like to mention that representing a 2D image using Gaussian splatting for editing is a new concept, and it is difficult to compare it with existing tools. Therefore, we apply comparisons with existing solutions such as DragGAN and PhysGen, which shows the potential of our approach.
In the case of PhysGen, we chose these models to highlight their differences. An interesting case is PhysGen's input control, which offers limited editing capabilities. In PhysGen, the authors utilized a physics engine for training, with a diffusion model serving as an intermediary. However, this approach restricts user control. In contrast, we demonstrate that MiraGe allows direct use of a physics engine for Gaussian representation, eliminating the need for a complex diffusion model conditioned on the physics engine. Additionally, our representation is compatible with multiple engines and tools, including Taichi Elements and Blender.
In summary our representation enables editing directly in 3D, making a comparison with simple pixel modifications insufficient. Ultimately, we use this comparison to highlight the strengths of our model and its potential applications.
C&E/ W
In 2D-MiraGe primitives are constrained to a 2D plane, meaning edits should only be made on a plane parallel to the selected one. Otherwise, during rotation, they will fade away, - much like a thin piece of paper viewed from the edge in real life. This is why 2D-MiraGe was designed for compatibility with 2D engines, similar to Graphine-MiraGe, which excels in layered editing scenarios.
Amorphous-MiraGe, on the other hand, is not strictly confined to a single plane, giving it a natural 3D effect. From a practical standpoint, this makes it the most intuitive to edit in 3D space. If only 2D edits, such as simple rotations in one plane, were applied, there would be no noticeable difference between the model versions. This distinction is illustrated in Fig. 6. However, we acknowledge that the image is too small, and we will enlarge it to improve clarity. We thank Reviewer for pointing this out.
We hope our explanation is sufficient, and we remain open to more questions.
W: (...) editing those Gaussians is quite trivial (..)
As 3D Gaussian editing still advances, so do methods for reducing artifacts. A recent study (arXiv 03.2025) [1b] enforces spherical shapes, while PhysGaussian [2b] uses an Anisotropy Regularizer—both preventing sharp artifacts during rotations.
In 2D achieving high-quality and robust nonlinear modifications images is still challenging, especially when performing affine transformations on low-resolution images, where inaccuracies can lead to the appearance of holes. However, with Gaussians, affine transformations preserve key properties such as color and opacity, allowing us to avoid numerical errors and eliminate this issue. Moreover, the additional 3rd dimension can simplify animation creation in certain cases. For example, it facilitates the natural motion of a waving flag as illustrated in Fig. 3. We hope that the use of Gaussians for 2D image representation will continue to evolve, leading to more advanced and mature editing tools in the future. Our work demonstrates that such editing is not only possible but also promising.
OC&S: (...) I am concerned whether ICML is a good fit for this work...
In our paper, we introduce a novel approach to 2D image representation, specifically designed for manual editing and integration with physical engines. As the reviewers pointed out, our method lacks direct competitors - a fact that, in our view, underscores its originality.
In the reconstruction task, our method achieves superior results in a shorter time. As discussed in our response to Reviewer u88z, W2, our approach outperforms the baselines in PSNR with just 5k iterations Moreover, MiraGe enables a range of capabilities:
- Integrating physical engines with 2D images
- Editing 2D images directly within a 3D space
- Enabling complex nonlinear modifications of 2D images
Therefore, we believe ICML is a suitable venue for this work, as we present a new approach to representing 2D images.
We are committed to improving our paper and greatly appreciate the feedback regarding the visibility of Fig. 6. We will address this concern and make the necessary adjustments to the camera-ready version.
---
Rebuttal Comment 1.1:
Comment: Thanks for the rebuttal. I acknowledge the novelty of the method fitting Gaussians to represent 2D images. Metrics in the paper and the rebuttal are good to me. However, regarding the authors' responses on Gaussian editing, I have a few more comments:
* EDOA: My point is that the proposed method cannot easily complete the editing task compared to generative models. For example, you only need to click a few keypoints to achieve the editing effect with DragGAN, but this method requires much more time and effort in meticulously manipulating lots of Gaussians to achieve similar editing effects.
* C&E/ W: The authors in the rebuttal mentioned "intuitive to edit in 3D space". The proposed method only does the faithful reconstruction of 2D images. I don't see any clear evidence that MiraGe can preserve decent 3D information in the reconstructed image. Without good 3D structure/geometry/semantics, directly editing in the 3D space is not an easy job. Providing renderings of Gaussians from different side views of the image plane would be beneficial to support the claim.
---
Reply to Comment 1.1.1:
Comment: Thank you for your response. We are happy to address any concerns or provide further clarification.
EDOA:
We agree that generative models have some advantages in editing but also have limitations. When we apply deep generative models for editing, such models can hallucinate – changing small elements of the objects. This is shown in our paper in Fig. 10. The second row demonstrates that when generative models are used to modify the position of the legs, unintended alterations occur in the woman's face. We interpret this as a limitation of the generative approach. If we want to force the model to produce the same object with modifications, it is not trivial and requires much time.
Our MiRaGe model requires manual triangle modification (or the application of a physical engine), but it guarantees consistent changes.
All models have advantages and limitations. Gaussian representation can also find applications in deep generative models, which can, in the future, integrate the strengths of both technologies.
C&E
Thank you for bringing this to our attention. This feedback allows us to refine our explanations for greater clarity. We agree that it is not trivial to represent a 2D image in 3D space. Consequently, we do not claim to produce a full 3D object. As noted in the introduction, our approach is grounded in human perception of 2D objects within a 3D environment, which we illustrate using the analogy of a sheet of paper (lines 047–048). We refer to 2.5D [1] for such modifications, which is well described in the literature and pertains to modifying 2D images in 3D space.
In the appendix (lines 559–565), we clarify that "Editing images in pixel representation is a well-established technique with many existing solutions, and 2D image editing tools (e.g. Photoshop, GIMP). MiraGe presents a concept that combines 2D and 3D representations to achieve the 2.5D effect commonly used in video games and VR [1].”
By ease of editing in 3D, we refer to the ability to manipulate such an image or photograph within a 3D space. This is illustrated in Fig. 3, with further demonstrations provided in the supplementary videos flag.mp4 and flag_triangle_soup.mp4. Figure 21 and the hand.mp4 video showcase examples of direct, manual interaction with the 3rd dimension. In Figure 20 (see 3D.mp4 in the supplementary materials), we demonstrate editing a shield that is partially occluded by a soldier. Our representation supports such transformation, which is why we describe it as intuitive to edit in 3D space.
Additional visualizations where the camera angle changes can be found on:
https://anonymous.4open.science/r/rebuttal-744F
To improve visualization, we provide additional videos in the supplementary material: flag_simulation_with_trajectory.mp4 (previous flag.mp4) and flag_triangle_soup.mp4. We also include flag_simulation_with_camera_changing_and_trajectory.mp4, which demonstrate the effect of changing camera views. Through these visualization paths, we aim to clearly show how the camera movement enhances perception of the simulation. Additionally, we include a full-scene example with a lantern.mp4 to highlight the potential applications of our method.
To illustrate practical applications, we reference the image of mountains or landscapes as an example of how a 2D object can be used. Notably, when using mountains as a background, it is not necessary to generate a full 3D model (e.g., via generative models), see train1.mp4 video in supplementary materials.
Given that these clarifications enhance the reader’s understanding of the section on editability, we will integrate this discussion into the main paper.
[1] FEYER, Stefan P., et al. 2D, 2.5 D, or 3D? an exploratory study on multilayer network visualisations in virtual reality. IEEE Transactions on Visualization and Computer Graphics, 2023, 30.1: 469-479. | Summary: The paper introduces MiraGe, a method for representing and editing 2D images using parameterized 3D Gaussian components. By embedding 2D images in 3D space with flat Gaussians and leveraging mirror cameras for training, MiraGe achieves high-fidelity reconstruction and enables intuitive 3D-like editing (e.g., bending, physics-based animations). The method integrates with physics engines (e.g., Blender, Taichi) for realistic deformations and outperforms existing INR and Gaussian-based models (e.g., GaussianImage, SIREN) in reconstruction quality on Kodak and DIV2K datasets.
## Update after rebuttal
I thank the authors for their response. I have no further concerns and will maintain my positive score.
Claims And Evidence: The authors claimed 1) state-of-the-art reconstruction quality, which is supported by the PSNR/MS-SSIM scores reported in Table 1; 2) 3D-like editing of 2D images, which is supported by Figures 3, 6, and 8 show manual edits (e.g., facial expressions, object bending) and physics-driven animations in Fig. 7.
Methods And Evaluation Criteria: Methods:
The use of flat 3D Gaussians with GaMeS parametrization (from prior work) is innovative for bridging 2D/3D editing. Mirror cameras enhance spatial consistency, and three Gaussian control methods (Amorphous, 2D, Graphite) offer flexibility. However, physics integration is treated as a "black box," with no details on coupling Gaussians with engine dynamics.
Evaluation:
Standard datasets (Kodak, DIV2K) and metrics (PSNR, MS-SSIM) are appropriate for reconstruction. However, editing capabilities are assessed only qualitatively. This paper only chose DragGAN and PhysGen as editing capabilities baselines and no non-generative baselines are compared in this paper.
Theoretical Claims: No theoretical proofs are provided for novel claims, but the method’s foundation in established techniques (3DGS, GaMeS) is reasonable.
Experimental Designs Or Analyses: Manual edits (Fig. 8) and physics animations (Fig. 7) are visually compelling but lack quantitative benchmarks. Many of the editing effects demonstrated in the paper and supplementary material appear to involve simple warping, which could also be achieved manually using traditional image editing tools like Photoshop. However, the proposed method offers a distinct advantage in its ability to integrate seamlessly with physics engines, enabling more dynamic and realistic modifications.
Supplementary Material: Yes, I reviewed the supplementary material including the provided video results.
Relation To Broader Scientific Literature: The proposed method combines the efficiency of Gaussian-based representations with editability, and integrates physics engines for realistic 2D image editing, expanding the application of physics-based simulations to traditionally 2D domains.
Essential References Not Discussed: The references are sufficient.
Other Strengths And Weaknesses: Strengths:
1. Novel integration of 3D Gaussians for 2D image editing.
2. High reconstruction quality and support for intuitive 3D manipulations.
3. Demonstrated compatibility with physics engines.
Weaknesses:
1. Limited quantitative evaluation of editing/physics realism.
2. Limited baseline methods for comparisons.
3. Most of the editing effects are relatively simple and subtle due to the method's non-generative nature, which limits its versatility and practical applicability.
Other Comments Or Suggestions: No other comments.
Questions For Authors: 1. How does MiraGe handle complex edits (e.g., occlusions, texture changes) compared to traditional tools like Photoshop?
2. How does the model handle edge cases where significant modifications introduce visual inconsistencies?
3. How does MiraGe scale to high-resolution images in terms of training time and memory usage?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We appreciate the Reviewer's thoughtful feedback. We are pleased for the recognition of the distinct advantage of our proposed method in seamlessly integrating with physics engines, allowing for more dynamic and realistic modifications compared to traditional tools.
W1/2
In our paper, we address two tasks. The first, reconstruction, is evaluated using widely recognized benchmarks and metrics, as noted by Reviewer u88z, who found the methods and evaluation criteria appropriate.
In the second editing task, we focused on qualitative assessment, acknowledging the limitations of our evaluation as the first to apply parametric 3D Gaussians to 2D images. Nevertheless, we compare our approach to generative methods to highlight differences in editing capabilities, aiming to introduce a novel 2D representation and inspire future advancements.
W3
In most generative methods, users have constrained control over edits. However, as shown in Fig. 10, our approach allows precise modifications, enabling users to adjust specific details. Additionally, we incorporate 3D representation and human perspective (Fig. 3), demonstrating that our method inherently possesses a 3D structure. This means that, beyond standard 2D transformations like rotation, we also have control over perspective.
In PhysGen authors claim that “despite advancements in video generative models the incorporation of real-world physics principles into the video generation process remains largely unexplored and unsolved.” We show that our method can leverage physics engines, producing videos from 2D images without the need for generative model predicting the simulation (see visualization in supplementary materials). We show that using Taichi to apply materials such as sand to objects, as demonstrated in Fig.7.
Q1
Our goal is not to compete with tools like Photoshop but to highlight the advantages of representing 2D images with parameterized 3D Gaussians. While Photoshop allows for seamless image modifications, it relies on numerous hidden features such as specialized interpolation, imputation, and other corrections. When applying a simple affine transformation to an image, artifacts often emerge, necessitating pixel interpolation to correct them. In contrast, Gaussian components inherently preserve their structure under affine transformations, as an affine transformation of a Gaussian remains a Gaussian. For this reason, we believe directly comparing MiraGe to the Photoshop tool would be inappropriate.
However similar to Photoshop layering, our image representation can incorporate the idea of image layers (as illustrated in Fig. 4). This allows for inpainting when parts of the image are occluded—for example, seamlessly inpainting in the background, as demonstrated in Fig. 11.
It is worth mentioning that our model builds on features from 3DGS, enabling the application of existing Gaussian-based models. We believe that in practice, MiraGe can incorporate various style transfer methods for Gaussians. For instance, StyleGaussian [1c] allows for color adjustments during style transfer. However, such modifications fall outside the scope of this paper, as our focus is on shape editing rather than texture or color alterations. We recognize this as a promising future research direction.
[1c] K. Liu, et al. "StyleGaussian: Instant 3d style transfer with gaussian splatting." SIGGRAPH Asia 2024
Q2
Due to the character limitation, answer to this question is referenced in W1 and Q4, Reviewer u88z
Q3
We consider this an interesting question, as also noted by Reviewer u88z. We will address this in the camera-ready version.
As part of our rebuttal, we conducted an experiment on a single image to illustrate how method scale. We selected a butterfly from the DIV2K dataset[2c]. For Training we used 100K initial Gaussians;5k, 10k, 30k iterations on the V100 GPU. In table we report compressed memory (MB) and training time (seconds).
From the table below, we can observe that our method consistently achieves higher PSNR results compared to the baseline.
[2c] https://data.vision.ee.ethz.ch/cvl/DIV2K/
|Model||Our-5k iter|||Our-10k iter|||Our-30k iter|||GaussianImage|default settings|
|---|---|---|---|---|---|---|:---|---|---|:---|---|---|
||PSNR|MB|Train time|⎮PSNR|MB|Train time|⎮PSNR|MB|Train time|⎮PSNR|MB|Train time|
|1/none|30.76|3.56|209|⎮36.17|12.2|586|⎮47.04|35.65|2709|⎮28.34|2.41|189|
|2|43.85|2.54|67|⎮47.21|4.20|158|⎮52.27|8.24| 651|⎮38.54|2.41|111|
|3|51.51|2.41|45|⎮54.20|3.53|104|⎮58.81|5.66|406|⎮41.53|2.41|105|
|4|56.86|2.36|40|⎮58.52|3.27|92|⎮65.02|4.83|341|⎮34.33|2.41|103|
In practice, for high-resolution images, GS can be initially trained at a lower resolution and progressively refined to higher resolutions, following the Hierarchical GS strategy [3c], which we believe can be applied as a future work.
[3c] B. Kerbl, et al. "A hierarchical 3d gaussian representation for real-time rendering of very large datasets." ACM Transactions on Graphics, 2024 | Summary: The paper proposes MiraGe, a novel approach for representing and editing 2D images using Gaussian Splatting. MiraGe uses flat-controlled Gaussian components positioned in 3D space, providing intuitive editing capabilities with a 3D perception. Key contributions include high-quality reconstruction results that outperform state-of-the-art methods such as GaussianImage, SIREN, and WIRE, and the integration with physics engines to enable physically plausible manipulations and realistic animations of 2D images. The method achieves notable improvements in reconstruction metrics (PSNR, MS-SSIM) compared to existing INR and 3D reconstruction approaches.
Claims And Evidence: The claims of improved reconstruction quality, realistic 3D manipulation, and physics-based editing are generally well-supported by experiments on standard benchmarks (Kodak and DIV2K datasets).
Methods And Evaluation Criteria: The methods and evaluation criteria employed are appropriate and well-chosen. The paper uses widely recognized benchmarks (Kodak and DIV2K) and metrics (PSNR, MS-SSIM) suitable for evaluating the proposed method against competitors. Using these datasets facilitates direct comparison with previous work.
Theoretical Claims: The paper does not include explicit theoretical proofs or theoretical claims requiring validation. It mainly presents empirical evidence and algorithmic contributions.
Experimental Designs Or Analyses: The experimental design and analyses are sound. The evaluations include comparative studies against relevant baseline methods (GaussianImage, NeuRBF, I-NGP, WIRE, SIREN). However, deeper investigation into computational complexity, particularly the trade-offs in memory and computational efficiency compared to baseline methods, could strengthen the paper.
Supplementary Material: Yes, I reviewed the supplementary materials. The provided supplementary includes extensive ablation studies on the initial number of Gaussians, the impact of mirror camera augmentation, detailed numerical analyses, and additional qualitative visualizations of image editing capabilities and associated artifacts.
Relation To Broader Scientific Literature: The paper positions itself well within existing literature by clearly explaining how it advances beyond GaussianImage's limitations of static representations. MiraGe leverages explicit Gaussian representations and integrates ideas inspired by recent developments in INRs and Gaussian Splatting's effectiveness in 3D representation. Thus, MiraGe contributes to both theoretical advancements in implicit neural representations and practical improvements in editable image representations.
Essential References Not Discussed: The literature review is thorough, and essential references such as WIRE, NeuRBF, SIREN, GaussianImage, and I-NGP are well-discussed. However, 4D Gaussian Splatting (CVPR 2024), extending Gaussian Splatting to dynamic scenes, were not discussed and would further enrich the paper's context and comparison.
Other Strengths And Weaknesses: ### Strengths:
- Clearly presents a novel and practical combination of Gaussian Splatting and 3D-like image editing.
- Demonstrates significant quantitative and qualitative improvements over state-of-the-art baselines.
- Integrates successfully with physics-based animation tools, extending applicability to various real-world use cases.
### Weaknesses:
- Significant edits produce visual artifacts, indicating potential limitations in practical usability without further refinement.
- The training time appears to be lengthy. While the paper includes a comparison between GaussianImage and 3DGS, incorporating comparisons with additional baselines would further highlight the strengths of this method.
Other Comments Or Suggestions: The paper is well-written and organized clearly.
Questions For Authors: 1. Could you discuss the computational overhead introduced by your approach compared to other baselines? Clarifying runtime performance or potential computational bottlenecks would influence the practical significance of the proposed method.
2. How does your method scale with image size or complexity (e.g., high-resolution images or more intricate scenes)? Providing additional insights or experiments on scalability would significantly improve the paper.
3. How well does your approach handle editing scenes with complex backgrounds? The examples in the supplementary materials appear somewhat simplistic—can you demonstrate editing effectiveness on images with more intricate backgrounds?
4. Can the artifacts arising from significant edits be mitigated systematically, or is the approach fundamentally limited by the Gaussian parametrization? A clear answer could help better understand the approach's limitations.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank the Reviewer for the feedback and constructive remarks regarding our paper that we believe will improve our paper. In particular, we are grateful for the Reviewer’s recognition that "the methods and evaluation criteria employed are appropriate and well-chosen".
W1
We acknowledge that significant edits can produce visual artifacts in the current version of our model and discuss it in in the Limitation Section. Nevertheless, our primary focus is on demonstrating the advantages of the proposed representation of 2D images using parametrized Gaussians and proving that such editing is feasible. We believe this work opens the door to numerous future research directions and improving even substantial edits.
Q4
It is a non-trivial question requiring substantial consideration.
As the field of editing 3D Gaussians continues to develop, so do the methods for mitigating artifacts appearing in 3D objects. For example, a recent study (arXiv 03.2025) [1b] introduces a loss function that enforces Gaussians to maintain spherical shapes. In PhysGaussian the authors use Anisotropy Regularizer [2b]. In both cases this helps prevent the creation of "sharp" visible artifacts during rotations.
In the context of 2D image “we introduced the mirror camera to ensure that Gaussians remain confined within a specific spatial region between the cameras, enhancing control and precision.” This approach effectively serves as a form of Gaussian regularization, as seen in Fig. 6 (first and second rows). To enhance readability, we will enlarge this figure.
It is also important to highlight that artifacts may arise naturally when working with 2D representations, such as fading effects that occur with significant changes in perspective (e.g., rotations of 90 degrees in 3rd dimension). A useful analogy is a piece of paper or a photograph: when rotated 90 degrees in the third dimension, it effectively disappears from view.
[1b] L Qiu, et al. ; “LHM: Large Animatable Human Reconstruction Model from a Single Image in Seconds”; arXiv 2025
[2b] T. Xie, et al.; “PhysGaussian: Physics-Integrated 3D Gaussians for Generative Dynamics”; CVPR 2024
W2
Below we present the supplementation of Tab. 1 and a comparison with existing methods. The metrics for the baselines were taken from [3b]; however, we re-ran the experiments for GaussianImage (GI) -70K (GI-70K) and our using a V100 GPU to ensure a more reliable comparison. Those experiments are denoted in the following table by “*” next to the method name.
| | Kodak | | Div2K | |
| --- | --- | --- | --- | --- |
| | PSNR | Train Time(s) | PSNR | Train Time(s) |
| WIRE | 41.47 | 14339 | 35.64 | 25684 |
| SIREN | 40.83 | 6582 | 39.08 | 15125 |
| I-NGP | 43.88 | 491 | 37.06 | 676 |
| NeuRBF | 43.78 | 992 | 38.60 | 1715 |
| 3DGS | 43.69 | 340 | 39.36 | 481 |
| GI-70K | 44.08 | 107 | 39.53 | 121 |
| GI-70K* | 44.12 | 116 | 39.53 | 112 |
| GI-100K* | 38.93 | 126 | 41.48 | 120 |
| Our-70K; 5k iter | 49.07 |**57**| 44.37 |**75**|
| Our-100K; 5k iter | 51.04 | 59 | 46.23 |79|
| Our-70K; 30k iter | 57.41 | 547 | 53.22 | 789 |
| Our-100K; 30k iter |**59.52**| 560 |**54.54**| 946 |
We include the table with training time comparison including multiple baseline methods. The time provided for our method is the full training time (30000 and 5000 iteration steps). Additionally, using the butterfly image from the DIV2K dataset as an example, we demonstrated that our method (Our-100K) achieves higher PSNR than GI in just 30 seconds, see Fig. 3. This is also supported by our method surpassing GI in PSNR with only 5k iterations, while also having a shorter training time.
Q1
While the inference of our method is fast, the storage cost introduced by the original 3DGS representation used by our method is high. To overcome this we use the existing compression tool spz [3b]. This allows us to reduce the memory overhead by up to 95%; please see Tab. 4 in supplementary material. Additionally we include GI as our baseline. Note that GI compresses the Gaussian representation as part of their pipeline, and spz compression algorithm is not applicable to their representation:
| | Camera setting | PSNR | Memory(MB) | Compressed memory (MB) |
| --- | --- | --- | --- | --- |
| GI (70k) * | - | 44.12 | - | 2.41 |
| GI (100k)* | - | 38.93 | -| 3.44 |
| Our (100k) | A/ One camera | 51.56 | 31.25 | 2.42 |
| Our (100k) | A/ Mirror camera | 59.52 | 117.25 | 7.80 |
[3b] https://github.com/nianticlabs/spz
Q2
Due to the character limitation, answer to this question is referenced in Q3, Reviewer VWK2
Q3
Indeed, in complex scenes with intricate backgrounds, the task becomes more challenging, as we mention in the Limitations Section. However, as shown in Fig. 11, our method allows for seamless object manipulation, such as repositioning a flower using a physic engine such as Taichi Elements, while effectively applying inpainting to ensure a gap-free result. | Summary: The paper introduces MiraGe, a novel method for representing and editing 2D images using flat 3D Gaussian components. The approach leverages Gaussian splatting in 3D space to enable high-quality image reconstruction and realistic editing capabilities. MiraGe allows for both 2D and 3D manipulations of images, creating the illusion of 3D transformations while maintaining the integrity of the original 2D image. The method employs parameterized flat Gaussians and integrates with physics engines for dynamic modifications. Experimental results demonstrate state-of-the-art performance in image reconstruction quality and editing capabilities.
## Update after rebuttal
Thanks for the author's rebuttal. It has well addressed my concerns. I suggest accept this work.
Claims And Evidence: The paper makes several claims about the effectiveness of **MiraGe** in image reconstruction and editing, which are well-supported by the following evidence:
- Quantitative results showing improvements in PSNR and MS-SSIM metrics compared to previous methods (Table 1).
- Visual comparisons demonstrating better reconstruction quality and fewer artifacts than competing approaches (Figures 5, 8, 10).
- Ablation studies highlighting the impact of different model components, such as the mirror camera setup (Table 2).
- Demonstrations of editing capabilities, including manual modifications and physics-based animations (Figures 3, 7, 18, 19).
The evidence convincingly supports the claims made. The experiments cover multiple datasets and provide both quantitative and qualitative comparisons. The ablation studies effectively isolate the contributions of different components of the proposed framework.
Methods And Evaluation Criteria: The method is clear, and the evaluation criteria are well-defined. It includes many quantitative metrics, along with qualitative comparisons to other methods, making the experiments very thorough.
Theoretical Claims: The paper does not present extensive theoretical proofs but rather focuses on conceptual framework and experimental validation.
Experimental Designs Or Analyses: The experimental setup is comprehensive.
And also, the authors compare their method with the generative approach Drag-GAN. Despite Drag-GAN being a generative model with extensive prior knowledge, this work still achieves comparable performance, which is very promising.
Supplementary Material: Yes, the supplementary material provides many visualization examples, demonstrating excellent visual results.
Relation To Broader Scientific Literature: This work demonstrates many applications. Compared to previous work, it offers better image representation and manipulation capabilities than Gaussian-Image (ECCV 2024). Unlike Drag-GAN (SIGGRAPH 2023), it doesn't require as much prior knowledge.
Additionally, it can integrate two images (Fig. 4), suggesting that it may also have potential for image harmonization, though real-world lighting conditions might add complexity.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: A small problem is that the author could add the PSNR/SSIM score on Fig.5, it would be more clear to see the advantage.
Overall I believe this is a great work.
Other Comments Or Suggestions: Does the MiraGe structure require training on a single image each time? Would this be considered low-efficiency? What plans do the authors have for improving this aspect in the future?
Questions For Authors: If more physical factors, such as real-world lighting, BRDF, and materials, are considered, would this enhance the performance of the work? If it possible to incorporate these factors to improve MiraGe's performance? In other words, does MiraGe have the potential to expand in the direction of inverse rendering (i.e. NeRFactor, Ref-NeRF)?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We sincerely thank the Reviewer for their valuable feedback and are pleased with the appreciation of our work. In particular, we are especially grateful for the recognition of the breadth and depth of our experiments "covering multiple datasets and providing both quantitative and qualitative comparisons."
W1. A small problem is that the author could add the PSNR/SSIM score on Fig.5.
Thank you for this suggestion. We will add the mentioned metrics to the Fig. 5 in the camera-ready version:
| name | PSNR | SSIM |
| --- | --- | --- |
| GaussianImage | 43.73 | 0.9993 |
| MiraGe | 62.00 | 0.9999 |
C&S1. Does the MiraGe structure require training on a single image each time? Would this be considered low-efficiency?
The pipeline does require training for each image individually. However, it is important to note that even with just 30 seconds of training, our method already produces better results compared to existing approaches (Fig. 9; Our-100k, using the butterfly image from DIV2K as an example). At the same time, longer training is beneficial for more-optimal PSNR performance. For more comparison, please refer to our answer to Reviewer u88z, W2 where we show that our method is surpassing baselines in PSNR with only 5k iterations, while also having a shorter training time.
C&S2. What plans do the authors have for improving this aspect in the future?
A possible direction to improve our approach with regards to training a different model for each individual image, could be the use of a generative model to prepare the collection of Gaussians based on the input image. While literature explores such an approach to the best of our knowledge current models work on foreground objects, and not full scenes like [1a]. In our case the images used are real life photographs, where both foreground and background are required to be reconstructed. Additionally, we would like to highlight that our model rapidly obtains high quality reconstruction.
[1a] TANG, Jiaxiang, et al. DreamGaussian: Generative Gaussian Splatting for Efficient 3D Content Creation. In: The Twelfth International Conference on Learning Representations.
Q1. If more physical factors, such as real-world lighting, BRDF, and materials, are considered, would this enhance the performance of the work? If it possible to incorporate these factors to improve MiraGe's performance? In other words, does MiraGe have the potential to expand in the direction of inverse rendering (i.e. NeRFactor, Ref-NeRF)?
Thank you for posting this interesting question. In literature there exist works that incorporate real-world lighting using 3D Gaussian Splatting [2a, 3a]. In contest to BRDF, 3D Gaussian Ray Tracing [4a] uses Ray Tracing to enable secondary lightning effects. Since all the mentioned methods (including ours) are based on 3D Gaussian Splatting, we believe that integrating similar ideas into MiraGe is possible. We consider this a promising direction for future work, which we will post in the main manuscript.
[2a] J. Gao, et al. “Relightable 3D Gaussians: Realistic Point Cloud Relighting with BRDF Decomposition and Ray Tracing”; ECCV2024
[3a] Z. Bi, et al. GS^3: “Efficient Relighting with Triple Gaussian Splatting”; SIGGRAPH Asia 2024
[4a] N. Moenne-Loccoz, et al.; “3D Gaussian Ray Tracing: Fast Tracing of Particle Scenes”; SIGGRAPH Asia 2024 | null | null | null | null | null | null |
SpeCache: Speculative Key-Value Caching for Efficient Generation of LLMs | Accept (poster) | Summary: The paper introduces SpeCache, a speculative KV caching mechanism designed to enhance the efficiency of LLM inference. SpeCache mitigates these drawbacks by offloading the complete KV cache to CPU memory and dynamically fetching KV pairs back into GPU memory during decoding. To minimize CPU-GPU transfer latency, it employs a speculative mechanism to predict the KV pairs required for the next decoding step, allowing memory transfer and computation to proceed in parallel. The method does not require retraining and significantly reduces memory usage while maintaining competitive accuracy.
## update after rebuttal
The authors’ response partially addresses my concerns. However, based on the discussions raised by other reviewers and overall rebuttal, I believe that my key concerns remain unresolved. Below, I elaborate on the remaining issues:
While SpeCache proposes a KV cache offloading technique to address the long-context problem, the motivation described in the paper does not adequately support this objective. Since the method is based on offloading KV cache from the GPU to CPU memory (not merely loading from GPU DRAM), the examples given in the introduction and the maximum sequence lengths of the models evaluated in the experimental section do not convincingly demonstrate the utility of SpeCache in genuinely resource-constrained environments. As such, I find it difficult to accept the claim that SpeCache is effective under constrained memory settings.
This paper presents Table 1 and Table 2 as the main evaluation results, but there are still concerns about whether these comparisons are fair and appropriate. In Table 1, the comparison with KIVI fixes the residual length at 64 and allocates 16-bit precision to the top-64 KV pairs. It is intuitive that assigning higher bit-precision to more important tokens would yield higher accuracy, making the comparison less informative. In Table 2, SpeCache is compared against baselines that adopt eviction strategies, while SpeCache itself stores the full KV cache in CPU memory (non-eviction). This setup favors SpeCache by design and does not ensure a fairness in accuracy comparisons.
The throughput evaluation also has room for improvement. The reported throughput gains are primarily achieved by increasing the batch size, which is similar to the benefits observed in prior work through KV cache size reduction. Moreover, the comparison is only made against FullKV, without including other CPU-GPU offloading methods. A more meaningful evaluation would involve direct comparisons with other CPU-GPU offloading methods, including the overhead from KV cache dequantization and other related costs.
While I appreciate the authors’ additional efforts in providing further experimental results, the fundamental concerns I raised have not been fully resolved. Therefore, I will maintain my original score.
Claims And Evidence: The claims in the paper are generally supported by clear evidence, but there are some points that deserve closer examination. The following is an evaluation of the claims and the evidence provided in this paper:
**1. Unclear Overhead of Parallel Prefetching and Computation**
• The paper states that "prefetching and computation can occur in parallel, avoiding any increase in inference latency." However, while Table 4 presents the latency gain when fetching and computation are executed sequentially, it does not provide results on the additional overhead introduced by the parallel prefetching and computation framework compared to standard inference.
• Without explicit analysis of the potential trade-offs, it is unclear how much overhead the parallel execution introduces in real-world inference scenarios, particularly when considering factors such as kernel launch overhead, synchronization penalties, or impact on GPU utilization.
**2. Questionable Relevance of the KV Cache Bottleneck Example**
• The introduction section states that for LLaMA-7B with a batch size of 16 and sequence length of 2k, the KV cache size reaches 8.4B parameters, and that this can be a bottleneck in memory-constrained environments like on-device inference.
• However, in local on-device inference, single-batch inference is more common than large batch sizes. A more appropriate example would be a single-batch input with a sequence length of 128k, which better reflects real-world usage scenarios.
• Recent models such as LLaMA-3.1-8B already support 128k sequence length with GQA, making the assumption that 2k is a long context less relevant. Furthermore, for a single batch with a 2k input length, the KV cache size is only about 0.26GB, which is unlikely to be a severe memory constraint in modern hardware setups. This weakens the claim that a 2k length input presents a significant long-context challenge.
**3. Peak Memory Usage Concern in Prefill Phase**
• One limitation of SpeCache is that during the prefill phase, the entire KV cache must be deployed on the GPU at least once before any offloading occurs.
• This means that peak memory consumption is not reduced, which can be a critical constraint for on-device inference applications with limited memory.
• The paper does not discuss whether SpeCache enables inference in environments where the full KV cache would otherwise exceed memory limits, which is crucial for evaluating its feasibility in resource-constrained scenarios.
Methods And Evaluation Criteria: The paper introduces a novel speculative KV caching method, integrating CPU offloading with speculative token decoding. The evaluation is based on:
• Accuracy on LongBench and Needle-in-a-Haystack benchmarks
• Memory efficiency (compression ratio and VRAM usage)
Theoretical Claims: The paper does not present a formal theoretical analysis but relies on empirical justification. The main theoretical intuition is that attention sparsity allows selective KV caching without performance loss. This assumption is supported by quantitative studies of attention sparsity and cache hit rates.
Experimental Designs Or Analyses: 1. The LongBench dataset includes sequences exceeding 32K tokens. However, the evaluation in the paper truncates sequences to 4K, 8K, or 32K depending on the model's maximum context length. This truncation lowers the upper bound of accuracy for full KV cache models, potentially making the reported accuracy gap between full KV cache and compressed KV cache models appear smaller than it would be with longer sequences. A more appropriate evaluation should be conducted using a model that supports 128K sequences without truncation, such as LLaMA-3.1-8B-Instruct, to ensure fair comparisons.
2. The paper evaluates SpeCache against older methods such as H2O and StreamLLM, but does not compare it with more recent and competitive methods like SnapKV [1].
3. Table 3 demonstrates the throughput improvements of SpeCache by increasing the maximum batch size due to KV cache compression. However, this approach does not isolate the direct impact of KV cache compression on KV cache loading time. A better approach would be to compare throughput gains at a fixed batch size, measuring the speed-up factor when using full KV cache versus SpeCache. This would more clearly demonstrate how much KV compression reduces KV cache loading time rather than conflating improvements from increased batch sizes.
[1] Yuhong Li, et al., "SnapKV: LLM Knows What You are Looking for Before Generation", arXiv:2404.14469.
Supplementary Material: The supplementary material includes detailed algorithms, additional benchmark results, and setting of benchmarks.
Relation To Broader Scientific Literature: The paper builds on and extends existing work in:
• KV cache compression
• Offloading techniques
• Speculative execution for LLMs
The method is positioned as a training-free enhancement, making it broadly applicable.
Essential References Not Discussed: The paper discusses all major prior works related to KV caching, attention sparsity, and speculative execution. No significant omissions were noted.
Other Strengths And Weaknesses: **Strength**
1. The paper presents a novel speculative prefetching mechanism for KV cache in LLMs, which differentiates it from conventional KV cache compression and offloading methods.
2. Unlike previous methods that rely on compression techniques such as quantization, merging, or eviction, SpeCache introduces speculative tokens to anticipate the next KV pairs required for decoding, which is an innovative approach.
**Weakness**
1. Unclear assumption for long context (See Claims and Evidence 1. and 2.)
2. Peak Memory Usage Concern (See Claims and Evidence 3.)
3. Unreasonable experimental results (See Experimental Designs or Analyses)
Other Comments Or Suggestions: Typo in line 302: “min X + 3 max X)” -> “(min X + 3 max X)”
Questions For Authors: See Claims and Evidence and Experimental Designs and Weakness.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank the reviewer for their thoughtful feedback! We address specific concerns and questions below.
> Q1. Unclear Overhead of Parallel Prefetching and Computation
Since our method is built upon KIVI, we can consider KIVI as the baseline when parallel pre-fetching and computation are not used. On Mistral-7B-Instruct-v0.2, we test the latency and VRAM usage of KIVI and KIVI+SpeCache with batch size of 1 and context length of 64k.
|Method|Latency (ms/step)|Allocated memory (GB)|
|-|-|-|
|Full KV|204.3|31.1|
|2-bit KIVI (g=64)|94.6|22.8|
|+ SpeCache|101.6|22.8|
|1-bit KIVI (g=64)|94.3|22.3|
|+ SpeCache|103.3|22.3|
In addition, we also provide the throughput of Mistral-7B-Instruct-v0.2 with context length of 32k when the batch size is increased to the maximum capacity that can be accommodated by 48GB.
|Method|Throughput (tok/sec)|batch size|
|-|-|-|
|2-bit KIVI (g=64)|36.5|22|
|+ SpeCache|34.6|22|
|1-bit KIVI (g=64)|50.8|36|
|+ SpeCache|47.3|36|
We can find that SpeCache only slightly increase the latency of KIVI.
> Q2. Questionable Relevance of the KV Cache Bottleneck Example
Thank you for pointing that out. Our example is indeed somewhat outdated. We will revise the description to specify the KV cache size for long sequences with a batch size of 1, such as for Mistral-v0.2-7B with a 32k context length, where the KV cache size exceeds 4B, and for Llama3.1 with a 128k context length, where the KV cache size exceeds 16B.
> Q3. Peak Memory Usage Concern in Prefill Phase
In fact, during the prefilling phase, **we do not need to keep the entire KV cache in GPU memory**. This is because the computation, quantization, and offloading of the KV cache are done layer-by-layer. In other words, at any given moment, only the KV cache of a single layer needs to be fully stored in GPU memory. Before the KV cache of one layer is computed, the KV cache from the previous layer has already been quantized and offloaded. For example, Mistral-7B has 32 layers, so at any given time, we only need 1/32 of the 16-bit KV cache in GPU memory. This also allows SpeCache to handle context lengths that full cache cannot accommodate.
> Q4. Experiments on LLaMA-3.1-8B-Instruct
We implemented SpeCache on Llama-3.1-8B-instruct and evaluated it on longbench.
|Method|KV Size|Qasper|MF-en|HotpotQA|2WikiMQA|Musique|GovReport|MultiNews|PRe|LCC|RB-P|Average|
|-|-|-|-|-|-|-|-|-|-|-|-|-|
|16-bit Full KV|1.00x|45.5|54.9|56.0|46.6|31.3|34.6|27.2|99.5|63.2|55.4|51.4|
|H2O|0.13x|38.8|42.6|43.2|37.7|25.8|26.0|21.2|96.0|54.1|49.5|43.5|
|1-bit KIVI (g=64)|0.10x|22.9|30.1|38.7|22.0|16.9|11.0|14.9|76.5|39.1|34.1|30.6|
|+ SpeCache|0.10x|43.0|53.0|50.4|40.6|30.4|34.7|27.5|98.0|57.7|48.1|48.4|
As you expected, the performance of Full KV significantly improves compared to the 8K context at 128K context. Our method, with just 10% KV size, has a 3% gap compared to Full KV, but still shows a 17.8% improvement over the purely quantization method, KIVI.
> Q5. Comparision with SnapKV
We added SnapKV as a baseline on longbench. Since SnapKV compresses the KV cache to a fixed size, to ensure a fair comparison, we dynamically calculated the SnapKV budget for each sample length, aligning its KV cache size with that of our method.
|Model|Method|KV Size|Qasper|MF-en|HotpotQA|2WikiMQA|Musique|GovReport|MultiNews|PRe|LCC|RB-P|Average|
|-|-|-|-|-|-|-|-|-|-|-|-|-|-|
|Mistral-7B-Instruct-v0.2|SnapKV|0.10x|25.0|45.1|34.1|18.7|18.8|26.2|24.4|79.5|51.8|51.4|37.5|
|Mistral-7B-Instruct-v0.2|1-bit SpeCache (g=64)|0.10x|31.1|49.6|43.9|26.9|18.3|27.8|26.7|76.8|52.3|50.4|40.4|
|LLaMA-3-8B-Instruct|SnapKV|0.11x|39.1|42.9|46.2|36.1|21.8|23.2|21.5|66.0|55.1|50.2|40.2|
|LLaMA-3-8B-Instruct|1-bit SpeCache (g=64)|0.11x|43.2|45.6|46.2|36.9|20.7|27.9|27.1|65.0|55.0|51.0|41.9|
Under the same KV cache size budget, SnapKV outperforms all other baselines. However, SpeCache still delivers superior performance. Our method is capable of working with an extremely small KV cache size (about 0.1x), whereas SnapKV tends to experience performance degradation under such conditions. This is because SnapKV compresses the KV cache all at once, which may result in the loss of information needed for subsequent tokens.
> Q6. Compare throughput gains at a fixed batch size
Thank you for your suggestion. We have provided some relevant results in our response to Q1. | Summary: This paper proposes to offload the KV cache to CPU memory and retrieve KV pairs based on the similarity between the query of a speculative token with quantized KV pairs.
Claims And Evidence: This paper has two claims: 1) Attention is sparse while each token requires different KV pairs. It emphasizes the importance of KV cache offloading. 2) The CPU-GPU communication significantly increases inference latency. These claims are supported by experiments in Fig.2
Methods And Evaluation Criteria: The paper proposes to decode an additional speculative token and load KV pairs into the GPU memory based on the speculative token before inference. The method is mainly evaluated on the LongBench dataset.
Theoretical Claims: As far as I see, there are no theoretical claims in this paper.
Experimental Designs Or Analyses: I checked the experimental results provided in this paper. The experiments are conducted to compare the proposed method with KV cache compression methods with ablation study about the proposed method. However, offloading KV cache to CPU memory is not a new idea, the comparison between the proposed method and the previous methods about KV cache offloading is lacked.
Supplementary Material: I have checked the supplementary material. The algorithm and full results on the LongBench dataset are provided.
Relation To Broader Scientific Literature: This paper focuses on the KV cache offloading technique. There is no relation to broader scientific literature.
Essential References Not Discussed: While this paper has cited previous works like [1], the discussion of the difference between the proposed method and previous works is not thorough. Offloading the KV cache to CPU memory is not a new idea. Previous works like [1] also select significant KV pairs based on reduced keys. A discussion of the difference between the proposed method and previous works is lacking.
[1] Tang,J.,Zhao,Y.,Zhu,K.,Xiao,G.,Kasikci,B.,andHan,S. QUEST: Query-aware sparsity for efficient long-context LLM inference. ICML,2024.
Other Strengths And Weaknesses: Strength:
The speculative token decoding for KV cache preloading seems to be an interesting and novel approach. Generally, the paper is clear and easy to follow.
Weakness:
While offloading the KV cache to CPU memory is not a new idea, there seem to be no experiments comparing the proposed method and previous KV cache offloading methods. While previous work[1] has proposed selecting KV pairs based on reduced keys, a more thorough discussion of the difference and the contribution of this paper is needed.
[1] Tang,J.,Zhao,Y.,Zhu,K.,Xiao,G.,Kasikci,B.,andHan,S. QUEST: Query-aware sparsity for efficient long-context LLM inference. ICML,2024.
Other Comments Or Suggestions: I would like to see more experiments and discussion about the difference between the SpeCache and previous KV cache offloading methods. The main contribution of the proposed method is introducing speculative decoding so that the selected KV pairs can be loaded before the decoding step. However, I still have doubts about the improvement of the proposed method over previous methods like QUEST. I look forward to further reply from the authors.
Questions For Authors: 1) Since each speculative token is decoded based on the previous speculative token, the error may accumulate. As the sequence becomes longer, will the speculative token be less accurate?
2) While it is said to decode two tokens in parallel, does the speculative decoding introduce more latency and GPU memory usage? Are there any experimental results regarding the cost brought by speculative decoding?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank the reviewer for their thoughtful feedback! We address specific concerns and questions below.
> Q1. Discuss the difference between SpeCache and QUEST and the contribution of SpeCache.
Although both QUEST and SpeCache focus on how to accurately select sparse KV pairs, their emphasis differs due to the distinct scenarios they address.
+ QUEST aims to reduce computation and the loading of KV cache **from GPU HBM** by reducing the number of KV pages involved in the attention computation, thereby accelerating the model. In contrast, SpeCache focuses on how to predict and load important KV pairs in parallel when the KV cache is **offloaded to lower-level storage devices (e.g., CPU memory)** for GPU memory saving. Since the CPU-GPU bandwidth (e.g., 16GB/s) is much smaller than the GPU HBM bandwidth (e.g., 1.5TB/s), SpeCache selects a much smaller number of KV pairs to load (64) compared to QUEST (over 1024), and focuses on parallel loading and computation.
+ From the experimental results, SpeCache demonstrates a more efficient use of sparse KV pairs. According to the results in QUEST, when the KV budget is less than 1024, model performance significantly declines on longbench (Fig. 7 of the QUEST paper). However, SpeCache performs well even when only 32 KV pairs are loaded (Fig. 5 in our paper). This is because the low-bit KV cache copy we employ can distinguish important KV pairs at a finer granularity, and the low-bit KV cache itself provides some coarse-grained information during decoding.
> Q2. As the sequence becomes longer, will the speculative token be less accurate?
We evaluate 2-bit SpeCache (g=64) and Mistral-7B-Instruct-v0.2 on two long sequence generation tasks, MultiNews and GovReport in Longbench. We track the Speculative Token Top-K KV Cache Hit Rate -- the proportion of the top-k KV cache needed for the next output token that is hit by the top-k KV cache of the speculative token. We separate calculated the hit rate at different decoding step intervals.
|dataset|[1, 10]|[11, 50]|[51, 100]|[101, 200]|[201, ]
|-|-|-|-|-|-|
|MultiNews|95.9|92.1|89.1|88.1|87.5|
|GovReport|97.0|92.5|86.9|87.0|86.8|
We find that as the output grows, the hit rate gradually decreases, but after dropping to around 87%, it stabilizes and maintains a relatively high hit rate.
> Q3. Does the speculative decoding introduce more latency and GPU memory usage?
Since both tokens share the same model weight matrices and KV cache during decoding, speculative decoding neither introduces additional latency from loading pages into the GPU HBM nor increases VRAM usage. Furthermore, as the decoding process is IO-bound and GPU units are not fully utilized, the added computational load does not significantly increase the latency. We verify this through experiments. On Mistral-7B-Instruct-v0.2, we test the latency and VRAM usage of KIVI and KIVI+SpeCache with a batch size of 1 and a context length of 64k.
|Method|Latency (ms/step)|Allocated memory (GB)|
|-|-|-|
|Full KV|204.3|31.1|
|2-bit KIVI (g=64)|94.6|22.8|
|+ SpeCache|103.6|22.8|
|1-bit KIVI (g=64)|94.3|22.3|
|+ SpeCache|101.3|22.3|
We can find that SpeCache only slightly increases the latency of KIVI.
---
Rebuttal Comment 1.1:
Comment: I appreciate the rebuttal, and I will increase my score
---
Reply to Comment 1.1.1:
Comment: Thank you very much for your prompt response and recognition of the paper. | Summary: This paper presents SPECACHE, a novel method to address the memory bottleneck caused by key-value (KV) caches in large language models when processing long sequences. The authors propose a training-free approach that offloads the complete KV cache to CPU memory while maintaining a low-bit copy in GPU VRAM. The key innovation is a speculative mechanism that predicts which KV pairs will be most relevant for the next token, allowing these to be prefetched from CPU to GPU memory in parallel with ongoing computations. This technique avoids both the information loss associated with compression methods and the latency penalties from offloading approaches. The authors evaluate SPECACHE on LongBench and Needle-in-a-Haystack benchmarks, demonstrating that it can maintain performance comparable to full KV cache while using only 10% of the GPU memory, enabling up to 12x larger batch sizes and 4.6x higher throughput.
Claims And Evidence: The authors' primary claims are well-supported by empirical evidence:
* The claim that KV cache is a memory bottleneck is substantiated with concrete examples in the introduction (page 1, paragraph 2), where they show that for LLaMA 2-7B processing sequences of length 2k with batch size 16, the KV cache size exceeds the model's parameter count.
* The assertion that attention in LLMs is sparse (page 2, paragraph 1) is backed by both references to existing literature and their own analysis in Figure 2 (left), which demonstrates that only 0.5% of keys can cover 90% of a query's attention.
* The claim that SPECACHE maintains model performance while significantly reducing memory usage is well-supported through extensive experiments across multiple models (LLaMA-2, LLaMA-3, and Mistral) on LongBench in Table 1 and Table 2. For instance, with Mistral-7B-Instruct-v0.2, they show a performance gap of only 2% compared to the 16-bit baseline while retaining only 10% of the KV cache size (page 7, paragraph 2).
* The throughput improvements claimed (up to 4.6×) are clearly demonstrated in Table 3 with detailed measurements across different context lengths and batch sizes.
However, I note that the claim about "avoiding inference latency caused by CPU-GPU communication" (page 2, paragraph 2) is slightly overstated. The method mitigates rather than eliminates latency, as shown in Table 4 where parallel prefetching reduces but doesn't eliminate the latency overhead.
Methods And Evaluation Criteria: The methods are sound and the evaluation criteria are appropriate for the research question:
* The authors use a comprehensive evaluation approach, testing on the established LongBench benchmark (covering 15 diverse tasks) and the Needle-in-a-Haystack task for specific evaluation of long-context retrieval ability.
* The baseline comparisons are thorough and fair. On page 6-7, the authors compare SPECACHE with several state-of-the-art methods including InfLLM, StreamLLM, H2O, and KIVI with varying compression ratios.
* The experimental setup is clearly described (page 5, section 4.1), specifying implementation details like the number of residual KV pairs and quantization group sizes.
I appreciate the realistic evaluation of throughput (Table 3) across different context lengths, which directly addresses the practical utility of the method. One minor issue is that the authors don't explicitly report statistical significance for their results, though the consistent improvements across multiple models and tasks suggest the findings are robust.
Theoretical Claims: The authors make several theoretical claims that I've verified:
* The analysis of attention sparsity in Figure 2 (left) is sound and aligns with previous findings in the literature. The comparison between query-dependent top-k attention and greedy cache eviction correctly illustrates why dynamic prefetching is necessary.
* The asymptotic analysis of CPU-GPU transfer time (Figure 2, right) correctly shows the linear relationship between transfer size and latency, providing a theoretical foundation for why prefetching only the most important KV pairs is beneficial.
* The assertion that LLM inference is memory-IO bound rather than compute-bound (page 3, end of section 2.2) is supported by both citations and their own measurements, justifying why simultaneous decoding of output and speculative tokens doesn't significantly increase latency.
* The improved 1-bit quantization method (page 5, section 3.4) is theoretically sound, with the modified zero-point and scaling factor ensuring better approximation for uniform distributions.
Experimental Designs Or Analyses: I checked several aspects of the experimental design and analyses:
* The evaluation on LongBench (Tables 1 and 2) is comprehensive and well-executed, covering multiple models and settings. The authors consistently report average performance across tasks, which gives a clear overall picture.
* The ablation studies (Figures 4 and 5, Table 4 and 5) are well-designed to isolate the impact of specific components. For example, the ablation on 'k' (number of prefetched KV pairs) in Figure 5 shows the trade-off between performance and transfer size.
* The comparison with non-speculative fetching (Table 4) effectively demonstrates the advantage of parallelizing prefetching and computation, showing both performance and latency metrics.
* The throughput measurements in Table 3 appropriately use maximum batch sizes that the GPU memory can handle, providing a realistic assessment of the method's practical benefits.
One analysis that could be improved is the mechanism for selecting the speculative token. On page 4, the authors mention using the output token to compute a speculative token, but don't fully explain how this approximates the next token. More details on this approximation would strengthen the paper.
Supplementary Material: I reviewed the appendix, which includes:
* The pseudocode (Algorithms 1-3) for the prefilling, pre-decoding, and decoding stages, which clarifies implementation details that were omitted from the main text for brevity.
* The detailed setup for the Needle-in-a-Haystack benchmark, including the scoring criteria (pages 11-12).
* Full results on all 15 tasks from LongBench (page 12), expanding on the 10 tasks reported in the main text.
These materials provide important details that support the claims made in the main paper and enhance reproducibility.
Relation To Broader Scientific Literature: N/A
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: Strengths:
* The proposed method is training-free and can be applied to existing pre-trained models without modification, enhancing its practical utility.
* The paper demonstrates impressive results across multiple models (LLaMA-2, LLaMA-3, Mistral) and a range of tasks, showing the broad applicability of the approach.
* The improvement to 1-bit KIVI quantization (page 5, section 3.4) is a valuable contribution in itself, enabling much higher compression ratios than previously possible.
* The method elegantly leverages the memory-IO bound nature of LLM inference to perform speculative decoding with minimal overhead.
* The approach is particularly impactful for long contexts and larger batch sizes, where memory constraints are most significant (Table 3).
Weaknesses:
* On page 4, paragraph 2, the paper states "speculative tokens may be less accurate for output." However, there's no analysis of how often the speculative token differs from the eventual output token, which would help readers understand the approach's limitations.
* The implementation relies on PyTorch's multi-stream mechanism, which the authors acknowledge is not theoretically optimal (page 8, paragraph 1). More details on how a custom implementation could further improve efficiency would strengthen the paper.
* While the authors show SPECACHE works well with KIVI quantization, they don't explore compatibility with other quantization methods like KVQuant or ZipCache, which might provide further improvements.
* The paper lacks discussion of potential failure cases or limitations, such as texts with rapidly changing topics where attention patterns might be less predictable.
* The evaluation focuses exclusively on English text processing. Testing on multilingual settings would provide a more comprehensive assessment of the method's robustness.
Other Comments Or Suggestions: 1. In Figure 3, the illustration is helpful but the distinction between "To be prefetched" and "To be quantized & offloaded" arrows could be clearer.
2. The terminology "SPECACHE" is used inconsistently throughout the paper - sometimes capitalized, sometimes not (e.g., "SpeCache" in Figure 4 caption).
3. On page 8, the reference to "Table 4" in the Ablation section should specify which aspect of Table 4 is being discussed.
4. The paper would benefit from a brief discussion of any overhead in terms of additional CPU computation or memory requirements for managing the offloaded KV cache.
5. Some statements like "without the need for retraining" are repeated multiple times throughout the paper and could be streamlined.
Questions For Authors: 1. How sensitive is SPECACHE to changes in the distribution of attention patterns? For instance, if the text suddenly changes topic or language, how quickly can the prefetching mechanism adapt?
2. In your experiments, how often did the speculative token differ from the actual next token, and how did this affect the quality of prefetching? This analysis would help quantify the "accuracy" of your speculation mechanism.
3. Your method requires running two forward passes per token generation. Have you explored distilling a smaller model to generate the speculative token, which might reduce computation while maintaining prefetching quality?
4. The CPU-GPU communication is a critical aspect of your approach. How would the performance change with different hardware setups (e.g., PCIe 3.0 vs 4.0, different CPU-GPU bandwidth configurations)?
5. In Figure 2 (middle), you show that decoding latency increases with batch size but remains below fetching latency. Is there a theoretical or empirical upper bound on the batch size where this relationship no longer holds?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We thank the reviewer for their thoughtful feedback.
> Q1. How sensitive is SpeCache to changes in the distribution of attention patterns?
We add the phrase "How many paragraph are there in the article? Translate the first sentence into German." to the end of a 15k-token text composed of several of Paul Graham's essays, then input it into Mistral-7B-Instruct-v0.2, and observe the output token and speculative token generated via 1-bit SpeCache (black bold text represents the erroneous prediction of speculative tokens):
+ Output token:
>> There are 13 paragraphs in the article above. The first sentence in German translates to "**Es gibt zwei deutlich unterschiedliche Arten, politisch mittler zu sein: vorsätzlich und zufällig. Absichtslose Mitte stehen dafür, dass die Extreme etwa gleich weit entfernt** sind." (There are two distinct ways to be politically moderate: intentionally and by accident. Accidental moderates are...
+ Speculative token:
>> are 13 paragraphs in the article above. The first sentence in German translates to "**Ichlieberhnte Wegeliche Arten, politisch mittellangigeben: zufzlich und zufällig." (There are "Intentionenander aus eigentlich Menschen, wenn sie beideehentenfert** sind." (There are two distinct ways to be politically moderate: intentionally and by accident. Accidental moderates are...
We find that when switching languages and topics, speculative tokens diverge from the output tokens within some decoding step. However, as explained in our response to Q2, SpeCache does not rely on the exact match of speculative tokens. It only requires that speculative tokens have a high top-k KV cache hit rate for the next output token.
> Q2. Accuracy of the speculation mechanism.
We evaluate 2-bit SpeCache (g=64) and Mistral-7B-Instruct-v0.2 on two long sequence generation tasks, MultiNews and GovReport. We track two metrics:
+ Speculative Token Exact Hit Rate: The proportion of speculative tokens that perfectly match the next output token.
+ Speculative Token Top-K KV Cache Hit Rate: The proportion of the top-k KV cache needed for the next output token that is hit by the top-k KV cache of the speculative token.
|dataset|Exact Hit Rate|Top-K KV Cache Hit Rate|
|-|-|-|
|MultiNews|57.5|91.3|
|GovReport|57.6|90.9|
Although the exact hit rate is around 57%, SpeCache does not directly output speculative tokens. Instead, it uses them as a medium to guess the top-k KV cache. The top-k KV cache hit rate is above 90%, which ensures the effectiveness of the speculative tokens.
> Q3. SpeCache requires running two forward passes per token generation. Have you explored distilling a smaller model?
+ Throughout the inference process, we only add one step of pre-decoding, and in the subsequent decoding phase, SpeCache runs **only one forward pass for each token generation**. This is because SpeCache uses both the Output token (e.g., $T_1$) and the Speculative token (e.g., $T'_2$) as input (i.e., [$T_1$, $T'_2$]) for decoding, which generates two tokens (i.e., $T_1$ generates $T_2$, $T'_2$ generates $T'_3$) in a single forward pass. These tokens are then used as input for the next step, with $T_2$ serving as the model's official output.
+ This is also the reason why the generation of the speculative token is a “free lunch” attached to the forward pass of the output token. Therefore, there is almost no additional overhead, and no need to distill an extra model to generate the speculative token.
> Q4. How would the performance change with different hardware setups.
Due to the varying computational capabilities of different GPUs and the differences in the optimization levels of their operators, it is challenging to conduct a direct ablation study on bandwidth. Therefore, we perform some theoretical analysis to address this. For example, on Mistral-7B-Instruct-v0.2, when the context length is 2K, the maximum batch size for 1-bit SpeCache supported by a 48GB GPU memory is 410. This requires transmitting 3.4GB of KV cache during each decoding step. Theoretically, since SpeCache can fully parallelize data transfer and computation, the decoding latency is 775ms/step. In other words, under optimal conditions, as long as the bandwidth is above 4.4GB/s, the decoding latency of SpeCache will not significantly change.
> Q5. Theoretical or empirical upper bound on the batch size where "decoding latency < fetching latency" no longer holds?
As the batch size increases, the fetching latency grows linearly, while the decoding latency increases sub-linearly due to improved computation parallelism. This results in the overall decoding latency being lower than the latency for fetching the entire KV cache when the batch size is large. Empirically, we have observed the following behavior: For Mistral-7B-Instruct-v0.2 on an A6000 GPU, with a context length of 2K, when batch size >= 4, fetching latency > decoding latency. Additionally, when the context lengths are 8K or 32K, the boundary conditions shift to 2 and 1, respectively. | Summary: This paper proposes storing low-bit KV on the GPU while offloading full-precision KV. Attention is performed between the overall full-precision KV of the top-k keys selected from the low-bit keys.
Additionally, the paper introduces the use of speculative tokens to speculatively prefetch the KV cache needed for the next token. Speculative tokens have been shown to be beneficial for reducing latency.
Claims And Evidence: Most of the claims of this paper are well-supported.
I have one question about table 3: is this throughput run with flash decoding?
I am worried about the slow implementation of torch attention and the overhead burden of two times attention and cpu-gpu io.
Methods And Evaluation Criteria: see claims.
Theoretical Claims: NA.
Experimental Designs Or Analyses: see claims.
Supplementary Material: yes.
Relation To Broader Scientific Literature: na.
Essential References Not Discussed: na.
Other Strengths And Weaknesses: Strengths:
1. This paper is well written with a neat idea.
2. Experiments demonstrate that this method can effectively improve throughput.
Weakness:
1. The improvement w.r.t 2bit KIVI is relatively small, less than 1.5 points. I do not know why the 1-bit improvement is so large. is that due to the 1-bit kivi implementation? I do not think 1 bit is a common setting for kv quant. What is the performance of KVQuant + spec cache?
2. How speculative tokens T2' generated is very confusing. I think it is the main part of this work. Does this spec token work layer by layer? What is pre-generated?
3. I have one question about table 3: Is this throughput run with flash decoding?
I am worried about the slow implementation of torch attention and the overhead burden of two times attention and cpu-gpu io.
Other Suggestions:
1. I suggest that the authors should add a Pareto optimal curve comparison, where the y-axis represents benchmark performance and the x-axis represents the throughput of different methods.
This is because Table 3 does not show a throughput comparison between the authors' method and KIVI, despite KIVI achieving almost the same performance as the authors' results.
2. Add more experiment results on RULER.
3. Add a cache hit rate for speculative tokens.
Other Comments Or Suggestions: table 3: throughput -> throughput (tokens/sec)
Questions For Authors: see weakness.
If the author answer these questions during rebuttal, I will improve 2->3.
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: We thank the reviewer for their thoughtful feedback! We address specific concerns and questions below.
> Q1. Why the 1-bit improvement is so large? Performance of KVQuant + SpeCache.
+ The improvement of SpeCache on 2-bit KIVI is relatively small because the performance of 2-bit KIVI on longbench is already close to that of 16-bit KV Cache, which can be considered as the performance upper bound after KV Cache compression. As a result, there is limited optimization space left. On the more complex RULER benchmark, SpeCache can provide a significant improvement to 2-bit KIVI (see Q5).
+ In our comparison, all instances of "1-bit KIVI" refer to our improved KIVI implementation described in Section 3.4, since original KIVI can hardly work with 1-bit (see Table 5). The larger improvement of SpeCache on the improved 1-bit KIVI is due to the fact that the improved 1-bit KIVI is still far from the upper bound, leaving more room for optimization.
+ Since the official KVQuant code does not include 1-bit quantization, we compared the performance of SpeCache with 2-bit KVQuant. We conducted experiments on LLaMA-2-7B and measured the PPL on Wikitext-2. The results show that SpeCache also improves the performance of KVQuant.
|Method|PPL|
|-|-|
|Full KV|5.12|
|2-bit KVQuant|7.03|
|+ SpeCache|5.37|
> Q2. Does this speculative token work layer by layer? What is pre-generated?
The pre-decoding phase is a single inference step we introduce between prefilling and decoding. Its purpose is to generate the first speculative token $T’_2$. During pre-decoding phase, $T_1$ is the model input, and the entire model output (i.e., the predicted next token) is used as $T’_2$. In the first decoding step, $T’_2$ is used alongside the $T_1$ as the query, and $T’_2$ will record the top-k KV pairs from each attention layer by layer during decoding, in order to prefetch them for use in the next step.
> Q3. Is this throughput run with flash decoding?
For Full KV Cache, we consistently use Flash-Attention2. For SpeCache and KIVI, during the prefilling phase, we also use Flash-Attention2. However, in the decoding phase, due to the involvement of low-bit operations, we use the low-bit CUDA operators provided by KIVI to compute attention.
> Q4. Throughput comparison between SpeCache and KIVI.
Thank you for your suggestion. Here, we first provide a throughput comparison between SpeCache and KIVI with context length of 32k on Mistral-7B-Instruct-v0.2.
|Method|Throughput (tok/sec)|Performance on Longbench|
|-|-|-|
|Full KV|10.3|42.3|
|2-bit KIVI (g=64)|36.5|39.7|
|+ SpeCache|34.6|42.0|
|1-bit KIVI (g=64)|50.8|28.9|
|+ SpeCache|47.3|40.4|
SpeCache only slightly reduces the throughput of KIVI. Since the computation of speculative tokens is parallelized with the output tokens, the simultaneous decoding of both tokens does not significantly increase the latency.
> Q5. Add more experiment results on RULER.
We evaluate LLaMA-3.1-8B-instruct on RULER with a 32k context length, and the results are as follows:
|Method|KV Size|N-S1|N-S2|N-S3|N-MK1|N-MK2|N-MK3|N-MQ|N-MV|QA-1|QA-2|VT|FWE|Average|
|-|-|-|-|-|-|-|-|-|-|-|-|-|-|-|
|16-bit Full KV|1.00x|100.0|100.0|100.0|99.8|99.6|99.6|98.3|98.7|76.8|50.2|98.3|87.1|92.4|
|2-bit KIVI (g=64)|0.16x|100.0|98.6|93.8|98.8|96.0|66.2|95.7|96.8|72.8|48.2|86.8|86.1|86.7|
|+ SpeCache|0.16x|100.0|99.8|99.6|100.0|99.0|95.8|98.9|99.0|75.0|49.4|95.7|87.3|91.6|
|1-bit KIVI (g=64)|0.10x|11.4|12.0|1.8|7.4|2.0|0.0|1.3|0.5|38.0|25.0|2.0|20.1|10.1|
|+ SpeCache|0.10x|100.0|94.6|94.4|97.2|65.6|34.0|80.6|82.5|59.0|34.7|74.8|74.5|74.3|
We find that 2-bit KIVI experiences significant performance degradation on RULER compared to Full KV, especially on the N-MK3 and VT tasks. However, SpeCache effectively mitigates this issue, keeping the performance gap from Full KV within 1%. While 1-bit KIVI completely fails on all tasks in RULER, SpeCache provides a significant performance boost and even reaches the Full KV cache level on certain tasks, such as N-S1.
> Q6. Add a cache hit rate for speculative tokens.
We evaluate 2-bit SpeCache (g=64) and Mistral-7B-Instruct-v0.2 on two long sequence generation tasks, MultiNews and GovReport in Longbench. We track two metrics:
+ Speculative Token Exact Hit Rate: The proportion of speculative tokens that perfectly match the next output token.
+ Speculative Token Top-K KV Cache Hit Rate: The proportion of the top-k KV cache needed for the next output token that is hit by the top-k KV cache of the speculative token.
|dataset|Exact Hit Rate|Top-K KV Cache Hit Rate|
|-|-|-|
|MultiNews|57.5|91.3|
|GovReport|57.6|90.9|
Although the exact hit rate is only around 57%, SpeCache does not directly output speculative tokens. Instead, it uses them as a medium to guess the top-k KV cache. The top-k KV cache hit rate is above 90%, which ensures the effectiveness of the speculative tokens.
---
Rebuttal Comment 1.1:
Comment: Considering that FlashDecoding or FlashInfer has effectively become the standard for long-context inference, I will not consider raising the score unless the authors add more experiments about this part, e.g., speccache+fd vs fd. However, I will make sure to keep track of the response throughout the entire rebuttal period.
---
Reply to Comment 1.1.1:
Comment: Thank you again for your constructive feedback. We provide some clarifications below.
> Is this throughput run with flash decoding?
Sorry for not explaining this clearly. In fact, Flash Decoding has already been integrated into FlashAttention2 (see https://github.com/Dao-AILab/flash-attention/issues/1002). When using FlashAttention2 by calling `flash_attn_func` as in our experiments, it heuristically determines whether to execute Flash Decoding.
To verify this, we replace all `flash_attn_func` calls with explicit `flash_attn_with_kvcache` (i.e., flash decoding) during Mistral-7B-Instruct-v0.2 decoding and test the decoding latency at a sequence length of 64k with batch size = 1:
|method|latency (ms/step)|
|-|-|
|Full KV ('flash_attn_func')|204.3|
|Full KV ('flash_attn_with_kvcache')|202.8|
The results show almost no difference between the two, which means that **Flash Decoding was indeed used in our Full KV evaluation**.
> SpeCache + FD vs FD
Since our attention design allows the quantized KV cache to participate in computation, it is not supported by official Flash Decoding. However, our customized low-bit kernel, based on KIVI (https://github.com/jy-yuan/KIVI/tree/main/quant), is specifically designed for decoding scenarios, making Flash Decoding unnecessary. To demonstrate this, we also test the inference latency on Mistral-7B-Instruct-v0.2 with a 64k context length and batch size = 1
|Method| Latency (ms/step)|
|-|-|
|Full KV |204.3 |
|SpeCache (2-bit)| 103.6|
|SpeCache (1-bit)| 101.3|
It is evident that our low-bit operator is more efficient than Flash Decoding, primarily because the efficient low-bit storage significantly reduces memory access overhead. | null | null | null | null | null | null |
Improving Rationality in the Reasoning Process of Language Models through Self-playing Game | Accept (poster) | Summary: The paper presents the Critic-Discernment Game (CDG), a self-play approach that enhances the reasoning of large language models (LLMs). In CDG, a "prover" generates solutions, while two critics—helpful and misleading—offer feedback. The prover learns to correct mistakes from the helpful critic and resist misleading critiques through reinforcement learning. The method is tested on tasks like mathematical reasoning, error detection, self-correction, and long-chain reasoning, showing significant improvements over baseline models. CDG enables LLMs to improve their reasoning capabilities without human supervision, demonstrating the power of self-play and reinforcement learning in model training.
Claims And Evidence: Yes.
Methods And Evaluation Criteria: Yes.
Theoretical Claims: No issues.
Experimental Designs Or Analyses: While the paper shows improvements on GSM8K and MATH500, one limitation is the lack of explicit testing for generalization to other problem domains or tasks outside of mathematical reasoning.
Supplementary Material: No.
Relation To Broader Scientific Literature: The key contribution of the paper is related to the following prior research:
1. Self-play and Reinforcement Learning for Reasoning. Self-play in LLMs has been explored in other contexts, such as the Adversarial Taboo Game for improving pre-trained models’ reasoning abilities (Cheng et al., 2024b), and the Spar framework (Cheng et al., 2024a), which improves instruction-following by training with self-play.
2. Improving Reasoning through Feedback. Process-based Reward Models (PRMs) (Zhang et al., 2025; Uesato et al., 2022a) and Step-DPO (Lai et al., 2024) also focus on improving reasoning by using feedback at the step level.
3. Mathematical Reasoning and Long-Chain Reasoning. Math Word Problem Solving (Cobbe et al., 2021a) and Mathematical Reasoning in LLMs (Gulcehre et al., 2023) have also seen substantial improvements from techniques like process supervision and feedback-based training. Chain-of-Thought Prompting (Wei et al., 2022) and OpenAI’s Chain-of-Thought Models (Wu et al., 2024a): These methods have been shown to improve performance on long-form reasoning tasks by encouraging models to reason through multiple steps explicitly.
Essential References Not Discussed: No.
Other Strengths And Weaknesses: Strength:
1. The paper introduces a novel Critic-Discernment Game (CDG) to enhance the rationality of reasoning in LLMs through a self-play framework. While self-play has been used effectively in domains like games (e.g., AlphaGo), its application to improving error correction and long-chain reasoning in LLMs is a unique contribution.
2. The authors demonstrate significant improvements across multiple tasks, including mathematical reasoning, stepwise error detection, self-correction, and long-chain reasoning.
3. By incorporating a self-reflection mechanism with iterative feedback, the paper proposes a method that could significantly improve performance on challenging problems that require several reasoning steps, a major strength in advancing LLM capabilities.
Weakness:
1. While the paper reports significant improvements on tasks related to mathematical reasoning and self-correction, the focus on these domains means the broader applicability of the CDG method remains unclear.
2. The paper does not provide an extensive discussion on the sensitivity of the model’s performance to hyperparameters (e.g., the thresholds used in the RL setup). These hyperparameters can significantly affect the outcome of reinforcement learning-based methods, and without clear validation or tuning, the results may not be as stable or generalizable in different contexts.
3. The training process involving multiple self-play rounds and critics is resource-intensive. While the paper demonstrates the effectiveness of CDG, it does not provide a comprehensive analysis of the computational cost or the training time involved. It would be helpful to include a comparison of the cost-benefit tradeoff between CDG and other methods, such as instruction tuning or preference optimization.
Other Comments Or Suggestions: While the experiments are well-conducted, some aspects of the methodology (e.g., dataset creation, sampling strategies) are not presented in full detail. For example, the paper mentions the use of regular expressions and the SymPy grader for evaluating solutions, but further clarification on how these tools are integrated into the RL training process would improve transparency.
Questions For Authors: Please see the weakness.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: > **Experimental Designs Or Analyses:**
> While the paper shows improvements on GSM8K and MATH500, one limitation is the lack of explicit testing for generalization to other problem domains or tasks outside of mathematical reasoning.
> **Weakness:**
> While the paper reports significant improvements on tasks related to mathematical reasoning and self-correction, the focus on these domains means the broader applicability of the CDG method remains unclear.
We agree that evaluating generalization beyond GSM8K and MATH is important. To this end, we conduct additional experiments on tasks outside the original training distribution, including diverse reasoning benchmarks (LogiQA, ARC-Easy, and ARC-Challenge) and more difficult mathematical problems (Minerva-MATH). Results are shown below:
| Model| Minerva| LogiQA| ARC-E| ARC-C|
|-|-|-|-|-|
| Llama3.1-8B-Instruct| 31.24| 31.18| 79.76| 54.95|
| + CDG| **33.10**| **32.26**| **80.05**| **55.80**|
These results show that CDG yields consistent gains across different domains, suggesting it enhances general reasoning capabilities.
We also train CDG on Dapo-17k [1], a harder dataset. Results on the challenge **AIME-24** test set are shown below:
| Model| Pass@1| Pass@4| Pass@8|
|--|--|--|--|
| Qwen2.5-1.5B-Instruct| 1.67| 6.67| 6.67|
| + CDG-1| 2.67| 3.33| 3.33|
| + CDG-2| 5.33| 6.67| 6.67|
| + CDG-3| **5.67**| **10.0**| **16.7**|
We average over 10 runs due to the small test size. CDG-3 improves performance from 1.67 to 5.67 using only 18k self-generated examples. For comparison, Qwen2.5-1.5B-MATH-Instruct reaches 10.0 after 2.5M CoT-annotated examples and GRPO. This highlights CDG’s data efficiency and effectiveness on low-performing tasks.
> **Weakness**
> The paper does not provide an extensive discussion on the sensitivity of the model’s performance to hyperparameters (e.g., the thresholds used in the RL setup).
The ReST approach involves very few hyperparameters and does not require a reference or critic model. Unlike PPO or DPO, where improper values of $\beta$ can lead to training collapse (e.g., duplicate or collapsed generations), ReST does not suffer from such instability. As for selecting the threshold $\tau$, we choose it based on data balance considerations and observed performance during training.
> **Weakness**
> The training process involving multiple self-play rounds and critics is resource-intensive. While the paper demonstrates the effectiveness of CDG, it does not provide a comprehensive analysis of the computational cost or the training time involved. It would be helpful to include a comparison of the cost-benefit tradeoff between CDG and other methods, such as instruction tuning or preference optimization.
We appreciate the reviewer’s concern regarding computational efficiency. We compare our method with traditional RL approaches such as Expert Iteration, from both inference (rollout) and training perspectives.
During the rollout stage, the prover first generate an initial solution. Based on this solution, the critic then generates multiple critiques. The prover subsequently produces multiple second-round responses conditioned on these critiques. The overall rollout cost increases by approximately 20% compared to Expert Iteration to produce the same amount of training data.
During training, the additional computational cost compared to Expert Iteration comes from training the critic. The amount of training tokens for the critic is about 25% of that for the prover.
Overall, while our approach involves more LLM instances, the practical computational overhead remains moderate due to reuse of generated content. In addition, our training does not require the reference model and critic model commonly used in many RL algorithms.
In the experiment for Table 3, for Expert Iteration, we report the best result under equal training budgets. For Step-DPO, we follow the original 3-round setup using 10k GPT-4o-annotated step-level preferences data.
> **Other Comments Or Suggestions:**
> While the experiments are well-conducted, some aspects of the methodology (e.g., dataset creation, sampling strategies) are not presented in full detail. For example, the paper mentions the use of regular expressions and the SymPy grader for evaluating solutions, but further clarification would improve transparency.
Many details of our dataset construction, sampling strategies, and hyperparameter settings are included in the appendix due to space limitations.
Using the SymPy grader to evaluate mathematical answers is a common practice; we follow the same evaluation setup as in qwen2.5-math-instruct [2]. We will also release the detailed evaluation code.
References:
[1] Yu Q, Zhang Z, Zhu R, et al. DAPO: An Open-Source LLM Reinforcement Learning System at Scale[J]. arXiv preprint arXiv:2503.14476, 2025.
[2] Yang A, Zhang B, Hui B, et al. Qwen2. 5-math technical report: Toward mathematical expert model via self-improvement[J]. arXiv preprint arXiv:2409.12122, 2024. | Summary: This paper introduces the Critic-Discernment Game (CDG), a self-play approach to improve reasoning in language models without human supervision. In CDG, three roles interact: a prover that solves problems, a helpful critic that identifies errors in incorrect solutions, and a misleading critic that fabricates errors in correct solutions. Through reinforcement learning, the prover learns to maintain correct answers against misleading critiques while correcting genuine errors. Experiments on mathematical reasoning, error detection, self-correction, and long-chain reasoning tasks demonstrate consistent performance improvements, in well-aligned models like LLaMA-3.1-8B-instruct, showing that this game-based approach effectively enhances reasoning capabilities beyond traditional fine-tuning methods.
Claims And Evidence: One limitation is that the mechanism by which CDG improves understanding of reasoning processes is somewhat indirect - the improvements in performance are clear, but the internal changes to model reasoning are primarily inferred from these performance gains rather than directly measured or analyzed, so it's unclear that if LLMs are truly doing the reasoning and verifications or just pretending to do so.
Methods And Evaluation Criteria: Outdated and easy dataset (GSM8k) and data sizes ( 200 positive and 200 negative samples) is somewhat concerning; The author should try to exploit more challenging mathematical reasoning dataset such as AIME to avoid potential data leakage to strength the arguments. Lack of concrete discussions on how the prover evaluates whether a critique is helpful or misleading.
Theoretical Claims: The mathematical formulation in Section 3 includes game modeling, reward functions, and reinforcement learning objectives, but these are definitions rather than theorems requiring proof.
Experimental Designs Or Analyses: The ablation studies isolate the contribution of each critic type, and comparisons with other RL methods use the same training data and budget, but simiarly to what I discussed on Claims and Evidences, one potential issue is that most evaluations assume that improving task performance equates to improving reasoning rationality, which may not always be true, but their comprehensive task suite mitigates this concern. Also the computational overhead (efficiency) problems should be discussed when comparing with other RL methods since the use of multiple LLM instances.
Supplementary Material: No.
Relation To Broader Scientific Literature: Process-based reasoning improvement: Extends work by Lightman et al. (2023) and Lai et al. (2024) on stepwise supervision, but without requiring human/superior model annotations; Builds on outcome-based methods (Anthony et al., 2017; Gulcehre et al., 2023) and step-level supervision (Zhang et al., 2025; Uesato et al., 2022), but uniquely derives rewards from game rules rather than explicit supervision
Essential References Not Discussed: No.
Other Strengths And Weaknesses: This work uniquely combines self-play games with RL for reasoning improvement, offering a novel training paradigm beyond traditional instruction tuning and preference optimization. See above for Weakness;
Other Comments Or Suggestions: No.
Questions For Authors: 1: How does the approach scale with increasingly complex reasoning tasks? Is there a limit to the reasoning length where CDG becomes less effective?
2: Could you elaborate on how the prover evaluates whether a critique is helpful or misleading? Is this purely reward-driven or are there explicit criteria?
3: What specific improvements did you observe in the reasoning process itself, beyond task performance metrics?
4: How does the approach handle ambiguous problems where multiple valid reasoning paths exist?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thanks for your constructive feedback on our paper. Our response to your questions is as follows:
> **Claims And Evidence:**
> One limitation is that the mechanism by which CDG improves understanding of reasoning processes is somewhat indirect. It's unclear that if LLMs are truly doing the reasoning and verifications or just pretending to do so.
Indeed, it is difficult to directly assess whether a model reasons in a rational manner. To address this, we evaluate performance across multiple tasks and dimensions to better capture whether the model reasons more rationally.
Our experimental setup is specifically designed for this purpose. For example, the error detection task uses problems the model already solves correctly. Just as human experts who understand a solution can identify and correct their own occasional mistakes, our setup tests whether the model can do the same. Failure in such cases indicates a lack of understanding of its own reasoning rather than a general capability gap.
> **Methods And Evaluation Criteria:**
> Outdated and easy dataset (GSM8k) and data sizes. The author should try to exploit more challenging mathematical reasoning dataset such as AIME.
Yes, with the rapid progress of reasoning models, GSM8K and MATH are no longer sufficient for evaluating mathematical capabilities. To address this, we train CDG on Dapo-17k [1], a more challenging dataset. The results on the **AIME-24** test set are shown below:
| Model| Pass@1| Pass@4| Pass@8|
|--|--|--|--|
| Qwen2.5-1.5B-Instruct| 1.67| 6.67| 6.67|
| + CDG-1| 2.67| 3.33| 3.33|
| + CDG-2| 5.33| 6.67| 6.67|
| + CDG-3| **5.67**| **10.0**| **16.7**|
We average the results over 10 runs due to the small test size. CDG-3 improves performance from 1.67 to 5.67 using only 18k self-generated examples. In comparison, Qwen2.5-1.5B-MATH-Instruct reaches 10.0 after training on 2.5M CoT-annotated examples with GRPO. This highlights the data efficiency of CDG and its effectiveness in improving initially low-performing tasks.
We further evaluate the CDG-trained models in the paper on harder math tasks (Minerva-MATH) and diverse reasoning benchmarks (LogiQA, ARC-Easy/Challenge), demonstrating the generality of our method:
| Model| Minerva| LogiQA| ARC-E| ARC-C|
|--|--|--|--|--|
| Llama3.1-8B-Instruct| 31.24| 31.18| 79.76| 54.95|
| + CDG| **33.10**| **32.26**| **80.05**| **55.80**|
> **Experimental Designs Or Analyses:**
> The computational overhead (efficiency) problems should be discussed when comparing with other RL methods since the use of multiple LLM instances.
We appreciate the reviewer’s concern regarding computational efficiency. We compare our method with traditional RL approaches such as Expert Iteration, from both inference (rollout) and training perspectives.
During the rollout stage, the prover first generate an initial solution. Based on this solution, the critic then generates multiple critiques. The prover subsequently produces multiple second-round responses conditioned on these critiques. The overall rollout cost increases by approximately 20% compared to Expert Iteration to produce the same amount of training data.
During training, the additional computational cost compared to Expert Iteration comes from training the critic. The amount of training tokens for the critic is about 25% of that for the prover.
Overall, while our approach involves more LLM instances, the practical computational overhead remains moderate due to reuse of generated content. In addition, our training does not require the reference model and critic model commonly used in many RL algorithms.
> **Questions For Authors**
A1: Yes, as noted in Methods and Evaluation Criteria, our method significantly improves performance on AIME24, a much more challenging dataset. The average score increased from 1.67 (pre-trained) to 5.67 (CDG-trained), demonstrating stronger capabilities on complex problems. Additionally, Section 4.4 shows clear gains on long-chain CoT tasks with average reasoning lengths exceeding 1000 tokens.
A2: The prompt template for determining whether a critique is helpful or misleading is detailed in the appendix. As specified, if the model deems the critic helpful, it outputs the corrected answer in the boxed section; otherwise, it returns “This critic is not critical.” Rewards are applied accordingly using a rule-based scheme.
A3: Beyond performance, we observe increased self-checking behavior. For instance, the usage of the word “check” increases by 22%, and “verify” by 69%, indicating enhanced internal verification.
A4: For the same question, we sample multiple solutions from the prover. In our setup, the helpful critic only engages with incorrect solutions—where the reasoning must contain errors—while the misleading critic targets correct solutions, attempting to induce mistakes.
References:
[1] Yu Q, Zhang Z, Zhu R, et al. DAPO: An Open-Source LLM Reinforcement Learning System at Scale[J]. arXiv preprint arXiv:2503.14476, 2025. | Summary: This paper introduces a self-play reinforcement learning approach called the Critic-Discernment Game (CDG) to improve language models' reasoning capabilities. In CDG, three roles interact: a prover provides solutions to problems, a helpful critic identifies genuine errors in incorrect solutions, and a misleading critic attempts to fabricate errors in correct solutions. The prover must learn to maintain correct answers against misleading critiques while revising genuinely incorrect solutions. Through experiments on mathematical reasoning, stepwise error detection, self-correction, and long-chain reasoning tasks, the authors demonstrate that CDG training improves the rationality of well-aligned models like LLaMA-3.1-8B-Instruct and Qwen2.5-1.5B-Instruct in their reasoning processes. The method outperforms alternative approaches like Expert Iteration and Step-DPO, highlighting the potential of self-play language games as a promising training paradigm beyond instruction tuning and preference optimization.
Claims And Evidence: The claims in the submission are generally supported by clear and convincing evidence through comprehensive experiments across multiple reasoning tasks. The ablation studies effectively demonstrate that both helpful and misleading critics are necessary components of CDG, while comparisons with other RL methods convincingly show CDG's advantages over alternatives. However, some claims could benefit from stronger evidence: the paper claims to improve "rationality in reasoning" but doesn't directly measure this construct beyond task performance; the improvements, while consistent, are sometimes modest (e.g., ~1.5 percentage points on GSM8K); and the long-term stability of the improvements and potential for overfitting to the game format aren't thoroughly explored, given that GSM8K and MATH are somewhat similar tasks.
Methods And Evaluation Criteria: The proposed methods are conceptually sound for improving reasoning, but the evaluation criteria suffer from limited scope. While the paper uses established mathematical reasoning benchmarks (GSM8K and MATH500), this narrow focus on mathematical reasoning alone raises significant concerns about generalizability. The absence of diverse reasoning datasets spanning different domains (such as commonsense reasoning, logical deduction, scientific reasoning, or counterfactual reasoning) leaves a critical gap in understanding whether CDG's benefits extend beyond mathematical problem-solving or are domain-specific.
Theoretical Claims: The paper does not contain formal mathematical proofs requiring verification, as it primarily presents algorithmic approaches and empirical results.
Experimental Designs Or Analyses: The evaluation framework is methodologically sound for measuring different aspects of reasoning. However, I identified several validity concerns: the limited dataset diversity focused only on mathematical reasoning restricts generalizability claims; there's insufficient reporting of statistical significance (e.g., standard errors); and the paper lacks proper controls for training computation across compared methods.
Supplementary Material: I did not review the supplementary material.
Relation To Broader Scientific Literature: The paper's contributions connect to several established research areas in the broader scientific literature like RLHF (Christiano et al., 2017; Ouyang et al., 2022), self-improvement methods (Huang et al., 2023; Zelikman et al., 2022), and chain-of-Thought reasoning (Wei et al., 2022; Yao et al., 2023).
Essential References Not Discussed: There are two particularly essential related works not adequately cited or discussed: "Self-critiquing models for assisting human evaluators" by Saunders et al. (2022) and "LLM Critics Help Catch LLM Bugs" by McAleese et al. (2024). Besides, the authors should carefully address the similarities and differences between their approach and Kirchner et al. (2024), particularly regarding the training dynamics and how both methods aim to improve the legibility and reliability of model outputs.
Other Strengths And Weaknesses: Please see the above reviews.
Other Comments Or Suggestions: Please see the above reviews.
Questions For Authors: - Do you use three separate models or a single model with different prompts for the three roles during training?
- What do you mean by “both before and after CDG training”?
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: Thanks for your constructive feedback on our paper. Our responses to your questions are as follows:
> **Claims And Evidence:**
> The paper claims to improve "rationality in reasoning" but doesn't directly measure this construct beyond task performance.
As mentioned in the introduction, recent studies suggest that LLMs often rely on pattern matching rather than truly understanding their reasoning processes. However, directly assessing whether a model reasons in a rational manner is inherently difficult. To address this, we evaluate performance across multiple tasks and dimensions to better capture whether the model is reasoning more rationally.
Our experimental setup is specifically designed for this purpose. For example, the error detection task is conduct on problems the model has already demonstrated proficiency in solving. Just as human experts who understand a solution can identify and correct their own occasional mistakes, our setup tests whether the model can do the same. Failure in such cases indicates a lack of understanding of its own reasoning, rather than a general capability gap.
> **Claims And Evidence:**
> The improvements, while consistent, are sometimes modest; the long-term stability of the improvements and potential for overfitting to the game format, given that GSM8K and MATH are somewhat similar tasks.
> **Methods And Evaluation Criteria:**
> Evaluation criteria suffer from limited scope.
We agree that evaluating generalization beyond GSM8K and MATH is important. To this end, we conduct additional experiments on tasks outside the original training distribution, including diverse reasoning benchmarks (LogiQA, ARC-Easy, and ARC-Challenge) and harder mathematical problems (Minerva-MATH). Results are shown below:
| Model| Minerva| LogiQA| ARC-E| ARC-C|
|-|-|-|-|-|
| Llama3.1-8B-Instruct| 31.24| 31.18| 79.76| 54.95|
| + CDG| **33.10**| **32.26**| **80.05**| **55.80**|
These results show that CDG yields consistent gains across different domains, suggesting it enhances general reasoning capabilities.
We further evaluate CDG on more challenging mathematical problems where the base model performs poorly. Specifically, we train CDG on the Dapo-17k dataset [1] and test on the **AIME-24**benchmark. Results are averaged over 10 runs due to the small test size:
| Model| Pass@1| Pass@4| Pass@8|
|-|-|-|-|
| Qwen2.5-1.5B-Instruct| 1.67| 6.67| 6.67|
| + CDG-1| 2.67| 3.33| 3.33|
| + CDG-2| 5.33| 6.67| 6.67|
| + CDG-3| **5.67**| **10.0**| **16.7**|
CDG-3 improves Pass@1 from 1.67 to 5.67 using just 18k self-generated examples. In contrast, Qwen2.5-1.5B-MATH-Instruct reaches 10.0 after training on 2.5M CoT-annotated samples with GRPO. This demonstrates CDG’s data efficiency and strong gains.
> **Experimental Designs Or Analyses:**
> There's insufficient reporting of statistical significance (e.g., standard errors); and the paper lacks proper controls for training computation across compared methods.
To assess statistical significance, we conduct t-tests and report p-values in the caption of Table 1. All four tasks show significant improvements (p < 0.05).
For Expert Iteration, we report the best result under an equal training budget. For Step-DPO, we follow the original 3-round setup using 10k GPT-4o-annotated step-level preference data.
> **Essential References Not Discussed:**
> There are two particularly essential related works not adequately cited or discussed.
> Besides, the authors should carefully address the similarities and differences between Kirchner et al. (2024).
Thank you for pointing this out. We acknowledge that Saunders et al. (2022) and McAleese et al. (2024) are relevant, as they also explore LLM-based self-critiquing and error detection. We will cite and discuss them in the revision.
As for Kirchner et al. (2024), while both approaches involve multi-agent interaction, the objectives differs. Their goal is to improve output legibility by training a helpful prover to outperform a sneaky one. In contrast, our focus is on enhancing the model’s understanding of its own reasoning by training a prover to distinguish helpful from misleading feedback—aiming for developing rational reasoning abilities than readability. We will clarify this distinction in the revision.
> **Questions For Authors:**
> Do you use three separate models or a single model?
> What do you mean by “both before and after CDG training”?
Q1: We use three separate models during training. Prompting alone results in noticeable style differences between the helpful and misleading critics, making them too easy for the prover to distinguish.
Q2: We compare two settings: (1) finetuning the base model on long-chain reasoning data (distilled from QwQ-32B-Preview), and (2) finetuning the model after CDG training using the exact same long-chain reasoning data.
References:
[1] Yu Q, Zhang Z, Zhu R, et al. DAPO: An Open-Source LLM Reinforcement Learning System at Scale[J]. arXiv preprint arXiv:2503.14476, 2025.
---
Rebuttal Comment 1.1:
Comment: Thank you for the response. Regarding the similarities and differences between Kirchner et al. (2024), while I understand the objective differs, the methodologies appear quite similar. Could you elaborate more on these methodological similarities?
---
Reply to Comment 1.1.1:
Comment: Thank you for the insightful follow-up question. While both approaches involve a prover interacting with other agents and may appear similar on the surface, the two games are fundamentally different. Below, we clarify the similarities and differences between our **Critic-Discernment Game (CDG)** and the **Prover-Verifier Game (PVG)** proposed by Kirchner et al. (2024), beyond the distinction in objectives.
**Overview of Kirchner et al. (2024)**
Kirchner et al. (2024) formulate a game with three roles:
1. **Helpful Prover**: A generative model aiming to produce a correct solution that is **easy for a verifier to validate**.
2. **Sneaky Prover**: A generative model aiming to generate an **incorrect solution that appears deceptively plausible**.
3. **Verifier**: A small classifier model trained to **distinguish between correct and incorrect solutions**.
While both approaches adopt a game-theoretic framework with multiple agents, the rule of the game, agent behaviors are fundamentally different from our method. In CDG, the prover engages in a second-round interaction with a critic, who may either be helpful or misleading. **The prover must then decide whether to revise or maintain its original solution based on the critic’s feedback, not just generating a verifiable answer in a single shot**.
It is worth noting that the Prover-Verifier game has been proposed in previous work[1] to improve the verifiability or checkability of generated answers. In contrast, to the best of our knowledge, we are the first to propose Critic-Discernment Game in which critics with opposing goals provide feedback on a model’s solution.
**Differences**
1. The two methods have different objectives.
2. The games are fundamentally different: **the game rules, as well as the agents’ tasks and behaviors, all differ.** The configuration of the role (e.g., model size, whether it acts as a generator or classifier, and the number of dialogue turns ) also differs.
3. In the Prover-Verifier Game, a **verifier (classifier)** judges whether solutions from different provers are correct, primarily to assess solution verifiability. In contrast, the Critic-Discernment Game requires the **prover itself** to evaluate the correctness of critiques directed at its own solution, thereby assessing its understanding of its own reasoning steps.
4. Kirchner et al. (2024) use PPO for optimization; we employ Rest for optimization.
**Similarities**
1. Both employ **three-role games**, where each role is played by a separate model, combining competition and cooperation.
2. Both involve **iterative training** across multiple rounds to improve the performance of each agent.
While both the Prover-Verifier Game and our Critic-Discernment Game leverage game-based training to enhance model capabilities, they differ significantly in terms of game rules, objectives, agent behaviors, and reward structures. The Prover-Verifier Game does not include a critic role that evaluates the internal reasoning steps of the prover, nor does the prover engage in self-assessment of its own solution during the game. Conversely, the Critic-Discernment Game does not involve a classifier to evaluate the checkability of the solution.
[1] C. Anil, G. Zhang, Y. Wu, and R. Grosse. Learning to give checkable answers with prover-verifier games. arXiv preprint arXiv:2108.12099, 2021. | Summary: The paper introduces a framework that involves training three models (prover, helpful critic, misleading critic) via reinforcement learning with the goal of improving the reasoning capability of the prover model. Through the proposed training process, the prover learns to rely only on helpful feedback, and to ignore misleading feedback, thereby gaining a better notion of correct vs. incorrect reasoning. The authors conduct experiments on two math tasks, and show some improvements over the base models.
Claims And Evidence: - It is unclear to me what the goal of the technique really is. The authors claim it is about teaching the models to "understand their reasoning process". The evidence provided to support this is not super convincing. First, the performance gains are quite marginal (e.g., 0.3% boost on gsm8k), and sometimes performance drops from mroe CDG iterations.
Methods And Evaluation Criteria: - Evaluation is done only on two math tasks, namely gsm8k and MATH. GSM8K is a very easy task, with the initial models already achieving ~90%, which might make me think that this technique only works when the base model is already good on the tasks in question. I would be more convinced of the proposed technique if it was applied to tasks where the initial performance is quite low.
- The proposed methods require sampling and training three different models, which can be quite expensive, and the helpful and misleading critics are discarded after training. Have the authors using the same model but with different roles?
Theoretical Claims: N/A
Experimental Designs Or Analyses: - The step-wise error detection experiment is done on problems that the model can fully solve. However, in practice, we want the model to still detect errors in its reasoning on unseen problems whether it can/cannot fully solve these problems. Overall, the experiment setup seems very artificial.
Supplementary Material: Yes, I have reviewed the appendix
Relation To Broader Scientific Literature: - I think the paper's main contribution is RL-based training of self-play with three different models. The idea is neat and interesting, although the performance gains do not justify the complexity of the approach.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: N/A
Other Comments Or Suggestions: N/A
Questions For Authors: - What if you use the same model for the three roles?
- How hard was hyperparameter tuning for the ReST approach? Could you elaborate on stability of the training with ReST?
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: We greatly appreciate your recognition of our idea and your constructive feedback. Here are our responses to your concerns:
> **Claims And Evidence:**
> The goal of the technique is unclear and the evidence provided to support this is not super convincing.
> **Experimental Designs Or Analyses:**
> The step-wise error detection experiment is done on problems that the model can fully solve.
We discuss these two points together, as our experimental design is closely aligned with the goal of the technique. As mentioned in the introduction, recent studies have shown that LLMs lack a true understanding of their reasoning processes and instead rely primarily on probabilistic pattern matching. Our goal is to alleviate this limitation through self-play training. However, performance on a single task (e.g., math problem solving) is insufficient to determine whether a model truly understands its reasoning process. Therefore, we evaluate the model across multiple dimensions to better assess whether it reasons in a rational manner. **As shown in Table 3, our method demonstrates clear and consistent improvements across all tasks, supporting our claim.**
We now clarify the motivation behind the stepwise error detection setting. Human experts, when they truly understand a solution, can identify and fix their own mistakes when such mistakes occasionally occur. Similarly, we focus on problems the model can usually solve correctly to control for knowledge or capability gaps. If the model still fails to detect errors in such cases, it suggests a lack of understanding of its own reasoning process rather than a lack of ability. This design is well aligned with our stated goal. In contrast, Section 4.2 (self-correction) makes no such assumption and evaluates the model on general problems, where initial answers may or may not be correct—thus covering more realistic error-correction scenarios.
>**Methods And Evaluation Criteria:**
>Evaluation is done only on two math tasks, namely gsm8k and MATH. I would be more convinced of the proposed technique if it was applied to tasks where the initial performance is quite low.
Yes, with the rapid progress in reasoning models, GSM8K and MATH may no longer sufficiently evaluate mathematical capabilities. To address this, we train CDG on Dapo-17k [1], a harder dataset. Results on the **AIME-24** test set are shown below:
| Model| Pass@1| Pass@4| Pass@8|
|--|--|--|--|
| Qwen2.5-1.5B-Instruct| 1.67| 6.67| 6.67|
| + CDG-1| 2.67| 3.33| 3.33|
| + CDG-2| 5.33| 6.67| 6.67|
| + CDG-3| **5.67**| **10.0**| **16.7**|
We average over 10 runs due to the small test size. CDG-3 improves performance from 1.67 to 5.67 using only 18K self-generated examples. For comparison, Qwen2.5-1.5B-MATH-Instruct achieves 10.0 after 2.5M CoT-annotated examples and GRPO. This highlights CDG’s data efficiency and effectiveness on low-performing tasks.
We further evaluate the CDG-trained models on harder math (Minerva-MATH) and diverse reasoning tasks (LogiQA, ARC-Easy/Challenge), demonstrating the generality of our method:
| Model| Minerva| LogiQA| ARC-E| ARC-C|
|--|--|--|--|--|
| Llama3.1-8B-Instruct| 31.24| 31.18| 79.76| 54.95|
| + CDG| **33.10**| **32.26**| **80.05**| **55.80**|
>The helpful and misleading critics are discarded after training. Have the authors using the same model but with different roles?
Yes, this is a very meaningful point. In fact, our initial design of CDG used a single model to play different roles via prompting, but we encountered two key issues:
1. The model’s responses as helpful and misleading critics differ noticeably in style and length under different prompts, making it easy for the prover to distinguish between them.
2. Training a unified model to generate misleading critiques can cause unintended side effects, such as hallucinations during regular problem solving.
To avoid these issues, we adopt three separate models with non-shared parameters. This setup yields more stable and reliable gains in the prover’s reasoning ability.
> How hard was hyperparameter tuning for the ReST approach? Could you elaborate on stability of the training with ReST?
The ReST approach involves very few hyperparameters and does not require a reference or critic model. Unlike PPO or DPO, where improper values of $\beta$ can lead to training collapse (e.g., duplicate or collapsed generations), ReST does not suffer from such instability. As for selecting the threshold $\tau$, we manually select it based on data balance and training performance.
References:
[1] Yu Q, Zhang Z, Zhu R, et al. DAPO: An Open-Source LLM Reinforcement Learning System at Scale[J]. arXiv preprint arXiv:2503.14476, 2025. | null | null | null | null | null | null |
SliM-LLM: Salience-Driven Mixed-Precision Quantization for Large Language Models | Accept (poster) | Summary: This work proposes a mixed-precision quantization approach with coarse-level and fine-level partitioning via proposed Salience-Determined Bit Allocation and Salience-Weighted Quantizer Calibration, respectively. The former leverages the double-pointer search algorithm, optimizing KL-divergence between the original model and with the given weight quantized and the line search to determine local-level outliers. The proposed approach is compatible with different quantizers. Slim-LLM is evaluated on top of GPTQ and learnable quantizer Slim-LLM+ on Llama-1,2,3 model family.
Claims And Evidence: The key aspect of the proposed method is the uneven bit width allocation according to weight saliency. While the introduced idea in the presented form is novel, the claim that it is largely overlooked in prior literature is inaccurate, as there are numerous methods that account for outliers in prior work via storing them in sparse format [1, 2] or orthogonal transformation [3, 4]. I would suggest restating the claim that this work proposes a new solution that accounts for uneven weight sensitivity.
The proposed saliency measure is identical to the one adopted in [1] to determine outliers and for sensitivity analysis (see Equation 2 and Figure 2). However, no reference is provided.
The presented empirical results show pretty reasonable performance for 2-bit quantization as compared to other uniform quantization methods.
---
**References**
[1] Dettmers, Tim, et al. "Spqr: A sparse-quantized representation for near-lossless llm weight compression." arXiv preprint arXiv:2306.03078 (2023).
[2] Kim, Sehoon, et al. "SqueezeLLM: Dense-and-Sparse Quantization." International Conference on Machine Learning. PMLR, 2024.
[3] Chee, Jerry, et al. "Quip: 2-bit quantization of large language models with guarantees." Advances in Neural Information Processing Systems 36 (2023): 4396-4429.
[4] Liu, Zechun, et al. "Spinquant: Llm quantization with learned rotations." arXiv preprint arXiv:2405.16406 (2024).
Methods And Evaluation Criteria: The evaluation protocol adopted is standard for research on LLM compression.
Theoretical Claims: This work provides primarily a practical contribution. The theoretical motivation of the proposed approach is sound.
Experimental Designs Or Analyses: Overall, experimental protocol and choice of baselines is sensible.
However, the comparison with DB-LLM [1], leveraging mixed precision, a natural competitor to the proposed approach, is absent. I believe it should be added for completeness of evaluation.
---
**References**
[1] Chen, Hong, et al. "DB-LLM: Accurate Dual-Binarization for Efficient LLMs." Findings of the Association for Computational Linguistics ACL 2024. 2024.
Supplementary Material: I have read the paper appendix.
Relation To Broader Scientific Literature: This work proposes a new way to account for uneven importance of weights via mixed precision with global and local criteria.
Essential References Not Discussed: DB-LLM is mentioned in the related work, but not compared with.
Other Strengths And Weaknesses: While the approach yields quite good performance at 2 bit compression, the performance still lags behind vector quantization methods [1, 2], which achieve same or better speed-ups.
---
**References**
[1] Tseng, Albert, et al. "QuIP $\# $: Even Better LLM Quantization with Hadamard Incoherence and Lattice Codebooks." Forty-first International Conference on Machine Learning.
[2] Egiazarian, Vage, et al. "Extreme Compression of Large Language Models via Additive Quantization." Forty-first International Conference on Machine Learning.
Other Comments Or Suggestions: -
Questions For Authors: * Which dataset is used for the double-pointer search - is it the same calibration set used for SilM-LLM+ (i.e 128 samples from Wikitext-2)?
* How much does it take to produce a quantized model with SilM-LLM?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Dear Reviewer H7Hr,
Thank you for your feedback. We will address your questions and recommendations one by one.
> Q1: The key aspect of the proposed method ... for uneven weight sensitivity. The proposed saliency measure ... However, no reference is provided.
A: We would like to clarify that in lines 45–46 of the paper, we emphasize that weights "exhibit a structured distribution" a phenomenon that has not been overlooked in previous works. Prior studies mainly focused on compressing weights based on the sparse distribution of salience but did not propose specific strategies to handle structured distribution. This insight motivated us to develop an inference-friendly mixed-precision quantization strategy. Thank you for your suggestion—we will highlight the characteristics of structured distribution more clearly.
Regarding SPQR, we explicitly reference SPQR (Line 199) in Definition 3.2 and also cite other works that adopt the same salience definition[1] [2] [3]. We would like to reiterate that the purpose of our work is not to emphasize the formulation of salience itself, but rather to identify its clustering characteristics within LLM weight matrices. SliM-LLM aims to illustrate, through Definition 3.2, the numerical impact of weight magnitude and activation distribution on the salience of LLM weight matrices and provides in-depth theoretical analysis in Theorem 1 and Appendix G, which further confirms the cause of the observed structured clustering of salience in SliM-LLM.
[1]SparseGPT: Massive Language Models Can Be Accurately Pruned In One-shot. ICML, 2023.
[2]PB-LLM: Partially Binarized Large Language Models. ACL 2024.
[3]LLM-MQ: Mixed-Precision Quantization for Efficient LLM deployment. NIPS, 2024.
> Q2: Overall, experimental protocol and choice of baselines ... be added for completeness of evaluation.
A: As summarized in Figure 1, DB-LLM is a QAT-based method, which requires a significant amount of data and extended distillation tuning to complete the quantization process. In other words, it relies on standard backpropagation techniques to adjust the weights. In contrast, SliM-LLM is a totally PTQ method. More importantly, the key advantage of SliM-LLM is its ability to deploy group-wise quantization kernels directly on the GPU, and its seamless integration with AutoGPTQ. DB-LLM is an effective weight-compression method, focusing on memory compression, and is not yet capable of achieving efficient inference and real acceleration, which is the gap we aim to address.
> Q3: While the approach yields quite good performance ...... [1, 2], which achieve same or better speed-ups.
A: QuIP# and AQLM are both highly effective 2-bit LLM codebooks-based or vector-based quantization methods that can be improved by additional fine-tuning to restore performance (referenced in our paper). They rely on backpropagation to adjust pre-trained weights to fit the quantization scenario. In contrast, as we emphasize, SliM-LLM is a fully PTQ-based quantization method, with no training on the original weights. For a fair comparison of quantization strategies, we only compare with state-of-the-art PTQ methods, and we have achieved strong low-bit quantization performance within the PTQ framework.
|#W PPL↓|Method|1-7B|1-13B|2-7B|2-13B|
|-------|---------|----|-----|-----|-----|
|2-bit|QuIP#|9.95|7.18|12.30|7.60|
|2-bit|SliM-LLM+|9.68|7.18|10.87|7.59|
Following your suggestion, we compared the non-trained QuIP# with our SliM-LLM+ at 2-bit. The results above show that even without additional weight tuning, SliM-LLM+ still achieves superior performance.
Regarding the speed-ups you mentioned, we conducted a thorough investigation and reproduction of results. We found that codebook-based and vector-based quantization methods, while effective in compressing weight memory, require complex lookup and decoding operations during real deployment, resulting in inference times that are approximately three times longer than that of fp16 LLMs (https://github.com/Cornell-RelaxML/quip-sharp/issues/63). In contrast, the structured mixed-precision quantization strategy employed by SliM-LLM allows for efficient deployment in AutoGPTQ through a group-wise approach, achieving significant speed-ups.
> Q4: Which dataset is used for the double-pointer search - is it the same calibration set used for SliM-LLM+ (i.e 128 samples from Wikitext-2)?
A: Yes, as demonstrated in Section 4, we used the same calibration data setting (128 samples from WikiText-2), and during quantization, we selected samples randomly. The calibration selection method for SliM-LLM+ is identical to that of OmniQuant, both using random sampling of 128 data points from WikiText-2.
> Q5: How much does it take to produce a quantized model with SliM-LLM?
A: When applying SBA and SQC for PTQ mixed-precision quantization under single-GPU (RTX 4090) edge conditions, the quantization process for a 7B model takes approximately 25 minutes.
---
Rebuttal Comment 1.1:
Comment: After reading the rebuttal addressed to me and other reviewers, I decided to raise my score.
While I still believe that a more accurate comparison with vector quantization methods—in terms of performance and speed-up—is necessary for one to fully appreciate the method’s efficacy and practicality, this is overall a decent work with the potential for practical deployment.
---
Reply to Comment 1.1.1:
Comment: Dear Reviewer H7Hr,
We sincerely thank you for your thoughtful feedback and for raising your score. We truly appreciate your acknowledgment of the potential for practical deployment of our work. Your constructive critique has been invaluable in helping us refine our paper, and we are pleased to have addressed your concerns.
We fully agree on the importance of a more accurate comparison with PTQ vector-quantization methods to thoroughly evaluate the efficacy and practicality of our approach. In response to your valuable suggestion, we will include a detailed comparison of SliM-LLM+ with the non-training QuIP# method (in terms of speed and accuracy) in our revised version.
Thank you again for your engagement and support ! | Summary: The paper introduces SliM-LLM, a novel PTQ framework for LLMs. The proposed method leverages the authors’ observation that important weights follow a structured distribution to preserve the model performance at extremely low-bit precision. Their two key contributions are:
- **Salience-Determined Bit Allocation** analyzes the structured distribution of weight salience to assign different precisions to groups of weights.
- **Salience-Weighted Quantizer Calibration** adjusts the quantizer parameters with a focus on the few highly salient weight elements within each weight group.
The experimental results show that SliM-LLM reduces perplexity compared to SOTA gradient-free PTQ methods while reducing memory usage by nearly 6x. The extended version with graidient-based optimization, SliM-LLM+, further improves the model performance.
## update after rebuttal
SliM-LLM achieved state-of-the-art performance in 2-bit quantization of large language models (LLMs) through two main contributions: Salience-Determined Bit Allocation and Salience-Weighted Quantization Calibration. While this approach effectively reduces the memory requirements of LLMs, it introduces a trade-off in terms of speedup — another critical benefit typically expected from quantization — in exchange for higher accuracy.
Overall, while the paper's claims are well-supported empirically and demonstrate strong experimental results and my other questions are well-addressed, further exploration is still needed regarding inference efficiency.
Claims And Evidence: The analysis of the structuredness of global salience of weights is well supported by results across various layers and models. However, the presence of structural outliers in the output activations of LLMs—and the corresponding salient weight channels—has been extensively addressed in previous works.
The analysis of local salience is relatively underdeveloped, and it has also been explored in recent previous works [1][2].
[1] Yi, Ke, et al. "Rotated Runtime Smooth: Training-Free Activation Smoother for accurate INT4 inference." arXiv preprint arXiv:2409.20361 (2024).
[2] Yu, Mengxia, et al. "The super weight in large language models." arXiv preprint arXiv:2411.07191 (2024).
Methods And Evaluation Criteria: SBA and SQC are logically designed methods that directly address the aforementioned problems. Evaluating using perplexity and zero-shot tasks is appropriate, as these metrics are standard in LLM compression work.
Theoretical Claims: The structured distribution of salience weights due to outlier activations has been pointed out and addressed in various works, and the existence of locally important weights also is not a novel issue introduced by this paper.
Rather than providing a mathematical proof, the paper seeks to validate these issues through experimental evidences.
Experimental Designs Or Analyses: Inference efficiency is another important aspect just as quantized model performance. Although Table 5 presents comparison results with GPTQ, the main text lacks an explanation and analysis of the comparison scenario. The title of subsection 4.3, which claims to address efficient inference, appears to discuss a different topic.
Supplementary Material: None
Relation To Broader Scientific Literature: This research is influenced by existing work on post-training quantization of LLMs. The goal of preserving accuracy by effectively handling outlier or salient values was already established by previous studies, and this work extends that by demonstrating a more hardware-friendly implementation.
Additionally, by addressing both local and global salience, the paper represents a significant extension of the field.
Essential References Not Discussed: The authors may add references for works that mentions occurrence of unstructured outliers (salient values) such as [1], [2] of part 2.
Other Strengths And Weaknesses: **Strength**
Strong performance at 2-bit compared to baselines
**Weakness**
Lack of analysis on latency and throughput, Relatively bad performance on new models
Other Comments Or Suggestions: I suggest to provide more details on
1) experiment settings on evaluating inference efficiency.
2) required time to apply proposed method
3) ablation study on group size
Questions For Authors: - In recent models like LLaMA-3, where there is a significant performance drop, can this method be considered practical?
- Why doesn't the paper provide results on the latest models for SliM-LLM+?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Dear Reviewer iFeq,
Thank you for your valuable feedback and suggestions. We will address your questions and recommendations one by one.
> Q1: (1)The analysis of local salience is relatively underdeveloped, and it has also been explored in recent previous works. (2)The authors may add references for works that mentions occurrence of unstructured outliers (salient values) such as [1], [2] of part 2.
A: The variation in weight importance distribution is crucial for LLM quantization, particularly regarding local salience. As noted in prior studies, our key contribution is using the element sensitivity criterion (Definition 1) to analyze significant weight clustering and provide a theoretical explanation for salience clustering.
We did not explore the underlying causes of local salience in detail, as they have been thoroughly discussed in works like [1] [2] and Section 3.3.2. Instead, we built on these insights to develop the Salience-Weighted Quantizer Calibration (SQC) strategy to reduce quantization errors. We appreciate your reference suggestions and will expand the discussion in the revised version.
> Q2: Inference efficiency is another important aspect ... efficient inference, appears to discuss a different topic.
Thank you for identifying the typo. This was a layout error, and we will correct it by including the full content of the "Efficient Inference on Device" section in the final version.
Specifically, we extend the CUDA kernel in AutoGPTQ to support experimental mixed-precision inference (details in Appendix B.2). We evaluate LLaMA-7/13B and LLaMA-2-7B under 2/3-bit settings, showing that our approach maintains a high compression rate on GPUs while significantly improving model accuracy, with only a slight inference speed reduction on the A800 due to bit-width alignment. As 1-bit operations currently lack hardware support, additional storage and computation are required. We recognize the potential for further optimization in mixed-precision computing and aim to improve this in future work.
> Comments Or Suggestions.
A: (1)Thank you for your valuable suggestions! We will follow your advice and add the complete inference settings in Section 4.3.
(2)The deployment time of SliM-LLM consists of two main parts: SBA bit-width search and SQC quantization parameter determination. As detailed in Section 3.2.2, the SBA dual-pointer search is highly efficient, and SQC computation time is comparable to standard calibration-based quantizers. SliM-LLM integrates seamlessly with existing PTQ strategies and, being training-free in a plug-and-play manner, completes 7B LLM quantization in about 25 minutes.
(3)For the ablation study on group size, we have discussed the differences in detail in Appendix F and provided experimental results in Table 7. We will further highlight this content in the main text to improve the readability of the paper.
> Questions For Authors.
A: (1)Thank you for your insightful observations. You are correct about the challenges with models like LLaMA-3. Despite this, SliM-LLM maintains leading quantization performance and remains highly practical.
As noted in prior works [1–4], quantization methods degrade more severely in knowledge-dense models like LLaMA-3, especially at ultra-low bit widths. Our experiments confirm this: in Table 1, LLaMA-3 8B with AWQ and GPTQ yields PPLs of 8.22 and 8.19 under 3-bit quantization, rising to 210 and 1.7e6 at 2-bit. This suggests that as models grow in knowledge density, conventional methods suffer greater quantization losses. In contrast, SliM-LLM achieves PPLs of 7.16 (3-bit) and 39.66 (2-bit), demonstrating its effectiveness.
Additionally, we have included 4-bit quantization experiments, which are more practical, to further highlight SliM-LLM’s advantages on LLaMA-3.
|Method|LLaMA-7B|LLaMA-13B|LLaMA2-7B|LLaMA2-13B|LLaMA3-8B|
|-|-|-|-|-|-|
|FP16|5.68|5.09|5.47|4.88|5.75|
|AWQ|5.81|5.30|5.62|4.97|6.63|
|GPTQ|5.85|5.20|5.61|4.98|6.50|
|SliM-LLM|5.83|5.16|5.59|4.95|6.42|
|Method|LLaMA-7B|LLaMA2-7B|
|-|-|-|
|Omniquant|5.77|5.58|
|SliM-LLM+|5.75|5.57|
(2)SliM-LLM+ incorporates our structured mixed-precision strategy into OmniQuant’s gradient quantizer. However, as OmniQuant and its comparator, AffineQuant, currently lack support for models like Gemma and Mixtral, we did not report results on these. We have contacted the OmniQuant authors to request updates and are actively working to extend SliM-LLM+ to more models.
[1] Rotated Runtime Smooth: Training-Free Activation Smoother for accurate INT4 inference. arXiv:2409.20361.
[2] Efficientqat: Efficient quantization-aware training for large language models[J]. arXiv:2407.11062.
[3] Compressing large language models using low rank and low precision decomposition[J]. NeurIPS, 2024.
[4] An empirical study of llama3 quantization: From llms to mllms[J]. Visual Intelligence, 2024. | Summary: This paper introduces a group-wise mixed-precision quantization method for LLMs, addressing challenges in accuracy and efficiency. The key contributions are two strategies: SBA, which optimally allocates bit-widths by minimizing entropy divergence through Hessian and weight salience analysis, and SQC, which enhances salient weight representation by adjusting quantizer sensitivity using a calibration parameter. To handle group outliers, the method balances scale and zero-point adjustments with a focus on scale sharing. Both strategies are compatible with various quantizers. Experiments show that Slim-LLM outperforms existing methods on LLAMA and OPT models.
Claims And Evidence: The submission's claimed phenomena and results are supported by detailed evidence.
Methods And Evaluation Criteria: The authors propose an innovative group-wise structured mixed-precision quantization strategy for LLMs, balancing accuracy and efficiency. It offers new insights into extreme compression under 2-bit and 3-bit settings and can be easily integrated into existing quantization tools. The observation and proof of the structured distribution of significant weights introduce a new paradigm for future LLM compression strategies.
Theoretical Claims: reviewed the correctness of the theoretical claims in Section 3.2.1. Figure 3 provides detailed evidence visualizing the weight clustering characteristics, and Section 3.2.1 theoretically establishes the relationship between the metric in Definition 3.1 and weight clustering. The discrete weight characteristics discussed in Section 3.2.2 are also supported by visualizations and additional explanations in the appendix. These proofs validate the proposed structured mixed-precision quantization framework.
Experimental Designs Or Analyses: The authors provide detailed experiments demonstrating the performance advantages of SliM-LLM, particularly achieving better results than existing methods on the ppl evaluation metric and commonsense benchmarks. The appendix includes additional results on challenging tasks like math after quantization. Figure 5 presents thorough ablation studies showing the contribution of each component in the quantization method. The paper also provides real hardware deployment results for memory usage and inference speed, making the experiments comprehensive.
Supplementary Material: The authors provide detailed supplementary materials in appendix.
Relation To Broader Scientific Literature: N/A
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: Strengths:
1. This work contributes a lot to the area of low bit quantization and compression. Make it efficient and accurate for different kinds of post training LLMs, especially under 2-bit and 3-bit. The structured mixed-precision proposed in SliM-LLM is a straightforward and effective method for the committee.
2. Evaluation of the method’s efficiency is rigorous and supported by an extensive set of experiments. The results are well-documented and demonstrate the practical applicability and effectiveness of the proposed approach. The performance comparisons with existing methods highlight the strengths of the paper’s contributions, offering promising insights into its potential impact on the field. The inclusion of various evaluation metrics further strengthens the reliability and generalizability of the findings.
Weaknesses
1. The authors are advised to consider testing on more challenging LLM benchmarks, such as GSM8K in the mathematics domain. Compared to MathQA, GSM8K may be more sensitive to the loss caused by quantization.
2. In group-wise mixed-precision inference, the allocation of quantization scales across different channels and the process of dequantization could provide deeper insights into the inference details of this structure. The authors are encouraged to provide further explanations on these aspects.
Other Comments Or Suggestions: There are minor typos, and the abbreviations WM and RM in Figure 5 lack annotations.
Questions For Authors: Although SLiM-LLM is a leading PTQ method in the 2-bit and 3-bit settings, which is a popular topic in the research field, it appears that the commonly used 4-bit quantization for industrial applications has not been explored in the paper. Could the authors provide a comparison of 4-bit PPL with RTN, AWQ, and GPTQ?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Dear Reviewer Ut3n,
We sincerely appreciate your insightful feedback and suggestions. Below, we will respond to your questions and recommendations individually.
> Q1: The authors are advised to consider testing on more challenging LLM benchmarks, such as GSM8K in the mathematics domain. Compared to MathQA, GSM8K may be more sensitive to the loss caused by quantization.
A: Thank you for your suggestion. We have conducted additional tests to evaluate the performance of our method on more challenging datasets, such as GSM8K. The results are shown in Table below.
|Model/Evaluation|Method|GSM8K|
|-|-|-|
|**LLaMA-7B**|GPTQ 3-bit|11.5|
||AWQ 3-bit|11.5|
||SliM-LLM 3-bit|11.5|
|**LLaMA-7B**|GPTQ 2-bit|0.0|
||AWQ 2-bit|0.0|
||SliM-LLM 2-bit|9.2|
|**LLaMA2-7B**|GPTQ 3-bit|13.0|
||AWQ 3-bit|13.4|
||SliM-LLM 3-bit|13.6|
|**LLaMA2-7B**|GPTQ 2-bit|0.0|
||AWQ 2-bit|0.0|
||SliM-LLM 2-bit|10.3|
The findings demonstrate that, even on GSM8K, our method exhibits less accuracy loss compared to other approaches, highlighting its robustness across different test sets.
> Q2: In group-wise mixed-precision inference, the allocation of quantization scales across different channels and the process of dequantization could provide deeper insights into the inference details of this structure. The authors are encouraged to provide further explanations on these aspects.
A: We have explained some details on how to allocate, store, and perform inference with quantization scales in Appendix B.2. This means that, while storing the quantized weights at extremely low bit widths, we also store the corresponding quantization scales for each row, and are able to perform dequantization operations on both scales and quantized integers on the CUDA Kernel, restoring them to the floating-point values required for inference. We will clarify and explicitly refer to this section in the main text.
> Q3: There are minor typos, and the abbreviations WM and RM in Table 5 lack annotations.
A: Thank you for your careful and thorough review! We will further check for any writing errors in the paper to ensure better readability. Regarding the issue you raised about the lack of explanations for WM and RM in Table 5, we would like to clarify that WM stands for Weight Memory and RM stands for Running Memory. We will also add the definitions of WM and RM in the relevant section to ensure they are accurately explained. Thank you for your helpful reminder.
> Q4: Although SLiM-LLM is a leading PTQ method in the 2-bit and 3-bit settings, which is a popular topic in the research field, it appears that the commonly used 4-bit quantization for industrial applications has not been explored in the paper. Could the authors provide a comparison of 4-bit PPL with RTN, AWQ, and GPTQ?
A: We sincerely appreciate your suggestion regarding comparative experiments with 4-bit quantization. We would like to clarify that although SliM-LLM is primarily optimized for 2-bit and 3-bit quantization, our method is also compatible with 4-bit mixed-precision quantization. In response to your suggestion, we have included additional experiments in the revised versions of Table 1 and Table 2. Furthermore, we have tested our method on several 4-bit models and are pleased to share the results with you below:
|Method|LLaMA-7B|LLaMA-13B|LLaMA2-7B|LLaMA2-13B|LLaMA3-8B|
|-|-|-|-|-|-|
|FP16|5.68|5.09|5.47|4.88|5.75|
|AWQ|5.81|5.30|5.62|4.97|6.63|
|GPTQ|5.85|5.20|5.61|4.98|6.50|
|SliM-LLM|5.83|5.16|5.59|4.95|6.42|
|Method|LLaMA-7B|LLaMA2-7B|
|-|-|-|
|Omniquant|5.77|5.58|
|SliM-LLM+|5.75|5.57|
\*The results of RTN are too worse than GPTQ and AWQ to be listed here.
---
Rebuttal Comment 1.1:
Comment: Thank you for the further clarifications. The authors' additional explanations and insights have further strengthened the paper's contributions. The proposed Slim-LLM is well-validated and has clear practical relevance for LLM quantization and compression. I maintain my original accept rating.
---
Reply to Comment 1.1.1:
Comment: Dear Reviewer Ut3n,
Thank you for your thoughtful and constructive feedback. We sincerely appreciate the time and effort you dedicated to reviewing our work. Your insights have been highly valuable in helping us identify areas for clarification and improvement. We have carefully considered your suggestions and incorporated them into our revised manuscript to enhance its clarity, rigor, and overall quality.
Thank you again for your valuable input—it has been instrumental in strengthening our work. | Summary: This paper proposes SliM-LLM, a post-training quantization (PTQ) framework for large language models (LLMs). Its core idea is to allocate bit-widths to weight groups adaptively and locally preserve important (salient) weights. The approach combines two techniques:
1. Salience-Determined Bit Allocation (SBA): Groups of weights are each assigned a suitable bit-width based on the group’s global importance (salience).
2. Salience-Weighted Quantizer Calibration (SQC): Within each group, a small subset of highly salient weights is given extra quantizer “attention” to reduce local discretization errors.
By focusing resources on channels or weight elements deemed most critical, SliM-LLM aims to achieve lower perplexity in ultra-low bit regimes (1–3 bits) without incurring major hardware overhead. Experimental results emphasize LLaMA (1, 2, 3) and OPT model families, showing that SliM-LLM outperforms existing PTQ baselines in perplexity reduction, and can be integrated into popular PTQ toolkits (e.g., GPTQ, OmniQuant). The paper also includes limited results on less-traditional architectures such as Gemma2 or Mixtral, in an effort to demonstrate some level of generalizability.
Claims And Evidence: The paper makes strong claims that its proposed SliM-LLM method yields significant performance gains at very low bit-widths (1–3 bits) and generalizes effectively across large language models. While the results on LLaMA (and to a lesser extent OPT) support improved perplexity and moderate memory overhead, **some claims remain only partly substantiated**:
1. **Claim: “SliM-LLM balances compression rate and inference speed with limited overhead.”**
- **Evidence**: The authors do show memory usage and token-throughput comparisons (e.g., Table 5), illustrating that at 2 bits, perplexity drops dramatically yet throughput also declines. The data partly confirms a trade-off.
- **Gaps**: There is **no systematic exploration** of how severe the latency penalty can become in different scenarios (e.g., multi-GPU, different batch sizes). This means the paper has not comprehensively demonstrated that SliM-LLM offers a robust speed–accuracy trade-off across diverse deployment conditions.
2. **Claim: “SliM-LLM generalizes well beyond LLaMA/OPT.”**
- **Evidence**: A few additional experiments (e.g., Gemma2-9B, Mixtral-8×7B) in the appendix are cited to show performance gains relative to GPTQ.
- **Gaps**: Most of the core experiments still focus heavily on LLaMA/OPT families, leaving limited discussion or validation on how the method behaves for architectures with different normalization schemes, or for radically different designs (e.g., multimodal LLMs). The authors do not deeply explore how outlier channels are altered by extra normalization layers in Gemma2, nor whether the salience-based approach needs to be adapted.
3. **Claim: “SliM-LLM’s salience-based bit allocation and quantizer calibration handle local outliers effectively.”**
- **Evidence**: The paper describes Salience-Weighted Quantizer Calibration (SQC) and provides ablation results indicating that it helps preserve a small fraction of crucial, high-magnitude weights.
- **Gaps**: The experiments assume that outliers make up only around 1–5% of weights. For more extreme cases—where outlier or salient weights are more widespread—the paper does not offer specific evidence. Thus, it is unclear how robust the approach is if the model’s salience distribution does not cluster or if many channels simultaneously exhibit high salience.
4. **Claim: “SliM-LLM introduces only minor hidden overhead.”**
- **Evidence**: The authors note a small increase in memory usage (e.g., ~0.1GB more than GPTQ at 2 bits on 7B-scale models) and mention that storing group-level bit-width maps is not a huge burden.
- **Gaps**: There is no detailed breakdown of overhead for very large models (70B+ parameters) or a thorough demonstration that the additional groupwise metadata stays modest across scales. The paper would be stronger if it rigorously measured overhead as model size and group granularity vary.
Overall, while the **performance claims** at low-bit quantization (especially on LLaMA and OPT) are convincingly supported by perplexity gains and ablations, the **generalizability and overhead** claims are not explored in as much depth. Addressing the trade-offs with speed, broader model architectures, and more diverse salience patterns would make the evidence more conclusive.
Methods And Evaluation Criteria: The paper’s methodology—mixed-precision post-training quantization evaluated via perplexity on language modeling benchmarks—fits well with the core objective of aggressively compressing large transformer-based LLMs. Perplexity and zero-shot accuracy are reasonable metrics for confirming whether the quantized model still preserves core language understanding.
However, **some limitations remain**:
1. **Narrow Focus on LLaMA/OPT Families**
Most tests rely on LLaMA and OPT, which both use Pre-LN Transformer designs widely known for pronounced outlier channels. This raises the question of whether SliM-LLM’s promising results might partly hinge on the fact that these specific architectures emphasize salience clustering. If newer Transformers (or non-Transformer models) suppress or redistribute outliers—an effect sometimes seen with extra normalization layers —the gains from SliM-LLM might be less pronounced or require modifications. More diverse experiments on architectures without those strong outlier characteristics would clarify whether these gains arise purely from leveraging Pre-LN behaviors or can generalize more broadly.
*Sun, Mingjie, et al. "Massive activations in large language models." COLM2024.
*Kedia, Akhil, et al. "Transformers get stable: an end-to-end signal propagation theory for language models." ICML2024.
*Oh, Jaehoon, Seungjun Shin, and Dokwan Oh. "House of cards: Massive weights in llms." arXiv 2024.
*Sun, Wenfang, et al. "The Curse of Depth in Large Language Models." arXiv 2025.
2. **Sparse Analysis of Inference Trade-offs**
While the paper includes perplexity vs. token/s results, there is no deeper experiment varying batch sizes, GPU setups, or real-time conditions. It remains unclear whether SliM-LLM consistently meets real-world speed demands, especially under heavy concurrency or stricter latency targets. The discussion on throughput is largely single-GPU, and additional multi-GPU or distributed benchmarks could confirm if memory/performance scales similarly.
3. **Evaluation Datasets**
The authors rely on standard data like Wikitext2, C4, and limited zero-shot tasks. Although these are reasonable starting points, evaluating reasoning or multimodal tasks could uncover further performance nuances and better reflect practical deployments. While perplexity is a solid metric, real-world usage often involves more specialized tasks. The paper does not yet assess how SliM-LLM behaves under such domain-specific conditions.
Altogether, the presentation (PTQ for LLMs assessed by perplexity and memory/speed) is well-aligned with the basic goal of compressing large language models. Yet the limited architectural variety tested, the lack of detailed real-time inference experiments, and the narrow range of evaluation tasks leave open questions as to how broadly and reliably SliM-LLM can be applied in production-scale environments.
Theoretical Claims: The authors briefly justify salience clustering by referencing Hessian approximations and outlier activation channels. These are not extremely formal proofs but rather high-level derivations consistent with prior work on Hessian-based importance. No obvious flaws stand out, though they remain somewhat heuristic in nature.
Experimental Designs Or Analyses: The experimental protocol mostly follows conventional PTQ setups (calibrate on a small set of input tokens, measure perplexity on standard test sets, compare with established baselines). The additional tables for Gemma2 and Mixtral do help, but only in a small-sample manner. Some analyses of memory overhead and speed trade-offs are provided (Table 5), but a deeper exploration of “how big is the hidden overhead for group-bit metadata?” or “which scenarios lose the most throughput from mixed-precision?” could be more thorough.
Supplementary Material: The appendices include:
- Detailed ablations on group size, different searching heuristics for SBA, etc.
- Additional results on Gemma2/Mixtral.
- Implementation details on how SQC calibrates local outliers.
These sections were reviewed and generally support or clarify the main text. The extra tables on speed vs. perplexity are valuable, though many are still quite brief.
Relation To Broader Scientific Literature: - The paper aligns with ongoing efforts to aggressively compress LLMs under 3-bit (e.g., QuIP, OmniQuant, GPTQ, etc.).
- Extends the salience-based approach of GPTQ but adds a structured mixed-precision angle, reminiscent of older “HAWQ” or “APTQ” but at a finer group level.
- Prior works that address outlier channels or element-wise mixed precision are referenced (e.g., AWQ).
Essential References Not Discussed: None
Other Strengths And Weaknesses: **Strengths**
- Empirical gains at low bit quantization, often outperforming prior PTQ baselines.
- Fairly robust experiments on standard language modeling tasks.
- Engineering details (Appendix B) on how to pack bits group-wise, which is helpful for reproducibility.
**Weaknesses**
- Discussion of trade-offs in real-world inference scenarios remains somewhat limited. While the paper acknowledges that speed can drop at 2 bits, it does not systematically measure it across different GPU kernels or larger-batch conditions.
- The usage of only a few beyond-LLaMA architectures (Gemma2, Mixtral) is a first step, but the explanation for why it should work in every scenario is short.
- Overall paper formatting (some references, layout) does not strictly follow typical ICML style, giving an unfinished impression.
- The theoretical discussion is primarily heuristic—though typical in quantization research, it might have benefited from deeper analysis or direct ablation on truly scattered salience distributions.
Other Comments Or Suggestions: None
Questions For Authors: - Could the authors elaborate how SQC would respond if *every* channel had moderate outliers rather than a few large outlier channels? Would the search for τ-parameters become unstable or scale poorly?
- Would additional codebook-based or vector-quantization steps (e.g., SpQR) further improve results?
- The paper includes a small table (Table 5) comparing memory usage and token throughput. Could the authors detail how much extra overhead is stored in the group-wise bit metadata at 2 bits vs. 3 bits, especially for large models (e.g., 70B+)?
- Do you foresee more advanced GPU kernels that specifically accelerate group-wise mixed-precision to mitigate the 2-bit throughput drop?
- If future LLM variants (e.g., multi-modal or heavily fine-tuned) produce qualitatively different activation distributions, how stable is the salience-based approach?
- Are additional calibration samples or adaptive re-quantization steps needed to maintain performance?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Dear Reviewer BegC,
Thank you for your valuable feedback. We have summarized your questions and concerns. Due to the character limit for reply, if there are any question that are not detailed, we will further reply in next stage. Thanks you so much.
> Q1:(1) There is...diverse deployment conditions. (2)Discussion of trade-offs...conditions.
As shown in Table 5, we analyzed deployment speed under different memory compression levels using a batch size of 1 (align with other works), focusing on extreme compression for single-GPU. We added inference experiments for the compressed LLaMA-7B model on different GPUs, testing various batch sizes.
|GPU|Method|Bit|Batch|Token/s|
|-------------|------------|-------|---------|-----------|
|RTX4090|SliM-LLM|2|4|55.1|
||||8|34.4|
|A100|SliM-LLM|2|4|59.2|
||||8|40.2|
Slight speed decreases with larger batch, consistent across frameworks like AutoGPTQ and AutoAWQ.
> Q2: (1)Most of the core...to be adapted. (2)The usage of...is short. (3) If future LLM...approach?
The LLaMA and OPT series are among the most widely downloaded and applied LLM architectures in the community. They are also commonly used as base models in other works. As you noted, we include more experiments in Table 11 to evaluate models with extra normalization layers. We claim that salience is a relative concept, as LLM training inherently produces such salience[1][2], even in multimodal or fine-tuned models. While architectures like Gemma2 use extra normalization layers, relative salience of features still emerges.
SliM-LLM focuses on compressing LLMs. Follow your suggestion, we expanded multimodal task on the LLaVA-Next 8B model(N:collapse accuracy).
||#W|#G|AI2D|ChartQA|DocVQA|MMBench|
|--------------------------|------|-------|--------|------------|-----------|------------|
|GPTQ|3|128|66.2|65.1|75.6|67.4|
||2|128|N|N|N|N|
|AWQ|3|128|67.7|65.4|74.4|68.0|
||2|128|N|N|N|N|
|SliM-LLM|3|128|68.2|67.5|74.8|68.9|
||2|128|57.2|49.3|60.6|60.9|
[1]From Attention to Activation: Unraveling the Enigmas of Large Language Models.
> Q3: (1)The experiments a...exhibit high salience. (2) The theoretical discussion...distributions.
The proportion of local outlier weights within groups is not an assumption but an observation supported by prior studies. Section 3.2.2 and previous work[1] consistently show that salient weights within groups remain a small proportion. Theorem 1 and detailed proofs in Appendix G explain this phenomenon.
[1] SpQR: A sparse-quantized representation for near-lossless LLM weight compression.
> Q4: (1)There is no detailed breakdown ...vary. (2)The paper...large models (e.g., 70B+)?
In Table 7, we provided the quantization performance of four LLMs under different group sizes. SliM-LLM introduces negligible storage overhead, which decreases further as model size grows. For instance, with LLaMA2-70B (group sizes = 64, 128, 256), a single transformer layer (size 8192 × 8192) requires a group matrix of size 8192 × 64/128/256. Using three precision levels, only a 2-bit flag (e.g., 01 = 1-bit, 10 = 2-bit, 11 = 3-bit) is needed per group. The additional storage overhead is $\frac{2}{8192 \times 64/128/256}$—virtually negligible at scale. Other quantization parameters are identical to frameworks like GPTQ.
Based on your suggestion, we will add 70B models results.
|LLaMA-2-70B #W|Method|WM|RM|PPL|Token/s|
|------------------|------------|---------|----------|-----------------|-----------|
|3-bit|GPTQ|28.0G|34.9G|3.85|6.5|
||SliM-LLM|28.0G|35.2G|3.67|6.2|
|2-bit|GPTQ|16.4G|23.3G|8.78|9.7|
||SliM-LLM|16.5G|23.5G|6.28|8.4|
> Q5: The authors rely on standard...domain-specific conditions.
Our paper evaluates quantized model performance on 13 benchmarks, including Wikitext2, C4, and 8 zero-shot tasks, aligning with other LLM quantization works. Appendix Table 13 includes benchmarks from Humanities, Social Sciences, and STEM, with reasoning tasks like MathQA highlighting SliM-LLM's strengths in math reasoning. We will add results for LLaVA-Next-8B on 4 multimodal tasks in Q2.
>Questions For Authors:
(1)As shown in Definition 3.1 and Theorem 1, salience is influenced by weight magnitudes and the Hessian. If all weights exhibit similar salience, the distinction between salient and non-salient weights (Equation 5) becomes negligible. In such cases, τ converges to 1, simplifying quantization and allowing parameters to be derived from basic statistics.
(2)Codebook-based methods can improve accuracy but significantly reduce inference speed—e.g., 2-bit code-book can be 3× slower. SliM-LLM’s structured mixed-precision quantization achieves competitive accuracy while maintaining practical inference speeds.
(3)Frameworks like recent HQQ show promising advancements in GPU kernels for 2-bit quantization. These developments could further improve SliM-LLM's inference speed.
(4)For calibration, SliM-LLM used only 128 random samples from WikiText2, avoiding additional data or adaptive re-quantization.
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Rebuttal Comment 1.1:
Comment: I appreciate the authors for the detailed responses and additional experimental results. Although some of the answers do not sufficiently answer the questions, I believe the additional experimental results, as well as the in-depth discussion, would be valuable for future research in this field. Therefore, I raise my original rating.
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Reply to Comment 1.1.1:
Comment: Dear Reviewer BegC,
Thank you sincerely for your detailed review and for the generous score adjustment. We greatly appreciate your recognition of our work and your thoughtful suggestions, which have been instrumental in further refining and strengthening our manuscript.
In response to your insightful comments, we have conducted additional experiments to substantiate our claims and further assess the robustness of our proposed method. These new results—covering various batch size and GPU settings, multimodal tasks, and the performance of larger-scale models—provide stronger empirical support and a deeper understanding of our method's effectiveness.
We will incorporate these supplementary results into the final version of the paper to enhance its completeness, rigor, and credibility. Once again, thank you for your kind support and invaluable feedback. | null | null | null | null | null | null |
Inducing, Detecting and Characterising Neural Modules: A Pipeline for Functional Interpretability in Reinforcement Learning | Accept (poster) | Summary: This paper addresses the challenge of interpretability in reinforcement learning (RL) models by proposing a method based on functional modules, aiming to overcome the scalability limitations of traditional neuron-level interpretability approaches. The authors introduce spatially aware regularization and neuron relocation techniques to promote weight sparsity and locality, thereby inducing the formation of functional modules within RL policy networks. Additionally, they extend the Louvain algorithm by incorporating a novel 'correlation alignment' metric to detect these modules effectively. Experiments conducted in 2D and 3D Minigrid environments demonstrate the emergence of distinct modules corresponding to different directional navigation tasks, with targeted interventions on network parameters validating the functional roles of these modules.
Claims And Evidence: The paper's primary claims are well-supported by empirical evidence. Notably, the authors demonstrate that increasing the strength of spatial regularization leads to more pronounced modular structures within the network. However, the functional validation of these modules relies on direct interventions in network weights, and the applicability of this approach in more complex or real-world scenarios remains to be fully established.
Methods And Evaluation Criteria: The proposed methods—including distance-based weight regularization, neuron relocation, the extended Louvain algorithm, and the correlation alignment metric—are clearly articulated and appropriate for the problem context. While the Minigrid environment serves as a suitable benchmark, its relative simplicity suggests that further validation in more complex tasks is necessary to assess the generalizability of the methods.
Theoretical Claims: The paper does not present formal theoretical proofs; thus, there are no theoretical claims to evaluate in this context.
Experimental Designs Or Analyses: The experimental design is robust, featuring ablation studies that elucidate the contributions of individual components, such as regularization and neuron relocation. However, the functional analysis methods—specifically, negative saturation and negation—are innovative but lack comparisons with existing interpretability techniques, potentially limiting the assessment of their effectiveness.
Supplementary Material: The supplementary material, located in the appendix following the references, includes additional ablation studies, parameter sensitivity analyses, and detailed training hyperparameters. This comprehensive information enhances the reproducibility and clarity of the experimental results.
Relation To Broader Scientific Literature: The paper situates its contributions within the broader context of neural network interpretability research, particularly concerning modularity and hierarchical interpretability methods. It effectively references recent advancements in module detection and spatial regularization, highlighting its alignment with current research trends.
Essential References Not Discussed: The paper's citations are comprehensive, covering essential works related to RL interpretability and neural modularity.
Other Strengths And Weaknesses: Strengths:
1. Innovatively proposes a functionally interpretable framework for RL models based on neural modularity.
2. Provides detailed technical implementations and rigorous experimental designs, enhancing reproducibility.
3. Introduces novel metrics, such as correlation alignment, contributing valuable tools to the interpretability research community.
Weaknesses:
1. The simplicity of the experimental environments may not fully capture the challenges present in more complex real-world tasks.
2. The reliance on direct weight interventions for functional validation may limit applicability across diverse neural architectures.
Other Comments Or Suggestions: 1. While the figures are clear, enhancing the legends and descriptions could improve reader comprehension, particularly regarding the directional aspects of network structures.
2. Conducting user studies to assess human understanding of the proposed modular interpretability approach could provide valuable insights into its practical utility.
Questions For Authors: 1. Applicability in Complex Scenarios: Can the negative saturation and parameter negation methods for module function validation be effectively applied to more complex, non-linear tasks? If so, what modifications would be necessary?
2. Alternative Validation Methods: Have you explored activation-based approaches as alternatives to weight modification for module function validation? If not, could such methods offer advantages in certain contexts?
3. Performance-Modularity Trade-off: Given the potential performance trade-offs associated with spatial regularization (λcc), have you investigated alternative strategies to mitigate performance loss while maintaining modularity?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your detailed consideration of our work. We appreciate the acknowledgment of our robust experimentation and the insightful questions raised.
**Figures and Captions.** We appreciate the advice on improving clarity. We have updated the network plots to include legends and have extended the captions to include sufficient detail for the core results to be understood from the figures and captions in isolation.
**User Studies.** We agree that user studies can be valuable for assessing the utility of interpretability approaches. Although we agree with reviewer qymG that human evaluation is not necessary to support the claims in our work, future work leveraging our approach in specific applications would certainly be enhanced by context-specific user studies.
**Function Validation: Complex Scenarios and Alternative Methods.** Our function validation approaches are not limited by the size or internal complexity of the modules. Our results instead show that the efficacy of ablation techniques in isolating module functionality are impacted by the level of connectivity between modules, which we regulate with the λcc parameter. We agree that activation-based intervention approaches may offer a valuable alternative, which we briefly discussion in the discussion section. Beyond this, we are excited about extending our approach to detect hierarchical modularity within complex tasks in future work.
**Validation in Complex Scenarios.** We appreciate that Minigrid presents a relatively simple task set and that validation in more complex and real-world scenarios is a valuable direction for future work. To advance in this direction, we have extended our work to a non grid-world task, Pong, as proposed by reviewer qymG, and will incorporate the results into the camera ready paper.
**Performance-Modularity Trade-Off.** We investigated a number of approaches to mitigating this, leading to the implementation of the λcc scheduling and the fine-tuning of the pruned modular networks (discussed in more detail in Appendix C), and the use of the log-based sparsity loss (discussed in Appendix A). We believe there may be further mitigation opportunities that merit testing in future work, for example by penalising inter-module connections and not intra-module connections in the later stages of training. | Summary: The authors identify that most (post hoc) interpretability methods focus on explaining models' units (e.g. neurons), which does not scale. They propose to have interpretability at the level of *functional modularity*. They just try to identify neural modules, which are groups of neurons that are functionally related.
They use a "connection cost" lost to induce greater sparsity (than classic L1-loss) in the neural network, and perform neuron relocation.
They show that their method is able to induce interpretable modules in a navigation task, and that these modules are more interpretable than the original network.
Claims And Evidence: The main claims are clearly outlined in introduction.
The biggest claim is that local and sparse Neural Network are more interpretable than dense ones, which is commonly agreed upon in the litterature. No evidence (requiring human evaluation) is provided to support this claim, but I don't think that it is necessary. They also further explain: " High isolation implies minimal inter-module connectivity, resulting in stricter decomposability and enabling more independent module analysis.", which is a good argument for the modules' interpretability.
In introduction, some minor claims are not supported by citations:
"When considering its scaling to complex domains, RL interpretability must be considered at a level of abstraction which
balances tractability with fidelity to the underlying model." (l 43-45). Such claims could be removed.
In the introduction, a lot of litterature argue against the use of black-box neural networks, and favor the use of instrinsically interpretable models (e.g. decision trees, supported by Bastani). I would suggest to also spend the intro motivating the necessity of increasing the interpretability of neural networks (which is the main focus of the paper).
The results detailled in Functional Interpretability should somewhat be already highlighted in the captions of the figures. You can write Forward/Backward module in 9a.
Methods And Evaluation Criteria: The proposed method:
* brings local and sparse networks to RL.
* proposes to use Logarithmic Sparsity Loss to increase even further sparsity in the network.
* extends the Louvain algorithm to detect modules in the network.
The authors evaluate their method on a navigation task, but only report interpretability, no performance metric is reported. Before checking for the level of interpretability of agents, we first need to check to which extent they learned to solve the task. I have not been able to find completion rate, or any other any performance metric in the paper.
In *Limitations and Future Work*, the authors mention that "*λcc controls this balance*", but I do not see any results on how the performance of the agents is affected by the value of λcc.
Theoretical Claims: Not Applicable.
Experimental Designs Or Analyses: There are 2 major points of improvement here.
The first one is about clarity. The experimental section is quite hard to follow. A very detailled analysis has been done, but it is hard to follow. I would suggest to have a more structured approach to the experimental section.
Specifically, I would suggest to have list of scientific questions at the beginning of the experimental evaluation section (often denoted Q1, Q2, ... etc), that are each answered in different paragraphs. For example
Q1/ Can more interpretable modules reach similar performances as non constrained baselines?
Q2/ Does our algorithm induce more interpretable modules than the original network? (maybe name your agents that include every interpretability inducing techniques)
Q3/ How does the regularisation parameter affect the performance and interpretability of the modules?
Q4/ other ablation studies.
The second is to also evaluate their method on a non maze environment.
The paper does not limit the methods' interpretability to mazes, maybe the evaluation should go beyond navigation tasks. (Maybe MinAtari (JAX implemented) or OCAtari ?).
I think that training one network on the OCAtari version of Pong might to similarly interpretable networks.
The input space is 6 dimensional (x and y coordinates for each relevant objects).
You could identify if e.g. the constant x positions of the Player and the enemy only have nul weights (as they are constant and thus do not lead to any information gain). You might be even able to get an insight to the Pong misalignment problem with your technique (by analyzing that the module focusing on the enemy's vertical position is having high weights).
Now, I know how work demanding it is to include yet another evaluation to the paper, but I think that it would be a great addition to the paper.
I was hesitating between weak reject and weak accept, but if all my concerns are adressed (or for the additional experiments, that could take time, if the authors start them and will include it in the camera ready version), I am willing to increase my score to strong accept if my concerns (also the ones bellow) are addressed in the rebuttal, as I think that the paper is very strong and has a lot of potential.
A more minor point: What do the communities stand for in e.g. Figures 5 and 6? What is the meaning of the colors? I would suggest to add a legend to the figures. Can you interpret the communities? (e.g. the red community is responsible for the vertical agent's movement)? This should go into the captions of the figures.
For the experimental results, I would suggest structuring the figures like this:
The first sentence should highlight the main message of the Figure/Table (e.g. "*Fine-tuned Internal Louvain* allow for more isolated (thus interpretable) modules than the other approaches.").
The next sentences then explain what is depicted in the Table/Figure. E.g. "Communities are detected by the Louvain algorithm, and the colors represent the different communities. The *Internal* variant leads to denser communities, *Fine-tuned* leads to less communities, which is a sign of more interpretable modules. The top row depicts ... while the bottom row depicts ... ."
Finally, details and references to e.g. appendix can be provided if necessary. E.g. Results on more environmnets are provided in appendix X.
This would greatly improve the readability of the paper. I personally tend to read the abstract and the figures first, and then the rest of the paper. If the figures are well structured, I can get a good understanding of the paper without reading the whole paper (and thus decide if I potentially dive into it). I know that this is also the case for many other readers.
Supplementary Material: I mostly checked appendix A, which gives a nice intuition on the log-based sparsity loss, and appendix D for the runtime results, but globally looked up everything.
Relation To Broader Scientific Literature: This is the 3rd major opportunity for improvement.
As said, I would rewrite the experimental section to have a more structured approach to the evaluation.
Thus, you could add a related work section that discuss interpretability and sparsity in RL (could be merged with the dicussion). I tend to place background before the method (as the background is necessary to understand the method), and the related work (i.e. other approaches to the same problems: interpretability and sparsity) after the evaluation of your method, to avoid having the readers biased towards thinking of other potential approaches while presenting yours.
You are missing many of the latest published Related Work on Interpretable RL. I hereafter provide a list of papers that should be included in your related work section:
* Delfosse et al. "Interpretable concept bottlenecks to align reinforcement learning agents." NeurIPS (2024).
* Luo et al. "End-to-End Neuro-Symbolic Visual Reinforcement Learning with Language Explanations." ICML (2024).
* Kohler et al. "Interpretable and Editable Programmatic Tree Policies for Reinforcement Learning." RLC workshop (2024).
* Delfosse et al. "Interpretable and explainable logical policies via neurally guided symbolic abstraction." NeurIPS (2024).
* Marton, et al. "SYMPOL: Symbolic Tree-Based On-Policy Reinforcement Learning." ICLR (2025).
* Shindo, et al. "BlendRL: A Framework for Merging Symbolic and Neural Policy Learning." ICLR (2025).
Essential References Not Discussed: While they are less essential, there are many published work on interpretable RL that should be discussed in RW.
Other Strengths And Weaknesses: I mostly checked appendix A, which gives a nice intuition on the log-based sparsity loss, and appendix D for the runtime results, but globally looked up everything.
Other Comments Or Suggestions: The paper could benefit from a more detailed discussion on the benefit and the intuition behind the Neuron Position Optimization.
I would bring algorithm 2 before the start of the experimental section and e.g. adjust the vertical space around the equations to have section 4 start on page 4. (This is very final formatting, but it would make this great paper even more appreciable). But the paper might heavily change, so this might not be accurate.
Questions For Authors: * You apply Neuron Position Optimization every T steps. Why do you need to apply it every T steps? Why not only at the end?
* How does the empirical computational cost grow with the size of the problem? Is it feasible to apply it to larger scale problems?
* Are you the first to propose a logarithmic sparsity loss? (This is quite an simple amazing idea, but I am not sure if it is novel).
* Can you provide more details on why the log-based sparsity loss is preferable to the exponential-log one? I have read appendix A, but
* Can you add scores in Figure 2 for the different methods on each task? Maybe next to $\lambda_{cc}$ ?
* What part of your algorithm is transferable to CNNs? (Neuron relocation? Louvain Algorithm?)
* Are there some modules that are not easily interpretable? Would one need to apply a post-hoc interpretability method to understand them? This would not be a reason to reject, but would be great to understand the limits of your method.
Intro could be shortened, directly go to the point (particularly if you create a *Related Work* section).
l 39: "to improving" -> "to improve"
l 10: "which directly implicate on" -> "which directly impact"
Code Of Conduct: Affirmed.
Overall Recommendation: 5 | Rebuttal 1:
Rebuttal: Thank you for your detailed and thoughtful review. We are grateful for your recognition of the potential of our work and the constructive feedback which we have applied as follows. We have also updated the figures and draft PDF on the project page to reflect the changes: https://sites.google.com/view/mod-xrl/home
**Additional Experiments.** We agree that a non-maze application would strengthen our results and appreciate the Pong suggestion - thank you! We have adapted the Gymnax version to return a symbolic observation, and have implemented the distance-weighted sparsity training. Initial results show this learns a single sparse module that uses only a subset of the inputs and actions. The agent focuses on the opponent even at high sparsity, and we are excited to conduct ablations to see if this offers insights into the Pong misalignment problem. We have added these early results to the project page, and will include complete findings in the camera-ready paper.
**Structure and Clarity.** We appreciate these helpful suggestions. We agree the claim regarding levels of abstraction is unecessary and have instead expanded the argument for the utility of interpretability. We have added task scores to Figure 2 and legends to Figure 9 and have extended all captions such that the results shown are now broadly understandable in isolation from the text. We have added a set of research questions to guide the Experiments section, reduced the Background to contain only necessary information and extended the removed information into a Related Work section. Thank you for the related papers, particularly Delfosse et al. (2024) and Kohler et al. (2024), which provide valuable examples for the utility of RL interpretability. We have included these in the Introduction and the other papers in Related Works. We have retained half a page for the Pong results, but may have to move a portion of these or the Related Works to the Appendices to meet the 9 page limit.
**Performance Metric.** Since the reward is 1 on task completion and 0 otherwise, the return in Figure 8 is equivalent to both the success rate and average reward. We have clarified this in the text and caption.
**Neuron Position Optimisation Intuition.** We appreciate your interest and describe our intuition below. We have added this to the Methods and App. E.2. We consider the distance weighting as encouraging computation to distribute across few weights and neurons, as each additional weight used is 'more expensive' than using the single shortest weight. Since we schedule λcc, sparsity is introduced when the network already implements relevant computations. Position optimisation thus allows existing important weights to move and become 'less expensive', while less important ones are more heavily penalised by the CC loss. We expect this same intuition holds without scheduling, as initial weights will bias learning towards specific local optima in the parameter space. Regarding the **frequency of position optimisation**: applying it every T steps improves module isolation and ARI (as reported in App. E.2). These metrics are artefacts of the learnt network connectivity, so we would not obtain the same benefits from relocating neurons after training.
**Computational Cost.** The complexity of the connection cost calculation is linear with depth and quadratic with width. Relocation is linear with layers and cubic with width, but this can be mitigated by reducing the number of swaps considered or increasing T. We trained a set of networks with increasing widths (32 to 512) and depths (2 to 50). With increasing width, the time increase due to the CC loss remains a relatively constant percentage of train time (15-19%), whereas the relocation percentage increases from 1% to 7% , which supports the theoretical complexity. We present network partitioning complexity results in App. D2.
**Log-loss Novelty.** We are unaware of prior work using a logarithmic sparsity loss, but can't definitively state that it has not been applied in contexts we have not identified.
**Exponential Log-loss.** We initially ran a small set of experiments with the exponential formulation and did not observe any differences in results. Since we trained networks with different numbers of weights, in hyper-parameter tuning and due to varying input and output dimensions, the non-exponential formulation was more desirable, as it is additive with number of weights and made selecting appropriate λcc ranges straightforward.
**CNN Application.** For conciseness, we point you to our response to reviewer jddf.
**Module Interpretability.** We did not come across any non-interpretable modules, but agree this is an interesting point and that high level modules in complex networks may not be immediately interpretable using ablations. We are excited about the potential to address this by applying our modularity technique in a hierarchical manner, which may enable the extraction of interpretable submodules.
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Rebuttal Comment 1.1:
Comment: On the additional experiments, the Pong misalignment issue has been detected on the (OC)Atari version of the Pong ALE environment, I am not sure if it is also present in gymnax. Do you know if the p1.x and p2.x are also constant in the gymnax version? It seems that the sparse model do not attach importance to these.
Thank you for your clarifications, I think that the discussion on the Neuron Position Optimisation Intuition and on the cost should be included in the paper if possible (at least in appendix and be referred to).
Apart from this, I find your answer and the overall approach quite inspiring, as it constitute a good first step to the development of more interpretable neural components for RL agents.
I am raising my score. Many thanks for this inspiring work!
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Reply to Comment 1.1.1:
Comment: Thank you for your appreciation of our work!
We do observe the same phenomenon as in OCAtari where the network attaches importance to the opponents y position. We will investigate performance in the No Enemy and Lazy Enemy cases proposed by Delfosse et al. (2024) and discuss this in the final paper.
P1x and P2x are constant in Gymnax as in (OC)Atari, but interestingly we find that the sparse network attaches a weak importance to the opponent's x position. This may reduce with continued training.
We will also include the Neuron Position Optimisation intuition briefly in the Methods, referencing the full description in the Appendix. Many thanks again for your helpful suggestions to enhance and clarify our work. | Summary: This paper presents a pipeline for inducing, detecting, and characterizing neural modules within reinforcement learning (RL) policy networks to enhance interpretability. By penalizing non-local connectivity and encouraging sparsity and locality in network weights, the fully connected networks used in the study exhibit functional modules. To automatically detect these modules, they extend the classical Louvain community detection algorithm by incorporating a “correlation alignment” metric that accounts for the unique architectural constraints of neural networks. The method is validated in both 2D and 3D Minigrid environments, where distinct navigational modules emerge that correspond to specific movement axes. Furthermore, the paper demonstrates that targeted interventions—such as disabling or perturbing specific modules—can empirically confirm their functional roles. Overall, the work offers a framework for decomposing and understanding complex RL decision-making processes through functional modularity.
Claims And Evidence: The paper’s claims are generally well-supported. It convincingly shows that spatial regularization and neuron relocation lead to the emergence of functionally coherent modules and that its extended Louvain method reliably detects these modules. Interventions validate that these modules serve distinct functions, and the trade-off between improved interpretability (and sparsity) and a modest performance drop is clearly demonstrated. However, while the results in simple 2D and 3D Minigrid tasks are promising, the **scalability claim** is supported only in these limited settings on fully connected networks, suggesting that further evidence on more complex tasks is needed to fully substantiate scalability.
Methods And Evaluation Criteria: Methods and evaluation criteria is the main strength of this paper, from inducing, to evaluation, and finally to knock out studies, all seem fine to me.
Theoretical Claims: N/A
Experimental Designs Or Analyses: Not very toughly, I am not much familiar with Minigrid tasks or the Louvain algorithm.
Supplementary Material: No
Relation To Broader Scientific Literature: The paper tries to bridge RL and interpretability literatures which make it well suited for broader scientific literature.
Essential References Not Discussed: Non detected
Other Strengths And Weaknesses: The paper’s approach of imposing spatial correlations is conceptually compelling and aligns well with neuroscience theories explaining feature maps in the visual cortex (as cited). This integration of spatial regularization into reinforcement learning offers enhanced interpretability and a clear mechanism for module emergence. However, a notable drawback is that this spatial constraint appears to cap model performance, as evidenced by previous studies and the modest accuracy drop reported here. Consequently, while the model yields solutions that are more interpretable, it may preclude discovering the high-performing strategies that less constrained, more powerful networks can achieve. This trade-off highlights a broader tension in mechanistic interpretability research—balancing the need for clear, interpretable mechanisms against the pursuit of state-of-the-art performance on complex tasks.
Other Comments Or Suggestions: None
Questions For Authors: To what extent the pipeline depends on the MLP architecture of the models tested? Can one apply the same pipeline for CNN or transformers?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your detailed response and consideration of our work. We appreciate your recognition of the compelling nature of our proposed approach, and respond to the points raised as follows:
**Scalability.** We agree that application to more complex tasks will be valuable for further evidencing scalability. Our automated module detection techniques, in particular, provide a robust foundation for this future work. As proposed by reviewer qymG, we have now implemented the framework on a non grid-world environment (Pong) and will formalise and incorporate these results in the final paper.
**Interpretability vs Performance Trade-off.** We acknowledge this trade-off, which, as you note, is a tension observed both in our work and the broader interpretability field. One advantage of our approach is the ability to moderate this balance using the regularisation factor λcc. This differs from other white-box approaches like decision trees and offers a valuable means of tailoring the interpretability-performance trade-off for different use cases.
**Extension to Alternative Architectures.** Thank you for raising the potential for extension to CNNs or transformers. We agree this is a valuable future research direction and share some preliminary thoughts about extending our work in this direction:
Considering CNNs, the sparsity and distance metrics are not obviously applicable to standard kernel computations, but there is potential to consider distance and sparsity metrics in branched architectures (such as the Inception models). Conceptually, the notion of functional modularity seems more applicable to decision-making than image-processing tasks. It may thus be more interesting to interpret modules within fully connected layers downstream of convolutional layers, and this may also improve the interpretability of the intermediate latent space.
Considering transformers, our modularity pipeline could be applied (with adaptation) by taking attention heads as network nodes or, as with CNNs, by interpreting MLP layers only. Alternatively, we could frame parameters as nodes and relocate vectors within attention head matrices and positions within the residual stream. | Summary: This paper proposes a method to learn a functionally modular and interpretable model in an RL policy network. It combines a few ideas:
- Spatially embedded neurons with a distance-weighted loss to encourage locality
- Neuron relocalization (Algorithm 1)
- Partitioning the model into different modules using variants of the Louvain algorithm that take into account functional connectivity (equation 5)
The paper tests these ideas on a few GridWorld RL environments, and find that the discovered modules are interpretable; when the modules are intervened upon, they display effects which are consistent with their modular nature.
Claims And Evidence: The paper claims to:
- extend local neural networks methods to RL
- create an extended Louvain algorithm to detect communities in the neural networks
- demonstrate that interventions on the network parameters that are derived from the Louvain algorithm are consistent with their purported roles
These are fairly thin claims–it seems to me like a straightforward application of prior methods on a slightly different problem, and strictly speaking their extensions are not necessary to make the method work specifically in the RL setting, they're more like enhancements of the methods in general–but they are well supported.
Methods And Evaluation Criteria: The methods and evaluation criteria are appropriate. These are still very much toy problems to demonstrate the method. If the ultimate goal is to apply this to non-trivial tasks, as the introductory framing in terms of AI ethics implies, one would want to extend this to larger and more complex environments.
As is often the case in interpretability research, the claims of finding insights are highly subjective. Their interventions in 4.5 partially address this issue, but it doesn't convince me that this will scale to non-trivial problems.
Theoretical Claims: N/A
Experimental Designs Or Analyses: The experiments are sound and appropriate.
Supplementary Material: I briefly looked at the supplementary, it seemed fine.
Relation To Broader Scientific Literature: This is a straightforward extension of Liu et al. (2023) to RL with a few bells and whistles to find good networks via the Louvain algorithm.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: This paper feels like a rather straightforward extension of prior work. It is well executed, however. My preference is to evaluate the content on execution rather than the more subjective issue of originality.
I found the Background and Related works section to be particularly well-executed and far-reaching.
Other Comments Or Suggestions: There's a few typos:
- "Comission"
- "cna"
- "combine" rather than combined on line 399
There's a sentence that doesn't make sense: "negative saturation of modules evidences their axes specific navigation function"
I don;t like the claim that conscious decision making relies on modular processing–it seems unnecessary to drag consciousness into this.
Questions For Authors: N/A
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for the thorough review. We appreciate the positive comments on the quality of our execution and are grateful for the constructive feedback, which we respond to below.
**Contributions.** We recognise that our training approach builds on Liu et al (2023). Specifically, we do this by adapting distance-weighted sparsity to RL policies rather than tasks with explicit mathematical structure, and by proposing extensions including log-based sparsity to improve performance. We further develop a novel clustering approach and propose modularity metrics which enable automated detection and characterisation of functional neural modules. We believe this is a crucial step to enabling scalable module interpretability.
**Interpretability Insights and Scalability.** We appreciate your understanding of the difficulties of finding objective insights in interpretability research, a challenge which we approached by quantifying the impact of modules through ablations. We agree that demonstration in more complex environments is an important direction for future work. To move towards this, we have now implemented the framework on a non grid-world environment (Pong), as proposed by reviewer qymG, and will formalise and incorporate these results in the final paper. We believe that our rigorous evaluation approach, particularly the ablation studies and hyperparameter analyses, will provide a solid methodological foundation for further scalability.
**Specific Corrections.** Thank you for drawing the typos to our attention - we have fixed these. The sentence about negative saturation was intended to explain that when modules are negatively saturated, the modified policy behaviour shows evidence of the modules' axis-specific navigation functions. We have clarified this sentence. We also acknowledge that the claim about consciousness is unnecessary to motivate our work and have removed it. | null | null | null | null | null | null |
Conformal Prediction as Bayesian Quadrature | Accept (oral) | Summary: This paper proposes a new Bayesian interpretation of conformal prediction, which recovers standard conformal prediction as its mean and provides additional finite sample uncertainty estimate. Interestingly, as a Bayesian algorithm, the uncertainty comes from both 'lack of precise input locations' and finite (insufficient) number of observations. Another nice thing is that by taking the supremum of all possible priors, the practitioners do not need to worry about the choice of prior, which is usually a huge headache in practice. In the experiments, the advantage of the proposed method is clearly demonstrated.
Claims And Evidence: Yes, the paper is well written.
Methods And Evaluation Criteria: N/A
Theoretical Claims: I have checked all the proofs in the appendix. The proofs are well-written and easy to follow.
Experimental Designs Or Analyses: Why the authors only include conformal risk control in the experiments and not do anything about split conformal prediction, given that the method works for both settings. I am quite familar with split conformal prediction, but I have to admit I know little about conformal risk control. I am not asking for more experiments, I am curious what make the authors only include experiments on conformal risk control.
Supplementary Material: I have checked all the proofs in the appendix.
Relation To Broader Scientific Literature: N/A
Essential References Not Discussed: Line 376-377. This paper claims that the Bayesian interpretation allows conditional coverage guarantees. I suggest the authors distingush their contributions from the real conditional coverage guarantee, find $\hat{C}\left(X_{n+1}\right)$ such that $\mathbb{P}\left(Y_{n+1} \in \hat{C}\left(X_{n+1}\right) \mid X_{n+1}=x\right)=1-\alpha$. See for example, https://arxiv.org/pdf/2305.12616, https://arxiv.org/abs/1903.04684. From my understanding, the authors' Bayesian interpretation can still only provide marginal coverage guarantees. I request the authors to make this distinction in the paper.
Other Strengths And Weaknesses: Strength:
1. The section 4 makes serveal very interesting observations. 1) The standard expectation can be translated to an integral of the inverse CDF function. Then, even if the input locations are not known, one can deduce that they follow a Dirichlet distribution from a classical result presented as Lemma 4.2. As a result, the dirichilet distribution over the input location quantifies an upper bound on the CDF of the final integral. 2) The posterior mean can be upper bounded by the integral of the 'worst-case' quantile function that is consistent with the observations. I really enjoy reading this section and read the proofs in the appendix. It is very enlightening.
Weakness:
1. The way Bayesian quadrature is written is not standard in the BQ literature as I am aware of. The authors use the standard notation for regression setting, i.e Equation (15) in https://arxiv.org/pdf/1807.02582, while personally I prefer more the interpolation notation for Bayesian quadrature, see Equation (20) in https://arxiv.org/pdf/1807.02582, as the likelihood function is degenerate.
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 writing a thoughtful and detailed review. We are happy that the review has recognized that the choice of prior can be a headache in practical problems and how our method circumvents this. We also thank the reviewer for reading our proofs. We are glad that the reviewer found them to be enlightening.
**Conformal Risk Control vs. Split Conformal Prediction.** We thank the reviewer for raising the point about the experiments being run on Conformal Risk Control rather than split conformal prediction. The main reason that the experiments focus on Conformal Risk Control is pragmatic in nature. CRC recovers split conformal prediction when the miscoverage loss is used (i.e. loss = 1 if prediction set/interval does not cover ground truth and loss = 0 otherwise), but allows more general loss functions to be considered. Therefore, in order to investigate more complex loss functions, the experiments focus on CRC. However, please see our next point below which includes results on Split Conformal Prediction.
**Additional Experiments.** During the rebuttal period we ran additional experiments in a more traditional prediction interval setting with heteroskedastic data. In each of the 10,000 random trials we use 200 calibration samples. We let $X \sim U[0, 4]$ and $Y|X \sim \mathcal{N}(0, X^2)$. Prediction intervals are formed as $[-\hat{\lambda}, \hat{\lambda}]$ where $\hat{\lambda}$ is to be selected by each method. The loss is the miscoverage loss and the target loss is set to 0.1 (i.e. 90% coverage). The maximum allowable risk failure rate is set to 5% (i.e. $\beta = 0.95$). Please note that since the miscoverage loss is used here, Conformal Risk Control and Split Conformal Prediction coincide.
| Method | Relative Freq. (Failure Rate) | 95% CI | Mean Prediction Interval Length |
|---|---|---|---|
| Split Conformal Prediction / CRC | 46.59% | [45.61%, 47.57%] | 7.67 |
| RCPS | 0.0% | [0.0%, 0.04%] | 13.99 |
| Ours ($\beta = 0.95$) | 3.75% | [3.39%, 4.14%] | 9.14 |
The results indicate that even in the heteroskedastic setting, our method allow more precise control of $\hat{\lambda}$. Unlike RCPS, which is overly conservative, ours produces the shortest prediction intervals while not violating the maximum allowable risk failure rate.
**On the nature of conditional coverage.** We thank the reviewer for raising this point. Previous work on conditional guarantees have focused on input-conditional guarantees, where the guarantee is conditioned on $X_{n+1} = x$ for all $x$ in the input domain. Guarantees of this nature have been shown to be generally impossible without stronger distribution assumptions. Our guarantees are perhaps better characterized by the term "data-conditional guarantee", where we condition on the set of observed loss values $\ell_{1:n}$. Our experiments demonstrate the practical benefits of this by achieving decisions that produce smaller prediction sets and intervals while not violating the constraint on maximum allowable failure rate. Our guarantees do not rely on strong distribution assumptions that would be necessary to produce an input-conditional guarantee. The distinction between input-conditional and our data-conditional guarantees is an important one and we will be sure to clarify this in the paper by adding a paragraph discussing this point.
**Notation.** We thank the reviewer for suggesting improvements to the notation. We would be happy to update the notation for clarity. However, unfortunately, the links in the review seem to be pointing to the same paper. If the reviewer would be so kind as to re-post the links in a comment, we would be glad to update our paper accordingly.
---
Rebuttal Comment 1.1:
Comment: Thank the authors for their rebuttals. I do not have further questions.
I prefer more the interpolation notation for Bayesian quadrature, see Equation (20) in https://arxiv.org/pdf/1807.02582, as the likelihood function is degenerate. | Summary: The paper proposes a Bayesian quadrature approach as a Bayesian alternative to conformal prediction, encompassing two widely used methods: split conformal prediction and conformal risk control. The equivalence between these approaches and Bayesian quadrature is clearly established through theoretical proofs. Empirically, the proposed Bayesian method demonstrates strong performance compared to frequentist alternatives, particularly in terms of lower risk violation frequency and more compact prediction sets.
## Update after rebuttal
I found the authors’ rebuttal satisfactory. I have maintained my score 4.
Claims And Evidence: The paper claims that the proposed Bayesian quadrature approach generalizes conformal prediction. Specifically, Propositions 3.1 and 3.2 demonstrate that split conformal prediction and conformal risk control can be reinterpreted within a decision-theoretic framework, while equations (30)–(32) show that the expected loss of the quantile spacing approach recovers the corresponding conformal methods. These claims are supported by theoretical proofs.
However, given my limited knowledge of conformal prediction, I am unsure whether these two methods alone are sufficient to establish that Bayesian quadrature is a generalization of conformal prediction. In this sense, the title may be somewhat strong. That said, I do agree that the proposed approach encompasses these two conformal methods.
Methods And Evaluation Criteria: They first establish the mathematical equivalence between their Bayesian quadrature approach and existing conformal prediction methods, specifically split conformal prediction and conformal risk control. They then present experimental results demonstrating that their proposed Bayesian posterior risk approach reduces the number of individual trials that exceed the target risk threshold while maintaining a smaller prediction set size compared to existing conformal methods.
Theoretical Claims: I have not verified all the theoretical proofs in detail, but the claims appear reasonable to me.
Experimental Designs Or Analyses: I reviewed the experimental results but did not examine all the details, such as the implementation code. However, the findings appear reasonable to me.
Supplementary Material: I have not reviewed the supplementary materials.
Relation To Broader Scientific Literature: Quantifying the uncertainty of black-box predictors is crucial for high-stakes applications and exploratory tasks. I expect this paper to benefit various decision-making domains, including autonomous driving, experimental design, and time-series forecasting.
Essential References Not Discussed: The literature review on Bayesian quadrature is relatively limited to fundamental works, which makes sense given that this paper’s approach differs significantly from recent advancements in Bayesian quadrature that rely on functional priors, such as Gaussian processes and kernel methods. Therefore, I have no concerns regarding the references.
Other Strengths And Weaknesses: Strengths:
1. I like the novel attempt to leverage Bayesian quadrature to reformulate conformal prediction. This perspective is interesting and bridges two distinct fields.
2. Applying a Bayesian approach to random quantile spacings is a clever idea, particularly in the context of integrating monotonic integrand functions like quantiles and cumulative density functions. Traditional kernel-based methods often struggle to enforce monotonicity from a functional prior, typically requiring crude approximations such as warped Gaussian processes. This method provides an interesting alternative.
3. The results appear promising. The improved risk violation and sample efficiency suggest a compelling direction for further research.
Weakness:
1. The Bayesian interpretation is somewhat unclear. I suspect this is because the paper is primarily written for the conformal prediction community, but some parts give the impression of denying Bayesian principles. For instance, Section 4.3 mentions the "elimination of the prior distribution," which, strictly speaking, contradicts the Bayesian viewpoint, where priors are valuable for incorporating contextual information beyond the observed data. I would appreciate a clearer explanation of the role of the prior in this approach. If the authors are referring to an uninformative prior, a prior that is robust against variation, or a weighted discrete distribution as the prior, it would be helpful to state this explicitly.
2. Figure 1 could be misleading. It depicts the typical Bayesian quadrature procedure, where a functional prior is placed over the quantile function $F^{-1}$, assuming smooth monotonicity. However, if I understand correctly, the authors do not ultimately place a function space prior directly. Instead, they propose placing a Dirichlet prior on quantile spacings and using a Heaviside step function (akin to an empirical CDF) as a deterministic function, then this forms the non-parametric functional prior. The resulting posterior over varying spacings then induces a smooth posterior over the integral in the expected values of $L^{+}$. Is this interpretation correct? Clarifying this aspect would improve the paper’s clarity.
Other Comments Or Suggestions: I did not find any typos.
Questions For Authors: See weakness section.
Ethical Review Concerns: Not applicable
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We thank the reviewer for writing a detailed review that recognizes the bridging nature of our work and its benefits for various decision-making domains.
**Generalizing Conformal Prediction.** One of our main contributions is to show how both split conformal prediction and Conformal Risk Control can be recovered by taking the posterior mean of our upper bounding loss random variable $L^+$. Thus, our method illuminates a broader viewpoint and uses this insight to choose $\lambda$ more effectively. We believe this is generally useful perspective that may have broader implications on conformal prediction in general. Nevertheless, we will update the text of the manuscript to clarify the nature of the generalization elaborated here (i.e. oriented towards split conformal prediction and Conformal Risk Control).
**Role of the prior.** We thank the reviewer for raising this nuanced but important point. Our goal is to show that the Bayesian viewpoint unlocks a richer interpretation compared to previous works, which focus on marginal guarantees that as we have shown in the paper correspond to the posterior mean. For better or for worse, there is still a big gap in the literature between traditional approaches to distribution-free uncertainty quantification, which are predominantly frequentist in nature, and methods like Bayesian quadrature which are firmly Bayesian in nature. Therefore, to draw an explicit correspondence between the two, the dependence on the prior is removed in Section 4.3. The intuition is that that any rational decision maker operating according to the rules of probability, regardless of prior (sufficiently expressive), would agree with the upper-bounding distribution of $L^+$ we derive. Naturally, commitment to a specific choice of prior would lead to tighter distributions over the posterior risk, and in future work we seek to bridge these fields even further by exploring specific choices of priors over quantile functions. We will add a paragraph explicitly discussing these points to the manuscript.
**Figure 1.** Thank you for raising this point. The interpretation stated in the review is correct: the smoothness does indeed result from the combination of a step function with the distribution over quantile spacings. Our original intention was to illustrate the general idea of Bayesian quadrature in our setting with Figure 1, and then move into the specifics of our method in Figure 2. However, we will update Figure 1 to more clearly signpost the use of the step function, both in the caption and by updating the figure itself. | Summary: The authors propose a Bayesian version of conformal prediction, which guarantees conditional coverage, rather than marginal coverage. The technique is distribution free, since it considers the worst case risk by maximizing over all possible priors. This is made tractable by leveraging some prior results on distribution free analysis of quantile spacings, combined with Bayesian quadrature. Their method includes frequentist split conformal prediction and conformal risk control (CRC) as special cases.They show significantly improved results (in terms of risk control and prediction set size) on synthetic data, and on controlling the false negative rate of multilabel classification on the MSCOCO, compared to CRC and Risk-controlling Prediction Sets (RCPS). Overall a very impressive paper.
Claims And Evidence: Theoretical claims (see summary) are supported by proofs (not checked) and compelling experimental results.
Methods And Evaluation Criteria: Yes, good eval on synthetic data and a standard challenging real world image classification benchmark.
Theoretical Claims: I did not check the correctness of the proofs.
Experimental Designs Or Analyses: Experiments seem sound.
Supplementary Material: No
Relation To Broader Scientific Literature: Related work is very well explained. This particular combination of techniques (Bayesian quadrature and distribution-free analysis of random quantil spacings) seems entirely novel, and is very creative.
Essential References Not Discussed: NA
Other Strengths And Weaknesses: As I said above, extremely strong paper.
Other Comments Or Suggestions: Emphasize that your method is conditional on observed data, and is better than a marginal guarantee.
This part of Bayes is more important than using a prior (which you avoid).
Questions For Authors: NA
Code Of Conduct: Affirmed.
Overall Recommendation: 5 | Rebuttal 1:
Rebuttal: We thank the reviewer for taking the time to write a thoughtful and detailed review. We are pleased that the review recognized the novelty of creatively combining Bayesian quadrature and distribution-free analysis of random quantile spacings.
We will update the paper to clarify that our guarantees are conditional on the observed calibration data. In essence, our guarantees are probabilistic statments about the risk conditioned on the observed losses (see e.g. the conditioning on $\ell_{1:n}$ in Theorem 4.3 and Corollary 4.4). This stands in contrast to previous approaches which rely on marginalizing over many possible realizations of the calibration losses that were not observed. We will add a paragraph to the paper explicitly clarifying this point. | Summary: This paper proposes a Bayesian reinterpretation of conformal prediction, framing it within a Bayesian quadrature framework. The authors shows that split conformal prediction and conformal risk control can be derived as special cases of Bayesian quadrature. By modeling uncertainty over quantile functions and leveraging Dirichlet-distributed quantile spacings, they derive a posterior distribution over expected losses, enabling more interpretable and adaptive risk guarantees.
Claims And Evidence: Yes.
Methods And Evaluation Criteria: Yes.
Theoretical Claims: As far as I can tell, the theoretical claims are correct.
Experimental Designs Or Analyses: The two datasets incorporated are well-designed and illuminating. I would love to see more experiments though, to provide some intuition on the strengths & drawbacks of the Bayesian quadrature method in practice. For example, would it be possible to test on synthetic data with non-monotonic loss functions or heteroscedastic noise?
Supplementary Material: I only skimmed the proofs and did not check them carefully.
Relation To Broader Scientific Literature: There have been attempts to formulate/use conformal prediction for Bayesian inference ([e.g.](https://arxiv.org/abs/2210.12496)), but non as unified as the proposed method.
Essential References Not Discussed: n/a
Other Strengths And Weaknesses: Coming from some one who is mostly familiar with the frequentist side of things, this paper provides very interesting and novel insights about UQ & decision making. It shines light on the conservatism (the method needs to work for *any* prior), and failure modes of CRC because of the limitation of expectation. Although the empirical experiments are not comprehensive, the theoretical contributions and interesting enough to make up for it.
Other Comments Or Suggestions: n/a
Questions For Authors: See experiments section.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank the reviewer for taking the time to write a thoughtful and detailed review of our work. We appreciate that the review has recognized the "very interesting and novel insights about UQ & decision making" provided by our paper.
We appreciate the desire for additional experiments to provide additional insight about our method. To this end, we have implemented experiments on heteroskedastic data. The findings are largely in line with the results from Section 5 of our paper: our Bayesian interpretation produces prediction intervals that are shorter than baselines while not exceeding the maximum acceptable failure rate.
In each of the 10,000 random trials we use 200 calibration samples. To achieve heteroskedasticity, we let $X \sim U[0, 4]$ and $Y|X \sim \mathcal{N}(0, X^2)$. Prediction intervals are formed as $[-\hat{\lambda}, \hat{\lambda}]$ where $\hat{\lambda}$ is to be selected by each method. The loss is the miscoverage loss and the target loss is set to 0.1 (i.e. 90% coverage). The maximum allowable risk failure rate is set to 5% (i.e. $\beta = 0.95$). Please note that since the miscoverage loss is used here, Conformal Risk Control and Split Conformal Prediction coincide.
| Method | Relative Freq. (Failure Rate) | 95% CI | Mean Prediction Interval Length |
|---|---|---|---|
| Split Conformal Prediction / CRC | 46.59% | [45.61%, 47.57%] | 7.67 |
| RCPS | 0.0% | [0.0%, 0.04%] | 13.99 |
| Ours ($\beta = 0.95$) | 3.75% | [3.39%, 4.14%] | 9.14 |
The results indicate that even in the heteroskedastic setting, our method allow more precise control of $\hat{\lambda}$. Unlike RCPS, which is overly conservative, ours produces the shortest prediction intervals while not violating the maximum allowable risk failure rate.
---
Rebuttal Comment 1.1:
Comment: Thank you for the additional experiments! Really cool work. | null | null | null | null | null | null |
Learning to Plan & Reason for Evaluation with Thinking-LLM-as-a-Judge | Accept (poster) | Summary: The paper proposes a new training pipeline for LLM-as-a-judge models, using online preference optimization techniques as well as an agentic workflow that lets the model first output a plan then the detailed execution followed by the verdict. Experiments indicate the superiority of their new approach
Claims And Evidence: Claims are sound and clear
Methods And Evaluation Criteria: Method is intuitive and makes sense
Theoretical Claims: N/A
Experimental Designs Or Analyses: Experimental design is valid
Supplementary Material: N/a
Relation To Broader Scientific Literature: The method proposed can be a good way to further enhance the LLM-as-a-judge ability of current LLM systems
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: # Strengths
- relevant and important topic investigated
- Easy to understand and clear paper writing
- intuitive and simple method
# Weaknesses
- it is unclear this manual decomposition of plan/execute is most optimal for models, or only good for the models tested.
- as the previous point, it is never ablated what happens if you simply CoT->verdict and use online preference optimization to optimize. There are no demonstrations of how the plan->execute->verdict pipeline is superior.
Other Comments Or Suggestions: Missing a limitation section in the main paper
Questions For Authors: - Since you are using offline preference optimization, isn't it ok to simply reverse the order of the candidates and edit the final answer accordingly, instead of actually switching the order and regenerating?
- How is your LLM decoded during evaluation? what was the temperature/top-p? If you had temperature > 0, what are the standard deviation statistics of the results shown?
- Did you try using techniques like self-consistency to further boost your results? did you notice any boost at all?
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: Thank you for your review!
> it is unclear this manual decomposition of plan/execute is most optimal for models
We added additional experiments to showcase the effectiveness of EvalPlanner (planning+execution) for smaller models. In particular, we experimented with Llama-3.1-8B-Instruct and obtained up to 14 points of absolute improvements -- see our answer to Reviewer 1bZh on “Does this method rely heavily on a strong seed model”.
> it is never ablated what happens if you simply CoT->verdict and use online preference optimization to optimize
Note that we already have such experiments in the paper. First, one of our baselines, Self-Taught Evaluators (Wang et al., 2024) uses similar data to EvalPlanner and performs preference optimization of simpler CoTs without extensive planning. EvalPlanner outperforms it on RewardBench by up to 4 absolute points (90.0 -> 93.9; Table 2), and by 9-10 points on the other benchmarks (Tables 3, 4, 5) . Second, in Table 7, we also ablate the effectiveness of EvalPlanner’s unconstrained plans with other kinds of plans, wherein we show that our plans outperform other baselines like “list of evaluation criteria”.
> isn't it ok to simply reverse the order of the candidates and edit the final answer accordingly
Note that the CoTs (plan+execution) change based on the order of the responses. So, only editing the final answer will make it inconsistent with the corresponding CoT and hence, it is important to perform preference optimization on the data (CoT+final verdict) obtained by reversing the response order.
> How is your LLM decoded during evaluation?
As noted in Line 307, we perform greedy decoding when inference.
> If you had temperature > 0, what are the standard deviation statistics of the results shown?
We sampled 8 generations with a temperature of 0.8 and top_p of 0.95. Our results on RewardBench are 93.4 with a standard deviation of 0.3. These results are comparable to what we report in our paper, thus showing the effectiveness of EvalPlanner under different decoding hyperparameters.
> Did you try using techniques like self-consistency to further boost your results?
We tried it with 8 samples (using the same temperature and top_p as above) and obtained a score of 93.8. So, we did not observe any further improvement in results. This is expected given the fact that the answer space is limited to only two choices (A or B) and the small standard deviation in our results, as noted in the previous answer.
> Missing a limitation section
We will add this in the next version. | Summary: This paper introduces EvalPlanner, which is a preference optimization algorithm for thinking-llm-as-a-judge. It first generates an unconstrained evaluation plan, followed by its execution, and then the final judgement. It uses a selftraining loop to iteratively optimizes data and evaluation predictions. The paper conducts extensive experiments to demonstrate the effectiveness.
Claims And Evidence: Based on my review, I did not find any issues with the claims made in the submission.
Methods And Evaluation Criteria: They make sense for me
Theoretical Claims: Does not apply as this paper does not involve any theoretical claims.
Experimental Designs Or Analyses: The paper conducts extensive experiments to validate the effectiveness on 2 llama-70b LLMs. However, a potential weakness is that it remains unclear whether the proposed method would also be effective on LLMs from other families or smaller-sized models
Supplementary Material: Yes. I read the prompts provided in the appendix
Relation To Broader Scientific Literature: Effective reward modeling is crucial. Unlike traditional models that output scalar scores, LLM-as-a-Judge utilizes test-time compute to generate CoT rationales, refining evaluation. EvalPlan tackles the current challenges in collecting high-quality training data, and the resulting model has effective prediction performance.
Essential References Not Discussed: I think most of the key related works are included in the submission
Other Strengths And Weaknesses: strengths:
1. The paper introduces a novel LLM-as-Judge training data synthesis method, which first generates an evaluation plan and then produces step-by-step CoT rationales for each plan.
2. Extensive experiments demonstrate the effectiveness of the proposed method.
weaknesses:
1. The method evaluates only on two llama-70b models. it's unclear whether the proposed method would also be effective on LLMs from other families or smaller-sized models
Other Comments Or Suggestions: see the strengths and weaknesses section
Questions For Authors: While effective, the EvalPlan model is expected to generate longer responses for evaluation. Compared to other methods, your inference cost is likely to increase—by how much exactly?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your positive comments about the novelty and the extensive experiments of our paper.
> it remains unclear whether the proposed method would also be effective on LLMs from other families or smaller-sized models
EvalPlanner, does in fact, work well even with smaller sized models. To show this, we conducted additional experiments with Llama-3.1-8B-Instruct – see our answer to Reviewer 1bZh on “Does this method rely heavily on a strong seed model”.
> Compared to other methods, your inference cost is likely to increase—by how much exactly?
EvalPlanner, on average, generates 1K tokens during inference. Note that the goal of EvalPlanner is to indeed increase test-time compute for evaluation. Complex evaluation is a reasoning problem and in line with recent literature on reasoning, we show that evaluation also benefits from expending more test-time compute. | Summary: The paper introduces EvalPlanner, a novel preference optimization algorithm designed to enhance the Thinking-LLM-as-a-Judge framework for evaluating LLM responses. The approach employs a self-training loop that iteratively optimizes synthetic evaluation plans and executions using Direct Preference Optimization (DPO). Key algorithmic innovations include generating diverse plans and executions for each instruction-response pair, followed by preference tuning to refine Chain-of-Thought (CoT) reasoning. The experiments demonstrate EvalPlanner’s superior performance over existing methods on benchmarks like RewardBench, RM-Bench, JudgeBench, and Follow BenchEval. The paper also highlights the method’s data efficiency, achieving competitive results with as few as 5K synthetic preference pairs, and its ability to generalize across diverse evaluation tasks, such as coding, math, and safety-related prompts.
## update after rebuttal
Thank you very much for the author's hard work in rebuttal. These replies solved some of my questions. I will raise my rating from 3 to 4. This is because I am paying increasing attention to the evaluation of LLM replies, and this paper makes a pioneering attempt.
Claims And Evidence: The claims in the paper are robustly supported by experimental evidence.
- Through iterative DPO, EvalPlanner demonstrates superior performance across a variety of evaluation tasks.
- The use of an unconstrained evaluation plan enhances its general-purpose planning capability across diverse domains.
- The method’s data efficiency is well-documented, achieving competitive results with as few as 5K synthetically generated preference pairs
Methods And Evaluation Criteria: The proposed EvalPlanner method and its evaluation criteria effectively assess the model's effectiveness, particularly through pairwise response comparisons. I agree that, compared to scalar-scoring reward models, the LLM-as-a-Judge approach offers greater robustness and interpretability. However, real-world scenarios often require evaluating a single response’s correctness (e.g., determining when self-reflective reasoning should terminate) or identifying the best among multiple sampled responses (e.g., in Tree of Thoughts at each step). Extending the evaluation to these cases could broaden the method’s applicability and practical impact.
Theoretical Claims: This paper primarily relies on empirical evidence to demonstrate the effectiveness of the proposed method, while lacking theoretical support. This is understandable, and I do not insist that the authors provide additional theoretical claims.
Experimental Designs Or Analyses: The experiments in this paper are fairly solid and effectively demonstrate the superiority of the proposed method. However, further analysis in the following directions would enhance the study:
- The paper employs different seed models. It would be helpful if the authors could further discuss the impact of these model choices on the experimental results. I noticed that the performance improvement from **LLaMA 3.3-70B-Instruct** over **LLaMA 3.1-70B-Instruct** is quite significant. Does this method rely heavily on a strong seed model?
- The paper decouples *thoughts* into planning and reasoning. I am curious whether this decoupling contributes to the model’s effectiveness. What would the performance be if only planning or reasoning were used independently?
- The performance improvement with the second iteration is promising. What about further iterations? I appreciate that the authors have already mentioned this in the paper, and I look forward to seeing future results.
I understand that running these additional experiments within the rebuttal phase is challenging, so I encourage the authors to address my questions to the best of their ability. I will take the time constraints into account.
Supplementary Material: I reviewed the supplementary material, specifically focusing on Appendix sections A (More Analysis), B (Prompts), and C (Examples of Plans Generated by EvalPlanner). These sections provided detailed insights into the scaling effects of plans and executions, the prompt templates used, and concrete examples of generated plans for coding, math, and safety tasks, enhancing the understanding of EvalPlanner’s methodology and performance.
Relation To Broader Scientific Literature: - This method could be integrated with variations of Chain-of-Thought (CoT), many of which require evaluation of responses, such as **Tree of Thoughts, Graph of Thoughts, self-reflection, and LLM blender**. It could serve as a general evaluator within these frameworks.
- Additionally, some methods analyze responses (mostly CoT-based) at a finer granularity, assessing the information gain and correctness of each step. In the context of long cot reasoning, this method could potentially be extended to evaluate each step individually.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: **Strengths:**
The paper presents several strengths for EvalPlanner:
1. It achieves performance surpassing baselines with fewer prompt pairs, demonstrating data efficiency with as few as 5K synthetic preference pairs.
2. It eliminates the need for human-annotated data by leveraging synthetically generated CoTs, enhancing scalability.
3. The unconstrained planning approach fosters general-purpose planning across multiple domains, as evidenced by its strong results on diverse benchmarks.
4. Future work could integrate EvalPlanner as a reward model in RLHF workflows, indicating promising adaptability for broader applications.
**Weaknesses:**
1. The method is primarily evaluated on pairwise response comparisons, raising questions about its applicability to broader scenarios, such as ranking multiple responses/assess single response. While multi-response comparison could be an extension of pairwise evaluation (potentially achievable with this approach), its effectiveness in such cases remains untested.
2. The integration of EvalPlanner with a wider range of CoT-based methods is underexplored, limiting insights into its compatibility with other reasoning frameworks beyond the proposed planning-execution-judgment structure.
3. The paper lacks deeper experimental analysis, such as the impact of the choice of seed model or a more granular ablation on decoupling planning and reasoning, which could clarify their individual contributions to performance.
4. Can you give the training cost of SFT and DPO?
Detailed comments are provided above.
Other Comments Or Suggestions: N/A
Questions For Authors: I would greatly appreciate it if the authors could address my questions and clarify the broader application scope of this method. In that case, I would consider adjusting my rating accordingly.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for your review and appreciating our work! We are also glad to hear that you’re willing to adjust your scores. We respond to your comments below.
> Evalplanner’s applicability to Best-of-N settings
Upon your suggestion, we conducted some experiments and obtained promising results. Please refer to our response to Reviewer bPFz on “Assess whether the proposed judge can be effectively applied to rejection sampling”
> Does this method rely heavily on a strong seed model
No, EvalPlanner works equally well, even with 8B models. We happened to experiment with a stronger seed model to maximize performance. As shown below, EvalPlanner w/ Llama-3.1-8B-Instruct improves the seed model by a large 14 points (69.5 → 83.0), almost matching the performance of the much larger Llama-3.1-70B-Instruct and Claude-3.5-Sonnet. Evalplanner does not make any model-specific assumptions and hence should be expected to work with any model for scaling up test-time compute for evaluation.
| | **Overall** | **Chat** | **Chat-Hard** | **Safety** | **Reasoning** |
|--------------------------------------------|-------------|----------|---------------|------------|---------------|
| **Llama 3.1-8B Instruct (seed)** | 69.5 | 92.7 | 46.1 | 64.4 | 74.7 |
| **Llama 3.1-70B Instruct (seed)** | 84.1 | 97.2 | 70.2 | 82.8 | 86.0 |
| **Claude-3.5-Sonnet** | 84.2 | 96.4 | 74.0 | 81.6 | 84.7 |
| **EvalPlanner (w/ Llama-3.1-8B-Instruct)** | 83.0 | 85.5 | 84.0 | 83.4 | 79.3 |
> What would the performance be if only planning or reasoning were used independently
Note that we do such ablations in the paper. First, one of our baselines –- Self-Taught Evaluators (Wang et al., 2024) — trains a judge that generates CoTs without a planning component. Next, in Table 7, we compare EvalPlanner’s plans to other kinds of constrained plans. Having an explicit step-by-step plan allows the model to better reason through it, leading to much better performance. Since the reasoning component always has to be there to produce a verdict, our paper contains ablations of (1) no plan, and (2) other kinds of plans. We’ll clarify this more in a future version.
> The performance improvement with the second iteration is promising. What about further iterations?
We did not try a third iteration because of the computational overhead associated with online DPO. This requires obtaining newer/harder prompts and preference pairs, generating outputs from the previous iteration of model, preparing data, and performing preference optimization. That said, with the right kind of data, we believe further iterations should lead to more improvements. We hope that future work can explore it in more detail.
> The integration of EvalPlanner with a wider range of CoT-based methods is underexplored
We already explored different forms of CoTs in the paper in Table 7 by varying the type of plan that the judge generates.
> The paper lacks deeper experimental analysis, such as the impact of the choice of seed model
Refer to our experiments with a Llama 8B model.
> a more granular ablation on decoupling planning and reasoning
We already have such ablations in our paper. First, one of our baselines, Self-Taught Evaluators (Wang et al., 2024) uses similar data to EvalPlanner and performs preference optimization of simpler CoTs without planning. So, it should be seen as a baseline with no planning. EvalPlanner outperforms it on RewardBench by up to 4 absolute points (90.0 --> 93.9; Table 2), and by 9-10 points on the other benchmarks (Tables 3, 4, 5) . Second, in Table 7, we also ablate the effectiveness of EvalPlanner’s unconstrained plans with other kinds of plans, wherein we show that our plans outperform other baselines like “list of evaluation criteria”.
> Can you give the training cost of SFT and DPO?
All our experiments are performed on A100 GPUs. SFT of a Llama 70B model requires 3 nodes (24 A100 GPUs) and DPO requires 8 nodes (64 A100 GPUs).
> clarify the broader application scope of this method
Evaluation, as we hypothesize in the paper, is a reasoning problem where the judge should plan for the evaluation recipe and then reason through it to arrive at the verdict. Current literature on reasoning (O1/R1) has shown major improvements by scaling up test-time compute. EvalPlanner should be seen as one of the first SOTA recipes for scaling up test-time compute, specifically for evaluation. Through additional Best-of-N experiments, we have also established the effectiveness of Thinking-LLM-as-a-Judge models like our EvalPlanner in improving policy models. Future work could explore its applicability in RLHF pipelines, where both generation and evaluation are scaled up at test time. | Summary: This paper proposes EvalPlanner, a method that separates planning from reasoning to enhance LLM-as-a-Judge evaluation. EvalPlanner iteratively improves itself using synthetic preference pairs, achieving state-of-the-art performance (93.9%) on RewardBench and strong results on RM-Bench, JudgeBench, and FollowBenchEval
Claims And Evidence: Most of the claims in the paper are well-supported by empirical evidence.
To further strengthen the justification of the proposed method’s effectiveness, the following additional studies would be valuable:
1. Assess whether the proposed judge can be effectively applied to rejection sampling, Direct Preference Optimization (DPO), or online reinforcement learning (RL).
2. Analyze how the model's performance evolves over different stages of iterative training to validate its self-improvement capability.
3. Examine how varying the amount of training data affects performance to determine the model’s data efficiency and scalability.
Methods And Evaluation Criteria: Yes, the proposed method is well motivated and makes sense. It is just a bit straightforward and seems to be an extension of [Pang et al., 2024], [Wang et al., 2024], and [Wu et al., 2024b] by adapting to LLM evaluation tasks with an additional planning step.
The used datasets are comprehensive.
Theoretical Claims: N/A
Experimental Designs Or Analyses: See above "Claims And Evidence" section.
Supplementary Material: Yes
Relation To Broader Scientific Literature: While the proposed training approach exists in existing literature, the application to llm-as-a-judge scenarios seems novel.
Essential References Not Discussed: No
Other Strengths And Weaknesses: n/a
Other Comments Or Suggestions: - It appears that the performance scores for "safety" and "reasoning" have been incorrectly placed for some baselines under the "Reward Models with Critiques" category. Could the authors clarify or correct this?
- Adding 1-2 small experiments demonstrating how the proposed evaluator can enhance generation quality in other policy models would strengthen the practical impact of the method.
Questions For Authors: - The baselines in the paper appear to use different training datasets, making it unclear how fair comparisons are ensured. Could the authors clarify how differences in training data impact the results?
- The experiments are conducted exclusively with LLaMA-3-70B models. Does this suggest that the proposed method relies on a strong base model as a prerequisite for effectiveness?
- If without control, the llm generated planning and evaluation may still contain systematic bias. What is the potential way to address this issue to make sure it makes fair evaluations?
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: Thank you for your review!
> Assess whether the proposed judge can be applied to rejection sampling …
First, note that performing extensive RLHF experiments with Evalplanner is beyond the scope of this work and requires separate studies. That said, upon your suggestion, we conducted additional Best-of-N experiments with Evalplanner, on two hard reasoning benchmarks – GPQA (diamond) and AIME2024, obtaining promising results. The experimental setup is as follows:
* For each test data point, we sample N (= 8/16) responses from Llama-3.1-70B-Instruct.
* Since Evalplanner is a pairwise judge, we then prepare samples of response-pairs, amounting to N*(N-1) pairs (considering both orders) for each data point.
* Then we evaluate all these pairs using EvalPlanner and compute ELO ratings to rank the N responses.
* As baselines, we also report results for pass@1, random@N, and self-consistency@N. As an upper bound, we report pass@N.
Below are the results on GPQA (Diamond), where BoN with EvalPlanner improves pass@1 by up to 5 absolute points.
| | **N=8** | **N=16** |
|------------------------------------|----------|----------|
| **Pass@1** | 42.1 | 42.9 |
| **Pass@N** | 80.8 | 87.3 |
| **Random@N** | 41.6 | 43.4 |
| **Self-Consistency@N** | 42.4 | 46.4 |
| **Best-of-N (w/ EvalPlanner 3.3)** | **44.5** | **47.8** |
Next, on AIME2024, EvalPlanner also improves Pass@1 by up to 15 absolute points.
| | **N=8** | **N=16** |
|------------------------------------|----------|----------|
| **Pass@1** | 21.6 | 20.8 |
| **Pass@N** | 43.3 | 43.3 |
| **Random@N** | 23.3 | 20.0 |
| **Self-Consistency@N** | 20.0 | 20.0 |
| **Best-of-N (w/ EvalPlanner 3.3)** | **36.7** | **30.0** |
Both these results show the promise of EvalPlanner in improving LLMs on downstream tasks.
> Analyze how the model's performance evolves over different stages of iterative training to validate its self-improvement capability.
Note that our paper already contains these results in Tables 2 and 3 (with related discussions in Section 4). We present them again below. Recall that EvalPlanner consists of one iteration of SFT and two iterations of DPO. On RewardBench, the accuracies after these three stages are 86.8, 92.3, and 93.9. SFT doesn’t improve results much, especially on the Chat-hard category which contains subtle differences in response-pairs. After we construct DPO pairs teaching models to recognize these differences, it leads to major improvements in the first iteration, even with a small number of prompts (5K). In the second iteration, we obtain further improvements.
> Examine how varying the amount of training data affects performance to determine the model’s data efficiency and scalability.
Once again, these results were already presented in the paper in Table 2, associated with a section dedicated specifically to "EvalPlanner is data-efficient and benefits from iterative
thought optimization". We show that with as few as 5K synthetic preference pairs, EvalPlanner is competitive with SOTA reward models on RewardBench, obtaining accuracy of 92.3.
> It is just a bit straightforward…
Straightforward methods that work well in practice should be preferred. In terms of novelty, to our knowledge, we are the first ones to design a SOTA method that leverages test-time compute for evaluation (via planning and reasoning).
> It appears that the performance scores for "safety" and "reasoning" have been incorrectly placed for some baselines
Thanks for noting this! We’ll fix this in the next version.
> how the proposed evaluator can enhance generation quality in other policy models
Refer to the answer to your first question!
> The baselines in the paper appear to use different training datasets, making it unclear how fair comparisons are ensured.
* First, one of the baselines – Self-taught Evaluator (Wang et al., 2024) uses training data similar to ours and we outperform them by a significant margin.
* Second, for the other baselines, we did not need to match their training data to show the effectiveness of EvalPlanner because EvalPlanner only relies on synthetic pairs and a much smaller number of them. With more or human-annotated data, we expect EvalPlanner to scale even better. This has generally been shown for thinking models that expend more test-time compute for reasoning.
> EvalPlanner with weaker seed models
Refer to our response to Reviewer 1bZh on “Does EvalPlanner rely on a strong seed model”.
> llm generated planning and evaluation may still contain systematic bias..
It’s a possibility but compared to scalar RMs, we expect a model like EvalPlanner that generates CoTs to be better and more interpretable when dealing with biases.
---
Rebuttal Comment 1.1:
Comment: Thank you for your comments. I have a few additional points:
1. I appreciate the inclusion of best-of-N results. However, I noticed that comparisons with other judge/reward models were not provided, which makes the evaluation a bit less comprehensive.
2. Regarding the bias issue, I'm not entirely convinced by the current argument. For instance, what about the possibility that the chain-of-thought (CoT) approach might be even more misleading or introduce its own biases? It would strengthen the discussion to include some case studies or empirical comparisons to support this point.
---
Reply to Comment 1.1.1:
Comment: > Comparison with other judge models
We added a couple of other baselines for Best-of-N with two different judges – (1) the seed Llama model and (2) Self-Taught Evaluators (Wang et al., 2024) which is also trained on a similar amount of data as EvalPlanner. EvalPlanner outperforms both these baselines on AIME2024 by a significant margin.
| | **N=8** |
|--------------------------------------------|:--------:|
| **Pass@1** | 21.6 |
| **Pass@N** | 43.3 |
| **Random@N** | 23.3 |
| **Self-Consistency@N** | 20.0 |
| **Best-of-N (w/ seed Llama-70B-Instruct)** | 16.7 |
| **Best-of-N (w/ Self-Taught Evaluator)** | 26.7 |
| **Best-of-N (w/ EvalPlanner 3.3)** | **36.7** |
We'd again like to note that in line with most prior works on Reward Modeling (SFR-LLaMA-3.1-70B-Judge, CLoud, Self-Taught Evaluators, Critic-RM, etc) we evaluate EvalPlanner on standard reward modeling benchmarks. These additional BoN experiments should be seen as additional evidence about the effectiveness of EvalPlanner. However, performing extensive alignment experiments with EvalPlanner is beyond the scope of this paper and we hope that future work can build on top of our work.
> chain-of-thought (CoT) approach might be even more misleading or introduce its own biases
Recent works suggest that CoT monitoring can be far more effective than monitoring agent actions and outputs alone (see Baker et al., 2025: https://arxiv.org/abs/2503.11926). Regardless, this is a topic that extends much beyond EvalPlanner and requires further research for thinking models, in general, that generate CoTs. We believe such research would benefit Thinking-LLM-as-a-Judge models as well like EvalPlanner.
We have tried to answer your questions by conducting multiple additional experiments and if they have, we would greatly appreciate it if you could revisit your score accordingly. | null | null | null | null | null | null |
SSHR: More Secure Generative Steganography with High-Quality Revealed Secret Images | Accept (poster) | Summary: This paper proposes an image steganography method based on the diffusion model. By introducing a reference image and adaptive keys, it solves the problems of "limited control of text prompts" and "insufficient key security" in current methods, improves the quality of the revealed secret images, and enhances the system security. Experimental results show that the method proposed in this paper outperforms existing methods in terms of image quality and security.
## update after rebuttal
Thanks for authors' response; I will keep my score.
Claims And Evidence: Yes, the claims in the paper are supported by clear experimental results.
Methods And Evaluation Criteria: It is meaningful. The method proposed in this paper can significantly improve the image quality of steganography using diffusion models without the need for complex training. At the same time, this paper provides a new idea for the application of cryptography in steganography.
Theoretical Claims: This paper does not involve theoretical proofs.
Experimental Designs Or Analyses: The experimental design and analysis in this paper are reasonable.
Supplementary Material: I have reviewed all parts of the supplementary materials.
Relation To Broader Scientific Literature: This paper focuses on the steganography scenario of hiding images within images using diffusion models. Compared with previous related papers, it achieves higher image quality and system security.
In the papers of CRoSS [1] and DiffStega [2], text prompts are used as private keys. However, due to the limited control of text prompts, the quality of stego images is poor. This paper uses reference images and adaptive keys to avoid above problem, resulting in stego images with higher quality.
[1] Yu, Jiwen, et al. "Cross: Diffusion model makes controllable, robust and secure image steganography." Advances in Neural Information Processing Systems 36 (2023): 80730-80743.
[2] Yang, Yiwei, et al. "DiffStega: towards universal training-free coverless image steganography with diffusion models." arXiv preprint arXiv:2407.10459 (2024).
Essential References Not Discussed: None. All the major works in this field have been cited and discussed in this paper.
Other Strengths And Weaknesses: Strengths
(1) Novel method design: This paper innovatively uses adaptive keys to control the conceal and exact reveal processes. Compared with previous methods relying on text prompts, it can improve the security of stego images.
(2) Excellent experimental results: Compared with other steganography methods based on diffusion models, the method proposed in this paper significantly improves the image quality.
Weaknesses
(1) Insufficiently clear description of the conceal process: In the description of the "Conceal process" section, this paper uses a large number of formulas but lacks deep explanations, which may cause reading difficulties for readers.
(2) Unclear experimental settings for steganalysis: In the "Steganographic analysis" experiment, there is a lack of explanations about the sample size of the experimental data and the steganographic covers.
Other Comments Or Suggestions: (1) A large number of formulas are unfriendly to readers. The authors should provide clear explanations for each process.
(2) What information needs to be shared between the sender and the receiver in advance? By reading the supplementary materials, it can be inferred that both parties share the same reference image, and the public key related to the secret image also needs to be sent together with the stego image. Such important information should be presented in the main paper rather than in the supplementary materials.
Questions For Authors: (1) Regarding Weakness 1, what processing steps does the secret image undergo after the DWT transformation? How exactly is the symmetric key used for encryption during the processing?
(2) In Paper [2], reference images were also used. However, in the experimental results, the stego images in [2] are significantly different from the reference images, while the stego images in this paper are almost indistinguishable from the reference images. Which designs in SSHR contribute to achieving the above results? Please provide a detailed analysis.
(3) Regarding Weakness 2, in the steganalysis experiment, the sample sizes of the training data and the test data are crucial and need to be stated in the experimental setup. Meanwhile, training a steganalysis detector requires "cover - stego" pairs. In generative steganography, it is necessary to clarify what the cover is (for example, in CRoSS [1], the stego image is directly generated from the secret image without a cover. So, what is the cover used in steganalysis?).
(4) In - depth discussion on reference images. In this paper, does the selection of reference images have a significant impact on the results? For example, are there obvious differences between the experimental results when the reference image is a real - world image and when it is a generated image?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We greatly appreciate your thorough feedback and the time you've dedicated to reviewing our work. We sincerely hope that our clarifications will address your concerns and strengthen your confidence in our work.
A1: (1) Conceal and Reveal Process. In the proposed model, the secret image $x_{sec}$ is initially taken as input and transformed into the latent space as $z_{sec}$ using the discrete wavelet transform. The latent representation $z_{sec}$ is then encrypted with the symmetric key $k_{sym} $ and the reference image $x_{ref}$, which has been pre-processed through the condition information guidance module. The conceal process follows Equation (12), with the input $z_0 = z_{sec}$ and the output $z_T = z_{stego}$, generating the latent representation $z_{stego}$ of the stego image $x_{stego}$. The final stego image $x_{stego}$ is then obtained by applying the inverse wavelet transform. The reveal process mirrors the conceal process, following Equation (14) with input $z_T = z_{stego}$ and output $z_0 = z_{rev}$, ultimately yielding the revealed secret image $x_{rev}$.
(2) Symmetric Key Usage. The symmetric key is employed to generate the weights for the Conditional Re-parameterization Convolution and the modulation parameters $\alpha$, $\beta$, $\gamma$ in the Condition Reaction Term. This design ensures that the symmetric key plays a crucial role in the conceal and reveal process.
Your constructive comments are both sincerely valued and deeply appreciated, and we will re-organize and add more clearer description in the future version.
A2: The outcome of this model is influenced by: the removal of the text prompt and the design of the model’s training objectives.
(1) The removal of the text prompt in the proposed model contributes to reducing the risk of semantic misalignment and improves control over specific semantic regions. The proposed model eliminates the text prompts entirely, relying solely on the reference images to guide the generation of stego images. This architectural simplification facilitates more natural stego images generation, reduces the risk of semantic misalignment and removes the need for balancing multi-modal prompts. In contrast, the DiffStega model integrates both reference images and text prompts to steer the generation of stego images. With the dual-modal guidance, DiffStega generates stego images that align with the constraints of text prompts and the visual features of the reference images. However, text prompts in generative steganography models offer inadequate control, leading to the trade-off between the two types of prompts.
(2) The design of the training objective plays a crucial role in achieving the results outlined in this question, aligning with the discussed design choices. The framework’s focus on reference-image guidance and its simplification of the generative process contribute significantly to the system’s overall efficacy.
A3: (1) Dataset Resolution. Both the training and test datasets are utilized at a resolution of 256$\times$256, as documented in the manuscript. To improve clarity and readability, the manuscript will be reorganized to provide a more structured presentation of the information.
(2) Steganalysis Protocol. The deep learning steganalysis architecture follows the training protocol established by SRNet (Deep Residual Network for Steganalysis of Digital Images). After training the deep steganalysis network, we assess the anti-steganalysis capabilities of various methods with the trained network. This enables a comprehensive assessment of the model's anti-steganalysis capabilities. Our experimental setup aligns with common practices used in existing steganography research, guaranteeing the objectivity of the results. We aim to explore more effective experimental settings in future work to further enhance the evaluation of different steganography models.
A4: This question closely resembles the first one of the second reviewer. With respect to the concerns you've raised, we will now provide a renewed explanation of this issue.
(1) Reference Image Selection. We would like to clarify that the selection of reference images does not significantly affect the model's performance. During both training and testing, reference images are randomly selected, which enhances the model's generalization ability, ensuring excellent performance across various types of reference images. This makes the proposed model more adaptable to different visual contexts.
(2) Model Performance. The proposed model consistently delivers high-quality stego-images and secure secret recovery, regardless of whether the reference images are real-world images or generated images.
Your insightful question presents a promising avenue, selection of reference images in generative steganography, for future exploration. We intend to investigate this aspect in future work to enhance the effectiveness and adaptability of generative steganography techniques. | Summary: The paper presents a novel generative steganography method, SSHR, which incorporates the diffusion model to address challenges in image steganography. It replaces the traditionally used text prompts with reference images and adaptive symmetric keys to generate stego images, providing greater control over the image generation process and enhancing the security and naturalness of the generated images. SSHR uses an Exact Reveal Process to improve the quality of revealed secret images and introduces a Reference-Secret Image Related Symmetric Key (RSRK) generation module to enhance the security of both the keys and the concealed secret images.
Claims And Evidence: Clear and convincing.
Methods And Evaluation Criteria: Yes.
Theoretical Claims: Correct.
Experimental Designs Or Analyses: Yes, the experiments are reasonable.
Supplementary Material: Yes.
Relation To Broader Scientific Literature: The paper addresses a significant problem in generative steganography, where the quality and security of secret images are at risk. The innovative integration of reference images and adaptive keys improves both the imperceptibility and security of the generated stego images, making this method highly relevant for modern image privacy and security applications.
Essential References Not Discussed: The references are efficient.
Other Strengths And Weaknesses: The approach introduced by the authors is highly original. The shift from text prompts to reference images for guiding stego image generation is a unique and creative solution. Additionally, the Exact Reveal Process and adaptive key generation offer new ways to improve the recovery of secret images and prevent unauthorized access.
Other Comments Or Suggestions: N/A
Questions For Authors: 1. How does the proposed SSHR model perform when the reference images used for generation contain irrelevant or conflicting features with the secret images? Does the model still maintain high-quality stego images and secure secret recovery?
2. Has the symmetric key generation process been tested against potential vulnerabilities, such as key leakage in real-world scenarios? Are there any theoretical risks to this approach in terms of cryptanalysis?
3. While the exact reveal process is claimed to improve the quality of revealed images, has this been verified for large-scale datasets with real-world complexities (e.g., varying lighting conditions, image compression, etc.)?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We greatly appreciate the very detailed feedback and your recognition of our contributions! We sincerely hope our response below will further enhance your confidence in our work.
A1: (1) Reference Image Selection and Model Performance. The selection of the reference image does not significantly impact the model’s performance. Reference images used for generative guidance in the proposed framework are randomly selected during both the training and testing phases. This stochastic selection mechanism ensures that the model demonstrates robust generalization across diverse reference images, maintaining effective steganographic performance even when the textures of the reference images are irrelevant or conflict with those of the secret images.
(2) Model Performance. The proposed model continues to produce high-quality stego-images and ensures secure secret recovery. The stochastic selection mechanism guarantees robust generalization across various reference images, preserving high-fidelity stego-image synthesis and secure secret recovery, even when the reference images contain irrelevant or conflicting visual features in relation to the secret data.
Furthermore, your insightful question holds significant value and highlights an important avenue for advancement. We plan to systematically investigate this direction to identify optimal reference image selection strategies that strike a balance between creative flexibility and security guarantees for generative image steganography frameworks in future work.
A2: (1) Symmetric Key Security. The symmetric key’s security is rigorously maintained during data transmission. In the proposed framework, only the public key required for symmetric key derivation is exchanged, eliminating the risk of exposing the private key. This design ensures that the symmetric key's confidentiality is upheld by securely storing the private key, thereby significantly enhancing the overall security of the system.
(2) Theoretical Security. The proposed cryptographic key generation process, grounded in robust, well-established algorithms, mitigates potential theoretical vulnerabilities. Specifically, the symmetric key generation method employs the Elliptic Curve Diffie-Hellman Ephemeral (ECDHE) algorithm. This choice ensures strong theoretical security guarantees, safeguarding the symmetric key’s generation and protection.
(3) Experimental Results. a) Evaluation on Various Datasets. We evaluated the proposed model on four distinct real-world datasets: the DIV2K test dataset (100 images), COCO (5,000 images), ImageNet (10,000 images), and UniStega (100 images). These datasets, sourced from real-world scenarios, were chosen to assess the model’s performance and generalization across a variety of image types. The results highlight the model’s outstanding performance, demonstrating its robustness and adaptability in diverse real-world scenario applications.
b) Evaluation on Various Keys. The proposed model was also tested with several types of keys, including constant keys, random Gaussian noise, the public key transmitted to the receiver, and the correct symmetric key. Experimental findings confirmed that third parties could not extract secret images from stego images when using incorrect keys. This result underscores the high level of security provided by the proposed key generation process in real-world scenarios.
A3: Datasets. The proposed model was evaluated on a diverse range of real-world image datasets that cover various scenarios and challenging conditions, such as varying lighting, resolution differences, and environmental factors. To ensure a thorough assessment and facilitate a comprehensive comparison with other steganography approaches, including both cover-based and generative methods, we adhered to prior steganography methods. The model was tested across four distinct real-world datasets: the DIV2K test dataset (100 images), COCO (5,000 images), ImageNet (10,000 images), and UniStega (100 images). These datasets encompass a variety of image resolutions, scenarios, and visual contexts, providing a robust foundation for evaluating the model's performance under different conditions. | Summary: This paper proposed a targeted solution to some drawbacks in diffusion model-based generative steganography with text prompts. Although various experiments indicate the proposed model can outperform existing methods in terms of recovery quality and secret image security, there still exist some issues：
1) In theory: Although the authors state that SSHR is a generative steganography model, it introduces an additional reference image, and the goal of the model is to make the generated stego image similar to that reference one. Thus, its essence is hiding image in image, and it is not strictly coverless generative steganography.
2) In technology: The proposed SSHR builds on previous work (Jing et al., 2021) and differs in that it is conducted in the frequency domain only. As for the innovations in generative modeling, it only introduce a condition term R(z, ksym, c) into the original PM diffusion model. In addition, the symmetric key is generated at the sender's end, so how does it be securely transmitted to the receiver?
3) In experiments: Although the authors have conducted a comprehensive experimental validation of the quality assessment of the generated images, the experimental aspects regarding steganographic security are problematic. Since the method is essentially hiding image in image, the reference image should be used as a COVER and the containing image should be used as a STEGO. In addition to using the deep learning-based steganalysis tools in the paper, a handcrafted feature-based steganalyzer should be considered for
detection.
4) In writing: There are some typos: “Peivate”, “within within”,…
Claims And Evidence: Yes
Methods And Evaluation Criteria: Partly
Theoretical Claims: No
Experimental Designs Or Analyses: Although the authors have conducted a comprehensive experimental validation of the quality assessment of the generated images, the experimental aspects regarding steganographic security are problematic. Since the method is essentially hiding image in image, the reference image should be used as a COVER and the containing image be used as a STEGO. In addition to using the deep learning-based steganalysis tools in the paper, a handcrafted feature-based steganalyzer should be considered for detection.
Supplementary Material: No
Relation To Broader Scientific Literature: N/A
Essential References Not Discussed: No
Other Strengths And Weaknesses: See Summary
Other Comments Or Suggestions: No
Questions For Authors: See Summary
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: We greatly appreciate your valuable feedback and sincerely hope our response adequately addresses your points and restores your confidence in our work.
A1: Fundamental Disparities from Cover-based Steganography. We clarify that the proposed method effectively bridges the gap between cover-based steganography and coverless generative steganography, markedly diverging from cover-based methods that directly embed secret data into cover images. The proposed method adheres to a generative steganography pipeline, with reference images serving as guidance for generating stego images. It offers a hybrid solution that unites cover-based steganography and coverless generative steganography. Unlike coverless methods, the proposed method exploits reference images to boost stego images' naturalness and imperceptibility.
A2: (1) Fundamental Disparities from HiNet. The proposed model presents a significant departure from HiNet (Jing et al., 2021), a cover-based method. The key distinctions are: a) Generative steganography vs Cover-Based steganography. The proposed method follows a generative steganography pipeline, with reference images serving as guidance for the generation of stego images. This distinguishes the proposed method from HiNet, which directly embeds secret data into cover images; b) Key Management. The proposed model dynamically derives secret-specific symmetric keys through public key exchange and shared symmetric key generation module. Conversely, HiNet lacks mechanisms for key management; c) Role of Auxiliary Images. Although both the proposed method and HiNet utilize auxiliary images, the functional roles differ fundamentally. In the proposed method, the reference images serve as image prompts and guide the stego images generation process, whereas HiNet treats secondary images as secret data containers.
(2) Main Contributions. The proposed method addresses several fundamental challenges in image steganography, including naturalness and imperceptibility, quality of the revealed secret images and security. Unlike modular approaches that rely on isolated components, our method integrates three main contributions: a) We systematically propose a novel generative steganography method joints the reference images with the adaptive keys to govern the entire steganography process, enhancing the naturalness and imperceptibility of the stego images; b) We methodically design an Exact Reveal Process to precisely reverse the conceal process, minimizing errors in the reveal phase and improving the quality of the revealed secret images; c) We propose a Reference-Secret Image Related Symmetric Key generation module for dynamic symmetric keys generation, bolstering the security of both the keys and the secret images. It is important to note that these challenges cannot be adequately resolved with any singular modular component operating in isolation. The proposed model achieves optimal performance only through the synergy of these contributions.
(3) Key Transmission. The symmetric key is not transmitted directly to the receiver. Only the public keys associated with the secret images are delivered. a) Public Key Exchange. The sender generates a public-private key pair and transmits the public key to the receiver alongside the stego image; b) Symmetric Key Derivation. The receiver uses the received public key within the shared symmetric key generation module to derive the symmetric key. This process decouples the symmetric key transmission from public key distribution and ensures key consistency without transmitting the symmetric key. Please refer to Section $\textbf{\textit{Reference-Secret Image Related Key}}$ and the supplementary materials $\textbf{\textit{Security of the Symmetric Key}}$ for detailed specifications of the transmission of keys and symmetric key derivation.
A3: (1) Experimental Setting. The proposed model presents a novel generative steganography method, distinguishing itself from cover-based methods. It bridges cover-based steganography and coverless generative steganography, and utilizes reference images as guidance for stego images generation rather than containers as in cover-based models. This fundamental divergence shapes the experimental design, which integrates elements of both cover-based and generative steganography, providing a unique and comprehensive evaluation framework.
(2) Steganalysis. We have employed the handcrafted feature-based steganalyzer to assess the anti-steganalysis capabilities of the proposed model. We utilize StegExpose, an open-source steganalysis tool integrates four handcrafted feature-based steganalyzers (Sample Pairs, RS Analysis, Chi-Square Attack and Primary Sets), for assessment. The experimental results, detailed in Section $\textbf{\textit{Steganographic Analysis}}$, demonstrate that the proposed model exhibits excellent resistance to steganalysis.
A4: Thanks for mentioning the typos in our manuscript. We will review and polish the entire manuscript.
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Rebuttal Comment 1.1:
Comment: （1）As you claimed, the public key should be transmitted to the receiver alongside the stego image, so how can the security of the public key transmission be ensured?
（2） StegExpose is outdated for a long time, you should use other SOTA ones, e.g., SRM + Ensemble.
---
Reply to Comment 1.1.1:
Comment: Thank you for taking the time to provide additional feedback. We sincerely hope the following clarifications could address your points.
A1: Public keys are designed for public transmission, representing a core tenet of key exchange protocols.
The proposed symmetric key generation module is derived from the Elliptic Curve Diffie-Hellman Ephemeral (ECDHE) [1] protocol. Within cryptographic key exchange protocols, security of the symmetric key is predicated not upon public key confidentiality, but rather on two main principles:
a) Mathematical Security Foundations. The security of key exchange protocols (e.g. RSA, ECDH) is mathematically grounded in computationally hard problems like integer factorization for RSA, and elliptic curve discrete logarithm problem for ECDH and so on. These foundational problems guarantee the computational infeasibility of deriving private keys or shared secrets from publicly available parameters.
b) Security Architecture. The security of symmetric keys and overall system integrity guarantees from: (1) the computational intractability of asymmetric mathematical problems; (2) ephemeral session key generation ensuring forward secrecy.
Key exchange protocols leverage sophisticated mathematical foundations to obviating the requirement for confidential public key dissemination.
This study pioneers the integration of cryptographic key exchange protocols into image steganographic systems, establishing enhanced theoretical and practical security assurances for both encryption keys and concealed image data. To the best of our knowledge, this is the first exploration to integrate key exchange protocols into image steganography.
A2: Following the common practices in the cover-based and generative steganography task (e.g., ISN [2], HiNet [3], CRoSS [4], DiffStega [5]), our evaluation framework employs StegExpose, XuNet, and SRNet, to systematically evaluate the anti-steganalysis capabilities of various models. The evaluation framework doesn't contain the SRM method, and this is justified by:
a) The evaluation framework can provide a comprehensive evaluation of anti-steganalysis capabilities. The proposed model undergoes rigorous comparative evaluation against SOTA steganography models, involving both cover-based and generative models. All evaluated steganography models undergo systematic assessment with both classical statistical steganalysis methods (StegExpose) and deep learning steganalysis models (XuNet/SRNet), to assess their anti-steganalysis capabilities. This multidimensional evaluation framework enables rigorous and comprehensive evaluation of anti-steganalysis capabilities across various models.
b) The evaluation framework achieves higher steganalysis accuracy relative to conventional SRM. Although SRNet, XuNet, and SRM all utilize noise residual computation and classification architectures, empirical evidence demonstrates that XuNet [6] and SRNet [7] achieve superior steganalysis performance compared to conventional SRM. This enhancement stems from their superior multi-scale feature extraction capabilities and superior noise residual characterization. The empirical evidence justifies prioritizing contemporary deep neural architectures exhibiting superior compatibility with modern steganography frameworks. Consequently, the SRM has not been contained in the evaluation framework.
Your insightful question highlights a critical methodological consideration. While current time constraints preclude immediate integration of the suggested steganalysis approach, we commit to its systematic implementation in both the final manuscript and subsequent research.
[1] Mehibel N, Hamadouche M H. A new approach of elliptic curve Diffie-Hellman key exchange[C]//2017 5th International Conference on Electrical Engineering-Boumerdes. IEEE, 2017: 1-6.
[2] Lu S P, Wang R, Zhong T, et al. Large-capacity image steganography based on invertible neural networks[C]//Proceedings of the IEEE/CVF conference on computer vision and pattern recognition. 2021: 10816-10825.
[3] Jing J, Deng X, Xu M, et al. Hinet: Deep image hiding by invertible network[C]//Proceedings of the IEEE/CVF international conference on computer vision. 2021: 4733-4742.
[4] Yu J, Zhang X, Xu Y, et al. Cross: Diffusion model makes controllable, robust and secure image steganography[J]. Advances in Neural Information Processing Systems, 2023, 36: 80730-80743.
[5] Yang Y, Liu Z, Jia J, et al. DiffStega: towards universal training-free coverless image steganography with diffusion models[C]//Proceedings of the Thirty-Third International Joint Conference on Artificial Intelligence. 2024: 1579-1587.
[6] Xu G, Wu H Z, Shi Y Q. Structural design of convolutional neural networks for steganalysis[J]. IEEE Signal Processing Letters, 2016, 23(5): 708-712.
[7] Boroumand M, Chen M, Fridrich J. Deep residual network for steganalysis of digital images[J]. IEEE Transactions on Information Forensics and Security, 2018, 14(5): 1181-1193. | null | null | null | null | null | null | null | null |
Integer Programming for Generalized Causal Bootstrap Designs | Accept (poster) | Summary: The authors proposed to numerically estimate the joint distribution with the highest variance thus leading to the ATE estimate with the lowest variance for an RCT.
Their optimization problem is modeled by all the posible choices of assignment rules but instead of optimizing over all possible assignments they optimize over all possible potential outcomes for the sample observed. This modification leads to the constraints where there is only one posible potential outcome per observation and its consistency with the ascertainment variable Z. Additionally for a random assignment the marginals of the observed vs missed outcomes must match which add an extra constraint which the authors relax a bit in order to get a more stable program. However this last constraint is relaxed to allow for general assignment probability.
The authors then proceed to prove asymptotic validity of their methods produce a true bound bye ensuring that the true distribution is always a feasible solution. They derive a high probability bound on the variance that depends on the slack factor and the sample size. the result is valid even in the case of individual confounded assignment.
Finally simulators rustles are presented.
Weakness
- Is a computationally expensive approach.
- The guarantees are for the variance, but there is no guarantees on the ATE.
Strengths
- The authors produce finite sample guarantees for their method.
- The authors extend their method to a wide variety of estimators.
Overall a very strong work
Claims And Evidence: The theory is sound and the experiments back up the results obtained.
Methods And Evaluation Criteria: Refer to the summary
Theoretical Claims: The math is sound
Experimental Designs Or Analyses: Refer to the summary
Supplementary Material: I checked some of the math in the appendix
Relation To Broader Scientific Literature: I am not well versed in the literature closely related to this paper.
Essential References Not Discussed: I am not well versed in the literature closely related to this paper.
Other Strengths And Weaknesses: refer to the Summary.
Other Comments Or Suggestions: none
Questions For Authors: - Besides the variance are there any asymptotic guarantees for the ATE? How the computed ATE from the sample obtained as the minimizer relates with the true ATE?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We thank the reviewer for their question about theoretical guarantees on the ATE. Our results all bound the variance of the ATE, so we believe the reviewer is asking about the bias of the ATE. Our results hold for a general class of quadratic-in-treatment estimators, which each have their own bias characteristics. This class includes estimators that are unbiased under SUTVA, such as Horvitz-Thompson. The class also includes a wide range of biased estimators, such as "any unbiased estimator plus a constant offset." Because of the generality of our estimator class, we do not aim to provide general characterizations of the bias of the ATE. | Summary: This paper proposed a new integer program to jointly address two sources of uncertainty in causal inference, the design uncertainty due to the treatment assignment mechanism, and sampling uncertainty. Traditional methods tend to address one of the two uncertainties, but do not handle them at the same time. Motivated by this gap, the paper proposed an integer program formulation which computes numerically the worst-case copula used as an input to the causal bootstrap method. Further, the paper proved the asymptotic validity of this method for unconfounded, conditionally unconfounded, and individualistic with bounded confoundedness assignments. Numerical experiments support the effectiveness of the proposed methodology.
### update after rebuttal:
I have read through the authors' response and updated my scores accordingly.
Claims And Evidence: Overall the paper stated its claims and evidence clearly.
- Theoretically, the proposed integer program aims to identify the joint potential outcome distribution that maximizes the variance of the chosen estimator, while being consistent with the randomization design and the observed marginal distributions of potential outcomes. The proposed optimization's objective and constraints were described in detail in Section 2 for the basic difference-in-means estimator.
- On the statistical validity front, the paper provided a rate for the probability that the proposed method upper-bounds the true variance in large sample limit, by bounding the probability that the observed and missing marginal distributions are uniformly within epsilon distance.
- In the special case of conditionally unconfounded assignments, the paper shows that one can further imposes equality of the conditional marginal distributions to fully utilize the covariate information.
The main claims were supported by convincing evidence.
Methods And Evaluation Criteria: The proposed method matters the most in settings with small fixed samples and heterogeneous treatment effects, such as in geographical experiments. Thus the paper used the GDP data report by IMF as a real-world geographical dataset. The proposed procedure were compared with three baselines including standard bootstrap and causal bootstrap proposed in prior works. The dataset and evaluation criteria are reasonable.
Theoretical Claims: Checked through section 2's theoretical Claims, including proofs in appendix A.2 - for which I did not find issue with their correctness.
Experimental Designs Or Analyses: I did not find particular issues with the experimental design.
Supplementary Material: Appendix A. 2
Relation To Broader Scientific Literature: The proposed integer programming is novel and interesting as in the broader literature, which brings a gap between the design uncertainty and sampling uncertainty.
Essential References Not Discussed: Essential references were discussed in this work.
Other Strengths And Weaknesses: The experiment section is relatively weak with one single dataset and limited comparisons. It will strengthen the work if a larger dataset and more baselines can be used for stress testing and comparisons.
Other Comments Or Suggestions: typos: "and and" in abstract
Questions For Authors: See comments above.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank the reviewer for their careful consideration of our work and overall positive review. The main concern seems to be with the number of datasets and baselines. We were unfortunately limited by space considerations, and relegated additional experimental results to Appendix A.1. We are excited about evaluating this method in a wide variety of contexts against many possible baselines, though we believe a truly comprehensive evaluation is best left to future work given the current space constraints. | Summary: This paper proposes a novel method for quantifying **design uncertainty** in causal inference settings, particularly when experiments involve small samples, heterogeneous treatment effects, or non-standard assignment mechanisms. The standard bootstrap only captures sampling uncertainty, while existing causal bootstrap methods are limited to completely randomized designs and simple estimators like difference-in-means. The authors generalize causal bootstrap by formulating the worst-case copula problem as an **integer programming** (IP) task, applicable to a broad class of estimators (linear- and quadratic-in-treatment) and assignment mechanisms (including unconfounded, conditionally unconfounded, and bounded confoundedness cases). They prove asymptotic validity of the approach, and showcase improved variance estimates and tighter confidence intervals on simulated geographical experiments using IMF data. The approach enables exact variance maximization without closed-form copulas, providing flexibility and rigor for real-world experimental designs.
Claims And Evidence: The main claims are:
- Existing causal bootstrap methods are limited in scope; integer programming enables generalization to arbitrary estimators and assignment designs.
- The proposed method provides valid, tighter confidence intervals across a range of realistic designs and estimators.
- The method remains asymptotically valid even under bounded confoundedness and conditional unconfoundedness.
These claims are strongly supported:
- The integer program is precisely formulated with all necessary constraints and relaxation mechanisms.
- The theoretical results (Lemmas and Theorems 4.1–4.3) provide probabilistic bounds and convergence rates.
- Simulations across additive and multiplicative effects, covariate scenarios, and design types (CR, matched pairs) validate the empirical advantages.
Methods And Evaluation Criteria: The core methodology—variance maximization via an integer program under potential outcome and assignment constraints—is well-motivated and mathematically sound. The paper systematically builds from the classic Neyman decomposition to modern extensions, supporting:
- Arbitrary potential outcome distributions via discretization
- Arbitrary linear- and quadratic-in-treatment estimators
- Known and probabilistic assignment mechanisms (CR, Bernoulli, matched-pairs)
Evaluation is appropriate:
- Experiments simulate realistic geographical designs
- Estimators include difference-in-means and doubly robust estimators
- Baselines include sampling bootstrap, conservative variance, and isotone copula
Theoretical Claims: The paper contains multiple rigorous theoretical results:
- Lemma 2.1 guarantees feasibility of the IP under relaxed marginal constraints
- Theorem 4.1–4.3 prove asymptotic validity under unconfounded, conditionally unconfounded, and bounded confoundedness regimes
- Proofs rely on marginal balancing, inverse-probability weighting, and probabilistic bounds (Hoeffding-type inequalities)
The clarity of the mapping from copula constraints to linear conditions on binary indicator variables is a notable strength.
Experimental Designs Or Analyses: The experiments are well designed:
- Real GDP data is used to simulate geographical treatment effects
- Both CR and matched-pairs designs are compared
- Outcome models include both additive and multiplicative effects
- Covariate information is incorporated through doubly robust estimation and growth modeling
CI width, power, and coverage are all reported. Tables are clear and informative. Solver runtimes and scalability are also discussed.
Supplementary Material: Appendices provide:
- Full proof of Lemma 2.1 with combinatorial construction of feasible assignment
- Details of variance decompositions, matching, and IP transformations
- Runtime statistics and full simulation tables
- Implementation notes (including use of CP-SAT solver)
Supplementary material is extensive and adds credibility.
Relation To Broader Scientific Literature: This paper fits well into the literature on causal inference and design uncertainty:
- Extends Aronow et al. (2014), Imbens & Menzel (2021) on causal bootstrap
- Goes beyond analytical copula assumptions by solving for optimal coupling numerically
- Relates to optimal transport and Frechet bounds literature
- Empirically complements recent work on balancing designs (Harshaw et al., 2024)
Positioning is clear and the novelty of integer-program-based causal bootstrap is well-motivated.
Essential References Not Discussed: Most relevant references are covered, including:
- Neyman, Aronow, Imbens, Robins, Harshaw, Ji et al., and causal bootstrap literature
One possible addition: more discussion of connections to **causal bounds via OT or copula methods**, such as:
- Ji et al. (2023, AISTATS) used dual OT but not explicit worst-case coupling
- Literature on robust causal bounds under partial identification (e.g., Manski-style or Fan & Park (2010))
However, this is a minor omission.
Other Strengths And Weaknesses: **Strengths:**
- Elegant use of integer programming to generalize causal inference tools
- Applicable to a wide range of estimators and designs
- Excellent theoretical backing and empirical validation
- Readable and well-structured exposition
**Weaknesses:**
- Integer programming scalability limits application to large-scale datasets (>1000 units)
- Requires discretization of outcome support, which may lead to approximation error
- Some approximations (e.g., empirical matching of marginals) may be fragile in heavy-tailed or sparse data settings
Other Comments Or Suggestions: NA
Questions For Authors: 1. **Scalability to Large-Scale Experiments:**
Your method is elegant but computationally heavy. Do you foresee any way to scale to thousands or millions of units (e.g., through greedy relaxation, LP relaxations, stochastic approximations)?
2. **Robustness to Outcome Discretization:**
Discretizing continuous outcomes is a strong assumption. How sensitive are your variance bounds and coverage to discretization granularity?
3. **Adaptive Grid Design:**
Have you considered adaptive or non-uniform binning (e.g., quantile bins) to improve efficiency or accuracy of the integer program formulation?
4. **Extension to Clustered Designs:**
Can your approach be extended to clustered randomizations or interference settings, where design uncertainty is entangled with spillover effects?
5. **Automated Constraint Tuning (ε):**
Is there a principled way to select or adaptively shrink the marginal balance slackness ε, beyond theoretical feasibility guarantees?
6. **Limitations of Matched-Pair Analysis:**
Your method identifies matched-pair isotone copula bootstrap as degenerate. Are there better imputations in that regime (e.g., hierarchical Bayesian)?
7. **Alternative Optimization Frameworks:**
Why integer programming instead of convex relaxations or dual OT (e.g., Kantorovich dual)? Is IP strictly necessary to preserve optimality?
8. **Comparison to Copula-Based Bounds (Fan & Park, 2010):**
How does your method relate in tightness or assumptions to classic copula-based bounds, or nonparametric bound estimators in econometrics?
9. **Multi-valued Treatments and Interaction Effects:**
Could the integer program be extended to handle multi-valued treatments, interactions, or factorial designs beyond binary assignments?
10. **Real-World Adoption and Open-Source Tools:**
Are there plans to release user-friendly packages or APIs for this method? What feedback have you received from practitioners in A/B testing platforms or policy experiments?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank the reviewer for their thoughtful engagement with our work.
## Responses to Questions
1. Thank you for this question; please see the discussion of scalability in our response to Reviewer bwtT.
2. We currently discretize the continuous outcomes using the grid of observed outcomes, so that the discretization is lossless. A bigger issue related to discretization is that we require the marginal distributions of the imputed joint distribution to match the observed marginals. While the observed marginal will converge to its expectation asymptotically, in finite samples there can be a significant gap between the empirical sample and the marginal distribution (characterized by the DKW inequality). This finite-sample gap can be mitigated through the epsilon slack parameter; see Section A.5 for results.
3. This is a nice suggestion to improve efficiency of the IP. We have not considered it, but it would be worthwhile to investigate in future work.
4. If SUTVA holds, our approach covers clustered designs, since they are usually implemented to be probabilistic and unconfounded, and the estimators they are usually paired with are linear- or quadratic-in-treatment. It is not immediately clear whether our approach yields good coverage when spillover effects are present. We agree with the reviewer that proposing a bootstrap procedure in this setting is an interesting area for future work.
5. This is a great question, and we would be happy to provide more practical guidance. In the regime of feasibility, the smaller epsilon is, the tighter the upper-bound for the variance, but the stronger the coverage guarantees as provided by Theorems 4.1 and 4.3 and Corollary 4.2. Some practitioners may choose to contrast the upper-bound provided by the Integer Program against these theoretical guarantees to select epsilon. In our simulations, we solved our IP with epsilon = 0 (feasible since N_1 = N_0, cf. Lemma 2.1) and found the coverage to be acceptable. The adaptive or selection of epsilon is an interesting area for future work.
6. We did not fully understand this question. For the matched-pairs design, the optimal copula is the one computed by our IP. If the reviewer was asking whether there are other (non-IP) ways to construct a copula for this design in the literature, then we are not aware of any.
7. The causal bootstrap proceeds by first imputing a single (deterministic) outcome to each unit for the treatment it did not receive, which is why we need binary assignment of outcome to units (hence an IP). A convex relaxation would overestimate the variance of the worst-case copula, which could negate any power gains from the causal bootstrap. The same applies to dual OT (which would have the same objective value as the convex relaxation by strong duality). In the case of complete randomization, we found that an LP reformulation of the imputation problem was possible, but this was not the case for general treatment covariance matrices.
8. Our method is also a copula-based bound; we are optimizing the least favorable copula numerically instead of deriving it analytically. Our method differs from previous work because we allow a broader class of treatment assignment mechanisms. For some concrete comparisons: (1) Aronow et al (2014) derive the assortative copula as variance-maximizing for the difference-in-means estimator under complete randomization. Our technique recovers their copula in this specific setting. (2) Fan and Park (2010) estimate quantiles of the treatment effect distribution under effect heterogeneity, assuming iid treatment assignments. They show that the assortative copula is not sharp for measuring quantiles of the distribution of the treatment effects. By contrast, our method estimates the ATE and allows assignment mechanisms other than iid.
9. This is an interesting idea. The choice of estimands and estimators grows with the number of treatment options, but a priori, such an extension should be possible in most cases, and would be worthwhile to explore in future work. Beyond the asymptotic validity results which would need careful consideration, one would need to make sure that the estimator variance and potential outcome constraints under multi-valued treatment remain optimizable.
10. We are deeply committed to open-sourcing valuable code and research, and hope to do so here. The feedback from practitioners has been positive: many practitioners find bootstrap methods intuitive, and shy away from complex variance formulas, which was the impetus for this work. Anecdotally, we find many users of A/B testing platforms shy away from implementing sophisticated randomized designs because they fail to see strong variance improvements when paired with the standard (but often incorrect) bootstrap confidence interval construction methods. We hope that making the construction of correct confidence intervals easier for practitioners to implement will encourage them to adopt more sophisticated designs. | Summary: The paper presents a method that employs integer programming to maximize the variance of proposed estimators in randomized experimental design, addressing the issue of design uncertainty. It extends linear-in-treatment and quadratic-in-treatment estimators and generalizes assignment mechanisms using integer programming. The approach is built on a strong theoretical foundation.
Claims And Evidence: Yes, the paper provides theoretical guarantees and empirical evidence to support the claims.
Methods And Evaluation Criteria: Yes, the authors validated the proposed approach via simulations on real data and compared it with three baselines.
Theoretical Claims: Yes
Experimental Designs Or Analyses: Yes
Supplementary Material: Yes
Relation To Broader Scientific Literature: Building on previous work, this paper extends to linear-in-treatment and quadratic-in-treatment estimators and introduces new assignment mechanisms using integer programming.
Essential References Not Discussed: No
Other Strengths And Weaknesses: **Strengths:**
1. The paper tackles the important challenge of design uncertainty in experimental design and extends previous work by incorporating linear-in-treatment and quadratic-in-treatment estimators, along with new assignment mechanisms using integer programming.
2. The proposed approach is supported by asymptotic guarantees under different assignment mechanisms.
**Weaknesses:**
1. Computational complexity and scalability of the integer programming formulation are not thoroughly discussed, which may pose challenges for large-scale experimental designs.
Other Comments Or Suggestions: No
Questions For Authors: 1. The authors establish the asymptotic validity of their approach under unconfounded, conditionally unconfounded, and individualistic assignments with bounded confoundedness. Could the authors elaborate on the assumptions underlying each of these assignment mechanisms?
2. Solving Integer Programming problems is computationally expensive as the problem size increases. Could the authors provide a more detailed discussion on the computational complexity and scalability of their approach?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We thank the reviewer for their careful and positive review of our paper. Below, we address the two questions raised.
Q1: Unconfoundedness implies that the treatment assignment is independent of any potential outcome, usually achieved through randomization. We distinguish between conditional and unconditional unconfoundedness, i.e. whether or not this independence requires conditioning on an observed covariate, though the literature does not always make this distinction. Strictly speaking, a stratified assignment is not unconditionally unconfounded and is instead conditionally unconfounded if the stratifying variable is correlated with the potential outcomes. In observational studies, we usually cannot eliminate confounders, and it is more common then to assume conditional unconfoundedness. An excellent discussion on the relationship between randomization and unconfoundedness is [1].
Bounded confoundedness is not a standard defined assumption like unconfoundedness is. It typically arises in the context of sensitivity analysis and assumes that the magnitude of any confoundedness is limited within some range, i.e. one where treatment probabilities do not change drastically with remaining confounders. An individualistic assignment is one where the treatment assignment of one unit is independent from the treatment assignment of other units. For example, a Bernoulli randomized design is individualistic, but a completely randomized design, strictly speaking design is not (it is unconfounded however, so it is covered by Theorem 4.1).
We would be happy to expand on these assumptions and include them in the paper if the reviewer would find it helpful.
[1] Sävje, Fredrik. "Randomization does not imply unconfoundedness." arXiv preprint arXiv:2107.14197 (2021).
Q2: Regarding IP scalability, we would first like to re-emphasize that our method is primarily motivated for small-sample experiments where design uncertainty dominates. Also, we note that given the results of a particular experiment, the IP only needs to be solved once. (In our simulations, the IP had to be solved multiple times for coverage and power analysis.) Nonetheless, we agree that for a general-purpose tool, scalability is important.
The scalability of solving the IP depends on the sparsity of the treatment covariance matrix. This is why we see sub-quadratic scaling for Matched-Pairs in Table 1 (Appendix A.8). For the case of complete randomization where the off-diagonal entries to the covariance matrix are all equal, an LP formulation is possible as mentioned in Section 5.
To scale the IP beyond hundreds of units, we see potential to apply relaxation or approximation algorithms, as also suggested by Reviewer XXTL.
For a relaxation, we could relax the IP to an LP. The objective would then provide an upper-bound (i.e., an overestimate) to the worst-case variance, which can be used for Neyman-style confidence intervals (e.g., 1.96 * sqrt(variance upper bound)). However, the LP solution could not be used for the causal bootstrap because it might not be feasible for the IP.
For approximation, on the other hand, we could apply some technique like LP rounding to obtain a feasible solution, but this would now underestimate the variance. However, if we can guarantee that we have a c-approximation (so that the solution objective is 1/c of the optimal, for c >= 1), then one could scale imputed unit outcomes by sqrt(c) to ensure the variance of the causal bootstrap distribution upper bounds the true variance. Developing LP rounding techniques for our IP is still an open question. | null | null | null | null | null | null |
Model Uncertainty Quantification by Conformal Prediction in Continual Learning | Accept (poster) | Summary: The paper addresses the problem of continual learning with calibration guarantees. More precisely, the purpose is to train a model to address a series of tasks, in a sequential way (i.e., one task after the other). The datasets used to train the model on the successive tasks are not exchangeable, and may even be forgotten. Then, building a calibration set becomes challenging. In a nutshell, to overcome this issue, the authors propose to use a replay-based strategy to construct the calibration dataset; this dataset is used to train a quantile regression model, based on which nonconformity scores can be predicted: the dataset is first "reconstructed" (features being obtained from the past nonconformity scores and outputs from the average current nonconformity scores). Thus, for any test instance based on the forest, nonconformity scores can be obtained, and therefore prediction intervals.
The introduction recalls the setting, motivates the paper and provides the main ideas of the contribution. Section 2 presents the related works, starting with continual learning and proceeding with a short refresher on conformal prediction. Section 3 provides a formalization of the problem addressed. Section 4 presents the main contribution of the paper, explaining how the calibration set is obtained, presenting the considered nonconformity score, and explaining how the quantile regression forest can be trained to predict NC scores and how decisions can subsequently be made. The whole pipeline is summarized in an algorithm. Section 5 provides a theoretical analysis of the proposal, providing a consistency property based on four assumptions. Section 6 reports the experiments realized on a synthetic dataset and on a real dataset (Tiny ImageNet). Section 7 concludes the paper.
### update after rebuttal
I would like to thank the authors for their aswers to my comments and questions. I updated my score accordingly.
Claims And Evidence: The paper presents a strategy for continual learning with calibration guarantees. This claim is backed by a theoretical analysis, and more precisely formalized into two theorems. The experiments realized are rather simple (a synthetic dataset, and a real-world dataset), but nevertheless back up the proposal.
Overall, the evidence provided rather convincingly supports the claim, even if the strength of the assumptions in Section 5 is not discussed. Some components in the proposal are also rapidly presented, and could have been better justified or at least clarified.
Methods And Evaluation Criteria: The experimental setting and the datasets considered make sense for the problem at hand, even if a more thorough experimental analysis would have been appreciated.
Theoretical Claims: I only briefly checked the soundness of the proofs (provided in the appendices); they seem correct.
Experimental Designs Or Analyses: The experimental study conducted seems valid; the experimental setup is convincing and the results are as the reader could expect.
Supplementary Material: I only briefly went through the appendices.
Relation To Broader Scientific Literature: The discussion on the related works seems to include the main references pertaining to the problem addressed.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: The paper is overall well written, but sometimes difficult to follow (see below for some comments).
Other Comments Or Suggestions: I'd suggest to improve the writing.
Some parts are difficult to understand, e.g. the end of the "Nonconformity score function" paragraph in Section 4 (page 4). As well, the paragraph dedicated to quantile regression forests (mainly the part page 5) is difficult to follow due to the notations, to the lack of explanations, and to an extensive use of math in the text.
In Equation (1), $\mu$ would have been formally defined, and the assumptions pertaining to it could have been made explicit. It seems that a norm is missing either in Equation (5) or in Equation (6). Equation (13) seems to be disconnected from what precedes.
There are some (minor) typos. A couple of words are missing here and there, e.g. "In continual learning setting" (page 2), "the scores in score set" (page 4), "score set", "on calibration set", "that conditional distribution function" (page 5). Page 2, in "(IMM) (Lee et al., 2017)", there should not be parentheses around "IMM". In Section 3 (page 4), $Z_{ut}=(X_{ut},Y_{ut})$ is not properly defined.
Some references seem incomplete, e.g. "Krizhevsky, A., Sutskever, I., and Hinton, G. E. Imagenet
classification with deep convolutional neural networks. In NeurIPS, 2012."
Questions For Authors: Could you elaborate on the nonconformity score function such as defined by Equation (6) ?
Could you discuss the assumptions made to establish the consistency results in Section 5.2 ?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: **R to OCOS1.** The end of the "Nonconformity score function" paragraph in Section 4 mainly discusses the score set calculated by the nonconformity score function. We are sorry that our notations is hard to follow. We will revised the confusing notations.
**R to OCOS2.** We will improve our writing of all equations in our paper to makes them easy to read. No norm is missing in Equations (5) and (6). Equation (13) aims to calculate the $\hat{\beta}$ in Equation (12).
**R to OCOS3 and OCOS4 .** We will fix these typos and incomplete references.
**R to Q1.** We introduce the sigmoid-based nonconformity score function for two reasons. Please refer to **R to Q1.** of Reviewer vzZS.
**R to Q2.** Assumptions 1 and 2 make assumptions on the conditional CDF. The conditional distribution function is assumed to be Lipschitz continuous in Assumption 1 and strictly monotonously increasing in Assumption 2. Assumptions 3 and 4 focus on the actual construction of trees. For each tree with separate parameter $\zeta _{k}$, there are $L$ leaves, where every leaf $l$ is associated with a rectangular subspace $R _{l}\subset\mathbb{B}$. These subspaces are disjoint and cover the entire space $\mathbb{B}$, i,.e. for any $x\in\mathbb{B}$, there is one and only one leaf which corresponds to $R _{l(x,\zeta _{k})}$. Denote the node-sizes of the leaves $l$ of a tree by $w _{\zeta _{k}}(l)=\|\\{i\in\{1,\ldots,N _{cal}-1\}:X _{i}\in R _{l(x,\zeta _{k})}\\}\|$. $X _{i}\in(0,1)^{N _{\tau}}$ is the observation to train QRF.
The key of Assumptions 3 is "For any $x\in \mathbb{B}$, $p _{i}(x)$ satisfies that $p _{i}(x)=o(1)$". We discuss Assumption 3 by **Example 1**: The minimal number of observations in a node is growing for large $N _{cal}$, i.e., $1/\operatorname*{min} _{l,\zeta _{k}} w _{\zeta _{k}}(l) =o(1), N _{cal}\to\infty.$. Recalling $p _{i}(x)=\sum _{k=1}^{K} p _{i}(x,\zeta _{k})/K$, we have $0\leq p _{i}(x)\leq 1/\operatorname*{min} _{l,\zeta _{k}}w _{\zeta _{k}}(l) =o(1)$, which means that $p _{i}(x)=o(1)$ for any $x\in \mathbb{B}$. Therefore, Assumption 3 represents the case of **Example 1**.
Assumptions 4 is "For any $x\in \mathbb{B}$, the rectangular subspace $R_{l(x,\zeta_{k})}\subseteq(0,1)^{N_{\tau}}$ of leaf $l(x,\zeta_{k})$ of tree $\zeta_{k}$ is defined by the intervals $I(x,m,\zeta_{k})\subseteq(0,1)$, i.e. $R_{\ell(x,\zeta_{k})}=\otimes_{m=1}^{N_{\tau}}I(x,m,\zeta_{k})$, where $\otimes$ means direct sum. We assume that $\max_{m}|I(x,m,\zeta_{k})|=o_{p}(1)$ for $N_{cal}\to \infty$". We discuss Assumption 4 by **Example 2** which consists of three situations. In **situation 1**, the proportion of observations in a node, relative to all observations, is vanishing for large $N _{cal}$ i.e., $\operatorname*{max} _{l,\zeta _{k}} w _{\zeta _{k}}(l) =o(N _{cal}), N _{cal}\to\infty.$. In **situation 2**, when finding a variable for a splitpoint, the probability that variable $m=1,...,N _{\tau}$ is chosen for the splitpoint is bounded from below for every node by a positive constant. In **situation 3**, if a node is split, the split is chosen so that each of the resulting sub-nodes contains at least a proportion $\gamma$ of the observations in the original node, for some $0<\gamma\leq0.5 $.
As any $x\in \mathbb{B}$ is dropped down a tree, several nodes are passed. Denote by $S(x,m,\zeta _{k})$ the number of times that these nodes contain a splitpoint on variable $m$. The total number of nodes that $x$ passes through is denoted by $S(x,\zeta _{k})=\sum _{m=1}^{N _{\tau}} S(x,m,\zeta _{k}).$ Using **situation 3**, the maximal number of observations in any leaf, $\operatorname*{max} _{l} w _{\zeta _{k}}(l)$ is bounded (for every tree) from below by $N _{cal} \gamma^{S _{\min}(\zeta _{k})}$ where $S _{\min}(\zeta _{k})=\operatorname*{min} _{x\in \mathbb{B}} S(x,\zeta _{k})$. Using **situation 1**, $\operatorname*{max} _{l} w _{\zeta _{k}}(l)$ is on the other hand bounded from above by an $o(N _{cal})$-term. Putting together, we conclude that $\gamma^{S _{\min}(\zeta _{k})}=o(1)$ for $N _{cal}\to \infty$. Hence there exists a sequence $s _{N _{cal}}$ with $s _{N _{cal}} \to \infty$ for $N _{cal}\to \infty$ such that $S _{\min}(\zeta _{k}) \geq s _{N _{cal}}$. As the probability of splitting on variable $m=1,...,N _{\tau}$ is bounded from below by a positive constant, by **situation 2**, there exists a sequence $g _{N _{cal}}$ with $g _{N _{cal}} \to \infty$ for $N _{cal}\to \infty$ such that $P\\{\min _m S(x,m,\zeta _{k})>g _ {N _{cal}} \\}\to1\quad N _{cal}\to\infty$. Using **situation 3**, we obtain that $|\\{i\in\{1,\ldots, N _{cal}-1\}:X _{i,m}\in I(x,m,\zeta _{k})\\}|/( N _{cal} -1) \leq(1-\gamma)^{S(x,m,\zeta _{k})}$. Putting together, we conclude that $\max _{m} | \\{ i\in\{1,..., N _{cal}-1\}:X _{i,m}\in I(x,m,\zeta _{k})\\}|/(N _{cal}-1)=o _{p}(1)$ which indicates $\max _{m}|I(x,m,\zeta _{k})|=o _{p}(1)$ for $N _{cal}\to\infty$. Therefore, Assumption 4 represents the case of **Example 2**. | Summary: The authors propose a Conformal prediction-based methodology to address the calibration problem, which is reliably quantifying model prediction uncertainty in continual learning settings. The authors first enumerate reasons why a standard conformal prediction method cannot be extended to continual learning settings, including performance changes due to the order of tasks, violation of data exchangeability, where this issue is caused by the continual learning setting, and limitations in constructing calibration sets due to inaccessibility of samples from previous tasks. To address these constraints, the authors constructed a calibration set, which is made by the replay samples in the continual learning, and proposed a sequentially dependent score function, which is used for continual setting. Through this, the authors demonstrate the connection between prediction interval length and forgetting and experimentally prove the significance of the proposed method in experiments with real/synthetic data.
Claims And Evidence: * The authors demonstrated convergence to the oracle prediction interval as the calibration set size increases, from the perspective that accurate calibration becomes possible for each task when storing many replay samples.
* The authors' proposed uncertainty measurement technique observes the forgetting phenomena of continual learning models, commonly known as deep learning models, performing poorly in continual learning settings. It serves as experimental evidence supporting their theoretical foundation.
Methods And Evaluation Criteria: The authors verified model uncertainty across various continual learning approaches using simulated data. They demonstrated validity by showing the algorithm's coverage for given significance levels. They also conducted similar experiments on real datasets to prove their effectiveness.
Theoretical Claims: The authors provide theoretical evidence for the significance of their method through two theorems. Typical continual learning scenarios are often compared to an oracle setting where all data is accessible. Similarly, the authors proved these two theorems from the perspective that if a large number of samples are stored for all tasks, it approaches the oracle setting. Additionally, they specify the essential assumptions necessary for these theorems.
(Theorem 1) The authors prove that as the number of samples in the Calibration Set increases, the estimated conditional CDF for a given input x converges in probability to the Oracle conditional CDF.
(Theorem 2) The authors prove that as the number of samples in the Calibration Set increases, the estimated conditional quantile also converges to the true conditional quantile.
Experimental Designs Or Analyses: * Comparative experiments are needed to evaluate the performance when using simple quantiles directly, even if it violates basic assumptions of the standard conformal prediction.
* To examine how uncertainty changes according to task order, I believe experiments are needed to evaluate whether the proposed method can effectively interpret situations using simulation data that creates scenarios where difficulty changes from easy to hard and hard to easy across various continual learning algorithms.
* Additionally, I would like to see validation on datasets like time series data.
Supplementary Material: * I reviewed the supplementary material to verify the validity of the authors' theoretical proofs.
Relation To Broader Scientific Literature: This method can be used across various fields as it can measure uncertainty in regression-type methodologies in continual learning. As data increases, a growing number of models are being trained in continual learning scenarios. Since this method can measure uncertainty regardless of model type, it can be used to analyze prediction models used across various fields.
Essential References Not Discussed: To my knowledge, this paper adequately covers relevant papers in the field.
Other Strengths And Weaknesses: * This paper applies the conformal prediction framework to regression tasks in continual learning. The authors propose a method to construct prediction intervals with conditional coverage guarantees to overcome the constraint of being unable to access samples from previous datasets. The authors explain their proposed method clearly and comprehensibly. Additionally, this approach is technically well-justified as an extension of existing methods.
Other Comments Or Suggestions: * I suggest revising the title of the authors' paper. The current title is too broad. I believe "conformal prediction" should be included in the title.
Questions For Authors: * The authors should provide a more detailed explanation for introducing the sigmoid-based nonconformity score function.
- Could they elaborate on potential concerns when using different functions?
* I have a fundamental question about whether Quantile Regression Forests (QRF) can accurately estimate quantiles in data with sequential dependencies through learning. I would like to know the authors' thoughts on this.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: **R to EDOA1.** We conduct experiments on simulated data by split conformal prediction (SCP) . Please refer to **R to Q5.** of Reviewer KEqT.
**R to EDOA2.** Here we conduct experiments on real-world data by creating the scenarios where tasks are ordered from easy to hard and hard to easy. In Section 6.2 of the main file, we conduct experiments using Tiny ImageNet and perform 20 runs with different random seeds. For each run, we form 5 tasks. To order the task, we utilize a pretrained AlexNet and calculate the accuracy of this pretrained AlexNet on each task. We can obtain the order of tasks from easy to hard by sorting the accuracies on different tasks from high to low. By reversing this order, we get the order of tasks from hard to easy. Due to the time limit, we only consider $\alpha=0.3$. Other experimental settings are the same as those on real-world data (Section 6.2). After learning all tasks, we present the average coverages and length for 20 runs in the following table.
| | Easy to hard | | Hard to easy | |
| ------------------ | ---------- |---------- |---------- |---------- |
| CL method | Average coverage % | Average length | Average coverage % | Average length |
| SI | 72.63| 6.44| 73.43| 8.97|
| EWC | 74.81| 4.65| 73.19| 6.52|
| MAS | 72.20 | 3.05| 72.33| 5.65|
| DGR | 73.59 | 2.26| 74.09| 4.88|
| Finetuning | 72.12 | 12.10| 71.25 | 17.41|
We observe that the average coverage for 20 runs with different continual learning methods are over the desired coverage 70%. These demonstrate the validity of our proposed CPCL in the scenarios where tasks are ordered from easy to hard and hard to easy. It can be observed that the average interval length in the scenario with tasks ordered from easy to hard is greater than that in the scenario with tasks ordered from hard to easy. For example, when we use SI as the CL baseline, the average interval length on easy to hard task order is 6.44 while that on hard to easy task order is 8.97. These results indicate that task order significantly affects model uncertainty in CL.
**R to EDOA3.** We find that our proposed CPCL cannot be directly applied on time series data. There is a sequence of tasks in CL. The CL setting requires that data within a task is exchangeable, while data between different tasks is not exchangeable. According to this setting, to train QRF, we obtain the reconstructed dataset $D^{R} _{T}=\{(X^{R} _{i},Y^{R} _{i})\}^{N _{cal}-1} _{i=1}$, where $X^{R} _{i}=[S^{1} _{i}, S^{2} _{i}, \dots, S^{T} _{i}]$ and each entry $S^{t} _{i}$ corresponds to a sample of task $t$ in the replay buffer. In contrast, time series setting requires that all data is not exchangeable, which means that it is hard to obtain the reconstructed dataset. Meanwhile, it is interesting and we will study this issue for time series setting in the future work.
**R to OCOS1.** We will include conformal prediction in the title.
**R to Q1.** We introduce the sigmoid-based nonconformity score function for two reasons. (1) The range of sigmoid-based nonconformity score function is $(0,1)$. We train QRF on the reconstructed dataset $D^{R} _{T}=\{(X^{R} _{i},Y^{R} _{i})\}^{N _{cal}-1} _{i=1}$, where each entry $S^{t} _{i}$ in $X^{R} _{i}$ is the calculated score. The training of QRF requires to construct trees. This process involves the intervals $I(x,m,\zeta _{k})\subseteq(0,1)$. The interval $I(x,m,\zeta _{k})$ is used to determine whether $X^{R} _{i}$ is in the node corresponding to $I(x,m,\zeta _{k})$, i.e., if $S^{m} _{i} \in I(x,m,\zeta _{k})$, then $X^{R} _{i}$ is in the corresponding node. Since $I(x,m,\zeta _{k})\subseteq(0,1)$, we need to define that the score function ranges in $(0,1)$ for rigorous proof. (2) Sigmoid-based nonconformity score function is invertible. In Equation (11) we present the prediction interval in terms of scores. The invertible function helps us to rewrite the prediction interval which is shown in Equation (12). A typical score function in CP is $s(X _{i}^{t},Y _{i}^{t}) =|\hat{\mu _{i}^{t}}|$ where $\hat{\mu _{i}^{t}} =Y _{i}^{t}-\hat{f} _{T}(X _{i}^{t})$. It is not invertible and the corresponding range is not $(0,1)$. Therefore, it is not suitable in this paper.
**R to Q2.** In Section 5, we provide the asymptotic coverage guarantee. Specifically, Theorem 1 demonstrates that the conditional CDF $\hat{F}(s|x)$ estimated by CPCL converges in probability to the true conditional CDF $F(s|x)$ as $N _{cal}\to \infty$, i.e. $ |\hat{F}(s|x)-F(s|x)|\to _p 0 \quad N _{cal}\to\infty$. Therefore, our proposed asymptotic coverage guarantee ensures that QRF can accurately estimate quantiles. | Summary: The paper introduces a conformal prediction-based continual learning (CPCL) method to quantify model uncertainty in continual learning models. CPCL constructs a calibration set using replay techniques and applies a nonconformity score function to measure prediction errors. Theoretical analysis and experiments on simulated and real-world data demonstrate CPCL’s effectiveness in achieving reliable uncertainty quantification.
Claims And Evidence: The paper introduces a Conformal Prediction-based Continual Learning method for quantifying model uncertainty in continual learning. The main claim is that CPCL can provide asymptotic coverage guarantees for prediction intervals. In addition, the confidence intervals proposed are agnostic to the method used.
Methods And Evaluation Criteria: The authors assess the performance using both simulated data and real-world datasets for different coverage probabilities.
Theoretical Claims: The proposed method provides theoretical guarantees. For instance, the authors show theoretical results for the relationship between the conditional distribution of CPCL and the true conditional distribution.
Experimental Designs Or Analyses: Experiments evaluate CPCL across five continual learning methods such as SI and EWC.
Supplementary Material: Appendices provide detailed proofs of the theorems and additional descriptions of baseline continual learning methods.
Relation To Broader Scientific Literature: The paper builds on conformal prediction literature, particularly adapting it for continual learning where data from previous tasks is inaccessible.
Essential References Not Discussed: The literature review is adequate.
Other Strengths And Weaknesses: Strengths:
Provides theoretical guarantees.
Experimental evaluation across multiple methods.
Weaknesses:
Does not explore scenarios with task overlap tasks or distribution shift.
Other Comments Or Suggestions: Just to let the authors know that in Adobe, I can’t see either the legends or the axis numbers. I can only see them if I open the PDF with Preview. I have the same issue on two different lap tops, so it might be a problem with the images.
Questions For Authors: Can the method be extended to handle domain-incremental scenarios with gradual shifts in data distribution?
Are the intervals recalculated from scratch each time a new task is obtained, or could they be derived from previously computed ones?
How does the number of tasks affect the width of the intervals?
At time t-1, we obtain confidence intervals with a coverage probability of 1-\alpha, for example. At time t, we obtain confidence intervals again with the same coverage probability. Are the intervals from t-1 still valid? In other words, are they simultaneous confidence intervals?
Could the given intervals be compared with those obtained using other conformal prediction methods or alternative approaches?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: **R to W1.** Here we conduct experiments in domain-incremental scenarios with gradual distribution shifts. We use the dataset of CORe50 [1], which contains 50 objects (classes). Each object has been collected in 8 distinct indoor sessions characterized by different backgrounds and lighting. Due to the time limit, we only consider $\alpha=0.3$ and perform 5 runs. In each run, we randomly select one object from the 50 objects and form 8 tasks. The dataset of each task consists of samples which are collected in one session for the selected object. Therefore, 8 tasks corresponds to 8 distinct sessions, respectively. Other experimental settings are the same as those on real-world data (Section 6.2). After learning all tasks, we present the average coverages and length for 5 runs in the following table.
| CL method | Average coverage % | Average length |
| ------------------ | ---------- |---------- |
| SI | 71.26| 7.54|
| EWC | 72.76| 5.14|
| MAS | 73.02 | 4.93|
| DGR | 73.18 | 3.67|
| Finetuning | 71.03 | 16.38|
We observe that the average coverage for 5 runs with different continual learning methods are over the desired coverage 70%. These demonstrate the validity of our proposed CPCL in domain-incremental scenarios.
[1] Vincenzo Lomonaco, Davide Maltoni: CORe50: a New Dataset and Benchmark for Continuous Object Recognition. CoRL 2017.
**R to O1.** We deeply appreciate your valuable comments. We will check all the images.
**R to Q1.** Please refer to **R to W1.** of Reviewer KEqT.
**R to Q2.** After learning the new task $t$, we obtain the trained model $\hat{f} _{t}$ which is changed compared to the model $\hat{f} _{t-1}$ at time $t-1$. According to Equation (5), for each observation $Z _{i}^{j}=(X _{i}^{j},Y _{i}^{j}), j<t$ in the calibration set, the prediction error $\hat{\mu _{i}}^{j} =Y _{i}^{j}-\hat{f} _{t}(X _{i}^{j})$ is changed, which results in calculating different nonconformity scores. Therefore, QRF needs to be trained form scratch, which indicates that intervals should be recalculated from scratch too. It is interesting to explore whether they can be derived from previously computed one. We will study this issue in the future work.
**R to Q3.** Figures 3(b), 3(d) and 3(f) in the main file show the average interval length on real-world data. As the number of learning tasks increases, we find that the average interval length based on any continual learning method tends to increase. For example, the average length of the prediction interval ranges from 5 to 10 after learning task 5, while it remains below 5 after learning task 3, when we us SI as the continual learning method and $\alpha=0.1$.
**R to Q4.** As stated in **R to Q2.** of Reviewer KEqT, the trained model $\hat{f} _{t}$ at time $t$ is different from $\hat{f} _{t-1}$ at time $t-1$. QRF needs to be trained form scratch, which indicates that intervals should be recalculated from scratch too. Therefore, for each test sample, the corresponding prediction interval should be updated at time $t$ and the output prediction interval at time $t-1$ is not valid.
**R to Q5.** Here we conduct experiments on simulated data by split conformal prediction (SCP) [1]. Due to the time limit, we only consider Finetuning as the CL baseline. Other experimental settings are the same as those on simulated data (Section 6.1). We present the average coverages for 100 runs in the following table.
| $\alpha$ | Average coverage % ||
| ------------------ | ---------- |---------- |
| | SCP | CPCL |
| 0.05 | 92.58| 96.51|
| 0.1 | 86.47| 91.74|
| 0.15 | 81.69 | 86.23|
| 0.2 | 76.08 | 81.30|
| 0.25 | 70.82 | 77.05|
| 0.3 | 65.53 | 71.29|
We find that CPCL succeeds at all significant levels $\alpha$, but the average coverage for each $\alpha$ doesn't reach the desired value when using SCP. SCP requires the principle of data exchangeability which is violated in continual learning. Therefore, the coverage of SCP can not be guaranteed with significant level $\alpha$.
[1] Vovk, V. Conditional validity of inductive conformal predictors. Mach. Learn., 2013 | Summary: This paper explores **calibration in continual learning**, specifically focusing on **model uncertainty quantification** using **Conformal Prediction (CP)**. CP provides **theoretical coverage guarantees** under the assumption that data are **exchangeable**, but this assumption is violated in **continual learning**, where tasks are learned sequentially with limited access to past data.
To address this, the authors propose **CPCL (Conformal Prediction for Continual Learning)**, which:
- **Constructs a calibration set using replay mechanisms** to address the lack of past-task data.
- **Designs a nonconformity score function** to quantify uncertainty in predictions.
- **Uses Quantile Regression Forests (QRF)** to estimate conditional quantiles for prediction intervals.
- **Theoretically proves asymptotic coverage guarantees** of the prediction intervals.
- **Empirically validates CPCL** on simulated and real-world datasets, demonstrating **robust uncertainty quantification** and a link between **prediction interval length and catastrophic forgetting**.
Claims And Evidence: ### Supported Claims
- **CPCL provides well-calibrated uncertainty estimates:** Empirical results confirm that CPCL maintains high prediction interval coverage across **different continual learning methods (e.g., SI, EWC, MAS, DGR, Fine-tuning)**.
- **Theoretical coverage guarantee:** The paper proves that **CPCL's estimated conditional quantiles converge to true quantiles** as the number of calibration samples increases.
- **Forgetting affects prediction interval length:** Experiments show that as **more tasks are learned, forgetting increases**, leading to **wider prediction intervals**, aligning with theoretical expectations.
Methods And Evaluation Criteria: ### Strengths
- **Appropriate benchmark selection:** CPCL is evaluated on both **simulated regression tasks** and **real-world Tiny ImageNet data**.
- **Fair baseline comparisons:** The study compares CPCL with **state-of-the-art continual learning methods (e.g., EWC, MAS, DGR)**.
- **Clear evaluation metrics:** **Prediction interval coverage** and **interval length** provide useful insights into uncertainty quantification and forgetting.
Theoretical Claims: ### Correctness of Theoretical Claims
- The **asymptotic coverage guarantee** of CPCL is mathematically proven, ensuring that **prediction intervals maintain the desired confidence level** as the number of calibration samples grows.
- The connection between **forgetting and prediction interval width** is logically derived and supported by empirical results.
### Concerns
- **Lack of alternative quantile estimation methods:** While QRF is used for quantile estimation, comparisons with other methods (**e.g., neural quantile estimators**) would strengthen the theoretical claims.
- **Potential distribution shift issues:** The paper assumes that **previous task samples stored in the replay buffer remain representative**, but real-world continual learning often involves **domain shifts** that could affect calibration.
Experimental Designs Or Analyses: ### Strengths
- **Comprehensive ablation studies:** The paper evaluates the impact of **different continual learning methods on CPCL's uncertainty estimation**.
- **Visualization of uncertainty evolution:** **Coverage and interval length plots** clearly illustrate how **prediction uncertainty changes over multiple tasks**.
- **Experiments on both simulated and real-world data:** Ensures robustness of the proposed approach.
### Limitations
- **Limited discussion on failure cases:** The paper does not analyze situations where **CPCL fails (e.g., high forgetting rates, significant distribution drift)**.
Supplementary Material: No
Relation To Broader Scientific Literature: The paper makes a meaningful contribution by integrating Conformal Prediction with Continual Learning, extending existing methods while providing new insights into model forgetting and uncertainty quantification.
Essential References Not Discussed: The paper focuses on **uncertainty quantification (UQ) in continual learning**, yet it does not reference prior works that have explored UQ in this setting. Some missing references include:
- **Van de Ven et al. (2022)**: Explored **Bayesian continual learning** with uncertainty-aware priors. Their findings highlight the role of **uncertainty in mitigating catastrophic forgetting**, which aligns with the paper’s motivation but is not cited.
- *Van de Ven, G. M., et al. "Bayesian Continual Learning: Uncertainty-Aware Priors for Sequential Task Learning." NeurIPS, 2022.*
- **Osawa et al. (2019)**: Investigated **Monte Carlo dropout-based UQ** for continual learning, showing that model confidence degrades over sequential tasks.
- *Osawa, K., et al. "Practical Deep Learning with Bayesian Principles." NeurIPS, 2019.*
These works **precede CPCL** in addressing **uncertainty in continual learning** but use **Bayesian approaches** instead of conformal prediction. The paper could compare CPCL to Bayesian methods and discuss their relative strengths/limitations.
Other Strengths And Weaknesses: No
Other Comments Or Suggestions: No
Questions For Authors: No
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: **C1. Lack of ...**
***R to C1.*** Here we discuss the essential difference of QRF against quantile regression (QR) approaches [1] in continual learning. QR approaches estimate the conditional quantiles of the response variable over varying predictor variables. At training time, QR approaches need to minimize the pinball loss while QRF needs to construct trees. Since the pinball loss depends on the significant level $\alpha$, QR approaches can be computationally expensive to train for multiple significance levels. In contrast, QRF is trained without $\alpha$ and can provide the asymptotic coverage guarantee with significant level $\alpha$ (Theorems 1 and 2). Neural quantile estimation [2] is based on conditional quantile regression. It incorporates the concept of quantile regression and considers the case of multiple dimensions. Therefore, the difference of QRF against [2] is similar to that of QRF against QR.
[1] Koenker, R. and Bassett Jr, G. Regression quantiles. Econometrica: journal of the Econometric Society, 1978
[2] He Jia. Simulation-Based Inference with Quantile Regression. ICML 2024
**C2. Potential ...**
***R to C2*** In our paper, the previous task samples stored in the replay buffer will not be changed. Therefore, even if there is a significant distribution shift between tasks, the samples stored in the replay buffer remain representative for previous tasks.
**L1. Limited...**
***R to L1*** In the experiments of Section 6.2, we consider a CL baseline finetuning which greedily trains each task without considering previous task performance---hence introducing high forgetting rates as the number of learning tasks increases. From Figure 3, we observe that the most swarms with finetuning are over the desired coverage lines. These demonstrate the validity of our proposed CPCL. However, the average interval length based finetuning increases as learning tasks.
**Essential References Not Discussed**
***R to ERND.*** We refer to the presented references as [3] and [4], respectively, which will be discussed and cited in the revision. The works of [3,4] leverage Bayesian approaches to consider uncertainty in continual learning. [3] studies Bayesian continual learning with uncertainty-aware priors and highlights the role of uncertainty in mitigating catastrophic forgetting. [4] successfully trains deep networks with a natural-gradient variational inference method, VOGN, on a variety of architectures and datasets. Due to the benefits from Bayesian principles, the performance of [4] for continual-learning tasks is boosted. These works and CPCL all focus on uncertainty in continual learning. Compared with these works, CPCL provides asymptotic coverage guarantee with a significant level for the prediction intervals. Moreover, CPCL shows the relationships between the length of prediction intervals and forgetting, which are not introduced by these works. | null | null | null | null | null | null |
EncryptedLLM: Privacy-Preserving Large Language Model Inference via GPU-Accelerated Fully Homomorphic Encryption | Accept (poster) | Summary: This privacy preservation for cloud-deployed LLMs is considered. This work proposes a GPU-accelerated Fully Homomorphic Encryption(FHE) for LLMs. Evaluations are made on a GPT-2 LLM.
Claims And Evidence: See Strengths And Weaknesses below
Methods And Evaluation Criteria: See Strengths And Weaknesses below
Theoretical Claims: See Strengths And Weaknesses below
Experimental Designs Or Analyses: See Strengths And Weaknesses below
Supplementary Material: Yes.
Relation To Broader Scientific Literature: See Strengths And Weaknesses below
Essential References Not Discussed: See Strengths And Weaknesses below
Other Strengths And Weaknesses: strengthens:
1. Promising performance (200 times faster than the CPU baseline).
2. Source code of the implementation provided as supplemental material.
Weaknesses:
1. The empirical evaluation is only done for GPT-2 small (124M), which is somewhat like a toy model compared to today’s mainstream open-sourced LLMs like LLAMA2 (7B/13B). it remains questionable whether the conclusion made on the former still hold for the latter.
2. The effect of FHE approximation on the utility performance. I am afraid an evaluation on only three benchmarks can hardly capture the performance of an LLM.
3. Lack of ablation study on the choices of implementation
Other Comments Or Suggestions: 1. L804: citation error.
2. The paper is written like a tech report for a software. I found it hard to grasp many useful insights, neither theoretical nor technical.
3. Some more works (eg [A]) on homomorphic encryption for transformers can be discussed.
[A] HETAL: efficient privacy-preserving transfer learning with homomorphic encryption. ICML’23.
Questions For Authors: N/A
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: Thank you for your review.
We refer to the rebuttal of reviewer gAoN for additional benchmarks with larger models. We will include these in the next version. | Summary: This paper addresses the practical challenge of performing LLM evaluation, where clients preserve the privacy of their inputs and model owners retain privacy of the model. They propose using FHE to achieve the goal: encrypt the client inputs, perform evaluation homomorphically over encrypted data, and the results can only be decrypted by the clients who own the decryption key.
Specifically, the authors contribute a practical implementation of GPU-accelerated FHE scheme and use it to realize and evaluate an encrypted GPT-2 forward pass.
The results show that they achieve 200x faster than the CPU-based FHE implementation.
Claims And Evidence: The claim that GPU-accelerated FHE-based LLM inference makes non-real-time applications practical is supported by their evaluation results that end-to-end forward pass takes several seconds using GPU acceleration.
Methods And Evaluation Criteria: The reason why they choose FHE is well-justified, as it maintains the same client-server communication pattern as in non-private inference.
The authors' rationale for evaluating the GPT-2 model is sound. GPT-2 is open-sourced and is a representative of the transformer model.
Theoretical Claims: This is a practical paper, no theoretical claim made.
Experimental Designs Or Analyses: The finding that their modifications incur in little accuracy degradation with respect to the baseline model. The results are congruent with findings in the quantization literature. This alignment across different research fields reinforces the reliability of the experimental design.
page 6 col 1 line 312-313: we benchmark generating a token at position 128.
Please clarify why 128 is chosen.
page 7 col 1 line 330-333: the comparison is confusing as the larger security parameter takes less time than the smaller security parameter. Please clarify this.
Supplementary Material: N/A
Relation To Broader Scientific Literature: The method can be extended to other operations that require the forward-pass as a subroutine, such as fine-tuning on private data.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: Strengths:
This paper is well-written. I really enjoy reading the paper. The clear explanations and structuring makes the methodology and findings accessible to readers.
Weaknesses:
* While engineering aspects are well-executed, the paper lacks substantial theoretical contributions. Most of the techniques used in this paper are quite standard, e.g., use polynomial approximations to improve the performance.
* Although the authors discuss the differences with other works in the related work section, including numerical data comparisons could significantly strengthen this work.
Other Comments Or Suggestions: Typos:
* page 2 col 2 line 98-100: This required computing the table of max lookup values, which we based on the extensive tests of the approximate model. (remove “we”?)
* page 7 col 2 line 372: could easily be proprietary, and The resulting model can (remove “The”?)
Comments:
* page 6 col 1 line 317-318: We note a few important optimizations that are incorporated into this benchmark
I was confused the first time I read the paragraph below cuz there’s only one optimization (batch evaluation), while “Input & Output Sizes” is a prerequisite for the optimization. And also this optimization is not FHE specific, but more like a general optimization approach.
Questions For Authors: * Please clarify how do you balance between privacy (security parameter) and utility
* Is there any engineering efforts that worth mentioned? Like how much lines have been added to the original framework?
* “LM evaluation harness library to select optimal parameters for the tradeoffs between efficiency and accuracy.”
Could you please clarify how you decide the criteria to choose those parameters?
* page 5 col 1 line 272-274: Our runtimes can be extended to models with many more parameters by linearly scaling the transformer architecture.
Could you please explain explicitly how linear scaling would work?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for your review.
Q1: We set the parameters of our approximation so that accuracy is essentially unchanged. To see the evidence of how well our approximations scale, please see the rebuttal for reviewer gAoN.
Q2: We added roughly 10k lines of code to the core OpenFHE library as well as an additional 5k lines for the LLM layer benchmarks & associated tests. This was a complete reimplementation of the core CKKS algorithms optimized for the high-throughput parallelism of a GPU.
Q3: We chose three standard benchmarks to test our approximations, and we selected the three values in the submission as varying sufficiently from one another. In the rebuttal for gAoN, we give benchmarks on additional datasets.
Q4: The CKKS homomorphic operations are highly parallel, so the runtimes of the activation function layers will mostly scale with the size of the input. The runtime of the linear layers will also grow, although proportionally this will still be a small additional overhead. Aside from minor changes due to the circuit layout, the model runtime can be computed by summing the runtimes of the individual layers. | Summary: The paper presents a novel approach to privacy-preserving inference for large language models (LLMs) using GPU-accelerated fully homomorphic encryption (FHE), specifically targeting the GPT-2 architecture. It addresses significant privacy concerns associated with LLMs, particularly when deployed on third-party cloud services, by allowing clients to encrypt their queries and perform secure computations without disclosing sensitive information. The authors introduce a GPU-based implementation of the CKKS scheme, which enhances the performance of homomorphic operations, achieving speedups of over 200 times compared to traditional CPU methods. Key contributions include efficient approximations for layer normalization and SoftMax operations, which maintain model accuracy while optimizing computational efficiency. The paper also discusses the architecture of the neural network decoder block and the use of polynomial approximations for activation functions to facilitate secure evaluations under FHE. Experimental results demonstrate the feasibility and practicality of their approach for applications such as document summarization and fine-tuning on private data. Overall, the research significantly advances the field of secure LLM inference, making it more accessible for sensitive applications in areas like healthcare and finance.
Claims And Evidence: 1. I think the technical contribution is very weak for this work. I think author should better clarify the challenge for using GPU to perform this large-scale task, and what is the main difference from CPU.
2, Missing important citation [1], this work also using GPU to do large-scale machine learning model inference in FHE. How is the difference between this work and [1]?
Reference:
[1] Zhang, J., Yang, X., He, L., Chen, K., Lu, W. J., Wang, Y., ... & Yang, X. (2024). Secure transformer inference made non-interactive. Cryptology ePrint Archive.
Methods And Evaluation Criteria: see above
Theoretical Claims: none
Experimental Designs Or Analyses: none
Supplementary Material: none
Relation To Broader Scientific Literature: none
Essential References Not Discussed: see above
Other Strengths And Weaknesses: none
Other Comments Or Suggestions: none
Questions For Authors: none
Code Of Conduct: Affirmed.
Overall Recommendation: 1 | Rebuttal 1:
Rebuttal: Thank you for your review.
We assure the reviewer that implementing GPU-accelerated FHE is a highly non-trivial task, requiring the synthesis of dozens of algorithms & optimizations from prior works. We additionally implemented several optimizations derived from the design of custom ASIC & FPGA implementations of CKKS. This includes the fusing of operations into CUDA larger kernels to maximize throughput. Overall, we added roughly 10k lines of code to the core OpenFHE library. We are happy to provide more details of our implementation in a comparison to the work [1] of Zhang et al. We had previously excluded [1] from our comparisons in an earlier draft of this work, since prior versions of [1] had serious errors in the reported benchmarks. The current version of [1] is the latest in a series of revisions correcting these major issues. We have not had a chance to confirm their latest results, although based on the benchmarks reported in the latest version of [1] our bootstrapping is at least 10x faster. We are confident we can outperform this work when using the same resources & parameters. | Summary: This paper presents a GPU-accelerated implementation of CKKS-based fully homomorphic encryption (FHE) for non-interactive private LLM inference. Specifically, it focuses on enabling privacy-preserving (for users' sensitive data) access to proprietary LLMs (e.g., ChatGPT) for latency-tolerant tasks such as document summarization.
To make the model compatible with HE-only inference, and also to reduce the computational burden, the authors employ off-the-shelf approximation techniques for nonlinear operations such as Softmax, GELU, and LayerNorm. The authors have shown a remarkable speedup—approximately **200×** over a standard CPU-based implementation (openFHE)—on the GPT-2 small model (12 layers, 12 heads, 768 embedding dimensions). This acceleration is primarily achieved by optimizing bootstrapping operations, which constitute the dominant source of latency in CKKS-based FHE.
Claims And Evidence: Yes.
Methods And Evaluation Criteria: Yes.
Theoretical Claims: There are no theoretical claims made in the paper.
Experimental Designs Or Analyses: Yes. The experimental evaluation (presented in Table 1) is quite limited, and it could have been more comprehensive. There are two key limitations: 1) the authors have used only the GPT-2 small model, and do not show the implication of performance degradation incurred from the approximation of nonlinear operations for deeper and wider models. For example, what happens (to the efficiency gain and performance degradation) when we increase the number of layers (from 12 to 18 or 24) and/or context size (from 128 to 256); and 2) since the authors have used the pre-trained model and evaluated the performance degradation on downstream tasks, it should have been included a more diverse set of downstream tasks (from the llm-evaluation-harness library).
Ideally, the implications of approximations should also be shown for training from scratch. How much does it increase the perplexity?
Supplementary Material: Yes. I reviewed the Appendix (not the code uploaded by the authors).
Relation To Broader Scientific Literature: It could have been much better when it comes to the connection with the prior related findings/results. For instance, the paper does not mention the some of the prior work on GPU acceleration (HE and MPC), and also the methods for improving the bootstrapping performance.
Essential References Not Discussed: [1] Watson et al., Piranha: A GPU Platform for Secure Computation, USENIX Security 2022
While this paper does not accelerate FHE on GPUs but rather focuses on MPC-based acceleration for nonlinear operations, the authors should have included a discussion on whether their approach could be extended to accelerate LLM nonlinearities such as Softmax, GELU, and LayerNorm.
[2] Kim et al., Cheddar: A Swift Fully Homomorphic Encryption Library for CUDA GPUs, 2024
This paper directly focuses on GPU acceleration for CKKS-based FHE. Could the NTT acceleration presented in [2] be integrated with the authors' bootstrapping acceleration for further improvement? If so, discussing the feasibility, potential challenges, and expected benefits of such a combination would strengthen the paper and provide valuable insights for future work.
[3] Jha et al., AERO: Softmax-Only LLMs for Efficient Private Inference, 2024
This paper removes LayerNorm and GELU activations to enable faster private inference in hybrid protocol settings (HE + MPC). Given this design choice, would the authors' GPU-accelerated approach be even more beneficial for LLMs with fewer nonlinear components? A discussion on how the acceleration scales with different levels of nonlinearity would strengthen the paper and provide insights into the broader applicability of their method.
Other Strengths And Weaknesses: ### Strength
$\bullet$ The authors have provided the code implementation and promised to open-source it, which could be beneficial for the researcher working in this field.
$\bullet$ Writing is coherent and the paper is easy to follow.
Other Comments Or Suggestions: $\bullet$ The threat model presented in Section 1.3 could be more clearly articulated. It is not explicitly stated whether the setting assumes a semi-honest or malicious client/server, which is crucial for understanding the security guarantees of the proposed approach.
$\bullet$ There is an excessive emphasis on the basics of LLM architecture and cryptographic protocols in the main text, which could have been more concise. Meanwhile, some key experimental results have been relegated to the appendix. In particular, the results in **Appendix E** are crucial to the paper’s core contributions and should be included in the main text for better visibility and impact.
**Line #385** Substituting BatchNorm with LayerNorm in LLM does not work. See [3]
[3] Wang et al., Understanding the Failure of Batch Normalization for Transformers in NLP, NeurIPS 2022.
Questions For Authors: $\bullet$ Did you include the final LayerNorm layer (in the LM-head) for end-to-end latency? A GPT-2 model with the 12 layers has 2*12 +1 LayerNorm layers.
$\bullet$ Does the GPU acceleration improve the NTT kernel?
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: Thank you for your review.
The threat model here is semi-honest.
We wrote this paper with a broad audience in mind, including cryptographers who may not be familiar with the LLM circuit. The paper describes the details of the LLM circuit as it is necessary to completely implement the LLM as a homomorphic encryption circuit, so in a sense this is a description of the homomorphic computation that is benchmarked in our work.
We agree that the results in Appendix E are very important, and our implementation of GPU-accelerated homomorphic encryption is a core contribution of this work. We placed these results in the appendix since the main audience for this work is machine learning researchers who may not be familiar with the FHE bootstrapping operation. We are happy to move them to the main body.
Q1: Yes, the final Layernorm time is included in the final argmax time. We will clarify this in the next version.
Q2: Yes, all FHE operations are performed on CUDA device vectors without transferring back to the CPU. This includes all low-level polynomial operations like the NTT as well as higher-order FHE algorithms like key switching, automorphisms, and residue number system decomposition.
Larger models:
Since the submission, we have run additional experiments on larger models with nearly identical approximation parameters.
All accuracy benchmarks are reported with the standard, unmodified benchmark first followed by the model run with polynomial approximations.
GPT-2 Small (additional benchmarks)
- Social IQA: 0.366, 0.374
- MNLI: 0.337, 0.331
- SST2: 0.550, 0.556
- OpenBook QA: 0.164, 0.186
- ANLI-R1: 0.341, 0.341
- ANLI-R2: 0.339, 0.329
- ANLI-R3: 0.349, 0.348
- Wic: 0.492, 0.511
GPT-2 Medium
- Arc Easy: 0.491, 0.489
- PIQA: 0.676, 0.675
- Social IQA: 0.391, 0.393
- MNLI: 0.352, 0.354
- SST2: 0.614, 0.638
GPT-2 Large
- Arc Easy: 0.532, 0.533
- PIQA: 0.703, 0.707
- Social IQA: 0.396, 0.393
- MNLI: 0.359, 0.357
- SST2: 0.5, 0.5 | null | null | null | null | null | null |
Demystifying Catastrophic Forgetting in Two-Stage Incremental Object Detector | Accept (poster) | Summary: The paper focuses on catastrophic forgetting in the two-stage object detector. The authors first analyse the forgetting in component-level and reveal that RoI Head classifier is the primary cause of catastrophic forgetting. Then the authors propose Regional Prototype Replay (RePRE) to mitigate forgetting via replay of coarse prototypes and fine-grained prototypes. The authors also propose using Null Space Gradient Projection (NSGP) to eliminate prototype-feature misalignment. Experiments on VOC and COCO show that the proposed method, NSGP-RePRE, can significantly improve the performance of Faster-RCNN in IOD.
## update after rebuttal
After reviewing all the reviews and responses, my primary concerns have been addressed. At this point, I am inclined to accept.
Claims And Evidence: No.
The authors claim that 'In sequential tasks, the stability of the RPN recall ability is largely maintained.'. However, all experiments are conducted on VOC and COCO, lacking experiments on drastic variations in target scale or target aspect ratio between different tasks.
Methods And Evaluation Criteria: No.
Theoretical Claims: There is no Theoretical Claim in the paper.
Experimental Designs Or Analyses: No. The paper lacks experiments on more datasets. Conclusions drawn from COCO and VOC may not be universally applicable.
Supplementary Material: Yes. The reviewer has reviewed the supplementary material including Implementation Details & Generalization on unseen classes of RPN & Null Space Gradient Projection Details & Different strategy generating fine-grained prototypes & RePRE Performance with Coarse Regional Prototype Only.
Relation To Broader Scientific Literature: Previous works in the IOD field usually treats the detector as a whole, lacking a fine-grained analysis. This paper decouples localization and classification and analyzes catastrophic forgetting with experimental results in two-stage detectors at the component level.
Essential References Not Discussed: No.
Other Strengths And Weaknesses: ## Strengths
1. The paper identifies a meaningful perspective in IOD with two-stage detectors and propose a solution to mitigate forgetting in classification.
2. Experiments on two widely-used datasets are adequate. The proposed method reaches state-of-the-art on multiple datasets and settings.
3. The writing of the papre is easy to follow and it is clearly structured.
## Weakness
**Major**
1. The paper lacks experiments on more datasets with significant variations in target scale and aspect ratio, which makes the conclusions of the paper more limited.
2. The NSGP seems to be a simple application of previous method, which is less innotative.
**Minor**
1. The authors only use Faster R-CNN in experiments. It is suggested to try more two-stage detectors like Cascade-RCNN to verify the generalizability of the conclusions to two-stage detectors.
2. The ablation in Tab 4 is insufficient. The authors are suggested to conduct more experiments on other settings, such as VOC 10-10.
3. The paper lacks visualization results. Including visualization results that demonstrate how the proposed method corrects misclassifications would provide readers with a more concrete understanding of its performance.
Other Comments Or Suggestions: 1. A Grammatical error in line 258~259 should be corrected: "To capture the entire spectrum of useful information on the distribution of RoI features."
2. The citation of BPF (ECCV'24) should be a conference version.
3. The result of ABR in the last column of Tab 2 is incorrectly bolded.
Questions For Authors: 1. All experiments are conducted on VOC and COCO. Do the findings about catastrophic forgetting in Faster R-CNN still hold on datasets with significant variations in target scale and aspect ratio (such as remote sensing detection datasets)?
2. The author mentions that the baseline employs a pseudo-labeling strategy, and the reviewer is interested in the performance of the proposed method after removing the pseudo-labels.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thanks for the insightful comments.
**Q1:** Dataset concern.
**R1:** To show the generalizability of our key findings, we conducted experiments on a wildly used remote sensing detection datasets DIOR. **The three key findings still hold with different two-stage IODs.** As shown in this link [DIOR](https://anonymous.4open.science/r/aosdhoaihfoiahsodjasjiohf/d.pdf), all curves are aligned with VOC dataset. Our results show that the detector's RPN struggles with unseen data, as indicated by the red curves. However, the detector performs well on seen data, suggesting the RPN and the RoI Head's regressor remain resilient and do not forget previously learned knowledge on DIOR.
We also conducted experiments on DIOR with our framework, as shown in
|DIOR|5-5|||\||10-10|||
|-|-|-|-|-|-|-|-|
||1-5|6-20|1-20|\||1-10|11-20|1-20|
|Baseline|43.6|56.9|53.6|\||61.03|63.9|62.5|
|NSGP-RePRE|54.8|57.0|56.5|\||66.4|62.25|64.3|
Our framework surpass the baseline by 2.9\% in 5-5 setting and 1.8\% in 10-10 setting, further showing the effectiveness of framework.
**Q2:** NSGP's novelty concern.
**R2:** Although NSGP has been explored in incremental classification, it is non-trivial to apply NSGP in IOD. The following table demonstrates the performance applying NSGP from Backbone to RoI Head accumulatively under VOC 5-5 setting.
||Backbone|+FPN|+RPN|+RoIHead|Ours|
|-|-|-|-|-|-|
|NSGPonly|62.6|63.3|63|63.2|65.7|
The catastrophic forgetting in two-stage detectors is mainly caused by the severe classifier instability in the RoI Head. However, directly appling NSGP on these two-stage object detector (i.e., FPN, RPN,RoIHead) shows limited performance improvements and can not well address the classifier instability issue, as illustrated in the above Table.
Instead, the proposed Regional Prototype Replay (RePRE) module addresses this issue by replaying coarse and fine-grained region prototypes in the RoI Head's classification branch. NSGP serves as an assistant component in our framework by mitigating semantic drift caused by parameter updates, thereby preventing toxic replay in RePRE. As shown in the table, our RePRE achieves a +2.4% gain compared with +FPN, underscoring the effectiveness of our proposed framework.
**Q3:** Architecutre-specific concern.
**R3:** To show the generalizability of our key findings, we also conducted experiments with two popular two-stage detectors, i.e. Cascade-RCNN and Vanilla Faster RCNN. **The three key findings still hold with different two-stage IODs as shown in these links [CascadeRCNN](https://anonymous.4open.science/r/aosdhoaihfoiahsodjasjiohf/c.pdf) and [VanillaFasterRCNN](https://anonymous.4open.science/r/aosdhoaihfoiahsodjasjiohf/v.pdf).** Detailed discussion can also be found in our response to reviewer huSY R3.
**Q4:** Insufficient ablation concern.
**R4:** Thanks for the suggestion. We conducted ablation study in VOC 10-10 setting as shown in
||||VOC|(10-10)||
|-|-|-|-|-|-|
|NSGP|Coarse|Fine|1-10|11-20|1-20|
||||69.3|73.3|71.3|
|x|||71.8|73.2|72.5|
||x||70.5|73.8|72.1|
|x|x||73.7|73.2|73.4|
|x|x|x|75.3|72.7|74.0|
The same conclusion can be drawn from this table as in ablation study in 5-5 setting.
**Q5:** Visualization of the results.
**R5:** As shown in this link [visualization](https://anonymous.4open.science/r/aosdhoaihfoiahsodjasjiohf/vis.pdf), we visualized images from VOC2007 test set under 10-10 setting. Task 1 represents visualization with model from time step 1 while baseline and NSGP-RePRE represents the visualization results are from time step 2 trained with corresponding strategy. In (a) baseline forgets "boat". In (b) and (c), baseline forgets "cat" and "car" due to the interference of new classes "dog" and "motorbike". Our NSGP-RePRE successfully remembers old classes while learning new classes effectively, suggesting that our methods achieves better stability while retaining comparable plasticity compared with baseline.
**Q6:** The pseudo labeling concerns
**R6:** One major problem in IOD is that objects from past tasks can be included in the subsequent tasks yet their labels are not annotated. For example, airplanes will be labeled as "airplane" in the first task but considered as background in the subsequent tasks. Optimizing with wrong label will leads to a drastic performance drop. Pseudo labeling(Mo et al.,2024; Liu et al.,2023;) are wildly adopted to alleviate such performance drop. Thus, we also choose pseudo labeling as our baseline to avoid this problem.
We also conducted experiments under the setting of without pseudo label. As shown in
|W/o Pseudo Label|\||5-5|||\||10-10|||
|-|-|-|-|-|-|-|-|-|
||\||1-5|6-20|1-20|\||1-10|11-20|1-20|
|Baseline (w/o pseudo label)|\||0|28.2|21.2|\||14.5|66.9|40.7|
|NSGP-RePRE (w/o pseudo label) |\||50.5|47.8|48.5|\||66.2|58.9|64.3|
Our NSGP-RePRE achieves +20% performance gain compared with baseline, demonstrating the effectiveness of our framework.
---
Rebuttal Comment 1.1:
Comment: Thanks for the responses. It resolved my main concerns.
---
Reply to Comment 1.1.1:
Comment: We sincerely thank the reviewer for their valuable comments and constructive suggestions. We truly appreciate the time and effort you dedicated to reviewing our submission and the opportunity to clarify and improve our work. | Summary: The paper addresses the critical challenge of catastrophic forgetting in incremental object detection (IOD). The authors focus on the Faster R-CNN architecture and identify that catastrophic forgetting predominantly occurs in the RoI Head classifier, while the regressor remains robust across incremental stages. Based on this insight, they propose NSGP-RePRE, which combines Regional Prototype Replay (RePRE) and Null Space Gradient Projection (NSGP) to mitigate forgetting in the RoI Head classifier. The method achieves state-of-the-art performance on the Pascal VOC and MS COCO datasets under various incremental learning settings.
Claims And Evidence: Yes
Methods And Evaluation Criteria: Yes
Theoretical Claims: NA
Experimental Designs Or Analyses: Sound
Supplementary Material: The experiment part
Relation To Broader Scientific Literature: NA
Essential References Not Discussed: NA
Other Strengths And Weaknesses: Strengths:
1. The paper provides a significant insight into the nature of catastrophic forgetting in two-stage object detectors, specifically identifying the RoI Head classifier as the primary source of forgetting. This challenges conventional assumptions and offers a new direction for addressing forgetting in IOD.
2. Comprehensive experimental results.
3. Topic is interesting
Weaknesses:
1. More theorical analysis, such as complexity analysis can be provided.
Other Comments Or Suggestions: See the Strengths And Weaknesses
Questions For Authors: See the Strengths And Weaknesses
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We sincerely appreciate the reviewer's positvie feedback and insightful comment. The Questions and Responses are as follows.
**Q1:** More theorical analysis, such as complexity analysis can be provided.
**R1:** Thanks for the suggestions. We provide a comprehensive analysis of the parameter, computational, and memory complexity of NSGP-RePRE:
**Parameter Analysis:**
The origional detectors contains a total of 96.89 M trainable parameters. Our approach maintains the same parameter count, ensuring no increase in model complexity.
**Computational Complexity:**
To assess the computational complexity during training, we present the FLOPs for key components of the model, as shown in the table below:
| | forward | +RePRE | backward | +NSGP |
|-------|:---------:|:-----------------:|:----------:|:----------:|
| GFLOPs | 551.35 | +2.78 | 1102.7 | +118.1 |
It is important to note that the computational complexities of RePRE and NSGP do not scale with batch size, whereas the forward and backward passes of the detector do. As shown in the table, the majority of the computational cost during training arises from the detector's forward and backward passes. In contrast, RePRE and NSGP contribute only about 1% of the additional computation compared to the forward and backward operations when scaling batch size to commonly used 8.
We also present the actual training time for different components on 1 RTX 3090 GPUs in the following table:
| | Baseline | NSGP | NSGP+RePRE |
|-----------|----------|--------|------------|
| Time/iter | 0.714s | 0.719s | 0.720s |
This table suggests that the additional computational cost of NSGP-RePRE is minimal, adding only ~1% overhead per iteration compared to baseline training, which is aligned with our complexity analysis.
**Memory cost of RePRE:**
The memory footprint of our RePRE scales linearly with the increase of the number of classes. In our implementation, each class consumes approximately 3.8Mb of memory in float32 with each prototype consuming 0.38Mb. Our method achieves performance comparable to the previous example-based SOTA method, ABR, using only one coarse prototype per class and without relying on NSGP in the 10-10 setting. Additionally, it consumes about 25% of the memory required by ABR. As shown in
| VOC(10-10) | | | | |
|--------------|---------|-------|-------|-------|
| Type | Memory↓ | 1-10 | 11-20 | 1-20 |
| ABR | 15.5Mb | 71.2 | 72.3 | 72.0 |
| RePRE-Coarse | 3.8Mb | 70.5 | 73.8 | 72.1 |
| NSGP-RePRE | 38Mb | 75.3 | 72.7 | 74.0 | | Summary: The paper investigates catastrophic forgetting in incremental object detection using standard Faster-RCNN architecture. The authors show that catastrophic forgetting mainly happens in the RoI part of the model, and the regressor behaves more robustly while learning subsequent tasks. Based on their observations, the authors propose Regional Prototype Replay (RePRE) method, which mitigates classifier forgetting via replay of coarse and fine-grained prototypes and Null Space Gradient Projection (NSGP). NSGPRePRE is evaluated on the Pascal VOC and MS COCO datasets, where it demonstrates improved stability compared to the other IOD methods.
Claims And Evidence: The claims made in Section 3 are consistent with the experimental results.
However, the claim that the Avg metric reflects a better trade-off between stability and plasticity (Line 371) is problematic, and the authors do not provide a good justification for it. For example, separately evaluating the accuracy of base and novel classes after each incremental learning step would offer clearer insights into how the method balances stability and plasticity over time.
Methods And Evaluation Criteria: The proposed evaluation is well-suited for the problem.
Theoretical Claims: Not applicable.
Experimental Designs Or Analyses: See **Questions**.
Supplementary Material: Yes, I reviewed the whole appendix.
Relation To Broader Scientific Literature: The key contributions of this paper are rooted in and extend the broader literature on incremental learning and object detection, addressing critical gaps in prior work. Previous IOD methods do not dissect component-level contributions to forgetting, and this paper reveals classifier instability as a key source of forgetting in IOD.
Essential References Not Discussed: See **Questions**.
Other Strengths And Weaknesses: See **Questions**.
Other Comments Or Suggestions: See **Questions**.
Questions For Authors: 1. NSGP projects gradients into the null space of old tasks to prevent feature drift. Could this restrict the model's plasticity, especially when new tasks require significant feature adaptation? How does NSGP balance stability and plasticity?
2. RePRE requires storing multiple prototypes per class. How does the memory footprint scale with the number of incremental stages? Is there a risk of prototype redundancy or interference when handling highly similar classes?
3. The conclusion about catastrophic forgetting being localized to the RoI Head classifier is based solely on Faster R-CNN. Have the authors validated this finding on other two-stage architectures? If not, how can we ensure this is a generalizable insight rather than architecture-specific?
4. How critical is pseudo-labeling to NSGP-RePRE’s performance?
5. How does the NSGP affect training time compared to baseline methods? Is the method practical for real-time applications?
6. As shown in the results, the proposed method performs well on base classes. However, I noticed that in Tables 1, 2, and 3, the proposed method underperforms its counterparts on incremental tasks. Does this imply that the method overly prioritizes stability while exhibiting weaker plasticity for learning new tasks?
While the authors present a novel finding, their validation is limited to Faster R-CNN, with little evidence of broader applicability. Additionally, critical experimental validations are still missing. I am temporarily giving this paper a weak reject, but I will continue to follow the author's response and the comments from other reviewers.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thanks for the insightful comments.
**Q0: On the Avg metric.**
**R0:** We show the Avg performance at every step.
|10-10|Step1|\||Step 2|Base|New|Avg|All|
|-|-|-|-|-|-|-|-|
|Baseline|77.8|\||Baseline|69.3|73.3|71.3|71.3|
|BPF*|77.8|\||BPF*|71.8|73.4|72.6|72.6|
|NSGP-RePRE|77.8|\||NSGP-RePRE|75.3|72.7|74|74|
|5-5|Step1|\||Step2|Base|New|Avg|All|\||Step3|Base|New|Avg|All|\||Step4|Base|New|Avg|All|
|-|-|-|-|-|-|-|-|-|-|-|-|-|-|-|-|-|-|-|-|
|Baseline|77.4|\||Baseline|63.1|79.9|71.5|71.5|\||Baseline|64.7|76.1|70.4|68.5|\||Baseline|58.0|59.6|58.8|58.4|
|NSGP-RePRE|77.4|\||NSGP-RePRE|72.6|78.1|75.3|75.3|\||NSGP-RePRE|70.8|76.3|73.6|72.6|\||NSGP-RePRE|67.9|59.0|63.5|65.7|
All represents the mAP of all seen classes, e.g. 1-15 in 5-5 setting step 3. Our method achieves the best Avg and All mAP at every time step, showing its superior balanced stability-plasticity properties.
**Q1 & Q6:On the plasticity-stability trade-off.**
**R1:** The plasticity-stability trade-off is explicitly controlled by the nullity of the uncentered feature covariance. In our experiments, we adopt an adaptive approach VPT-NSP^2(Lu e al.,2024)
and achieved better trade-off.
**Q2: On the scaling of memory requirement and prototype interference risk.**
**R2:** The memory footprint of our RePRE scales linearly with increasing number of classes. Each class consumes approximately 3.8Mb, and each prototype consumes 0.38Mb.
The comparison between our method and previous exampler-based SOTA method ABR is shown below.
|VOC(10-10)|||||
|-|-|-|-|-|
|Type|Memory↓|1-10|11-20|1-20|
|ABR|15.5Mb|71.2|72.3|72.0|
|RePRE-Coarse|3.8Mb|70.5|73.8|72.1|
|NSGP-RePRE|38Mb|75.3|72.7|74.0|
We address redundancy by setting a distance between prototypes to capture the whole distribution of the feature space. Our results show consistent gains, suggesting effective handling of similar classes.
**Q3: conclusion on other two-stage architectures.**
**R3:** To show the generalizability of our key findings, we also conducted experiments with two popular two-stage detectors, i.e. Cascade-RCNN and Vanilla Faster RCNN without FPN and RoI Align. **The three key findings still hold with different two-stage IODs,** as shown in these links [CascadeRCNN](https://anonymous.4open.science/r/aosdhoaihfoiahsodjasjiohf/c.pdf) and [VanillaFasterRCNN](https://anonymous.4open.science/r/aosdhoaihfoiahsodjasjiohf/v.pdf). We conducted the same anotomy to these detectors in our paper, all curves are aligned with Faster RCNN using Pascal VOC 5-5. These two detectors' RPN Recall curve show that seen models even can surpass current model, suggesting that our findings are universal in most two-stage IODs.
We also evaluated our method on these detectors.
|CascadeRCNN|5-5|||\||10-10|||
|-|-|-|-|-|-|-|-|
||1-5|6-20|1-20|\||1-10|11-20|1-20|
|Baseline|57.2|65.4|63.4|\||69.7|74.3|72.0|
|NSGP-RePRE|66.8|66.6|66.7|\||74.1|74.6|74.4|
|VanillaFasterRCNN|5-5|||\||10-10|||
|-|-|-|-|-|-|-|-|
||1-5|6-20|1-20|\||1-10|11-20|1-20|
|Baseline|13.3|27.5|23.9|\||27.2|32.3|29.8|
|NSGP-RePRE|19.2|26.9|25.0|\||29.8|32.6|31.2|
Our method achieved noticeable performance improvement.
**Q4: Concerns about pseudo-labeling.**
**R4:** One major problem in IOD is that objects from past tasks can be included in the subsequent tasks yet their labels are not annotated. Optimizing with wrong label will lead to a drastic performance drop. Pseudo labeling(Mo et al.,2024; Liu et al.,2023;) are widely adopted to alleviate such performance drop. Thus, we also choose pseudo labeling as our baseline.
We also conducted experiments with pseudo label been ignored(neither foreground nor background). As shown in
|W/o Pseudo Label|\||5-5|||\||10-10|||
|-|-|-|-|-|-|-|-|-|
||\||1-5|6-20|1-20|\||1-10|11-20|1-20|
|Baseline (w/o pseudo label)|\||0|28.2|21.2|\||14.5|66.9|40.7|
|NSGP-RePRE (w/o pseudo label) |\||50.5|47.8|48.5|\||66.2|58.9|64.3|
Our NSGP-RePRE achieves +20% performance gain compared with baseline under the settings of without pseudo label module, demonstrating the effectiveness of our framework.
**Q5: How NSGP affect training time.**
**R5:** Our NSGP-RePRE maintains high efficiency.
NSGP introduces additional training time by SVD decomposition and null-space projection. Both SVD and projection's required time only increases with the size of the model. For SVD, it only computes once at every incremental step and only took around 30 seconds in our experiments, much less than the whole training time. As for null-space projection, it also adds only ~1% overhead per iteration compared to baseline training as shown in
||Baseline|NSGP|NSGP+RePRE|
|-|-|-|-|
|Time/iter|0.714s|0.719s|0.720s|
NSGP-RePRE does not introduces extra overhead during inference, which makes it practical for real-time application.
---
Rebuttal Comment 1.1:
Comment: Thank you for the response. Most of my concerns were resolved at this point.
Q0: BPF is still missing from the comparison for the 5-5 setting, while the results for the 10-10 setting show that it is competitive and outperforms NSGP-RePRE in terms of the performance on the new classes.
Q1&6: I would encourage including a discussion on this in the manuscript, instead of merely referring to another paper, as this is an interesting aspect of your approach.
Given the author's response and other reviews, at this point, I am also leaning toward acceptance of the paper.
---
Reply to Comment 1.1.1:
Comment: Thank you for your comment.
**Q0:** The original BPF paper does not provide source code for long-sequence IOD, nor does it report intermediate results at various learning stages. We are currently re-implementing BPF in the long-sequence setting, and we will update its performance results in our project page once we have a reliable and consistent implementation.
Regarding the lower performance on the "New" class, it's important to highlight that continual learning focuses on achieving a balance between *stability* (retaining previous knowledge) and *plasticity* (acquiring new knowledge), rather than optimizing performance on newly introduced classes alone. While our method shows slightly lower accuracy on "New" in the 10-10 setting, it achieves superior results on the Avg and All metrics—both of which are better indicators of the stability-plasticity trade-off. This suggests that our method performs better overall in the IOD task compared to competing methods.
**Q1 & Q6:** Thank you for your suggestion. We will consider incorporating it into the final version of the paper.
The stability-plasticity trade-off in our method is explicitly controlled through the nullity of the uncentered feature covariance matrix. We adopt the adaptive nullity selection approach proposed in VPT-NSP² (Lu et al., 2024), which dynamically determines nullity during training. To evaluate its effectiveness, we conduct experiments using different eigenvalue thresholds defined as $\beta \times \lambda_{min}$, where $\lambda$ denotes the eigenvalues.
The following table shows the mAP results under different β values in the 5-5 setting:
| β | 10 | 30 | 50 | 70 | 90 | 100 | Adaptive |
|--------|------|------|------|------|------|------|----------|
| mAP | 61.3 | 63.2 | 63.7 | 64.6 | 65.1 | 64.3 | **65.7** |
This result demonstrates that adaptive nullity achieves the best mAP, indicating that it provides the most effective balance between plasticity and stability in IOD.
We sincerely thank the reviewer for your valuable comments and constructive suggestions. Your feedback has been instrumental in helping us improve the quality of our work. | Summary: This paper addresses the challenge of catastrophic forgetting in incremental object detection, particularly in two-stage detectors like Faster R-CNN. The authors identify that catastrophic forgetting predominantly occurs in the RoI Head classifier, while the RPN and regression branches remain robust across incremental stages. Based on these findings, they propose NSGP-RePRE, a framework combining Regional Prototype Replay (RePRE) to mitigate classifier forgetting via coarse and fine-grained prototypes and Null Space Gradient Projection (NSGP) to counteract feature extractor drift by projecting gradients orthogonally to the subspace of old task inputs. This approach ensures alignment between prototypes and updated feature distributions. The experiments are conducted on the PASCAL VOC and MS COCO datasets under various incremental learning settings.
Claims And Evidence: Yes, the two components, RePRE and NSGP are well described, and the motivation is clear.
Methods And Evaluation Criteria: Yes, the paper adopted standard evaluation criteria as in the literature.
Theoretical Claims: There is no fundamental theoretical claim.
Experimental Designs Or Analyses: The experimental design follows previous works and the analysis is sound.
Supplementary Material: The appendix
Relation To Broader Scientific Literature: By addressing the unique challenges of IOD, RePRE contributes to the broader literature on replay-based incremental learning. NSGP focuses on null-space projections for incremental learning, whose core idea has been explored in “Training networks in null space of feature covariance for continual learning, CVPR 2021”
Essential References Not Discussed: No
Other Strengths And Weaknesses: Strengths:
1. Insights into Catastrophic Forgetting in IOD
2. Extensive experiments and good results
3. Clear writing.
Weaknesses:
1. Using NSGP has been explored in the literature for continual learning.
2. Although the specific form of replying regional prototype has not been explored, the idea of prototype based continual learning has been proposed in the literature.
Online Prototype Learning for Online Continual Learning, ICCV 2023
Prototype-Guided Memory Replay for Continual Learning, IEEE TNNLS 2024
The above two points make the paper's contribution is not so significant.
================= After rebuttal ================
Based on the authors' feedback and other reviews, I would like to upgrade my score from weak accept to accept.
Other Comments Or Suggestions: no
Questions For Authors: no
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We sincerely appreciate the reviewer's positvie feedback and insightful comment. The Questions and Responses are as follows.
**Q1**: Using NSGP has been explored in the literature for continual learning.
**R1**:Although NSGP has been explored in incremental classification, it is non-trivial to apply NSGP in IOD. The following table demonstrates the performance applying NSGP from Backbone to RoI Head accumulatively under VOC 5-5 setting.
| | Backbone | +FPN | +RPN | +RoIHead | Ours |
|----------|----------|--------|-------|-----------|------|
| NSGP only| 62.6 | 63.3 | 63 | 63.2 | 65.7 |
The catastrophic forgetting in two-stage detectors is mainly caused by the severe classifier instability in the RoI Head. However, directly appling NSGP on these two-stage object detector (i.e., FPN, RPN,RoIHead) shows limited performance improvements and can not well address the classifier instability issue, as illustrated in the above Table.
Instead, the proposed Regional Prototype Replay (RePRE) module addresses this issue by replaying coarse and fine-grained region prototypes in the RoI Head's classification branch. NSGP serves as an assistant component in our framework by mitigating semantic drift caused by parameter updates, thereby preventing toxic replay in RePRE. As shown in the table, our RePRE achieves a +2.4% gain compared with +FPN, underscoring the effectiveness of our proposed framework.
**Q2**: Although the specific form of replying regional prototype has not been explored, the idea of prototype based continual learning has been proposed in the literature. Online Prototype Learning for Online Continual Learning, ICCV 2023 Prototype-Guided Memory Replay for Continual Learning, IEEE TNNLS 2024
**R2**: While naively applying prototype-based methods on the classifier does achieves performance gain for the detector, our work makes distinct contributions in the context of IOD as we considered RoI Head's uniqueness in pre-processing MLPs before classifier. Further, we extend our method to fine-grained regional prototype replay to capture the distribution of regional object features, which is crucial for preserving old knowledge in continual learning.
To validate our design, we compare NSGP-RePRE against a baseline ("Classifier") that applies prototype replay only to the classifier (mimicking classification-focused approaches):
| | 5-5 | | |\|| 10-10 | | |
|------------------|------|------|------|-------|-------|------|----|
| | 1-5 | 6-20 | 1-20 |\|| 1-10 | 11-20 | 1-20 |
| w/o Prototype | 62.3 | 63.6 | 63.3 |\|| 71.8 | 73.2 | 72.5 |
| Classifier | 63.6 | 63.3 | 63.4 |\|| 73.2 | 73.3 | 73.2 |
| NSGP-RePRE | 64.6 | 66.1 | 65.7 |\|| 75.3 | 72.7 | 74.0 |
As shown in the table, our method outperforms "w/o Prototype" by +2.4%(5-5) and +1.5%(10-10). Though Classifier achieves performance gain compared with w/o Prototype, our method outperforms "Classifier" by +2.3% (5-5) and +0.8% (10-10). These results demonstrating that regulating only the classifier (as in classification-based works) is insufficient for IOD.
**In addition, we also find our finding still holds across two extra two-stage detectors and a remote sensing dataset, which further highlights the reliability of our findings and the effectiveness of our framework. The reviewer may find them in our response to Reviewer huSY(Q3, architecture) and Reviewer K17L(Q1,dataset).**
We emphasize that our goal is not to propose an overly complex method, but to offer a simple yet effective solution grounded in our analysis of catastrophic forgetting in two-stage detectors. We hope this work contributes to bridging the gap between continual learning for classification and detection.
In the end, we like to thank the reviewer for their valuable suggestions and questions. | null | null | null | null | null | null |
Meta-Reinforcement Learning with Adaptation from Human Feedback via Preference-Order-Preserving Task Embedding | Accept (poster) | Summary: This paper focuses on meta-reinforcement learning with human in the loop adaptation scenario and proposes the Preference-Order-preserving EMbedding framework. The core idea of this framework is that if the optimal strategy of the environment achieves better performance in the other task, then the two tasks are more similar and the task embeddings are also closer. During the training phase, the framework trains an encoder and aligns the task embeddings with the preferences. In the human in the loop adaptation phase, the framework employs a task embedding inference method.
## update after rebuttal
My concern was resolved, and I raised my score.
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: The authors propose a novel method building upon the broader scientific literature.
Essential References Not Discussed: No.
Other Strengths And Weaknesses: Strengths:1.
1.This paper focuses on meta-RL with human-in-the-loop adaptation, which I believe is an important topic.
2.The authors perform an evaluation on MuJoCo and Meta-World, demonstrate better performance compared to SOTA methods.
3.The paper is well-written, clearly explaining its contributions and well-grounded in prior literature.
Weaknesses:
The use of the policy optimzation loss function to replace the optimal policy in Algorithm 1 requires further discussion.
2.The motivation behind Algorithm 2 needs to be explained in more detail.
3.Additionally, experiments on dynamic changing tasks should be included.
Other Comments Or Suggestions: No.
Questions For Authors: 1.In Algorithm 1, the policy optimization loss is used to replace the optimal policy, while the preference loss requires the policy to be optimal. However, both losses are used simultaneously at the beginning of training. Would it be better to use only the policy optimization loss initially and introduce the preference loss after n epochs?
2.I still cannot fully understand why Equation (9) and line 17 of Algorithm 2 are designed in this way. Could the authors provide further explanation in plain language as to why this formulation leads to high query efficiency?
3.In Algorithm 2, would it be beneficial to further query the preferences of z in Q? For example, based on the pairs ($z_{1}$,$z_{2}$) and ($z_{3}$,$z_{4}$) in Q, could querying ($z_{1}$,$z_{3}$) lead to better results.
4.The method should also be applicable to tasks with dynamic changing. How does the method perform in such environments?
If the authors address the concerns I have raised, I'm willing to increase my score.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We are grateful and indebted for the time and effort invested in evaluating our manuscript and for all the suggestions to make our manuscript better.
>**Weakness 1 and Q1**
**Answer:** Thanks for pointing out the important observation. In both the existing context-based meta-RL methods, such as PEARL (Rakelly et al., 2019), and this paper, the ideal case of the meta-training can be using the optimal policy to reconstruct the decoder policy, and using the optimal policy to train the encoder. As you kindly mentioned, this can help avoid the error due to the current policy being not optimal. However, the optimal policies are not accessible, we have to replace the optimal policy reconstruction loss by the policy optimization loss.
In PEARL, the authors also use the policy optimization loss to train the output conditional policy (the decoder policy) and train the encoder simultaneously at the beginning of training. Although the policies during the training for the encoder are not optimal, the method is shown to be effective and efficient. One reason could be that although the policies are not optimal, they could provide an effective approximation to guild the optimization during the training to the correct direction. Therefore, we follow the same encoder-decoder training pattern in this paper, which keeps the algorithm statement concise.
>**Weakness 2 and Q2**
**Answer:** Explanation of Equation (9), i.e., $(\hat{z}^{\prime}, \hat{z}^{\prime\prime})={\arg\min}_{z^{\prime},z^{\prime\prime} \in \mathcal{Z}_k}( \max \lbrace|\mathcal{Z}^{(1)}|,|\mathcal{Z}^{(2)}| \rbrace )$:
In Equation (9), $\mathcal{Z}^{(1)}=\lbrace z\in \mathcal{Z}\_k: S(z,z^{\prime} ) >\_\epsilon S(z,z^{\prime\prime} )\rbrace$ and $\mathcal{Z}^{(2)}=\lbrace z \in \mathcal{Z}\_k: S(z,z^{\prime\prime} ) >\_\epsilon S(z,z^{\prime})\rbrace$.
When $z^{\prime}$ is preferred over $z^{\prime\prime}$, i.e., $S(z,z^{\prime} ) >\_\epsilon S(z,z^{\prime\prime} )$, any embedding in $\mathcal{Z}^{(1)}$ will satisfy the preference condition and remain to the valid embedding candidate. Similarly, when $z^{\prime\prime}$ is preferred over $z^{\prime}$, i.e., $S(z,z^{\prime\prime} ) >\_\epsilon S(z,z^{\prime} )$, any embedding in $\mathcal{Z}^{(2)}$ will remain as the valid embedding candidate. If the number of the remaining valid embedding candidates is smaller, the range of the valid embeddings will be quickly narrowed, and then the query efficiency will be higher.
Therefore, the goal of Equation (9) is to make the number of the remaining valid candidates as small as possible.
As we do not know what the queried preference is and which set of $\mathcal{Z}^{(1)}$ and $\mathcal{Z}^{(2)}$ will be remaining, we have to consider the worst case, i.e., the one between $\mathcal{Z}^{(1)}$ and $\mathcal{Z}^{(2)}$ with the larger size
will be remaining. Therefore, Equation (9) first takes the set $\max \lbrace |\mathcal{Z}^{(1)}|,|\mathcal{Z}^{(2)}|\rbrace$ to pick the larger set in $\mathcal{Z}^{(1)}$ and $\mathcal{Z}^{(2)}$, and then minimizes its size.
Explanation of line 17 in Algorithm 2, i.e., $z^k=
\mathop{\arg\max}\_{z \in \mathcal{Z}_k} {\sum}\_{(z^{\prime},z^{\prime\prime}) \in \mathcal{Q}\_k} \log \mathrm{Pr} [S(z,z^{\prime} )>S(z,z^{\prime\prime})]$:
In the $k$-th iteration of the human-in-the-loop adaptation, the candidate embedding set $\mathcal{Z}_k$ includes multiple valid embedding candidates. However, we need to pick one as the output for the $k$-th iteration. Therefore, line 17 is to use the maximum likelihood over all the valid embedding candidates in $\mathcal{Z}_k$ to determine the output task embedding $z^k$.
>**Q3**
**Answer:** After query the preferences of $(z_1,z_2)$ and $(z_3,z_4)$, it will be beneficial from querying $(z_1,z_3)$. However, $(z_1,z_3)$ is not the most query-effective pair to be queried. As mentioned in the **Answer to Q2**, we use Equation (9) to determine which pair is the most query-effective.
Note that, in Algorithm 2, sampling two new embeddings other than $z_1, z_2, z_3, z_4$ in $Q$, incurs almost no cost, as it merely involves sampling from a normal distribution. However, the human preference is the most expensive step in the human-in-the-loop adaptation. Therefore, $(z_1,z_3)$ in $Q$ will not be used to query the human preference if it is not the most query-effective pair computed by Equation (9).
>**Weakness 3 and Q4**
**Answer:** Our method cannot handle tasks in which the dynamics change over time within a single task. If the dynamics is changing over time within any single task. When the task is revealed to the agent, the agent needs to query a human for preference comparison gradually and optimize the policy based on all the historical preference queries. However, when the dynamics change over time, the historical preference queries from humans may become invalid, which leads to a wrong direction for the policy optimization. Solving tasks with dynamics changing over time is an interesting future work. | Summary: This paper presents a novel meta-reinforcement learning (meta-RL) framework called Preference-Order-Preserving EMbedding (POEM), which enables test-time preference-based human-in-the-loop adaptation of the meta-RL policy. The main research problem is how to meta-train a policy when there exists a discrepancy between the reward feedback available at training time, and human preference-only feedback at test time. The paper proposes a preference-order-preserving task embedding algorithm that maps tasks into a latent space where task embedding similarity preserves preference orderings. At test-time, the method infers task embeddings from human preference queries and finds the best task-specific policy. Both theoretical and empirical results are presented in the paper. Theoretical results include a provably preference-order preserving similarity metric that addresses an issue with standard cosine similarity, and convergence guarantee for the adapted policy at test time. Empirical results compare POEM with baseline meta-RL methods such as ANOLE and MAML on standard simulated robotic continuous-control domains, showing significant improvement.
Claims And Evidence: 1. The paper presents a preference-order preserving task encoder for context-based meta-RL learning that enables human-preference adaptation at test-time.
This claim is strongly supported by the description of POEM, theoretical derivation of similarity and the resulting encoder implementation, theoretical convergence guarantee, and details on the meta-train and adaptation algorithms.
2. POEM achieves performance comparable to meta-RL oracle, with a 20%-50% improvement over baselines on standard continuous control tasks.
This claim is strongly supported by experiment results on nine continuous control environments using standard benchmarks (MuJoCo and MetaWorld) and comparisons against multiple baselines (ANOLE, MAML-reward).
Methods And Evaluation Criteria: The methods and evaluation criteria used in the paper are mostly appropriate for the problem.
One minor weakness in the evaluation is the experiments are limited to continuous control robotics tasks, and the task spaces are mostly target locations. In these setups the level of difficulty in generalizing to different goals may not be very high. How would POEM perform in more complex task spaces?
Theoretical Claims: The paper makes 2 theoretical claims, both supported by proofs.
Theorem 1: Proves that an embedding space can be constructed where task similarity aligns with preference order.
Theorem 2: Shows that the adapted task embedding converges to the true task embedding with sufficient preference queries.
Experimental Designs Or Analyses: The experimental design is well done, with ablations for different components of POEM. Details of the experiment sets, including evaluation tasks, hyperparameters, are given. Experiments also study how noise in the preference oracle affects the learned policy.
Supplementary Material: N/A
Relation To Broader Scientific Literature: The paper is well-placed within existing works on context-based meta-RL.
Essential References Not Discussed: None.
Other Strengths And Weaknesses: Presentation of the paper is a clear strength. From motivation to the theoretical results to implementation choices are all clearly explained.
Other Comments Or Suggestions: L196, right column “the embedding \tau_{\pi}” -> “the embedding \tau_{r}”
L324, left column “PREAL” -> “PEARL”
L347, right column “mile” -> “mild”
L383, right column “APACE” -> “POEM”
L760, “mile” -> “mild”
Questions For Authors: None.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We are grateful and indebted for the time and effort invested in evaluating our manuscript. Thanks for the typo reminders and the suggestions to make our manuscript a better and stronger contribution.
>**Methods And Evaluation Criteria: One minor weakness in the evaluation is the experiments are limited to continuous control robotics tasks, and the task spaces are mostly target locations. In these setups the level of difficulty in generalizing to different goals may not be very high. How would POEM perform in more complex task spaces?**
**Answer:** In the conducted experiment, MetaWorld-ML10, the task is defined by the type of manipulation rather than the target location. The task family includes multiple types of manipulation tasks. As shown in Figure 8 (page 17), the interactions between the robot and the environment vary across tasks, encompassing different types of manipulation such as ‘assembly,’ ‘basketball,’ and ‘door opening.’ The training task set in this benchmark is highly heterogeneous, making the task space complex. As shown in Figure 5, the proposed method achieves a 50\% improvement over the baselines on MetaWorld-ML10.
---
Rebuttal Comment 1.1:
Comment: I thank the authors for the rebuttal. I maintain my original score. | Summary: The paper presents a framework for meta-reinforcement learning (meta-RL) called Preference-Order-preserving Embedding (POEM), which aims to facilitate few-shot adaptation to new tasks using human preference queries instead of traditional reward signals. The framework comprises a task encoder that maps tasks into a preference-order-preserving embedding space and a decoder that generates task-specific policies from these embeddings. During the adaptation process, the encoder efficiently infers embeddings for new tasks based on human preferences, ensuring that task embeddings reflect similarity in task performance. The authors provide theoretical guarantees for the convergence of the adaptation process to optimal task-specific policies and demonstrate through experiments that POEM significantly outperforms existing methods, achieving a 20%-50% improvement in performance on various continuous control tasks.
Claims And Evidence: No. The approach is quite similar to the work proposed by ANOLE. The only difference is the partitioning of the embedding into reward and policy spaces, which seems like a relatively incremental improvement.
Methods And Evaluation Criteria: Yes . The method tries to solve very relevant problem in RL.
Theoretical Claims: Yes. However, Theorem 2 requires the encoder-decoder network to be well-trained. However, the definition of "well-trained" is unclear, as the policy reconstruction loss is not used initially, and it is not mentioned when it starts being used. How can we ensure that the encoder-decoder is properly trained?
Experimental Designs Or Analyses: The authors compute extensive results, demonstrating impressive improvements over the state-of-the-art. However, a) it is unclear what would happen if the environment configuration changes across tasks. b) If there is an imbalance in tasks distribution, it could affect π-θ, which in turn might introduce an inductive bias in the encoder. This issue is not addressed or discussed in the paper.
Supplementary Material: Yes
Relation To Broader Scientific Literature: The approach of learning composite features that consist of both reward and policy in the embedding is non-trivial. The using of human feedback data to infer the task embedding instead of using encoder and context in meta-test phase is innovative
Essential References Not Discussed: SoA is satisfactory
Other Strengths And Weaknesses: Strength
The paper formulates the theorem and its proof in a satisfactory manner.
The authors also compute extensive results, demonstrating impressive improvements over the state-of-the-art.
Weakness
The comparison with ANOLE might not be entirely fair. In their paper, they meta-train for 4M steps on the ant task and 2M steps on the cheetah task, while this paper only trains for 1M steps. It is unclear what would happen if they trained for a similar number of steps, making direct comparisons of the results problematic.
Limited ablation study: The paper lacks an ablation study on the selection of hyperparameters.
The training details are also limited. During the meta-test phase, if multiple new tasks (T4, T5) arise, what will happen to the previously learned tasks (T1, T2, T3)? Will the learned meta-tasks perform the same way?
There are several notational and spelling errors throughout the paper, which make it difficult to understand the concepts. For instance, in lines 196-200.
Other Comments Or Suggestions: Nothing
Questions For Authors: Refer weakness section
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: >**Claims and Evidence: The approach is quite similar to the work proposed by ANOLE.**
**Answer:** The partitioning of the embedding into reward embedding and policy embedding spaces is only an initial and minor design of the paper. The main contribution of the proposed method is that we train a preference-order-preserving task encoder, which establishes a connection between task embeddings and human preferences. This connection facilitates the efficient inference of task embeddings for new tasks during human-in-the-loop adaptation.
In terms of the algorithm design, as you pointed out, this paper first designs an encoder that partitions the embedding space into reward embedding space and policy embedding space. Second, based on the embedding space, we prove that an encoder exists under the embedding space partition, which holds the preference-order-preserving property (Property 1 in Section 4). Third, in Section 5, we train an encoder that enforces that Property 1 holds by using the preference loss term (equation (6) in line 241), which penalizes violations of Property 1. Fourth, in Section 6, the preference-order-preserving property of the encoder enables the task embedding inference from human preferences for the human-in-the-loop adaptation.
Note that all the above four steps of the algorithm design are different from ANOLE, which addresses the issue of ANOLE that the task encoder cannot capture preference-related features across tasks.
>**Theoretical Claims: The definition of "well-trained" is unclear. The policy reconstruction loss is not used. How to ensure the encoder-decoder is properly trained?**
**Answer:** The definition of "well-trained" is given by the three assumptions of Theorem 1. Specifically, the assumption (i) (lines 375-377, Theorem 1) states that the posterior distribution is the normal distribution; the assumption (ii) (lines 377-379) requires that Property 1 holds, i.e., the preference-order-preserving property of the encoder holds; and the assumption (iii) (lines 379-381) requires that the optimal policy is accurately reconstructed.
To achieve the above three requirements, i.e., the encoder-decoder network is well-trained, we use the KL divergence loss term in line 273 to achieve assumption (i), use the preference loss in Equation (6) (line 240) to achieve assumption (ii), use the optimal reconstruction loss in Equation (5) (line 235) to achieve assumption (iii). Therefore, including the policy reconstruction loss, all the losses included in Section 4 are used to support Theorem 2.
>**Experimental Designs or Analyses a)**
**Answer:** In the conducted experiment, MetaWorld-ML10, the tasks family has multiple types of manipulation tasks. As shown in Figure 8 (page 17), the interactions between the robot and the environment are different for different types of manipulation tasks, and therefore their state transition functions are different and change. For example, it is easy to see that the state transition in the "assembly" task and that in the "basketball" task are different. As shown in Figure 5, the proposed method achieves 50\% improvement over baselines on MetaWorld-ML10.
>**Experimental Designs or Analyses b)**
**Answer:** There are several works, such as [1,2], addressing the issue of imbalance in task distribution in meta-learning/meta-RL. Their approaches are agnostic to the meta-RL methods and can also be used to address the issue in this paper. However, this paper primarily focuses on a new problem of meat-RL with human-in-the-loop adaptation. Addressing the issue of imbalance in task distribution is an interesting future work.
[1] "Learning to Balance: Bayesian Meta-Learning for Imbalanced and Out-of-distribution Tasks", 2020.
[2] "Improving Generalization of Meta Reinforcement Learning via Explanation", 2024.
>**Weakness 1**
**Answer:** The numbers of steps between this paper and ANOLE are exactly the same for the ant task and the cheetah task. In both this paper and ANOLE (Ren et al., 2022), cheetah-vel uses 1M steps (check the first figure in Figure 5 in this paper and the second figure of Figure 1 in ANOLE paper), cheetah-fwd-back uses 2M steps (check the first figure in Figure 9 in this paper and the first figure of Figure 1 in ANOLE paper). In this paper, we also use 4M steps on the ant task (check the second and third figures in Figure 9 in this paper).
>**Weakness 3**
**Answer:** Meta-RL with human-in-the-loop adaptation is to train a meta-model from the training tasks (T1, T2, T3), such that it can be adapted to new tasks with limited human preference queries. The learned meta-model is fixed during the meta-test phase. When a new task T4 arises, the meta-model learned from (T1, T2, T3) will be adapted to solve T4. Similarly, when a new task T5 arises, the meta-model will be adapted to solve T5. If any of the training tasks T1, T2, T3 arises in the meta-test, the meta-model is adapted to solve the task, which is easier than solving a new task T4. | Summary: The authors present the adaption via Preference-Order-preserving EMbedding (POEM) framework. Their key insights that are if the trajectory of a task is distilled into an embedding, the similarities between tasks should be evident in these embeddings and that the optimal policy on one task should do sufficiently well on another if there is sufficient enough similarity. They leverage these properties to create an algorithm that allows a human in the loop to do a preference-based selection between two policies to progressively move closer to the already-known policy that works best for the new task. This is essential due to the new task not providing the model with an environmental reward. They further include a relaxation on their initial insight (trajectory similarity being captured in embeddings) to account for human error in the preference selection.
Claims And Evidence: The authors claim a three-fold contribution in being the "first to propose the preference-order-preserving task encoder for context-based meta-RL training, which establishes a connection between task embeddings and human preferences"; experiments with their new framework conducted in a modified Mujoco and MetaWorld; and a proof for the theoretical result for their algorithm which guarantees convergence to the optimal task-specific policy.
No claims are problematic aside from the second, primarily because I am unclear how the environments were modified despite section D in the appendix.
Methods And Evaluation Criteria: The proposed methods follow clearly from Insights 1 and 2. I could see issues with Property 1 being called into question in scenarios where similarity between task embeddings may not be sufficient to ensure policy transferability, such as long-horizon dependencies, however I believe the relaxation in equation (8), while explained to be used to account for noise in human preference selection, should also clarify this. The environments also are well-suited to testing the proposed algorithm, though I would appreciate more detail about how the human-in-the-loop was given the trajectories (ie, text description, final reward, video?)
Theoretical Claims: I have read through and do not see any issue with the proofs provided in Appendix B.
Experimental Designs Or Analyses: I've read through the task descriptions of how the authors evaluated their methods in the corresponding environments and do not see any issue with these tasks, nor do I feel the environment to be invalid for the proposed algorithm. The primary concern is not understanding how these environments were modified. I did not see this explicitly outlined in D1 or D.2.
Supplementary Material: I have read through the appendix and referenced the material multiple times throughout this review.
Relation To Broader Scientific Literature: The key contributions of this paper are very related to the fields of RL, specifically meta-RL, continuous control and preference ordering. I believe these contributions to be relevant to the field of Machine Learning as a whole.
Essential References Not Discussed: I am not aware of any essential references not discussed.
Other Strengths And Weaknesses: This is a very strong paper. Technically, outside of lacking a few details that I may have just missed, I cannot find any fault with the paper. The proposed method is very clearly motivated and the only issues I could think of regarding their methods were already addressed. They show strong results in their evaluation and justify their approach with a rigorous proof.
Other Comments Or Suggestions: Despite the technical strength of this paper, I take very strong issue with the related work being relegated to the appendix. Even if the authors only use half of a column to address it in the main paper, I believe it is critically important for previous and related work to be given its proper acknowledgement by the scientific community. This is the primary motivating factor behind my score.
Questions For Authors: 1.) Could the authors explain how the policies were presented to the human-in-the-loop during evaluation? How many iterations of this were required per task?
2.) Could the authors please explain the difference between the base Mujoco and their modified version?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We are grateful and indebted for the time and effort invested in evaluating our manuscript and for all the suggestions to make our manuscript a better and stronger contribution.
>**Methods And Evaluation Criteria 1: I could see issues with Property 1 being called into question in scenarios where similarity between task embeddings may not be sufficient to ensure policy transferability, such as long-horizon dependencies, however I believe the relaxation in equation (8), while explained to be used to account for noise in human preference selection, should also clarify this.**
**Answer:** In this manuscript, we do **not** claim that, Property 1 always holds, and the similarity between task embeddings is sufficient to ensure the policy preference, for any encoder.
Instead, we claim and prove that in Section 3, under the MDP (including the case of long-horizon dependencies), **there exists** a task encoder such that Property 1 holds, i.e., there exists an encoder such that the similarity ordering of task embedding pairs is expected to align with human preference order. Next, in Section 4, we train an encoder that enforces that Property 1 holds under the encoder.
To achieve this, we design a loss term for the encoder network, the preference loss term (equation (6) in line 241), which penalizes violations of Property 1.
Therefore, although Property 1 may not be naturally satisfied without the training, once the encoder is trained under the supervision of the preference loss term, Property 1 holds approximately.
Furthermore, as you kindly pointed out, we also incorporate the relaxation in Equation (8) to account for noise in Property 1, enhancing the algorithm’s robustness.
>**Methods And Evaluation Criteria 2: I would appreciate more detail about how the human-in-the-loop was given the trajectories**
**Answer:** During the meta-test (human-in-the-loop adaptation), a new task ${\mathcal{T}}_{new}$ is given. The agent explores the environment and provides two trajectories (the rewards along the trajectories are unknown) to the human. Then, the human will tell the agent which one is better, and the agent will adapt the policy according to this human feedback.
One time of the human preference query is denoted as one iteration of the human-in-the-loop adaptation.
The detail of the human feedback is introduced in Section 2, lines 95-109.
>**Experimental Designs or Analyses: The primary concern is not understanding how these environments were modified.**
>**Question 2: Could the authors please explain the difference between the base Mujoco and their modified version?**
**Answer:** Thanks for pointing out the confusion. In this paper, we do not modify the environment of Mujoco. Instead, we directly use the environment in Mujoco and design the reward functions for multiple tasks for the meta-RL setting.
The details of the reward design are shown in Appendix C.2.
To avoid the confusion, we will modify the "Modified Mujoco" to "Mujoco".
>**Suggestions: Despite the technical strength of this paper, I take a very strong issue with the related work being relegated to the appendix. Even if the authors only use half of a column to address it in the main paper, I believe it is critically important for previous and related work to be given its proper acknowledgment by the scientific community. This is the primary motivating factor behind my score.**
**Answer:** Thanks for pointing it out. In the modified version, we will move the related work section in Appendix A (lines 608 to 662) to the main body of the paper.
In the related work section, we comprehensively review the works related to (i) meta-RL methods, (ii) RL from human feedback (RLHF), and (iii) methods for meta-RL with human-in-the-loop adaptation, and provide details of the comparisons between the problem settings, the problem formulations, and the algorithm designs in this paper and those in the existing works. Specifically, in (i), we discuss three categories of meta-RL methods and whether they can be applied to the problem of meta-RL with human-in-the-loop adaptation. In (ii), we discuss the existing methods for RLHF and the motivation of studying meta-RL with human-in-the-loop adaptation based on RLHF. In (iii), we discuss the existing methods for meta-RL with human-in-the-loop adaptation, including ANONLE and meta-reward, and discuss the differences between their algorithm designs and this paper.
>**Question 1: Could the authors explain how the policies were presented to the human-in-the-loop during evaluation? How many iterations of this were required per task?**
**Answer:** Please refer to the answer to **Methods And Evaluation Criteria 2** for the explanation of the human-in-the-loop adaptation.
As shown in Figures 5 and 10, we conduct at most 10 iterations for human-in-the-loop adaptation for each task, and it usually requires about 5 iterations to achieve the near-optimal performance per task. | null | null | null | null | null | null |
From Complex to Atomic: Enhancing Augmented Generation via Knowledge-Aware Dual Rewriting and Reasoning | Accept (poster) | Summary: The authors propose a knowledge aware rewriting and reasoning framework, a variant of retrieval augmented reneration (RAG), which is suitable for multi hop question answering tasks since it can aggregate knowledge from different documents. It consists of 4 steps: knowledge atomizer, query proposer, atomic retriever and atomic selector. During knowledge atomizing, a chunk is given to a LLM and asked to produce as many questions as possible whose answer is contained in the given chunk -- this will be included in the knowledge base together with the original chunk. In the next step, a LLM is prompted to break down the original question is broken down into subquestions (atomic query proposals) and if there are any chunks/question pairs from previous step in the knowledge base, these are passed in the context. The next step is the atomic retriever, which uses traditional similarity search with cosine similarity to retrieve top-k atomic questions/chunks that are most similar to the query proposals. Finally, a LLM is again used to select which question/chunk is most useful for the atomic query proposal. The experiments section showcase that their method is competitive with respect to other baselines ( RAG, zero shot CoT, Self-Ask, IRCoT and ProbTree) wrt F1 and using a LLM evaluator.
Claims And Evidence: The claims made in the submission supported by clear and convincing evidence
Methods And Evaluation Criteria: The authors showcase their method's performance using three different multi hop QA datasets : hotpot QA, mystique and 2wiki. These benchmarks are relevant to assess performance.
Theoretical Claims: There are no proofs in the paper and the claims are well supported.
Experimental Designs Or Analyses: I checked and the experimental design and analysis are solid. The only detail I couldn't find is how many tokens per chunk are included or whether the chunks are at sentence or paragraph level.
Supplementary Material: No
Relation To Broader Scientific Literature: The contributions from the paper are related to the broader scientific literature for improving vanilla retrieval augmented generation when the knowledge source is included in more than one chunk.
Essential References Not Discussed: The authors do a good job including the relevant references to other works in this research area. Since retrieval augmented generation is a very active area of research, I would mention in the paper that the works included do not include other RAG techniques where the knowledge augmentation happens at training or fine-tuning but only at inference time.
Other Strengths And Weaknesses: The paper is well written and easy to follow with respect to all the algorithmic details. I would like to know which embedding model they used for the retriever step (or if they used BM25). I would also like to know the chunk size and number of chunks retrieved.
Other Comments Or Suggestions: - It would be interesting to see an ablation of how the chunk size and number of chunks affects performance of the method.
- I would rename the metric Acc to LLM evaluator or similar since Acc typically refers to another metric so it's confusing to overload the term.
- I would ask the authors to flesh out the other requirement which is to have a LLM with a context window sufficiently long to include the - increasing context they provide.
- When you reference Gao et al. 2023, since it's a survey, I would explicitly say "and references therein"
Questions For Authors: - Which embedding model they used for the retriever step (or did you use BM25)?
- What is the chunk size and number of chunks retrieved?
- You mentioned that there are RAG approaches that use question decomposition without considering available knowledge in L65 of page 2, which work is this? Please include a reference
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We appreciate the valuable feedback and insightful comments from the reviewer. Below, we address each concern point by point. All tables are accessible via [hyperlinks](https://tinyurl.com/R4-tables).
### *Q1.* Embedding model used for retrieval.
The text-embedding-ada-002 model is used across all experiments demonstrated in the paper. For more hyper-parameter settings, you can refer to Appendix A.2 (line 654 ~ 668).
### *Q2.* Chunk size and number of chunks retrieved.
As introduced in line 370 ~ 373 in the paper, we compile the context paragraphs without additional chunking, resulting in a chunk size of around 500 chars. The detailed statistics are listed in [Table 1](https://tinyurl.com/R4-tables). In retrieval phase, the retriever is configured to retrieve 4 atomic questions per atomic query with a relevance threshold of 0.5. However, the actual number of chunks retrieved varies based on the number of queries proposed and their associated relevance scores. Additionally, since there is an atomic selection step incorporated in each decomposition round, a maximum of one chunk may remain after each round. Given decomposition loop constrained up to 5 rounds (N = 5) in our main experimental setup, no more than 5 chunks will be utilized during final answer generation phase.
### *Q3.* Which work is the RAG approach (mentioned in L65 of page 2) that use question decomposition without considering available knowledge?
Thanks the reviewer for pointing it. One such example is Self-Ask ([Press et al., 2023]). We will clarify this in the revised version and explicitly refer to Self-Ask to ensure the statement is supported and precise.
### *Q4.* Paper do not include other RAG techniques where the knowledge augmentation happens at training or fine-tuning but only at inference time.
Thanks for the suggestion regarding related work. In the revised version, we will include the key works that incorporate knowledge augmentation during training or fine-tuning, such as *REALM: Retrieval-Augmented Language Model Pre-Training ([Guu et al., 2020])*, and *LLaMA-Adapter: Efficient Fine-Tuning of LLaMA for RAG ([Zhang et al., 2023])*, among others.
### *Q5.* Rename the metric Acc to LLM evaluator or similar.
Thanks for the suggestion! We understand how the term "Acc" might cause confusion. In the revised version, we will rename the metric to something more descriptive, such as "LLM Evaluator", to better reflect its purpose and avoid overloading the term.
### *Q6.* Use a LLM with a context window sufficiently long to include the increasing context.
To explore the dependency of our approach on the context window size, we analyzed the token distribution on MuSiQue (using GPT-4), considering settings where N = 5 and N = 10 (N represents the decomposition round limit, detailed in line 2 of Algorithm 1). The findings are presented in [Table 2 and 3](https://tinyurl.com/R4-tables). Table 2 shows that the maximum number of input tokens is around 6K, while the maximum output tokens is around 0.5K across all LLM interactions. Additionally, this maxmium token consumption shows only a slight increase as N increases but remains within the same order of magnitude. This suggests that the maximun token requirement grows gradually. Futhermore, Table 3 demonstrates that over 99% of the LLM calls are accommodated by models with a token limit of 4096, a capacity commonly supported by existing LLMs. For models providing context windows of at least 8K tokens, all LLM calls can be handled without the need for any token truncation.
Table 3: Prompt Token (per LLM call) Distribution of KAR³ on MuSiQue.
|Prompt Token|Percentage of Calls (N = 5)|Percentage of Calls (N = 10)|
|-|-|-|
|<= 512|49.38%|34.11%|
|<= 1024|91.87%|77.61%|
|<= 2048|97.16%|97.10%|
|<= 4096|99.78%|99.89%|
|<= 8196|100.00%|100.00%| | Summary: This paper addresses the challenge of solving complex, multi-hop queries in domain-specific contexts by introducing a method called KAR^3-RAG. Traditional Retrieval-Augmented Generation (RAG) techniques often rely on straightforward text retrieval methods, which can struggle when queries require multiple steps or hops to reach an answer.
The key idea behind KAR^3-RAG is to reorganize or “atomize” the knowledge base (KB) into smaller units of knowledge in the form of atomic question–answer pairs. From a query standpoint, the method then uses:
1. A knowledge atomizer to decompose the large KB into these atomic QA pairs.
2. A query proposer to break down the original complex question into more granular sub-queries (or atomic queries).
3. An atomic retriever to efficiently retrieve relevant QA pairs.
4. An atomic selector that uses these retrieved QAs to generate either an answer or a next-step question.
Empirical results suggest that KAR^3-RAG outperforms various baselines, including on legal question-answering benchmarks and general multi-hop QA tasks.
Claims And Evidence: The authors claim that KAR^3-RAG:
1. Improves multi-hop retrieval performance by decomposing the KB into atomic QA pairs.
2. Outperforms competing retrieval-based methods on both general and domain-specific QA tasks.
These claims are generally supported by the experimental results reported. That said, the methodology for constructing the atomic QA pairs (the knowledge atomization process) provides KAR^3-RAG with an advantage that other methods may not share, so it would be helpful to see a discussion on this additional effort and how it compares to simpler or alternative preprocessing steps.
Methods And Evaluation Criteria: The proposed method makes sense for multi-hop retrieval because it directly tackles the need for stepwise reasoning by structuring the KB itself into smaller, more retrievable units. The evaluation spans both general multi-hop QA tasks and domain-specific (legal) QA, which aligns well with the claim that the approach is general yet especially useful for specialized domains.
However, additional clarity on how much preprocessing effort is involved—and to what extent alternative approaches could achieve similar results with less overhead—would be beneficial. The evaluation is done via standard QA metrics, which is appropriate for comparing question-answering performance.
Theoretical Claims: There is no theoretical claim in this paper.
Experimental Designs Or Analyses: From the experiments, the methodology seems sound: the paper compares KAR^3-RAG against strong retrieval baselines on multi-hop QA datasets and domain-specific data (e.g., legal documents). The results show improvements in retrieval accuracy and final QA accuracy.
However, one concern is the fairness of the comparison. Because KAR^3-RAG performs a knowledge atomization step, it is not entirely clear whether the other baselines had an equivalent chance to restructure their knowledge bases or if they simply used plain text as-is. The paper might benefit from more discussion on how to ensure each method has a similar knowledge “preparation” or from a deeper ablation study on the effect of atomization.
Supplementary Material: I did not review the supplementary material.
Relation To Broader Scientific Literature: The paper contributes to the ongoing research in multi-hop retrieval and question answering by introducing the idea of an atomic knowledge base—turning all or most of the raw text segments into smaller question–answer pairs that can be more directly retrieved. This idea builds on previous multi-hop QA work but takes it further by making the entire knowledge base “query-friendly.”
This approach relates to existing multi-hop retrieval frameworks that attempt to break down complex questions into sub-questions. However, instead of focusing purely on query decomposition, KAR^3-RAG also restructures the knowledge base itself. This is a novel angle worth discussing in comparison with other knowledge-base transformation methods.
Essential References Not Discussed: One relevant line of work is the transformation or rearrangement of knowledge bases for tree-based or structured retrieval. For example, there is a method described in:
[Sarthi et al., 24] “RAPTOR: Recursive Abstractive Processing for Tree-Organized Retrieval.”
Although not widespread yet, this work (or similar) might provide a useful point of comparison. It would be good to see how KAR^3-RAG stands relative to these approaches in terms of complexity, performance, and scalability.
Other Strengths And Weaknesses: **Strengths**
- Novel restructuring of the knowledge base into atomic QA pairs, which helps address the complexity of multi-hop queries.
- Demonstrates strong improvements in both general and specialized (legal) QA tasks, which suggests broad applicability.
- Brings a fresh perspective to retrieval by rethinking how knowledge is stored and accessed.
**Weaknesses**
- The cost and scalability of knowledge atomization are not explored in depth, leaving uncertainty about applying this method to large-scale knowledge resources (e.g., Wikipedia).
- It is not fully clear how to compare the results fairly, as the proposed approach benefits from pre-processing the KB, while baselines typically rely on unstructured plain text.
- Comparison to other potentially simpler or less costly knowledge-base transformation approaches is missing (e.g., [Sarthi et al., 24]).
[Sarthi et al., 24] RAPTOR: RECURSIVE ABSTRACTIVE PROCESSING FOR TREE-ORGANIZED RETRIEVAL
Other Comments Or Suggestions: - Including more details on the size of the knowledge base used in the experiments (e.g., line 371) would help contextualize the results.
- A discussion on the computational cost and feasibility of creating atomic QA pairs for large-scale knowledge sources would be valuable.
- It might be instructive to conduct an ablation or pilot study on partial or dynamic atomization to see how much the approach relies on the full-blown transformation.
Questions For Authors: - How large was the knowledge base in your experiments, and how computationally intensive was the process of generating atomic QA pairs? Do you foresee your approach being scalable to something the size of Wikipedia or large internal corporate/legal databases?
- Could you clarify whether baselines also employed any form of preprocessing or KB re-structuring? If not, how might that affect the reported performance differences?
- Are you aware of tree-based or partial KB re-structuring methods (e.g., [Sarthi et al., 24]) and how might those compare to your full-scale atomic approach, particularly in terms of complexity and performance?
- How can we ensure the quality of knowledge atomizer? Considering its importance, it is highly crucial to perform the high-quality atomization.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We appreciate reviewer's feedback. All tables are accessible via hyperlinks.
### *Q1-1.* How large was the knowledge base in the experiments?
[Table 1](https://tinyurl.com/R3-tables) provides detailed statistics. All chunks are derived from the context paragraphs of the sampled QA, with chunk count varying by dataset. Additionally, the count info is included in Appendix A.1.
Table 1: Chunk Statistics
|Dataset|Avg. Len|Count|
|-|-|-|
|Hotpot|546|4950|
|2Wiki|422|3410|
|MuSiQue|484|7120|
### *Q1-2.* How computationally intensive was the process of generating atomic questions?
[Table 2](https://tinyurl.com/R3-tables) shows the computational cost. Per Appendix A.3, atomization is a one-time step requiring LLM calls equal to chunk count, with cost scaling linearly based on chunk sizes and generated questions.
Table 2: Preprocessing Token Consumption
|Dataset|Avg. Tokens|Calls|
|-|-|-|
|Hotpot|338|4950|
|2Wiki|321|3410|
|MuSiQue|320|7120|
### *Q1-3.* Discussion of scalability and simpler preprocessing method.
Our approach mitigates scalability for larger datasets through three key features:
- Dynamic addition of atomic questions without structural changes
- Linear preprocessing cost scaling with corpus size
- Compatible with open-source LLMs (Table 2 in paper), reducing cost with only 3% performance drop on MuSiQue
Following the valuable suggestion to **employ simpler preprocessing steps**, we tested using plain-text sentence splitting via *spacy* instead of LLM-based atomization. Each sentence serves as an atomic question. After revising the selection prompt (Appendix line 1375-1396), results in [Table 3](https://tinyurl.com/R3-tables) show that while performance drops 7% on MuSiQue, this method still outperforms most baselines from Tables 1 and 2 in paper. This demonstrates its effectiveness in case lower-cost preprocessing needed, offering a flexible performance-efficiency tradeoff alongside "dynamic addition".
### *Q2.* Clarify whether baselines employed preprocessing or KB re-structuring? How might that affect the performance？
Most baselines use standard retrieval methods without preprocessing (details in Appendix Table 5, page 14). Only Self-Ask explicitly generates sub-questions that can query atomic questions using a similar retrieval path (sub-question -> atomic question -> chunk).
Testing atomic questions with Self-Ask, IRCoT, and Iter-RetGen shows slight performance improve for Self-Ask (1.6%) due to its natural retrieval path, but decreased performance for IRCoT and Iter-RetGen (see [Table 4](https://tinyurl.com/R3-tables)). This demonstrates that atomization alone cannot contribute significantly to performance.
Table 4: Abalation study of baselines with atomic questions
|Variant|Hotpot Acc|2Wiki Acc|MuSiQue Acc|
|-|-|-|-|
|Self-Ask w/ Atomic Question|80.00|77.60|53.00|
|IRCoT w/ Atomic Question|77.80|65.20|47.20|
|Iter-RetGen w/ Atomic Question|82.20|63.60|46.80|
|**KAR³**|**88.00**|**82.20**|**62.60**|
### *Q3.* Awareness of tree-based or partial KB re-structuring methods ([Sarthi et al., 24]). How might those compare to your approach？
We compared KAR³ with other KB-restructuring methods like GraphRAG and RAPTOR (Tables 6, 14, 15 in appendix, and [Table 5](https://tinyurl.com/R3-tables)). Both underperform in F1 scores, likely due to their focus on summarization which can introduce redundancy. KAR³'s precise chunk atomization enables more accurate retrieval and reasoning, leading to better performance on complex questions in 2Wiki and MuSiQue.
As for complexity, the preprocessing cost of both KAR³ and RAPTOR scales linearly with chunk size, while GraphRAG incurs significantly higher cost due to its hierarchical KG construction. This highlights that KAR³ achieves outstanding performance with reasonable computational cost compared to RAPTOR and GraphRAG.
Table 5: Comparison of KB re-structuring methods
|Method|Hotpot F1|Hotpot Acc|2Wiki F1|2Wiki Acc|MuSiQue F1|MuSiQue Acc|
|-|-|-|-|-|-|-|
|RAPTOR|12.46|81.40|10.03|69.80|6.86|55.00|
|GraphRAG|10.66|**89.00**|11.83|71.20|9.62|49.80|
|**KAR³**|**76.48**|88.00|**75.00**|**82.20**|**57.86**|**62.60**|
### *Q4.* How can we ensure the quality of knowledge atomizer？
KAR³ reduces dependence on high-quality atomization in two ways:
- *Atomic Questions Mainly as Multi-aspect Indexing*: Generates multiple atomic questions from different perspectives, providing relatively comprehensive coverage without requiring perfect atomization.
- *Separation of Retrieval and Reasoning*: Uses atomic questions only for retrieval, with downstream LLMs handling reasoning, making the system robust to imperfect retrieval.
In Table 3 of paper, using Llama3 instead of GPT-4 for all components only reduces MuSiQue performance by 2.9%, demonstrating KAR³'s robustness to atomizer quality. While better atomization would improve performance, KAR³ can achieve this incrementally since it naturally supports adding new atomic questions to existing databases on the fly. | Summary: This paper proposes a framework for handling multi-hop questions which require complex reasoning which has 4 main components; an atomizer which generates atomic questions from document chunks, a query processor which iteratively generates atomic queries using the input question and current context, an atomic retriever which maps the atomic queries with the atomic questions generated by the atomizer and hence also mapping the atomic questions with a document context and finally an atomic selector which selects the atomic question-query-chunk triplet to either append to the context or respond the the user question. The authors have evaluated their proposed methods against six existing methods and have showcased 20.4% improvements over the second best method. They have also discussed the limitation of their method which is mainly the reliance on the reasoning ability of the underlying LLM in use. They have also conducted ablation study to understand the impact of the individual components in their pipeline.
Claims And Evidence: Yes. The authors have successfully showcased that their method is effective in multi-hop question answering systems, and their method is especially effective when domain awareness is required for domain specific complex question answering. For effectiveness in multi-hop question answering they have demonstrated that the proposed method is better compared with existing methods such as standard RAG, Zero shot COT based step by step question answering, Self-Ask w/ Retrieval etc. However, for domain specific complex question answering they evaluated their method on just two datasets from a single domain where clearly the method has an advantage due to its inherent nature and how the task of the datasets are designed. Thus, a more holistic evaluation with diverse set of tasks and domain should be done.
Methods And Evaluation Criteria: Yes, The method discussed in the paper are mainly around multi-hop question answering. The evaluation datasets and metrics used for experimentation are aligned.
Theoretical Claims: Yes, I verified the results shared in the paper and those are accurate.
Experimental Designs Or Analyses: Yes, The experimental design of the paper is sound with respect of multi-hop question answering evaluation.
Supplementary Material: No, I have not reviewed any supplementary materials.
Relation To Broader Scientific Literature: The paper discusses how iterative context building and query to knowledge mapping improves the response generation of the RAG system. This is aligned with some of the other papers such as
Essential References Not Discussed: Nothing that I am aware of.
Other Strengths And Weaknesses: Strength: The paper highlights how static query to document chunk mapping followed by dynamic query to context and user question mapping improves the response generation in a multi-hop question answering scenario. The novelty is explained in a clear manner with clear evaluation datasets and methods.
Weakness: The paper does not do a good job in terms of providing evidence for the claim that the method is effective for cases where domain knowledge is required for complex problem solving. The paper also does not discuss an important limitation of the method that it is a resource heavy method and can not be used practically when retrieving from dynamic datasources or large volume datasources such as the web.
Other Comments Or Suggestions: N/A
Questions For Authors: This method demands a lot of resources. Do you have any thoughts on the trade-off between resource usage and efficiency, and how to effectively weigh the advantages?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We appreciate the valuable feedback and insightful comments from the reviewer. Below, we address the raised concerns point by point.
### *Q1.* Discussion on the important limitation of the method that it is a resource heavy method and can not be used practically when retrieving from dynamic data sources or large volume datasources such as the web.
While resource demands are an important consideration, our approach incorporates several key features and optimizations that mitigate these challenges and enhance practicality.
**Dynamic Integration of Data Sources:**
Our method supports dynamic addition of data sources without requiring structural modifications. This contrasts with knowledge graph-based extraction methods, which necessitate updating the graph when expanding the corpus. This flexibility ensures seamless integration of new information.
**Scalable Preprocessing Costs:**
The construction of our knowledge base involves a one-time preprocessing cost that scales linearly with the size of the corpus. This scalability ensures that our approach remains efficient and suitable for processing large-scale datasets. The detailed preprocessing cost of three benchmarks are provided in Table 12 in the Appendix (page 18).
**Optimizations for Large-Scale Data:**
We acknowledge the need to further optimize preprocessing for extremely large datasets, such as web-scale data, where resource efficiency becomes critical. To address this, we propose alternative atomization strategies to reduce preprocessing costs while maintaining competitive performance.
1. *Using Open-Source Models:* We explore replacing computationally expensive LLMs like GPT-4 with more resource-efficient open-source models such as LLaMA 3 during the chunk atomization step. In additional experiments, this substitution significantly reduced preprocessing costs, with only a minor accuracy drop (~3% on MuSiQue dataset), as shown in Table 1.
2. *Sentence-Level Segmentation:* for scenarios requiring even lower-cost preprocessing, we propose using sentence-level segmentation as atomic units for retrieval. Although this approach reduces performance (55.2% on MuSiQue), it still outperforms the majority of baselines presented in Table 1 of the main paper, demonstrating its practicality in resource-constrained settings.
Table 1: Ablation study on the preprocessing method on MuSiQue
|LLM Used|Variant|F1|Acc|
|-|-|-|-|
|Llama 3|KAR³ w/ plain-text|45.88|54.20|
|Llama 3|**KAR³**|**50.68**|**59.70**|
|GPT-4|KAR³ w/ plain-text|50.72|55.20|
|GPT-4|**KAR³**|**57.86**|**62.60**|
### *Q2.* Thoughts on the trade-off between resource usage and efficiency, and how to effectively weigh the advantages?
The trade-off between resource usage and efficiency is an important consideration for our method, and we have designed it to balance these aspects effectively while offering flexibility based on specific use cases. To this end, we propose alternative atomization strategies that allow users to tailor preprocessing costs to meet their needs.
For example, substituting computationally intensive models like GPT-4 with lighter open-source models such as LLaMA 3 significantly reduces preprocessing costs, with only a minor performance drop (~3% on MuSiQue). Additionally, for resource-constrained scenarios, sentence-level segmentation can be employed, reducing preprocessing overhead while still outperforming most baselines (55.2% on MuSiQue).
The choice of strategy depends on the specific application: high-accuracy requirements may justify the use of more powerful models, while dynamic or resource-limited settings can benefit from cost-effective alternatives. These considerations ensure that our method remains adaptable and effective across a range of scenarios, balancing resource usage and performance as needed. The detailed experiment results are provided in Table 2 of main paper and Table 1 in this response.
In the revised manuscript, we will incorporate a detailed discussion on the trade-off between resource consumption and efficiency, accompanied by experimental results of alternative preprocessing methods.
### *Q3.* Evaluation with diverse set of tasks and domain should be done.
Thanks for the constructive suggestion. We agree that evaluating our method on a broader set of tasks and domains is crucial to demonstrating its robustness and generalizability. To address this, we have included evaluations on two legal benchmarks in Appendix A.5，which further validate the effectiveness of our approach.
Furthermore, we have applied our method to develop RAG systems in specialized domains, such as manufacturing and healthcare, achieving consistent accuracy improvements of over 15% across a variety of tasks. Due to privacy restrictions, we are unable to release the data from these domains. To further validate and benchmark our method, we are actively exploring publicly available datasets in specialized domains to conduct more rigorous evaluations. | Summary: The authors present a new RAG framework suitable for addressing complex questions with a focus on multi-hop. The main idea is based on an iterative process of collecting evidence and generating follow-up questions as required. To devise this iterative process, the authors describe four main components: (1) Knowledge Atomizer: mapping doc chunks to set of answerable questions, (2) Query Proposer: mapping user question and intermediate context to reformulated question candidates, (3) Atomic Retriever: a high-recall lightweight ranking of atomic questions and their respective docs, and (4) Atomic Selector: LLM-based selector of top atomic question and its respective doc to be added to context.
Authors test their method on several datasets corresponding to specialized domains, and compare it against several comparable yet differentiated benchmarks. The authors demonstrate significant enhancement across benchmarks.
Claims And Evidence: All claims in the paper are well supported, except for the following one:
The paper claims that LLMs struggle with specialized fields and links RAG systems as a solution to address this shortcoming, attributing this shortcoming to reasons such as unawareness to technical terminologies. Although the claims were supported by references, such a claim might be outdated with contrasting evidence such as: https://www.frontiersin.org/journals/oncology/articles/10.3389/fonc.2023.1219326/full . The other issue with this claim is missing a main application of RAG which is equipping LLMs with knowledge crossing its cutoff date.
Additionally, the authors motivated this work on specialized fields but later demonstrated the system on pop culture questions which reflected a disconnect between the original claim/motivation and the later support. With all that being said, the demonstrated enhancement on specialized datasets closes the gap.
Methods And Evaluation Criteria: Yes they do. Benchmarks and baselines are well represented.
Theoretical Claims: The paper does not make any theoretical claims but is rather a systems paper.
Experimental Designs Or Analyses: No issues found with experimental design.
Supplementary Material: Yes, I reviewed:
- Case 6(a) referred to in the main manuscript
- Prompts used
- Cost analysis
Supplementary materials were found to be helpful but not properly organized with misaligned tables and figures.
Relation To Broader Scientific Literature: This work establishes the connection to the broader scientific literature mainly through comparing against similar, yet differentiated, RAG setups, most notably: Self-Ask and IterRetGen. KAR-RAG mainly distinguishes itself by using context to generate follow-up questions and by representing the KB as appended by atomic questions for easier atomic retrieval. The paper also demonstrates enhanced performance over said baselines.
Essential References Not Discussed: None that I can think of.
Other Strengths And Weaknesses: Strengths:
- comparison against a large set of representative baselines and across a diversified benchmark.
- enhanced performance on benchmarks.
- ablation study showing benefit of each component.
- representing document chunks as a set of answerable questions, simplifying retrieval
- helpful supplementary materials
Weaknesses:
- The paper can use more analysis of the results and anecdotes to drive home the advantage of the system presented over other baselines.
- The paper is harder to read than necessary. It can be simplified by reducing unnecessary jargon and the use of running examples.
Other Comments Or Suggestions: - Authors can do a better job differentiating between atomic questions coming from the original question, and the atomic questions coming from the knowledge base. It got confusing in the doc.
- I highly recommend the authors to use a running example earlier in the doc. The paper starts off with crowded jargon that is unexplained. Having a running example to explain steps along the way would enhance the paper. The authors did provide examples later in the doc but I found them to have arrived a bit too late.
Questions For Authors: - the paper addresses and demonstrates KAR-RAG on complex questions that require iterative subtasks, but it is not clear how the system would fare on questions that require parallel subtasks. In other words, the question can be divided to atomic subquestions that are not dependent on each other. I would like to hear the authors' thoughts on how the KAR-RAG system would fare in such examples.
- Although most of the pseudo algorithm is clear, it is unclear what is the stopping criteria for the system when no high quality proposed questions (or possible answers) are available. In other words, it is clear how the system would stop when hitting N, or when the system would deem available context sufficient, but it is unclear how it would deem the set of proposed question insufficient to find proper evidence/context.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We appreciate the valuable feedback from the reviewer. Below, we address each concern point by point.
### *Q1.* How KAR-RAG system would fare on questions that require parallel subtasks.
KAR³ is specifically designed to handle complex questions by decomposing them into multiple subqueries, enabling effective retrieval and iterative reasoning. This decomposition mechanism allows KAR³ to address both sequential and parallel subtasks. For instance, consider the parallel comparison question provided in Figure 5 of the Appendix (page 22): "Which film came out first, What Women Love or Ramudu Kadu Krishnudu?" KAR³ decomposes this question into atomic subqueries:
(a) "What is the release date of What Women Love?"
(b) "What is the release date of Ramudu Kadu Krishnudu?"
In the first iteration, KAR³ retrieves a chunk tagged with the atomic question "In what year was the film 'What Women Love' released?" relevant to subquery (a) and add it to the context. In the second iteration, using the updated context and the original question, the system regenerates subquery (b) and retrieves the relevant chunk tagged with the atomic question "In what year was the film 'Ramudu Kadu Krishnudu' released?" Through this iterative decomposition and retrieval, KAR³ resolves parallel subtasks.
### *Q2.* What is the stopping criteria for the system when no high quality proposed questions (or possible answers) are available?
When no high-quality proposed queries or no relevant atomic questions, the atomic selector may return an empty or out-of-range atomic question index after evaluating the provided context, which consists of the retrieved atomic questions. This means that no additional relevant chunks can meaningfully contribute to answering the original question. In such cases, the decomposition loop terminates, and the system generates a final answer based on the information already accumulated in the context.
### *Q3.* The paper can use more analysis of results and anecdotes to drive home the advantage of the system presented over other baselines.
Thank you for the constructive suggestion. We agree that incorporating additional analysis and case studies will help to emphasize the advantages of our method over the baselines. In the revised version, we will include more baseline analysis and case studies to highlight the strengths of our method.
### *Q4.* The claim on LLMs' unawareness to technical terminologies may be outdated given newer evidence and missing a key RAG application which is equipping LLMs with knowledge crossing its cutoff date.
We appreciate the insightful feedback and the opportunity to clarify and strengthen our claims.
**Potential outdated nature of our claim:** While we acknowledge that recent advancements have improved LLMs' performance in specialized fields, challenges persist in areas requiring precise understanding of technical terminologies, particularly in dynamic domains with evolving jargon. For example, in OLED-related technologies, the term *CSE* is often misunderstood by LLMs as "Charge Spread Effect" or "Charge Sheet Effect" when it actually refers to "Channel-Shortening Effect". Such examples highlight the ongoing limitations of LLMs in accurately handling domain-specific acronyms and terminology, especially when context-specific disambiguation is required. We will refine our claim to acknowledge progress in LLMs while addressing areas where challenges remain.
**RAG’s role in addressing knowledge cutoff issues:** We agree that one of RAG’s critical advantages is mitigating knowledge cutoff limitations by retrieving up-to-date information. We regret the omission of this important point and will explicitly highlight it in the revised manuscript as an important benefit of RAG systems.
### *Q5.* Differentiating between atomic questions from the original question and the atomic questions from the knowledge base.
Thanks for your valuable suggestions. **Atomic query proposals** decomposed from the original query are derived to break down the original query into subqueries that aid in addressing the query. In contrast, **atomic questions** generated from chunks (knowledge base) are the questions that are relevant and can be answered by the given chunk. In the revised manuscript, we will replace the term "atomic questions" with "atomic tags" to clearly distinguish it from "atomic query proposals" and include illustrative examples.
### *Q6.* Suggestions: a) reducing unnecessary jargon, b) early use of running examples, c) properly organizing supplementary materials.
Thanks for your valuable suggestions. In the revised version, we will a) simplify technical language by reducing unnecessary jargon and using clear, concise terminology, b) introduce running examples early on to illustrate key concepts step-by-step, making the explanations more accessible and easier to follow, c) carefully review and reorganize the supplementary materials to address misalignments in tables and figures. | null | null | null | null | null | null |
PlaySlot: Learning Inverse Latent Dynamics for Controllable Object-Centric Video Prediction and Planning | Accept (poster) | Summary: The paper tackles the problem of learning controllable object-centric video prediction from actionless videos. The proposed method, PlaySlot, combines slot-attention-based object-centric representations with a previous slot dynamics prediction module (OCVP) conditioned on learned latent actions (inverse module). A latent policy is also learned to infer latent actions at inference time. The model is evaluated on robotic datasets, two simulated and one real-world (Sketchy).
Claims And Evidence: * Claims are clear – designing a controllable video prediction model.
* Evidence: very marginal improvement over baselines (except the simplistic GridShapes dataset), especially over the “holistic” baselines (like CADDY). It doesn’t seem that the object-centric decomposition provides significant gains, except for certain cases where the “holistic” approaches don’t model object-interactions, but these cases seem rare as evident by the close pixel-metrics (also, hard to tell without video rollouts of the baselines how severe the issue is).
* Evidence: no quantitative results on the real-world Sketchy dataset or comparison with baselines on that dataset.
* Evidence: in the provided video rollouts, the predictions (e.g., on Sketchy) don’t seem very “stable”, objects randomly move/wiggle There are no video rollouts of the baselines.
Methods And Evaluation Criteria: * The proposed method and idea make sense for the problem; however, the method is not entirely clear.
* The benchmarks make sense, but they are too simple to draw a conclusion regarding the performance of the proposed method.
Theoretical Claims: There are no theoretical claims in this paper.
Experimental Designs Or Analyses: * The experimental design is sound.
* There are ablations.
* I raised some questions under the questions section and had several concerns under “Claims and Evidence”.
Supplementary Material: * I went over the supplementary material and watched the included videos.
* The appendix is very detailed.
Relation To Broader Scientific Literature: * The key contribution of this paper is complimenting a slot-based object-centric video-prediction model with a latent action module, which enables handling stochastic transitions (e.g., an action performed by a robot).
* In that sense, there is a contribution to the community; however, the chosen benchmark includes simple simulated datasets and one real-world dataset (with no comparisons to baselines).
* The performance of the method is not significant with respect to the baselines.
Essential References Not Discussed: The paragraph “Unsupervised Object-Centric Learning” under the Related Work section should be renamed to “Unsupervised Slot-based Object-centric Learning” as it completely ignores other unsupervised OC families, such as the patch-based family (e.g., SPACE-https://arxiv.org/abs/2001.02407) and the particle-based family (e.g., DLP-https://arxiv.org/abs/2205.15821). The other approaches don’t use the term “slots”, so if you decided to ignore the previous work in unsupervised OC, use the correct terms. While it is true that the object-centric community is mostly focused on slot-based models, I find it a bad habit to ignore the other types of object-centric models.
Other Strengths And Weaknesses: **Strengths**:
* Open-source code.
**Weaknesses**:
* The paper is hard to follow and includes obscure descriptions of the components (especially regarding the latent actions modules).
* No video rollouts of the baselines.
Other Comments Or Suggestions: Add a reference in the main text to limitations and future work in the appendix.
Questions For Authors: * In the provided video rollouts, the predictions (e.g., on Sketchy) don’t seem very “stable”, objects randomly move/wiggle. Is there an explanation for that? Maybe the latent action and slots are not entirely disentangled (I would expect static objects to remain static unless interacted with).
* Latent action design choices: to my understanding, the sampled Gaussian latent action is quantized? I find this an odd design choice. How is $v_t$, the “action variability embedding” modeled? This information is missing in Section 3.2.1 (or have I missed it?). According to lines 244-251, at inference, $v_t = \hat{z}_t - p_t$. Is that what happens at train time as well? $v_t$ is the residual?
* I thought the whole-point was to learn from actionless videos, but it seems that you regress the ground-truth real actions with an action-decoder? This information is obscured from the reader until Section 3.5. So does this approach require labeled actions? Or is it used for evaluation or task-related (Section 4.4) purposes only? It is unclear from the text how the latent actions are learned, and what is the use of the action decoder that requires labeled real actions?
* How does one choose between the inverse model variants? Is it just trial-and-error? Shouldn’t the M variant work-well for all cases?
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: Thanks for the constructive review. We are happy that you find our claims clear and our experimental design sound.
For the final version, we will try to improve the description of the latent action modules and we will rename the subsection to “Unsupervised Slot-based Object-centric Learning”.
Below we address your specific questions and comments:
**Predictions on Sketchy don’t seem very “stable”. Is there an explanation for that?**
This is indeed an interesting observation. We attribute this behavior to two main factors:
- *Simplicity of rendering module*: PlaySlot (following SAVi) uses a shared simple CNN to decode slots into object images and masks, which only interact with each other via a weighted sum. We hypothesize that a more expressive rendering module that jointly decodes all slots, e.g. transformer-based or diffusion-based, could overcome this limitation.
- *Error-Accumulation*: Our object-centric predictor is an autoregressive transformer, which can be susceptible to error accumulation over long prediction horizons. Since each predicted frame conditions the next, small inaccuracies in early steps can propagate and amplify, leading to noticeable object drift or flickering. One interesting future research direction would be to introduce temporal regularizations to minimize this effect.
Nevertheless, we observe that baselines such as SVG or CADDY also suffer from lack of temporal consistency on Sketchy: https://anonymous.4open.science/r/Rollouts-7F68/
**Is the sampled Gaussian latent action quantized? How is the $\mathbf{v}$ modeled? Is it the residual?**
The latent actions $\mathbf{\hat{z}}$ are indeed sampled from a learned Gaussian distribution.
Additionally, we decompose each latent action into an action prototype $\mathbf{p}$ and a variability embedding $\mathbf{v}$. This hybrid parameterization helps us learn semantically meaningful action prototypes, while also being able to model more complex actions (e.g. interpolations or modifications) by using the variability embedding.
Namely:
- $\mathbf{p}$ is obtained by vector quantizing the latent action: $\textbf{p} = VQ(\mathbf{\hat{z}})$
- The variability $\mathbf{v}$ is the residual: $\mathbf{v} = \mathbf{\hat{z}} - \mathbf{p}$
These specifics on how $\textbf{p}$ and $\textbf{v}$ are computed are described in Sec. 3.2.2 Lines 187-192-Col.2, but we will make this also explicit in Sec. 3.2.1.
**Use of real actions to train the action-decoder:**
PlaySlot learns to infer latent actions and learns robot behaviors in a completely unsupervised manner from actionless videos.
An action decoder is trained to map latent actions to real-actions, but this module is only needed to execute latent actions in the simulato for evaluation. See detailed answer to reviewer 19cQ.
We will try to make this clearer in the final version of the paper.
**How does one choose between the inverse model variants?**
If we know that there is a single agent in the scene (e.g. tabletop robotic scenarios), we use the InvDynS variant.
When multiple objects (> 2) are moving, we show that using a single latent action is not powerful enough, and explicitly modelling the action of each agent/object using InvDynM proves to be beneficial.
Therefore, we use InvDynS on the robotic scenarios, and InvDynM on GridShapes.
**No quantitative results on the real-world Sketchy dataset or comparison with baselines on that dataset.**
We now include a quantitative evaluation of PlaySlot and baselines on Sketchy.
See detailed answer to review R5dN.
Additionally, we provide videos in the following link featuring qualitative comparisons with the baselines on Sketchy and all other datasets: https://anonymous.4open.science/r/Rollouts-7F68/
**Marginal improvement over baselines**
While pixel-wise metrics are indeed close in some cases, our method still demonstrates notable advantages. In particular, on BlockPush, PlaySlot achieves the best results, highlighting its ability to model object dynamics and interactions effectively. Furthermore, PlaySlot achieves the overall best performance on Sketchy (see table in response to reviewer R5dN) and remains competitive in non-object-centric scenarios such as ButtonPress.
It is important to note that BlockPush contains object interactions in every test scene, where the robot must push a block to a target location. Among the compared methods, only PlaySlot consistently captures these interactions and generates coherent sequence predictions.
Moreover, while small object sizes in BlockPush may limit the impact of object localization errors on quantitative video metrics, this does not diminish the benefits of object-centric decomposition.
Additionally, beyond immediate gains in pixel-based scores, our InvDyn module, in combination with a structured slot-based representation, enables sample-efficient behavior learning, as detailed in App. E.2. This makes PlaySlot particularly valuable in settings where data efficiency is crucial.
---
Rebuttal Comment 1.1:
Comment: I appreciate the authors effort during the rebuttal period. The additional clarifications and evaluations indeed make the picture a bit more clearer. However, it seems that the choice between model variants requires priviledged knowledge of the environment and I'm still unconvinced by the quantitative results on Sketchy, seems like there is not much improvement (if any, seems like there is no statistical significance). The method is interesting but its performance is not entirely convincing. While most of the object-centric models are evaluated on synthetic datasets, I think it is worthwhile to demonstrate them on real-world datasets (this is why I truly appreciate the Sketchy experiments). Overall, I'm open to increasing my score after further discussion with the reviewers and AC, but currently I find it hard to do so as I don't think there is enough evidence the proposed approach indeed improves upon the baselines (and I acknowledge that the authors do not agree with the reviewers on this point). Thank you again for your effort.
---
Reply to Comment 1.1.1:
Comment: Thank you for engaging with our response and for taking the time to consider our clarifications and additional results. We truly appreciate your thoughtful comments and your openness to further discussion. We are especially glad to hear that you value our Sketchy experiments — we also believe that further pushing object-centric models towards real-world applications is an important and necessary step for the field.
We understand your concerns regarding the performance improvements, especially on Sketchy. While we acknowledge that some of the gains may appear marginal in terms of pixel-level metrics, and that PlaySlot may not universally outperform all baseline methods, we believe that slot-based object-centric representations offer meaningful benefits for world modeling and behavior learning. These advantages include explicit modeling of object relations and interactions, improved interpretability, and a natural structured representation for downstream control applications — beneficial properties that are not always fully captured by standard quantitative metrics. That said, we appreciate your perspective and agree that stronger quantitative comparisons would help strengthen the case, and this is something we aim to improve upon in future work.
To further highlight the strengths of PlaySlot and the use of a slot-based structured latent space, we have compared our proposed PlaySlot with LAPO (Schmidt & Jiang. ICLR. 2024), a recent method for sample-efficient behavior learning, on both the *ButtonPress* and *BlockPush* environments.
Specifically, we evaluated and compared how effectively each method learns target robot behaviors in a sample-efficient manner from a limited number of expert demonstrations.
A detailed discussion of these experiments and results is provided in:
- https://anonymous.4open.science/r/Rollouts-7F68/BEHAVIOR_LEARNING.md
Below, we summarize the key findings:
- PlaySlot and LAPO perform comparably on the *ButtonPress* environment, which is less reliant on object-centric reasoning. Nonetheless, PlaySlot achieves slightly better sample-efficiency and higher performance than LAPO across most data regimes.
- On the more challenging *BlockPush* task — where understanding object properties and their relations is crucial — PlaySlot consistently outperforms LAPO by a large margin across all data regimes, demonstrating much stronger sample-efficiency and substantially higher performance.
These results highlight the strengths of object-centric representations for sample-efficient behavior learning, especially in tasks that require understanding object properties and their relations. By parsing the scene into individual objects, PlaySlot is able to generalize more effectively from limited and noisy demonstrations and infer complex behaviors, which are challenging for models relying on monolithic, holistic representations.
Thanks again for your thoughtful and constructive comments and engagement throughout the review process. We sincerely hope that our response has helped clarify the remaining concerns, and we would be very grateful for your consideration in increasing your score. | Summary: This paper introduces PlaySlot, an object-centric video prediction model that learns inverse latent dynamics for controllable future frame forecasting and can be used in downstream tasks. PlaySlot infers object representations and latent actions from unlabeled video sequences instead of action annotations, leveraging these representations to predict possible futures. To achieve that, the model integrates an inverse dynamics module to capture scene dynamics and a conditional object-centric predictor for forecasting. Through experiments on various environments, the authors demonstrate that PlaySlot outperforms both stochastic and object-centric baselines in video prediction accuracy, while enabling robot behavior learning from demonstrations.
Claims And Evidence: Although the authors claim that the inferred latent actions enable sample-efficient learning of robot behaviors from unlabeled video demonstrations, the action decoder still requires ground-truth actions for training, which contradicts the claim of a fully unsupervised approach.
Methods And Evaluation Criteria: Yes
Theoretical Claims: N/A
Experimental Designs Or Analyses: In the comparison presented in Table 1, PlaySlot infers latent actions using future frames before utilizing them for predicting subsequent frames, which raises concerns about potential information leakage. This approach may grant an advantage over baseline methods that do not have access to future frames, calling into question the fairness of the comparison.
Supplementary Material: I watched the video provided but did not read the entire appendix.
Relation To Broader Scientific Literature: This paper builds on the work in object-centric learning, particularly methods that decompose visual scenes into structured representations using slot-based models such as SaVi. Additionally, it relates to object-centric video prediction, which has been explored in works such as SlotFormer and OCVP, but differs by emphasizing controllability through inferred actions. PlaySlot extends these approaches by incorporating inverse latent dynamics, drawing inspiration from prior research in learning latent actions from unlabeled videos.
Essential References Not Discussed: As far as I am concerned, the paper discusses the most relevant prior work.
Other Strengths And Weaknesses: ### Strength
- The authors provide extensive experiments and model analysis.
- The authors explore action-conditioned object-centric video prediction.
### Weakness
- The main weaknesses are listed in the previous sections.
- While the paper claims novelty in combining object-centric video prediction with latent action models, both object-centric prediction and latent action learning in conditional video prediction have been previously explored.
- Expert data is required for behavior learning.
- The GridShapes environment seems visually too simple.
Other Comments Or Suggestions: N/A
Questions For Authors: 1. Equation 7: Can you explain why the latent action is the difference between two consecutive embeddings?
2. How is the meaning of latent actions mapped to action numbers, as shown in Figures 5 and 6?
3. Since the model uses a pretrained SAVi, does each frame’s representation solely encode visual information from that frame? If so, would two consecutive frames be insufficient to infer an action?
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: Thanks for the constructive comments. We are delighted that you consider our experimental section and model analysis as a strength.
Below we address the highlighted weaknesses and questions, and clarify some misunderstandings.
**The action decoder still requires ground-truth actions for training, which contradicts the claim of unsupervised learning of robot behaviors from unlabeled demonstrations.**
We respectfully disagree with this statement and would like to provide further clarification.
The action decoder is only needed to decode and execute latent actions in the simulator, both for qualitative evaluations (e.g. Fig. 7 ‘Sim. Actions’) and quantitative evaluation (i.e. measuring success rate as in Appendix E.2.).
Nevertheless, PlaySlot learns robot behaviors in a completely unsupervised manner within its latent imagination. The policy model is trained in isolation to predict latent actions inferred by the inverse dynamics model from unsupervised expert demonstrations, without relying on ground-truth actions entirely.
In summary, PlaySlot learns robot behaviors and to infer inverse dynamics from unlabelled demonstrations in an unsupervised manner, and the ground-truth labels are solely needed to train an action decoder for evaluation purposes only.
**Regarding potential information leakage when using future frames.**
We follow the same evaluation protocol as CADDY, where the model is first used to infer latent actions using future frames, and then it uses those same latent vectors to forecast/reconstruct the future video frames given the inferred latent actions and a small number of seed frames.
This protocol is consistently applied across all controllable and stochastic models (CADDY, SVG, and PlaySlot), ensuring a fair comparison.
Furthermore, we mitigate information leakage by enforcing an information bottleneck on the latent actions, ensuring they capture only scene dynamics rather than the full target scene state. This prevents the model from directly encoding future frame details into the latent actions.
**Equation 7: Can you explain why the latent action is the difference between two consecutive embeddings?**
The latent action is modeled as the difference between two consecutive scene dynamics’ embeddings, thus capturing the state transformation between frames.
Since each embedding independently encodes information from its respective frame, their difference isolates the temporal change, which corresponds to the performed action.
Additionally, we assume that action embeddings are Gaussian-distributed and independent, ensuring that their difference also follows a Gaussian distribution, facilitating a probabilistic formulation for action prediction.
**How is the meaning of latent actions mapped to numbers as shown in Figs 5 & 6?**
The numbers correspond to the action prototype that represents such movement. We simply add a text-label describing the action (e.g. ‘move up’) to make visualizations clearer.
**Since the model uses a pretrained SAVi, does each frame’s representation solely encode visual information from that frame? If so, would two consecutive frames be insufficient to infer an action?**
Yes, each frame’s representation encodes information from that frame alone. Therefore, we need our Inverse Dynamics module to infer a latent action that encodes the scene dynamics between each pair of consecutive frames.
We indeed only use two consecutive frames to infer the latent action executed between them.
**Weakness: GridShapes seems visually too simple.**
GridShapes is indeed a visually simple dataset. However, to correctly solve this task, a method must be able to jointly model the motion of multiple moving objects.
We find out (Fig. 4) that PlaySlot successfully models the motion of multiple (e.g. 5) objects, whereas baselines such as CADDY fail for more than two objects despite the visual simplicity of the dataset.
This highlights the potential of object-centric world models for dynamic scenarios with multiple moving agents.
In the following link, we show qualitative rollouts on GridShapes with 2 & 3 objects. We can see how the CADDY baseline fails to jointly model the motion of 3 shapes, whereas PlaySlot solves the task.
- https://anonymous.4open.science/r/Rollouts-7F68/
**Weakness: Expert data is required for behavior learning.**
Similar to latent action models, e.g. Genie (Bruce et al. ICML 2024) or LAPO (Schmidt & Jiang. ICLR 2024), PlaySlot indeed requires expert demonstrations to learn robot behaviors.
However, as shown in Appendix E.2, we demonstrated that PlaySlot can learn behaviors from unlabelled video demonstrations (without access to simulators and without action information) in a sample efficient manner.
To make this clearer, we will include the experiments showing sample-efficient behavior learning into the main text for the final version.
---
Rebuttal Comment 1.1:
Comment: Thank you for your rebuttal. I still have concerns regarding the fairness of the comparison. The paper mentions using the original implementation of SVG in the appendix. As I understand it, SVG is a typical video prediction method in which the model does not have access to future frames during prediction. I am still not convinced about the protocol used in the paper, as it seems more like a reconstruction task rather than true prediction, which raises doubts about the validity of the comparison.
Regarding the need for ground-truth actions, I understand the authors’ point. However, I believe the paper introduces ambiguity and potentially overclaims by suggesting that ground-truth actions are unnecessary, as also noted by reviewer nim7. The paper claims that ground-truth actions are not required, but when it comes to deploying the learned robot behavior, they are still necessary, which may mislead readers.
---
Reply to Comment 1.1.1:
Comment: Thank you for engaging with our rebuttal and for taking the time to consider our clarifications. We truly appreciate your comments and your openness to discussion.
We would like to respectfully emphasize that the main two concerns you raise appear to stem from slight misunderstandings of our methodology. We address each of these below in detail, and also provide further clarifications and new results that support our claims:
**Fairness of comparisons and use of future frames:**
We respectfully disagree with the concern regarding unfair comparisons due to the use of future frames for inferring latent actions.
In our work, **we follow the exact same evaluation protocol as CADDY**, where future frames are used to infer latent actions, which are then used along with the seed frames to predict future frames.
This protocol is consistently applied across all methods, including PlaySlot and the baselines, thereby ensuring a fair comparison.
We agree that this evaluation setup reflects a *video reconstruction* task rather than pure *open-loop prediction*. However, this is a deliberate choice following prior work where the focus is on evaluating how well the model captures the stochastic scene dynamics and uses them to forecast future frames. This is a well-established practice and not specific to our method.
**Remarks regarding SVG:**
As you correctly point out, SVG is a stochastic video prediction model.
Importantly, SVG includes a *posterior module* that **explicitly uses future frames as input** during training to infer latent vectors, which capture stochastic scene dynamics and guide future predictions.
This same mechanism is often used at inference time as well — where the posterior is used to generate rollouts that better reflect the true underlying dynamics of the target scene. For example, SVG provides qualitative evaluations using this approach (https://sites.google.com/view/svglp/), where Approx. Posterior rollouts are shown using future-frame-informed latents.
Our evaluation protocol mirrors this exact same structure: we use future frames to infer latent actions (analogous to SVG’s stochastic latents), which are then used to condition the prediction of future frames from seed frames.
In both cases, future information is used to infer a compact representation of stochastic scene dynamics—not the exact future frames themselves.
This form of *posterior inference with future frames* is well-established and widely accepted in the stochastic video prediction literature. As such, our evaluation setup is entirely in line with existing methodologies and **does not give PlaySlot an unfair advantage over the baselines**.
**Need for ground-truth actions:**
We understand your concern regarding the use of ground-truth actions and appreciate your acknowledgment of our clarification.
To reiterate: **ground-truth actions are never used to train the world model, policy, or inverse dynamics modules**. They are used solely to train a lightweight action decoder for evaluation — specifically to decode latent actions into executable robot commands within the simulator for evaluation purposes only.
This is consistent with standard practice in the literature, such as Genie (Bruce et al. ICML. 2024) and LAPO (Schmidt & Jiang. ICLR. 2024), where evaluation requires an action decoder to deploy policies trained in latent space.
The core learning process of PlaySlot is fully unsupervised, operating entirely on unlabelled (actionless) videos. No part of learning the world model, robot behaviors or inverse dynamics requires action labels, and the resulting policy operates in latent space. We agree this point could be made clearer and will revise the paper to avoid any ambiguity.
**Additional Evaluations:**
To further support our claims and respond to reviewers’ comments, we conducted additional experiments during the rebuttal period:
- Qualitative comparisons (rollouts) with baselines and results on Sketchy: https://anonymous.4open.science/r/Rollouts-7F68/README.md
- Comparison of PlaySlot vs LAPO for sample-efficient behavior learning from demonstrations: https://anonymous.4open.science/r/Rollouts-7F68/BEHAVIOR_LEARNING.md
We believe our work offers a meaningful contribution to the community by being the first to integrate object-centric representations with latent action models for controllable video prediction and planning. This combination enables structured, interpretable world modeling that goes beyond traditional holistic approaches. Our results demonstrate that slot-based object-centric world models are not only feasible in this setting but also highly effective—particularly in robotic tasks that require relational reasoning and explicit modeling of object interactions.
Thanks again for your constructive comments and your engagement in the review process. We sincerely hope that our response has helped clarify remaining concerns, and we would be very grateful for your consideration in raising your score. | Summary: This work introduces a novel approach for the video prediction task using object-centric representations. It proposes an InvDyn module to learn latent action embeddings and a conditional object-centric predictor to forecast future object slots. Extensive experimental results demonstrate superior performance compared to previous methods, including evaluations on a real-robot video dataset.
Claims And Evidence: Yes, the results strongly support the claims.
Methods And Evaluation Criteria: The method is well-founded, and the evaluation follows standard practices.
Theoretical Claims: No theoretical claims are proposed in this work.
Experimental Designs Or Analyses: The experimental design is well-structured, but it lacks an analysis of the low performance on the ButtonPress dataset.
Supplementary Material: Yes, the video samples are provided.
Relation To Broader Scientific Literature: This work presents an improvement in video prediction using object-centric learning.
Essential References Not Discussed: No.
Other Strengths And Weaknesses: Strengths:
1. The method is novel and interesting.
2. The experiments are well-designed and robust.
3. The paper is well-written.
Weaknesses:
1. Clarification on ButtonPress performance: In Table 1, the lower performance on the ButtonPress task requires further clarification.
Comparison with prior work: In Section 3.2, what are the key differences between the proposed InvDyn module and Menapace et al. (2021)?
2. Handling multiple input types during inference: In Figure 1, can multiple input types be combined during inference? I understand the other two types, but what would a human input look like?
3. What format does it take?
4. How is it processed, considering that the outputs from the InvDyn module or a learned action policy are probabilistic and implicit, whereas human inputs (e.g., "move up" or "move down") are explicit, discrete, and symbolic?
Other Comments Or Suggestions: No.
Questions For Authors: Overall, this is a solid paper. However, I have one question that many researchers in this field often face: beyond the relatively simple block-based scenarios (even on the Sketchy dataset), how can this approach generalize to more real-world domains and complex scenarios? I believe this remains the main bottleneck for slot-based methods.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thanks for the positive review, acknowledging our experimental design, highlighting that our method is novel and interesting, and that our paper is well-written.
Below we address some of your questions and add clarifications about certain weaknesses:
**Clarification about the lower performance on ButtonPress.**
The Metaworld Button-Press task is inherently non-object-centric, i.e., there is no need to reason about object properties and interactions to press the button. Therefore, no large gains can be obtained from using a structured object-centric representation of the scene.
Nevertheless, we demonstrate that our PlaySlot model is general and still remains competitive in non-object-centric scenarios, ranking second among the evaluated methods on ButtonPress.
**What are the key differences between the proposed InvDyn module and Menapace et al. (2021)?**
There are two main differences:
- *Scene representation*: CADDY models scene dynamics using a holistic representation, while our InvDyn model leverages object slot representations, enabling finer-grained object-centric reasoning.
- *Action Parameterization*: Both methods represent actions differently, leading to distinct modeling choices.
A more detailed discussion of these differences is provided in the Appendix D.2.
**About inputs provided by a human to PlaySlot**
PlaySlot parameterizes an action with a discrete action prototype, which represents the action taking place, and an action variability embedding, which allows to interpolate between different motions or modify the action prototypes (e.g. changes in speed or direction).
To allow a user to control PlaySlot, we first qualitatively measure the effect of each learned action prototype and then assign a semantic meaning (e.g. ‘move left’) to each action prototype according to the motion it represents.
At inference time, a user can specify actions by selecting the corresponding action prototypes, while setting the action variability embedding as zero.
**How can this approach generalize to more real-world domains and complex scenarios? I believe this remains the main bottleneck for slot-based methods.**
Recent works, such as DINOSAUR (Seitzer et al. ICLR 2023) or SlotDiffusion (Wu et al NeurIPS 2023), show that slot-based models can be extended to handle more realistic data by using large self-supervised pretrained encoders, or powerful diffusion-based decoders.
As discussed in the Limitations & Future Work section (Appendix A), we plan to explore in future work these architectural designs to learn robot behaviors in more complex robotic scenarios
---
Rebuttal Comment 1.1:
Comment: I will keep my score.
---
Reply to Comment 1.1.1:
Comment: We are pleased that we were able to address the reviewer’s comments and questions, and we sincerely thank the reviewer again for the constructive review and positive score.
We really hope that our work motivates the community to further explore slot-based object-centric models for world modelling and planning, which is a research direction we are genuinely excited about.
We sincerely appreciate your comments and the time you took throughout the review process, and we are happy that the strengths of our work came through. Thanks again! | Summary: The papers proposes PlaySlot - a novel approach to controllable video prediction that builds on previous work on object-centric learning and latent action learning. Unlike previous approaches to video prediction based on object-centric learning, PlaySlot incorporates the InvDyn module for inferring latent actions between observations, which allows PlaySlot to learn in a self-supervised manner, enabling controllable generation (or planning) of multiple possible futures conditioned on different latent actions. In contrast to previous latent action learning approaches (such as CADDY or LAPO), PlaySlot infers object representations as slots and models the dynamics in terms of them via the transformer-based predictor. The authors use SAVi to infer slots and adapt the architecture of forward dynamics and inverse dynamics models to work specifically with slots. Latent actions are factorized into deterministic action prototypes and action variability continuous embeddings. Using simple robotic manipulation tasks (ButtonPress, BlockPush) and a synthetic dataset (GridShapes), the authors empirically demonstrate that PlaySlot outperforms considered baselines in terms of prediction quality. Experiments also show that the resulting latent actions are meaningful and consistent, allowing for sample-efficient fine-tuning with a small number of ground truth actions.
# update after the rebuttal
I was initially reluctant to raise the score much, but during the rebuttal the authors addressed most of my concerns either by providing experimental evidence or by describing planned changes to the text. Although the changes are large and change the claims, I consider them positive. I also saw the seriousness of the authors during the rebuttal, which gives me confidence that all changes will be included in the final version of the paper.
Claims And Evidence: There are two main claims in the paper (direct quotes from the text):
> 1. PlaySlot outperforms several video prediction models across diverse robotic environments, while showing superior interpretability and control capabilities.
> 2. The object representations and latent actions inferred by PlaySlot can be used to learn robot behaviors from unlabeled video demonstrations sample efficiently.
Firstly, it seems to me that the experiments presented do not allow the authors to claim superiority "across different robotic environments", as only two simple robotic environments were used, and GridShapes is not in the robotic domain. Furthermore, on ButtonPress PlaySlot does not outperform the baseline SVG (and this is just one of many tasks in MetaWorld, and not the most difficult), and even on BlockPush, which is specifically designed to favour object-centric representations, PlaySlot does not outperform the baseline by much. However, it is difficult to judge here as no standard deviation or confidence intervals were provided. Similarly, for the most interesting benchmark - real-world robot videos (Sketchy) - only PlaySlot results are provided, without the baselines and metrics.
Secondly, there is currently no evidence in the main text that PlaySlot can be used to learn robot behavior in a sample efficient manner, as only a qualitative evaluation is provided. However, there are such experiments in the Appendix, and they are quite convincing, at least for the environments tested. However, they don't include LAPO as a baseline, which I find odd given its large influence on latent action learning research and its overall simplicity. What if, despite its simplicity, it learns latent actions more suitable for efficient fine-tuning even on BlockPush?
Thus, I think that the current main claims are not sufficiently supported by the evidence provided. The authors should either provide more evidence (more than one environment for each type, clearly state number of random seeds used, provide metrics of variation, baseline metrics on Sketchy, bring experiments showing sample-efficient fine-tuning into the main text and compare with the LAPO), or remove the exaggerated claims to match the experiments provided. I understand that there may be limitations in computational resources, but this does not justify overclaiming. I still find the proposed approach novel, exciting and potentially useful. I may increase the score if some of the comments are addressed.
Some other minor claims:
> We further show how PlaySlot effectively captures precise robot actions and seamlessly scales to scenes with multiple moving objects or to real-world robotics data, outperforming several stochastic and controllable video prediction baselines
>
As noted above, there are no comparisons with baselines on real world robotics data.
> However, both CADDY and Genie operate on holistic scene representations, which are limited for tasks that require relational reasoning, often struggle to model object relationships and interactions, and require human supervision to generalize to scenes with multiple moving agents.
>
Currently there are no references in the text which support this claim.
> This approach shares similarities with Schmidt & Jiang (2024). However, whereas their method learns policies for simple games with a small discrete set of actions …
>
If I'm interpreting the numbers correctly in the Appendix A.4 from the LAPO paper, they used latent actions of dimension 128, which were then reshaped to 8 discrete ones, each with a codebook size of 64. Which gives a total of 64^8 actions. I wouldn't call that small.
Methods And Evaluation Criteria: Despite the fact that the evaluation is limited to a few simple domains, they are fully suitable for potentially verifying the claims of the article. The benchmarks considered include domains that require non-object and object-centred reasoning, as well as real-world robotics data. The experiments also use standard and widely used metrics for video prediction.
However, the evaluation itself is questionable. Nowhere in the paper (including the appendix) is it stated how many random seeds were used for the experiments. Results are also reported without standard deviation or confidence intervals (for video prediction experiments as well as for performance after fine-tuning with ground truth actions).
The hyperparameter search process is not explicitly documented. Was there one, or did all methods use the default hyperparameters? If so, was it explicitly considered that all methods should use the same enumeration budget? Were the methods explicitly balanced in the number of weights and gradient updates? I think the authors should state this explicitly and include a table with the number of trainable weights for each method.
Theoretical Claims: The paper does not present any new theoretical results or claims. After careful examination, I do not see any flaws or errors in the formulas used to present the approaches, e.g. SlotAttention and other components of the PlaySlot pipeline.
Experimental Designs Or Analyses: Apart from the concerns discussed in 'Methods and evaluation criteria', I think the only concern with experimental design is too much focus on qualitative comparisons.
First, it's pretty hard to tell if it's not cherry picking, which is quite possible even without explicit intent. Second, it's quite repetitive, better to demonstrate it once and use the remaining space for more valuable experiments (e.g. sample-efficient fine-tuning with ground truth actions).
Finally, while visual quality is important for video generation, it is less important for world modelling and planning (unless the goal is to train policies in image space rather than compact latent space, but this is rare). A world model can be globally inaccurate and still be better for planning and downstream performance than a more accurate one (see [1]).
Therefore, to support the claim that PlaySlot captures precise robot actions useful for planning and fine-tuning, which is what most practitioners would value, it's necessary to include fine-tuning experiments in the main part of the paper.
As for the ablations, I don't have any concerns. I think they show the right things and actually improve the understanding of the proposed method.
References:
1. Lambert, N., Amos, B., Yadan, O., & Calandra, R. (2020). Objective mismatch in model-based reinforcement learning. *arXiv preprint arXiv:2002.04523*.
Supplementary Material: Yes, I reviewed all parts of the Appendix.
Relation To Broader Scientific Literature: PlaySlot is a novel combination of object-centric learning, i.e. SAVi, and latent action learning, pioneered by the seminal work on Imitating Latent Policies from Observation (ILPO) [1], and recently significantly improved by LAPO [2] and LAPA [3]. PlaySlot, on the other hand, borrows many design decisions from CADDY [4]. However, the empirical evidence provided is rather weak and does not allow to conclude that the PlaySlot approach is definitely a better way for latent action learning, e.g. compared to LAPA, which also uses the robotics domain. Without such evidence, the main contribution is rather incremental.
References:
1. Edwards, A., Sahni, H., Schroecker, Y., & Isbell, C. (2019, May). Imitating latent policies from observation. In *International conference on machine learning* (pp. 1755-1763). PMLR.
2. Schmidt, D., & Jiang, M. (2023). Learning to act without actions. arXiv preprint arXiv:2312.10812.
3. Ye, S., Jang, J., Jeon, B., Joo, S., Yang, J., Peng, B., ... & Seo, M. (2024). Latent action pretraining from videos. *arXiv preprint arXiv:2410.11758*.
4. Menapace, W., Lathuiliere, S., Tulyakov, S., Siarohin, A., & Ricci, E. (2021). Playable video generation. In *Proceedings of the IEEE/CVF Conference on Computer Vision and Pattern Recognition* (pp. 10061-10070).
Essential References Not Discussed: To my knowledge, paper cites all the relevant papers essential for understanding the context and key contributions.
Other Strengths And Weaknesses: Strengths:
- The paper is clearly written and presents the method in a way that's easy to understand.
- The method is novel in the sense that, to my knowledge, there is no other work that combines object-centred representations with latent action learning.
- The related work section provides all the necessary context and does not overlook important papers in both fields.
Weaknesses:
- As discussed in the sections above, the empirical evidence is weak.
- The evaluation protocol is not clearly explained. Information on number of random seeds, standard deviations or confidence intervals, hyperparameter search is not provided.
Other Comments Or Suggestions: I do not have any other comments or suggestions.
Questions For Authors: 1. Does ablation on action representations include variants without sampling/stochasticity (e.g. continuous part)? Is there really any benefit to sampling? LAPO claims that it can capture stochasticity, and they do not sample latent actions.
2. Where these experiments reported?
> We empirically verify that the information bottleneck enforced by vector quantization achieves comparable performance to the one proposed by (Menapace et al., 2021), while requiring significantly fewer hyper-parameters.
>
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thanks for the constructive review and for finding our proposed approach novel, exciting and potentially useful.
Below we address your questions and main comments. We will address other comments (e.g. remove exaggerated claims and add missing references) in the final version of the paper. Furthermore, we will reduce the number of qualitative evaluations on the main text, and include the sample-efficient Behavior Learning experiment instead.
**Lack of quant. evaluation and baselines on Sketchy**
We quantitatively evaluate PlaySlot, as well as SVG and CADDY on the real-robot Sketchy dataset. The results are:
| | **PSNR** | **SSIM** | **LPIPS** |
| --- | --- | --- | --- |
| **SVG** | *24.24*| *0.813* | 0.076 |
| **CADDY** | 23.65 | 0.809 | **0.059** |
| **PlaySlot** | **24.43** | **0.815** | *0.063* |
We observe that all methods achieve an overall similar performance on this dataset, with PlaySlot slightly outperforming the baselines. We show qualitative comparisons and prediction rollouts for all methods in the following link: https://anonymous.4open.science/r/Rollouts-7F68/
Despite not outperforming the baselines by a significant margin, these results show that object-centric models like PlaySlot can be applicable for playable video prediction and as a world model on real robot data. In future work, we plan to extend our method with more expressive encoders and decoders (see Appendix A) to apply PlaySlot on more complex real robotic scenarios.
**Lack of LAPO baseline for behavior learning**
We are currently working on training and training LAPO on our BlockPush environment. We hope to provide a comparison between PlaySlot and LAPO by the end of the rebuttal period.
**Some additional differences with LAPO/LAPA**
LAPO & LAPA are primarily designed and optimized for latent-action pretraining in the context of learning policies for 2D games (LAPO) or robot behaviors (LAPA). However, these models are not designed for autoregressive future prediction, limiting their effectiveness as world models.
In contrast, PlaySlot incorporates a powerful object-centric world model, which enables the generation of future trajectories conditioned on latent actions.
**Does ablation on action representations include variants without stochasticity (e.g. continuous part)? Is there really any benefit to sampling?**
Our ablation includes a comparison with an oracle model that does not perform any sampling. However, the remaining PlaySlot variants (hybrid, continuous, discrete) sample latent actions $\hat{\mathbf{z}_t}$ from a learned Gaussian.
Inspired by literature in stochastic video prediction, e.g. SVG (Denton & Fergus 2018), CADDY (Meanapace et al. 2021) or SLRVP (Franceschi et al. 2020), we use a stochastic formulation to learn a structured latent space that captures uncertainty and enables controllable video prediction.
**Were these experiments reported? ',.. information bottleneck enforced by vector quantization achieves comparable performance to the one proposed by CADDY while...'**
No, these experiments were not included in the paper. We conducted early experiments where both variants performed comparably and decided to stick with our approach.
The method proposed by Menapace et al. involves numerous hyper-params (e.g., many loss weights and Gumbel-Softmax temperature scheduling), which impact performance. A poor choice of these hyper-params often leads to suboptimal training runs where multiple latent actions represent the same motion, or where multiple action prototypes did not encode any meaningful representations.
We found that tuning the hyper-params for all datasets would be challenging and expensive. Therefore, we favored our approach, which is more practical.
**Training and Compute Hyper-parameters**
To ensure a fair comparison, we balance the number of learnable params and compute requirements for all methods. Below, we report the number of trainable params for each model:
SVG: 18.84M; CADDY: 9.34M; SlotFormer: 3.97M (2.96M for predictor & 1.01M for SAVi); OCVP: 4.86M (3.85M for predictor & 1.01M for SAVi); PlaySlot: 8.49M (3.19M for InvDyn, 4.27M for cOCVP & 1.01M for SAVi).
Regarding hyper-param tuning, we use the following structured approach:
- For CADDY and SVG we start with the hyper-params from the BAIR dataset and manually refine them for our datasets.
- For SlotFormer, OCVP and PlaySlot, we use the default OCVP hyper-params as a baseline and further adjust them for optimal performance on our datasets.
While we acknowledge that a more exhaustive hyper-param search could yield better results, conducting extensive searches for all methods was infeasible due to compute budget and hardware constraints.
Regarding the number of random seeds. We run the behavior learning experiments (Appendix E.2) with 3 different seeds and report now the mean success rate and standard deviation. The results on ButtonPress are provided in: https://anonymous.4open.science/r/Rollouts-7F68/
---
Rebuttal Comment 1.1:
Comment: I thank the authors for taking into account the feedback and putting time and effort into improving the paper. I see this as a positive development and believe that the changes will strengthen the claims.
I raise my score to 3. As these are quite large changes that I won't be able to validate during this review, I can't raise my score any higher.
---
Reply to Comment 1.1.1:
Comment: We are pleased that we were able to address the reviewer’s comments and questions, and we sincerely thank the reviewer for recognizing our efforts in the rebuttal and for increasing the score.
We believe that our work contributes meaningfully towards understanding the utility of object-centric world models for controllable video prediction and planning. While our proposed method may not universally outperform all baseline approaches, we strongly believe that slot-based object-centric representations offer a valuable complement to world models and latent action models — particularly in robotic tasks that demand relational reasoning or explicit modeling of object interactions.
To further emphasize the strengths of PlaySlot and the use of a slot-based structured latent space, as well as motivated by your review, we have compared the performance of our proposed PlaySlot model with LAPO (Schmidt & Jiang. ICLR. 2024) on both the *ButtonPress* and *BlockPush* environments.
Specifically, we evaluated and compared their ability to sample-efficiently learn robot behaviors from a limited number of expert demonstrations. A detailed discussion of these experiments and results is provided in:
- https://anonymous.4open.science/r/Rollouts-7F68/BEHAVIOR_LEARNING.md
Below, we summarize the key findings:
- PlaySlot and LAPO perform comparably on the *ButtonPress* environment, which is less reliant on object-centric reasoning. Nonetheless, PlaySlot achieves slightly better sample-efficiency and higher performance than LAPO across most data regimes.
- On the more challenging *BlockPush* task — where understanding object properties and their relations is crucial — PlaySlot consistently outperforms LAPO by a large margin across all data regimes, demonstrating much stronger sample-efficiency and substantially higher performance.
These results highlight the strengths of object-centric representations for sample-efficient behavior learning, especially in tasks that require understanding object properties and their relations. By parsing the scene into individual objects, PlaySlot is able to generalize more effectively from limited and noisy demonstrations and infer complex behaviors, which are challenging for models relying on monolithic, holistic representations.
We would like to thank you again for your thoughtful and constructive comments and engagement throughout the review process. We sincerely hope that our response has addressed any remaining concerns, and we would greatly appreciate your consideration in raising your score. | null | null | null | null | null | null |
Synthesizing Software Engineering Data in a Test-Driven Manner | Accept (poster) | Summary: This paper proposes a TDD-driven data synthesis framework `UnitFlow`, which can
generate data samples for incremental development tasks based on real-world
GitHub project and unit tests. Based on this framework, this paper constructs a
promising benchmark `UnitFlow-Eval`, which contains data samples from 74
real-world Python projects. Fine-tuning code models on this dataset can
effectively enhance LLM performance in incremental development tasks. This paper
has practical value for the development of `AI for SE` and code models but still
has issues to be clarified.
## update after rebuttal
I have updated my review after the rebuttal. Main concerns are addressed so I raised the score.
Claims And Evidence: The authors provide the necessary preliminaries and definitions in Section 2 and
exhibit detailed experimental results and benchmark information in the Appendix.
However, the authors fail to provide sufficient evidence to support the claimed
contribution, namely, `effectively enhances LLM performance in incremental
development tasks'. Specifically, the author only shows the improvement of the
Pass Rate after finetuning one single model on their dataset. It will better
illustrate the practical significance and contribution of this benchmark if the
authors can provide some comparisons of the fine-tuning results of other models
(even small models of 7b and 14b) or show the performance of the fine-tuned LLM
on other development tasks/datasets.
Methods And Evaluation Criteria: The paper itself proposes to generate a benchmark, which I think the synthesis method is promising and should be studied. It is still hard to demonstrate that the generated data aligns with real-world data.
User studies were not conducted to get a sense of the quality and practicality of the generated dataset.
Theoretical Claims: n/a
Experimental Designs Or Analyses: The experiment cannot provide sufficient evidence for the claimed contributions.
Only involving 74 projects in the Python programming language, limits the practical value of the benchmark.
Supplementary Material: Yes, I have read all materials.
Relation To Broader Scientific Literature: This paper proposes a data synthesis framework, which is guided by the concept
of TDD to synthesize code samples for incremental development tasks from
open-source repositories. It is related to the prior SWE-benchmark but is
different. This paper splits one project into incremental steps, in line with
the process of real-world software development. This paper has cited appropriate
related works in Section 7 and Appendix and discussed differences between this
work and prior works.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: Cannot find `Figure 5 in appendix` mentioned in the right part of line 319. Figure 5 is on page 8 and shows the efficiency.
Other Comments Or Suggestions: The axes in Figure 5 are not suitable. Its caption claims that each axis is a software engineering task, but it actually refers to a repository. Such a design seems to follow the design of the SWE benchmark (Figure 4 in their paper).
However, UnitFlow-Eval and SWEbenchmark are different, and this paper breaks up a project into several incremental development tasks. In this case, simply evaluating the effectiveness of LLM code generation on a project is not appropriate. I think a more appropriate approach might be to summarize the types of tasks involved in incremental development. For example, some incremental development solves bugs in the code, while some supplement new functions. They are different tasks with different targets.
The authors may consider summarizing these incremental development tasks and then designing new axes (each one is an incremental development task). Based on such classification, the evaluation of the pass rate and efficiency value of different LLMs will be more in line with the needs of incremental development scenarios. New axes can also allow this benchmark to measure the capabilities of LLM in incremental development.
Questions For Authors: This paper uses LLMs to generate development documents and docstring in Lines 212 and 233. I wonder how authors deal with the hallucinations in the LLM generation.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Dear reviewer,
We are grateful for the reviewer’s valuable suggestions. Our detailed responses to the concerns are provided below.
---
> **Concern D1:** The paper would benefit from additional empirical evidence to substantiate the claimed improvements in LLM performance on incremental development tasks, such as comparisons with other fine-tuned models or evaluations on other benchmarks.
We fine-tuned **Qwen2.5-Coder-32B-Instruct** using the **UnitFlow synthetic dataset** and evaluated its performance on **SWE-Bench-Verified** using the **Agentless** framework. The results are as follows, reported as the average over three runs with standard deviation:
| **Model** | **SWE-Bench-Verified Accuracy** |
| - | :-: |
| Qwen2.5-Coder-32B-Instruct | 33.79% ± 0.32% |
| +Ours (fine-tuned with UnitFlow data) | **35.27%** ± 0.26% |
**UnitFlow-Bench** evaluates models on incremental software engineering tasks, whereas **SWE-Bench-Verified** targets automated bug fixing. Improvements observed on both benchmarks demonstrate the robustness and effectiveness of our synthetic data generation approach.
> **Concern D2:** It is still hard to demonstrate that the generated data aligns with real-world data.
UnitFlow is explicitly designed to simulate real-world incremental software development, based on a detailed analysis of unit tests from real open-source projects.
Specifically, we:
- Use existing unit tests to define realistic development goals,
- Synthesize code changes that mirror typical developer behavior,
- Ensure the process is traceable, reproducible, and guided by real testing practices.
All instances are validated in executable environments, ensuring both correctness and practical feasibility. In summary, the design, source, and validation process of UnitFlow strongly support its alignment with real-world development workflows.
> **Concern D3:** User studies were not conducted to get a sense of the quality and practicality of the generated dataset.
While user studies can be valuable for assessing perceived quality, our focus is on systematic, executable validation: each UnitFlow-generated instance is tested in a execution verifiable environment to ensure that:
- the code runs correctly, and
- the intended behavior is preserved or modified as expected.
This process provides a scalable, objective, and reproducible measure of data quality, which we believe is more precise and reliable than subjective user feedback, especially for software engineering tasks
> **Concern D4:** The experiment cannot provide sufficient evidence for the claimed contributions. Only involving 74 projects in the Python programming language, limits the practical value of the benchmark.
We would like to clarify that the current scale of our dataset has significantly expanded.
Since the initial submission, we have successfully constructed over 6,000 executable environments across diverse real-world Python projects. Based on these, we have synthesized over 200k validated data instances, making UnitFlow-Bench a substantially larger and more practical benchmark than initially reported.
Moreover, models fine-tuned on UnitFlow-synthesized data demonstrate consistent performance gains on UnitFlow-Bench-Lite and SWE-Bench-Verified. These results highlight the effectiveness and generalizability of UnitFlow-generated data, further supporting the practical value and impact of the benchmark.
To support further research and demonstrate practical scalability, **we will release all synthetic data and executable environments**.
> **Concern D5:** This paper uses LLMs to generate development documents and docstring in Lines 212 and 233. I wonder how authors deal with the hallucinations in the LLM generation.
As described in Section 3.4, we manually inspected samples from several models before scaling up generation. For tasks such as generating development instructions and docstrings, Qwen2.5-Coder-32B-Instruct performed consistently well, and we did not observe hallucinations in the sampled outputs, they were semantically aligned with the code or tests.
Additionally, all generated instances undergo executable validation: if the synthetic data fail runtime checks, they are automatically discarded. This ensures that only accurate and functionally correct data are retained, effectively filtering out hallucinated or inconsistent outputs.
> **Concern D6:** Figure 5 not found in appendix.
The prompt format figure referenced in line 319 was accidentally left out during compilation. We will make sure it is included in the revised manuscript.
---
We’re happy to clarify any remaining questions you may have. If you feel our response resolves your concerns, we would be grateful if you could consider raising your score. | Summary: This paper introduces UnitFlow, a novel data synthesis framework based on Test-Driven Development (TDD), which automatically generates software engineering data by inferring incremental development steps directly from unit tests. The framework constructs a Runtime Dependency Graph (RDG) to capture function interactions, enabling the generation of structured development schedules and verifiable TDD tasks. In addition, the authors created the UnitFlow-Eval benchmark by generating 16,061 training instances and 2,020 test instances from real-world GitHub projects. The paper demonstrates that fine-tuning a large language model (LLM) on this synthetic dataset significantly enhances performance in TDD-based programming.
Claims And Evidence: Some claims are not supported by clear and convincing evidence. The paper could show/prove the validity and quality of the synthesized software engineering data. Is the synthesized data valid and of high quality?
Methods And Evaluation Criteria: Pass Rate and Efficiency Value are used to measure the performance of several different LLM on UnitFlow-Bench-Lite. The paper shows that the limitations of current large language models in handling practical software engineering challenges could be addressed by fine-tuning LLMs with the synthesized data. However, the authors only fine-tuned the Qwen2.5-Coder-32B-Instruct model and evaluated it on the UnitFlow-Bench-Lite test set. More experiments could be conducted.
Theoretical Claims: The paper does not contain theoretical proofs and claims.
Experimental Designs Or Analyses: The model UF-Coder-32B-Instruct is actually a fine-tuned version via synthesized training data, so I am not sure if the performance improvement on UnitFlow-Bench-Lite can demonstrate the effectiveness of UnitFlow-synthesized data.
Supplementary Material: I reviewed the supplementary material. Table 1 only mentioned in appendix B.2. The table could be moved to page 15, instead of showing the table in Section 7 Related Work.
Relation To Broader Scientific Literature: N/A
Essential References Not Discussed: The paper did not consider the scenario of software evolution, where software (including its structure/dependency graph) keeps changing, such as those discussed in the following paper:
Dewu Zheng et al., Towards more realistic evaluation of LLM-based code generation: an experimental study and beyond
https://arxiv.org/pdf/2406.06918.
Other Strengths And Weaknesses: The paper is generally well written.
The data and code are not publicly available (data link cannot be found in the paper)
Other Comments Or Suggestions: . Figure 3 never get referred in the whole paper.
. Page 8, line 398. “The evaluation results are presented in Figure 5 and Table 6 in the appendix”, Figure 5 is actually not in the appendix.
. Page 6, line 308 and line 318. Line 308 “Finally, we obtain 74 projects that can pass all the unit tests in the installed test environment.” Line 318 “We only keep the unit tests that pass.” Line 318 implies that there are unit tests that cannot pass while line 308 claims that all unit tests can pass. Are there any differences between the criteria in the ‘Preparation of Test Environment’ and ‘Verifiable Data Generation’?
. “Among these projects, 12 projects are selected for testing, and the remaining 62 projects are used for training”. Did you select these projects for testing and training randomly or not? Any criteria for projects selection?
. Page 3, line 3 “UnitFlow removes the implementation of core functions covered by the current…” and Page 4, line 205 “that cover the same Core Function Nodes (CFNs).” Does these “Core Functions” refer to both Target Core Function and Dependent Core Function?
. Page 7, line 317, “The pass rate is defined as the ratio of successfully completed tasks (those that pass unit tests)…” The word "task" is confusing. Does it mean an unit test? What is the granularity of a task?
. Page 4, line 205 “we first merge all TTFNs that cover the same Core Function Nodes (CFNs)”. Does the CFNs refer to both Target Core Function Node and Dependent Core Function Node? Any clarification?
Questions For Authors: As the model UF-Coder-32B-Instruct is actually fine-tuned using synthesized training data, can the performance improvement on UnitFlow-Bench-Lite demonstrate the effectiveness of UnitFlow-synthesized data?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Dear reviewer,
We sincerely appreciate your thoughtful and constructive feedback. Please find our responses to the concerns below.
---
> **Concern C1:** Is the synthesized data valid and of high quality?
We fine-tuned the **Qwen2.5-Coder-32B-Instruct** model using data synthesized by UnitFlow, resulting in a substantial accuracy improvement on the UnitFlow-Bench benchmark. To further validate the effectiveness of UnitFlow-generated data, we conducted evaluations using the **Agentless** framework on the **SWE-Bench-Verified** dataset, reporting results as the average over three runs with standard deviation.
| **Model** | **SWE-Bench-Verified Accuracy** |
| - | :-: |
| Qwen2.5-Coder-32B-Instruct | 33.79% ± 0.32% |
| +Ours (fine-tuned with UnitFlow data) | **35.27%** ± 0.26% |
The consistent improvements observed on both **UnitFlow-Bench** and **SWE-Bench-Verified** demonstrate the practical utility and generalizability of the synthetic data produced by UnitFlow.
> **Concern C2:** The model UF-Coder-32B-Instruct is actually a fine-tuned version via synthesized training data, so I am not sure if the performance improvement on UnitFlow-Bench-Lite can demonstrate the effectiveness of UnitFlow-synthesized data.
As mentioned above, we also fine-tuned **Qwen2.5-Coder-32B-Instruct** and evaluated it on **SWE-Bench-Verified**. The results provide further evidence of the effectiveness of the synthetic data generated by **UnitFlow**.
> **Concern C3:** The paper did not consider the scenario of software evolution, where software keeps changing.
We are exploring ways to incorporate software evolution into our setting, but we have found it to be a challenging problem.
We constructed executable and verifiable environments for 1,276 repositories related to SWE tasks. However, since the environments were built based on the latest commit on the main branch, some environments became invalid when checking out historical commits—due to changes in the software’s structure or dependencies over time. As a result, out of the 24,961 instances covered by these repositories, only 1,242 instances could be successfully validated using the prebuilt environments.
> **Concern C4:** Are there any differences between the criteria in the ‘Preparation of Test Environment and Verifiable Data Generation’?
During the construction of executable verification environments, we use the **exit code of pytest** as an indicator of environment status. Some key exit codes are interpreted as follows:
- **Exit code 0**: pytest ran successfully and all unit tests passed.
- **Exit code 1**: pytest ran successfully but some unit tests failed.
- **Exit code 3**: pytest failed to run, typically due to import errors caused by an incomplete or broken environment.
In the environment construction phase, we treat both **exit code 0 and 1** as indications of a **successfully built environment**. However, during the data synthesis phase, we retain **only instances where unit tests pass** (exit code 0), to ensure that each synthesized data point can be **verified within the current environment**. Instances that fail unit tests are discarded to maintain data quality.
> **Concern C5:** “Among these projects, 12 projects are selected for testing, and the remaining 62 projects are used for training”. Did you select these projects for testing and training randomly or not? Any criteria for projects selection?
The **test projects** were selected based on **functional diversity**. Specifically, we chose 12 projects that serve **distinct purposes** (e.g., visiualization, data processing) to ensure broader coverage. The selection criteria also included **popularity (GitHub star count)** and **recent activity** (i.e., whether there were commits within the past six months).
We will clarify the project selection criteria more explicitly in the revised paper.
> **Concern C6:** Does these “Core Functions” refer to both Target Core Function and Dependent Core Function?
Yes, your understanding is correct. We will clarify this in the revised version of the paper.
> **Concern C7:** The word "task" is confusing. Does it mean an unit test? What is the granularity of a task?
Yes, by "task" here, we are referring to whether the given development task can be completed successfully and pass the corresponding unit tests.
> **Concern C8:** Does the CFNs refer to both Target Core Function Node and Dependent Core Function Node? Any clarification?
Yes, your understanding is correct. We will clarify this in the revised version of the paper.
> **Concern C9:** Typos
We sincerely appreciate your careful reading and for identifying the typos in **Figure 3** and **Figure 5**. These will be fixed in the revised version.
---
Please feel free to reach out. We would be happy to clarify any remaining questions you may have. If you find our response addresses your concerns, we sincerely hope you would consider raising your score accordingly. | Summary: This paper proposes a data synthesis framework UnitFlow that leverages Test-Driven Development to automatically generate high-quality, structured, and verifiable training data for LLMs in software engineering. It constructs a Runtime Dependency Graph (RDG) from unit tests to capture function interactions and generates a step-by-step development schedule. For each step, UnitFlow produces a partial codebase, a requirement document based on unit tests, and a reference solution. Using UnitFlow, the authors synthesized a dataset of 16k training instances and 2k test instances, which they used to fine-tune the Qwen2.5-Coder-32B-Instruct model, resulting in the UF-Coder-32B-Instruct model. Experiments on the UnitFlow-Eval benchmark demonstrated significant improvements in the model's ability to perform TDD-based coding tasks.
## update after rebuttal
I appreciate the rebuttal by authors. My concern has been addressed and I would like to keep my score.
Claims And Evidence: Yes.
Methods And Evaluation Criteria: Yes, but could be further improved.
Theoretical Claims: Not applicable.
Experimental Designs Or Analyses: The evaluation of the proposed method is limited to the UnitFlow-Eval benchmark, which shares the same distribution as the training data. The authors did not conduct experiments on other software development benchmarks such as SWE-Bench. This limitation may affect the assessment of the method's generalizability across different software development contexts and tasks.
Supplementary Material: Yes, Section A and C.
Relation To Broader Scientific Literature: No.
Essential References Not Discussed: No.
Other Strengths And Weaknesses: Other Strengths:
- Clear writing and organization.
- Scalablility of the proposed method.
Other Weaknesses:
- While the approach demonstrates theoretical scalability, the volume of synthetic data and the experimental evaluation are confined to supervised fine-tuning.
Other Comments Or Suggestions: No.
Questions For Authors: Please refer to Experimental Designs and above Weaknesses.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Dear reviewer,
We are grateful for your valuable suggestions. Our detailed responses to the concerns are provided below.
---
> **Concern B1:** The evaluation of the proposed method is limited to the UnitFlow-Eval benchmark, which shares the same distribution as the training data. The authors did not conduct experiments on other software development benchmarks such as SWE-Bench. This limitation may affect the assessment of the method's generalizability across different software development contexts and tasks.
We agree that evaluating the generalizability of the proposed method beyond the UnitFlow-Eval benchmark is important. In addition to our main evaluation on UnitFlow-Eval, we conducted further experiments using the **SWE-Bench-Verified** benchmark, which differs significantly from our training data in both distribution and task format. Specifically, we fine-tuned **Qwen2.5-Coder-32B-Instruct** with UnitFlow synthetic data, and evaluated it using the **Agentless** framework. The results are as follows, reported as the average over three runs with standard deviation:
| **Model** | **SWE-Bench-Verified Accuracy** |
| - | :-: |
| Qwen2.5-Coder-32B-Instruct | 33.79% ± 0.32% |
| +Ours (fine-tuned with UnitFlow data) | **35.27%** ± 0.26% |
This improvement of **+1.48%** indicates that our method not only improves performance on in-distribution tasks but also enhances the model’s ability to generalize to real-world software engineering tasks under different settings.
We appreciate the reviewer’s suggestion and will include these results in the revised version to strengthen the generalizability evaluation of our method.
> **Concern B2:** While the approach demonstrates theoretical scalability, the volume of synthetic data and the experimental evaluation are confined to supervised fine-tuning.
Since the initial submission, we have significantly scaled up the synthetic data generation process. Specifically, we have automated the construction of 6,008 executable repository images and used *UnitFlow* to synthesize over **200k** task instances.
Our analysis suggests that supervised fine-tuning (SFT) benefits saturate around **20k–30k** instances. Therefore, we plan to leverage the additional data in the **continued pretraining** phase, which contributes to improving general code understanding and task generalization.
To support further research and demonstrate practical scalability, **we will release all synthesized data and executable environments**.
---
Please feel free to reach out if you have any further questions — we’d be happy to clarify. If you find our response addresses your concerns, we sincerely hope you would consider raising your score accordingly. | Summary: The paper introduces UnitFlow, a novel framework for synthesizing test-driven software engineering data. Unlike prior datasets that rely on human-submitted issues, UnitFlow generates incremental development steps directly from unit tests. The framework constructs a Runtime Dependency Graph (RDG) to capture function interactions, enabling structured development tasks that mirror real-world iterative coding practices. Evaluation of state-of-the-art LLMs and agents, demonstrating that current models struggle with complex software engineering workflows.
Claims And Evidence: The core claims are well-supported by experimental results.
Potential Limitations:
- Comparison with other benchmarks is limited. The paper discusses SWE-Bench but does not provide a direct side-by-side comparison in terms of realism or task difficulty.
- The robustness of UnitFlow-generated data against real-world code review practices is unclear.
Methods And Evaluation Criteria: ++ The Runtime Dependency Graph (RDG) effectively captures function dependencies.
++ Using unit test execution traces instead of static analysis improves accuracy in identifying function interactions.
++ Benchmarking both LLMs and agents provides a systematic and well-defined evaluation.
-- The evaluation does not compare against human-written commit sequences, which could serve as a valuable real-world baseline.
-- The study does not report how often models generate nearly correct but slightly misformatted code, which may impact pass rates.
Theoretical Claims: Not applicable (no formal proofs or theoretical claims in the paper).
Experimental Designs Or Analyses: ++ The choice of models is reasonable, covering OpenAI, Google, and specialized models.
++ The benchmarking methodology is sound.
-- The paper lacks statistical significance tests for performance differences—are observed differences robust under variations in prompts or datasets?
Supplementary Material: Yes, I reviewed the appendices.
Relation To Broader Scientific Literature: - Prior benchmarks like HumanEval, MBPP, and SWE-Bench focus on single-step or static QA, whereas UnitFlow emphasizes incremental development.
- Unlike SWE-Bench, which extracts tasks from GitHub issues, UnitFlow synthesizes development tasks, making it more scalable and controllable.
Essential References Not Discussed: No.
Other Strengths And Weaknesses: Strengths:
- Automated and scalable dataset generation.
- Benchmark evaluates LLMs in an iterative development setting, making it more realistic than static function-based tasks.
- Fine-tuned LLM outperforms baselines, validating the effectiveness of the dataset.
Weaknesses:
- No qualitative analysis of whether models learn good coding practices or just pattern-match training data.
Other Comments Or Suggestions: - Section 4.1, line 319: Reference to Figure 5 appears incorrect.
- Section 5.2, line 370: The term "unitflow-bench-lite" should be introduced earlier for clarity.
Questions For Authors: 1. Have you analyzed how often models generate near-correct solutions with minor formatting issues (e.g., missing imports, minor syntax mistakes)?
2. How does UnitFlow compare to human-written commit sequences in terms of task structure and complexity?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Dear reviewer,
We deeply appreciate your thoughtful review and your recognition of our contributions. Below, we provide point-by-point responses to your concerns and suggestions.
---
> **Concern A1:** The evaluation does not compare against human-written commit sequences, which could serve as a valuable real-world baseline.
Given that the unitflow-bench benchmark comprises more than 2,000 test cases, conducting experiments with human-written commits is quite time-intensive. Regrettably, we were unable to complete these experiments within the rebuttal timeframe. Nonetheless, we are committed to performing the experiments and will include the results in the revised version of our paper.
> **Concern A2:** The study does not report how often models generate nearly correct but slightly misformatted code, which may impact pass rates.
We calculated the accuracy of the solution format generated by each model and present the results in the table below.
|Model|Empty Patch|Empty Replace|
|-|:-:|:-:|
|claude3.5-sonnet-1022|0.00%|0.00%|
|DeepSeek-Coder-V2-Instruct-0724|2.00%|1.67%|
|DeepSeek-R1|1.67%|1.67%|
|DeepSeek-V3|4.01%|6.66%|
|gpt-4o-2024-08-06|0.00%|0.00%|
|Llama-3.1-405B-Instruct|6.67%|8.03%|
|Llama-3.3-70B-Instruct|2.04%|1.04%|
|o1-mini-2024-09-12|5.34%|3.33%|
|Qwen2.5-72B-Instruct|3.51%|0.59%|
|Qwen2.5-Coder-32B-Instruct|2.71%|0.33%|
|UF-Coder-32B-Instruct|4.17%|1.38%|
> **Concern A3:** The paper lacks statistical significance tests for performance differences, are observed differences robust under variations in prompts or datasets?
In the evaluation, we standardized only the format of the prompts, which contained solely the essential formatting instructions. Since the actual content of the prompts changed significantly based on the contextual information of each test instance, the robustness of the experimental results is preserved.
> **Concern A4:** No qualitative analysis of whether models learn good coding practices or just pattern-match training data.
Our UF-Coder-32B-Instruct model is trained based on Qwen2.5-Coder-32B-Instruct. As shown in the error format statistics table above, the proportion of formatting errors generated by UF-Coder-32B-Instruct is comparable to that of Qwen2.5-Coder-32B-Instruct — in fact, the latter even exhibits a slightly lower error rate. However, the accuracy of UF-Coder-32B-Instruct is significantly higher than that of Qwen2.5-Coder-32B-Instruct. This suggests that UF-Coder-32B-Instruct has not merely memorized patterns from the training data, but has indeed improved its capability in software development tasks.
> **Concern A5:** How does UnitFlow compare to human-written commit sequences in terms of task structure and complexity?
Compared to human-written commit sequences, which often vary in granularity and mix different types of changes, UnitFlow provides a more structured and goal-driven development trajectory. By aligning each commit with the satisfaction of a specific unit test, UnitFlow enforces a clear functional decomposition and promotes modular, incremental progress. Despite being automatically generated, the commit sequences can capture meaningful task dependencies and span multiple components, reflecting a level of complexity comparable to real-world development. This makes UnitFlow a valuable tool for generating realistic and reproducible development workflows, particularly in settings where systematic task structure and functional clarity are desired.
> **Concern A6:** Typos and Suggestions
We will incorporate these improvements in the revised version.
---
We sincerely appreciate your thoughtful and positive review. Should you have any further questions or suggestions, we would be glad to provide additional clarification. | null | null | null | null | null | null |
A Closer Look at Generalized BH Algorithm for Out-of-Distribution Detection | Accept (poster) | Summary: The paper investigates methods for setting a decision threshold for out-of-distribution (OOD) detection using a calibration set, ensuring that the resulting detector achieves a desired performance on unseen data. The authors examine the g-BH algorithm, a recently proposed method for threshold selection [Ma 2024], and extend it in two ways. First, they characterize the distribution of the expected True Positive Rate for decision rules using thresholds set by the g-BH algorithm, demonstrating that the TPR follows a Beta distribution with parameters dependent on the calibration set size and the target $\alpha$-level. Second, they propose an ensemble-based algorithm to address the inefficiency of the g-BH algorithm when using small calibration sets. Both contributions are empirically validated on standard OOD benchmarks.
## update after rebuttal
I acknowledge that I failed to fully grasp the setup and purpose of the proposed algorithm based on the current presentation. While I did not consult [Ma et al., 2024], which may provide additional context, I believe the paper should be self-contained and provide a clear and complete definition of the problem it addresses.
The authors' rebuttal offered some clarification, but key aspects remain unclear to me. For instance, the claim that "a larger calibration set improves the performance of the g-BH algorithm in terms of TPR" is difficult to interpret meaningfully without addressing other performance metrics such as FPR. Since the method revolves around setting a decision threshold on a small calibration set, reporting improvements in TPR alone seems insufficient for a full evaluation.
The paper may contain valuable ideas, but the current presentation does not clearly convey them to me. This limits my ability to fully understand the core contributions and assess their significance. While I recognize the possibility that the misunderstanding lies on my side, I made an effort to engage with the paper.
Claims And Evidence: A central claim, reiterated multiple times in the paper, is that larger calibration sets enhance the performance of the g-BH algorithm in terms of the true positive rate (TPR). However, this claim is somewhat misleading and, in my opinion, fundamentally incorrect, as it does not align with the intended purpose of the g-BH algorithm or its guarantees. The algorithm is designed solely to set the decision threshold such that the actual false discovery rate (FDR) or TPR does not exceed a specified threshold at a given confidence level.
Methods And Evaluation Criteria: The authors devote a significant portion of the paper to empirically analyzing how the calibration set size affects the performance of the OOD detector configured by the g-BH algorithm. However, the experimental setup is not clearly described, and its purpose remains somewhat unclear. In particular, the confidence level (p-value), and the desired FDR threshold are not consistently defined across all experiments.
Furthermore, since the core issue addressed in the paper is the randomness introduced by small calibration sets, the experiments should account for this variability. This could be done by running multiple trials and reporting summary statistics (such as the mean and standard deviation) rather than presenting single-value metrics (e.g., FPT, F1), which are merely realizations of random variables with high variance.
Theoretical Claims: I did not verify the proofs in detail, but I believe Theorem 4.1 is correct. The setup and results closely resemble those found in problems related to characterizing the coverage of a conformal predictor. Specifically, the claim that coverage—computed in the same manner as in the BH algorithm—follows a Beta distribution has been previously established in:
Vovk, "Conditional validity of inductive conformal predictor," ACML, 2012.
Experimental Designs Or Analyses: As previously noted, the design and analysis of the experiments have the flaws mentioned earlier.
Supplementary Material: No.
Relation To Broader Scientific Literature: The authors cite relevant literature. I see a connection between Theorem 4.1 and a similar problem in conformal prediction, as discussed earlier. However, I do not view the omission of this reference as a significant issue.
Essential References Not Discussed: No.
Other Strengths And Weaknesses: As mentioned earlier, the problem to be addressed is not clearly defined, the claims lack clarity and precision, and the descriptions of the algorithms and experiments are insufficiently detailed. Examples of issues related to problem formulation and vague claims have already been provided. Additionally, several key details are missing regarding the algorithms and experimental setup. For instance, it is unclear how the weights of the ensemble algorithm are determined, what $n_0$ represents in Theorem 5.5 and Corollary 5.6, and how the p-values and FDR thresholds were set across all experiments.
Characterizing the distribution of the true positive rate (TPR) for the g-BH algorithm, along with the analysis of the proposed ensemble algorithm, could provide solid contributions. However, the paper's presentation is far from ideal, making it difficult to thoroughly assess its validity and clearly grasp its main message.
Other Comments Or Suggestions: No.
Questions For Authors: One of the shortcomings of the paper is the lack of a clear problem definition, which should be stated explicitly at the beginning. Based on my understanding, the goal is to set a threshold on the calibration set such that the False Discovery Rate (the proportion of true OOD samples incorrectly identified as OOD by the detector) on unseen data remains below a specified threshold with at least $1-\alpha$ confidence. Can you confirm if this is the intended problem being addressed?
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: **Q1**: about the claim and goal of our paper.
**Ans1**: We first emphasize that FDR is closely related to TPR and FPR. Based on [1], we have
$$ FDR = E(\frac{1}{1 + \frac{P}{N}\cdot \frac{1-FPR}{1-TPR} }) $$
where P is the number of ID data in test set and N is the number of OOD data in test set. Obviously, larger TPR and smaller FPR leads to smaller FDR. [1] points out that traditional decision rule just considers TPR when choosing decision threshold. By contrast, FDR can balance the TPR and FPR. __By controlling FDR, g-BH can better trade off the performance between ID and OOD data and further improve total decision performance (F1)__ (The details can be seen in third paragraph of Section 5.2 of [1]). The experiments in [1] also show that they care more about TPR, FPR and F1, instead of only controlling FDR. The meaning of our claim is that larger calibrated set can improve the TPR of g-BH and decrease its FPR, leading to smaller FDR and larger F1. Our Theorem 4.1 and experimental results of Figure 1 and Tables 1-4 support this claim. Hence, our claim is align with the purpose of g-BH, and is correct without misleading.
The goal of our paper is to __deeply study the influence of calibrated set on g-BH__, which has been repeatedly pointed out in Abstract (line 20-24) and Introduction (line 32-38, right). Overall, our paper consists two parts: 1, we find that small calibrated set degrades the performance of g-BH, and establish Theorem 4.1 and conduct extensive experiments (Tables 1-4) to verify this phenomenon. 2, we propose the eg-BH algorithm to solve the issue caused by small calibrated set. The performance of hypothesis testing algorithm depends on precise p-value. Since the distribution of ID data is unknown, [1] directly uses empirical p-value to estimate real p-value. Glivenko-Cantelli theorem indicates that this estimation method performs well for large calibrated set. When calibrated set is small, the estimation error of p-value increases, leading to a poor performance of g-BH. Our core goal is to mitigate estimation error problem of p-value caused by small calibrated set. The entire Section 5 focuses on discussing how to obtain a good computation method of p-value based on small calibrated set. Combining our estimation method of p-value and g-BH, this algorithm is called eg-BH. Hence, our core goal is not simply to address the randomness caused by calibrated set, nor to set a threshold such FDR remains below a specified threshold.
**Q2**: about the understanding of some concepts.
__Ans2__: we first give a correct interpretation of FDR. FDR is the expectation of false discovery proportion (FDP). FDP can be expressed as A/B where A is the number of ID examples in test set falsely classified as OOD and B is the number of examples classified as OOD in test set. Hence,
"False Discovery Rate (the proportion of true OOD samples incorrectly identified as OOD by the detector) on unseen data" is incorrect. Besides, FDR is a real number without randomness. "at a given confidence level" is often used to describe random event. So, "at a given confidence level" is not suitable to describe FDR control. Different from conformal prediction, in hypothesis testing, p-value can not be called "confidence level". $\alpha$ is only upper bound of FDR and not used to describe confidence level. Moreover, p-value is the function of socre of testing example, instead of hyper-parameter, and thus can not be prespecified.
**Q3**: about experimental settings and some notations.
**Ans3** Our code is based on [2] and we use same experimental setup as [2], which has been emphasized in Section 6.1 (line 362-363, left). The details, such as optimizer, learning rate, epoch, can be found in
Section 4.1 of [2]. Besides, the code of [2] run 5 times for every model, and all experimental results are the mean of 5 trials. You can find these information in Section 4.2 of [2]. We will provide these details in Appendix.
Our theoretical framework is based on [1] and we use the same notations and definitions as [1], which have been emphasized in Section 3 (line 102-104, right). The computation method of empirical p-value has been clearly presented in Section 5 (line 196-198, right) and Algorithm 1 (step 8) for two times. Following [1], $\alpha$ is set as 0.05 (see Section 2.3 of [1]). The weights in eg-BH is 1/L, which has been clearly pointed out in Theorem 5.3. We will describe the weights in Experiments again. $n _0$ is the number of ID data in test set, which has clear description in the proof of Theorem 5.5. You can also find its detailed description in Sections 2.2 and 3 of [1].
[1] A Provable Decision Rule for Out-of-Distribution Detection
[2] OpenOOD: Benchmarking Generalized Out-of-Distribution Detection | Summary: The paper explores the role of the calibrated set in the performance of the g-BH algorithm for OOD detection. Theoretical results indicates the large calibrated set will improve the performance of the g-BH algorithm but small calibrated set tends to degrade the performance of
It. Then, the authors propose a novel eg-BH algorithm to tackle the limitations of g-BH algorithm on the small calibrated set. Finally, the authors conduct extensive experiments to demonstrate the correctness of the theoretical results and the validity of proposed method. In summary, this paper represents a meaningful step forward in OOD detection study and provides valuable insights into multiple hypothesis testing applications.
Claims And Evidence: Yes. This paper first verify the new finding about the g-BH algorithm on the small calibrated set by rigorous theoretical analysis and numerous experiments on real-world datasets. Then, this paper conducts extensive experiments to demonstrate the superiority of the proposed method over the g-BH algorithm on the small calibrated set.
Methods And Evaluation Criteria: Yes. This paper uses many evaluation criteria, including TPR, FPR, F1-score, AUROC, AUPR and FPR95. These criteria are suitable for the OOD detection problem.
Theoretical Claims: Yes. I check the proofs in the Appendix. especially for Theorem 4.1 and Theorem 5.3, since these theorems are the key contributions of this paper.
- Theorem 4.1 derives the distribution of conditional TPR on calibrated set, the distribution parameters are determined by the significance level and size of the calibrated set;
- Theorem 5.3 provides a concrete method for integrating multiple p-values, which is the basis of the proposed eg-BH algorithm.
Experimental Designs Or Analyses: Yes. In experiments, this paper first verifies the correctness of theoretical results. The experimental results show the same conclusions as Theorem 4.1. Then, this paper conducts extensive experiments to demonstrate the superiority of the proposed method over the g-BH algorithm on the small calibrated set.
Supplementary Material: No.
Relation To Broader Scientific Literature: This paper finds the limitations of the g-BH algorithm on the small calibrated set and proposes a novel method to address this problem.
Essential References Not Discussed: No, the paper includes all essential and relevant references.
Other Strengths And Weaknesses: Strengths
- This paper reveals the influence of calibrated set on the g-BH algorithm.
- This paper establishes a mathematical relationship between the size of the calibrated set and the conditional TPR expectation of the g-BH algorithm.
- This paper proposes a novel method to improve OOD detection performance on the small calibrated set by aggregating multiple empirical p-values.
- This paper show the impact of different calibrated set sizes using various OOD datasets (CIFAR-10, SVHN, TinyImageNet, etc.). Besides, this paper shows that the proposed method consistently outperforms g-BH algorithm on the small calibrated set.
Weaknesses
I have not found any obvious weaknesses. It would be more comprehensive if the following questions are addressed:
- The paper uses numerous terms from hypothesis testing, such as type-1 error, significant level and FDR, which may lead to difficulties for the readers unfamiliar with hypothesis testing. So the author should provide more explanations for these concepts.
- In Theorem 4.1, what are the assumptions about the score functions?
- In Algorithm 1, how do you choose the number L?
Other Comments Or Suggestions: No
Questions For Authors: See above
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: __Weakness 1__: about the interpretations of some concepts, including type-1 error, significant level and FDR.
__Ans1__: we interpret these concepts as follows:
Significance level: If the probability of obtaining a result as extreme as the one obtained, supposing that the null hypothesis were true, is lower than a pre-specified cut-off probability (for example, 5%), then the result is said to be statistically significant (the null hypothesis is rejected), and the cut-off probability is called significant level.
Type-1 error and FDR: In statistical hypothesis testing, a type-1 error is the rejection of the null hypothesis when it is actually true.
FDR can be considered as the generalization of the probability of type-1 error in single hypothesis testing. In multiple testing, the null hypotheses rejected by the detection algorithms are called discoveries. FDR is used to describe the expected proportion of erroneous discoveries among all discoveries.
__Weakness 2__: in Theorem 4.1, what are the assumptions about the score functions?
__Ans2__. We just require that the score function is continuous, without more strong assumptions. For example, two famous score functions MSP and Energy satisfy this demand.
__Weakness 3__: in Algorithm 1, how do you choose the number L?
__Ans3__: In practice, we can obtain a well performance of OOD detection when L is set to 3 or 4. | Summary: Based on the recent work [1], this paper aims to study the influence of the calibrated set on the generalized BH (g-BH) algorithm for out-of-distribution (OOD) detection task. By theoretical analysis and experimental results on the real data, the authors show that the small calibrated set tends to degrade the performance of the g-BH algorithm. Then, the authors propose an enhanced approach, the ensemble g-BH (eg-BH) algorithm, which integrates multiple empirical p-values to solve this issue. The claims in this paper are built on strong theoretical foundations and supported by extensive empirical validation
Claims And Evidence: Yes.
Methods And Evaluation Criteria: Yes.
Theoretical Claims: Yes. I check some proofs in Appendix, but do not carefully read them step by step.
Experimental Designs Or Analyses: Yes. they seems quite sound.
Supplementary Material: No.
Relation To Broader Scientific Literature: This paper provides a new decision framework based on the existing score functions, which enables to be adapted to small calibrate set.
Essential References Not Discussed: No, the paper includes all essential and relevant references.
Other Strengths And Weaknesses: Strengths
(1) Theoretical analysis. The authors develop a novel theoretical understanding of the role of calibrated set in the g-BH algorithm.
(2) Novel method. The proposed method extends g-BH algorithm by integrating multiple empirical p-values, mitigating the problem due to small calibrated set.
(3) Extensive performance. The experimental setup, including the variation of calibrated set sizes, provides strong empirical support for the theoretical results. Additionally, the the authors use different score functions, such as Energy-based and Maximum Softmax Probability, to assess the robustness of the proposed approach on various benchmarks.. The evaluation is comprehensive, ensuring the generalizability of the results.
Weaknesses
(1) The proposed method requires a hold-out set. However, since the hold-out set consists of ID examples, this is not a significant restriction.
(2) Why does the authors only use the empirical p-values in Algorithm 1?
(3) Suggest checking and standardizing the format in Section 4.
Other Comments Or Suggestions: No
Questions For Authors: See Weaknesses
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: __Weakness 1__: the proposed method requires a hold-out set. However, since the hold-out set consists of ID examples, this is not a significant restriction.
__Ans1__: We emphasize that the calibrated set consists of ID data, without the need of OOD data. We directly extract some examples from training data to construct calibrate set. Hence, it is easy to obtain a calibrated set for our proposed method.
__Weakness 2__: why does the authors only use the empirical p-values in Algorithm 1?
__Ans2__: We must clarify that in practice, any valid computation methods that satisfy the definition of p-values can be used. Since the distribution of ID data is unknown, we choose a non-parametric method: empirical p-values to estimate real p-values. Essentially, it is equivalent to use empirical distribution to estimate real distribution.
__Weakness 3__: Suggest checking and standardizing the format in Section 4.
__Ans3__: Thanks for your careful review. We have checked the typos in Section 4. We will fix these typos in new version.
---
Rebuttal Comment 1.1:
Comment: Thanks author for the response. They have answered my questions well. I keep my positive score. | Summary: This paper investigates the impact of the calibrated set on the generalized BH (g-BH) algorithm[1] for Out-of-Distribution (OOD) detection. The authors provide a theoretical analysis showing that the conditional expectation of the true positive rate (TPR) follows a beta distribution, demonstrating that a small calibrated set negatively affects performance of g-BH algorithm. To address this problem, they introduce the ensemble g-BH (eg-BH) algorithm, which integrates multiple empirical p-values for decision-making. Extensive experiments validate the theoretical findings, and show that eg-BH algorithm outperforms g-BH algorithm, particularly on small calibrated set.
Claims And Evidence: Yes.the claims made in the submission appear to be supported by clear and convincing evidence.
Methods And Evaluation Criteria: Yes. the proposed method makes sense for the OOD detection.
Theoretical Claims: Yes. I check some proofs, including Theorem 4.1, Lemma 5.1, Theorem 5.2 and Theorem 5.3.
Experimental Designs Or Analyses: Yes. The experimental designs and analyses are sound.
Supplementary Material: No.
Relation To Broader Scientific Literature: This paper focus on studying the influence of calibrated set on the performance of the g-BH algorithm. Besides, to address the problem caused by small calibrated set, this paper proposes the eg-BH algorithm to integrate the multiple empirical p-values for making decision.
Essential References Not Discussed: No.
Other Strengths And Weaknesses: The analytical framework of this paper is well-grounded in the statistical hypothesis testing. Hence, the conclusions have strong theoretical guarantee. The paper presents a rigorous theoretical analysis for the g-BH algorithm, demonstrating that small calibrated set tends to weaken the performance of it. The proposed eg-BH algorithm effectively enhances OOD detection performance on small calibrated set by integrating multiple empirical p-values, compared with g-BH algorithm. Extensive experimental results demonstrate the effectiveness of the proposed method.
Some weaknesses are listed below:
W1: The proposed eg-BH algorithm depends on multiple p-values. the advantages of integrating multiple p-values should be discussed.
W2 The proofs in line 572 - line 583 in appendix should be more detailed.
Other Comments Or Suggestions: No.
Questions For Authors: What are the advantages of controlling FDR?
Code Of Conduct: Affirmed.
Overall Recommendation: 5 | Rebuttal 1:
Rebuttal: __W1__: The proposed eg-BH algorithm depends on multiple p-values. the advantages of integrating multiple p-values should be discussed
__Ans1__. A small calibrated set leads to under-representative empirical p-values, which fail to capture the distributional
characteristics of the ID data. To address this issue, we utilize the available
information in training set to generate multiple empirical p-values. We then integrate these empirical p-values to a single p-value with more information of ID data, making it more discriminative.
__W2__. The proofs in line 572 - line 583 in appendix should be more detailed.
__Ans2__. Following your suggestions, the detailed steps are as follows:
$$
\begin{aligned}
\mathbb{E}(\mathrm{TPR}| \mathcal{T}^{cal}) & = \mathbb{P}(f(p(X_{1}^{test})) > \alpha | \mathcal{T}^{cal}) \\\\
& = \mathbb{P}\left( \frac{ \sum_{j=1}^m \mathbf{1}(s(X_{j }^{cal})\leq s(X_{i}^{test}))+1}{m+1} > f^{-1} (\alpha) | \mathcal{T}^{cal} \right) \\\\
& = \mathbb{P}\left( \sum_{j=1}^m \mathbf{1}(s(X_{j }^{cal})\leq s(X_{i}^{test})) > f^{-1} (\alpha)(m+1 ) - 1 | \mathcal{T}^{cal} \right) \\\\
& = \mathbb{P}\left( \frac{ \sum_{j=1}^m \mathbf{1}(s(X_{j }^{cal})\leq s(X_{i}^{test}))}{m} > \frac{f^{-1} (\alpha)(m+1 ) - 1 }{m} | \mathcal{T}^{cal} \right) \\\\
& = \mathbb{P}\left( \hat{F} ( s(X_{i}^{test})) > \frac{f^{-1} (\alpha)(m+1 ) - 1 }{m} |\mathcal{T}^{cal} \right)
\end{aligned}
$$
__Q1__. What are the advantages of controlling FDR?
__Ans3__. It is well-known that there is a tradeoff between the detection performance of ID and OOD examples for a trained score functions. Therefore, we cannot only consider the true positive rate (TPR) or false positive
rate (TPR) when designing the OOD detection algorithm. Factually, an ideal OOD detection algorithm should achieve low FPR while maintaining a high TPR, which leads to a small FDP. Thus, controlling FDR can achieve a well tradeoff between the detection performance of both ID and OOD examples.
---
Rebuttal Comment 1.1:
Comment: My questions have been addressed. Thanks for the reply. | null | null | null | null | null | null |
The Meta-Representation Hypothesis | Reject | Summary: This paper proposes "the meta-representation hypothesis", i.e., learning a representation that reflects the abstract, high-level understanding of inputs can lead to better generalization of RL agents. The paper models the generalization problem in RL using an MDP generator and assumes that all different MDPs the agent interacts with are generated from the same underlying MDP. Theoretically, the paper shows that minimizing the TV distance between the policies in different MDPs could improve the lower bound of the generalization performance. Empirically, the paper shows that deep mutual learning (DML) can regularize the agent's representations, resulting in improved generalization (though I think the main idea is slightly different from the original DML, see "Other comments and suggestions" for details). The proposed method is evaluated on Procgen.
**Post rebuttal update:**
After considering the author's rebuttal and going through all the reviews, I decided to lower my score by 1 due to two reasons: (1) the authors did not provide a convincing clarification of the difference between the proposed "meta-representation" and invariant representations; (2) the main idea of using DML in RL to facilitate generalization turns out to be not new. I also think addressing (1) may require quite a bit of rewriting, which I would let AC and other reviewers decide whether it warrants another round of review.
Claims And Evidence: All claims made in the paper are supported by theoretical or empirical evidence.
Methods And Evaluation Criteria: The proposed method and evaluation criteria all make sense to me.
Theoretical Claims: I briefly skimmed through the proofs and did not find any major problems.
Experimental Designs Or Analyses: The main experiments are conducted on Procgen, which is a standard benchmark for RL generalization. The authors mainly compare their method with a standard PPO baseline, which is acceptable in my opinion since the authors do not claim to achieve state-of-the-art performance but mostly focus on demonstrating the effectiveness of DML. Visualizations and ablations are sufficient.
Supplementary Material: I reviewed all supplementary materials.
Relation To Broader Scientific Literature: In my opinion, the claimed main contributions of the paper are twofold:
- Theoretical analysis showing that robustness to irrelevant features can facilitate RL generalization.
- Empirical analysis showing that DML improves RL generalization.
Given the naturality of the first point, I think its contribution to the broader scientific literature is a bit limited---quite similar ideas have been proposed and at least partially analyzed in related areas such as invariant representation learning and representation learning in RL (see "Essential references not discussed" for more details).
I think the second point is more interesting---although DML itself is not new, to my knowledge, applying similar ideas to RL by simultaneously training multiple agents and letting them mutually regularize each other's policies to improve generalization is novel.
Essential References Not Discussed: I think prior work in two related areas should be discussed:
- **Invariant representation learning:** The authors view "meta-representations" as representations that induce the same policy for all MDPs with the same underlying MDP. This formulation is similar to learning invariant representations across multiple training domains, which was first proposed in the supervised learning context (e.g., [1]) and has also been extended to RL [2].
- **Representation learning in RL:** Meta-representations also relate to state representations that discard task-irrelevant information in the agent's raw observations, e.g., via bisimulation metrics [3]. Discussing the work in this area is also necessary.
[1] Arjovsky et al. Invariant risk minimization. 2019.
[2] Sonar et al. Invariant policy optimization: Towards stronger generalization in reinforcement learning. L4DC, 2021.
[3] Learning invariant representations for reinforcement learning without reconstruction. ICLR, 2021.
Other Strengths And Weaknesses: **Strengths:** The paper is well-written.
**Weaknesses:** The theoretical part is a little hard to follow. In particular, I do not really get the necessity of introducing the first-order approximation $L_{\pi}$ as in TRPO.
Other Comments Or Suggestions: In the original DML paper, different models are trained on the data with the _same_ distribution. Yet in this work, different agents mostly sample different MDPs with _different_ state distributions (this is also reflected in the motivating example in Appendix B). The authors may consider discussing this point in more detail.
Questions For Authors: - What is the relation between "meta-representations" and invariant representations in the literature?
Ethical Review Concerns: N/A
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: Dear Reviewer twjt,
Thank you for your positive assessment of our work. Below, we will address your concerns.
>I think prior work in two related areas should be discussed:
>- **Invariant representation learning** [1, 2].
>- **Representation learning in RL** [3].
Thank you for your valuable suggestion. As the rebuttal process does not permit submitting revised PDF files, we will address these two aspects in the related work section of our future extended version.
>The theoretical part is a little hard to follow. In particular, I do not really get the necessity of introducing the first-order approximation $L_ {\pi}$ as in TRPO.
We would be happy to briefly explain for you. We first define the training performance
$$\eta(\pi)=\frac{1}{1-\gamma}\mathbb{E}_ {f\sim p_{\mathrm{train}}(\cdot),s\sim d^{\mu_f}(\cdot),a\sim\mu_f(\cdot|s)}[r(s,a)].$$
Next, according to the performance difference lemma, we have
$$\eta(\tilde{\pi})=\eta(\pi)+\frac{1}{1-\gamma}\mathbb{E}_ {f\sim p_{\mathrm{train}}(\cdot),s\sim d^{\tilde{\mu}_f}(\cdot),a\sim\tilde{\mu}_f(\cdot|s)}[A^{\mu_f}(s,a)].$$
Therefore, our objective is to obtain an updated policy $\tilde{\pi}$ based on $\pi$. However, the state distribution $s\sim d^{\tilde{\mu}_f}(\cdot)$ and action distribution $a\sim\tilde{\mu}_f(\cdot|s)$ in their performance difference are all sampled from the new policy $\tilde{\pi}$, where $\tilde{\mu}_f(\cdot|s)=\tilde{\pi}(\cdot|f(s)),\forall f\in\mathcal{F}$, which is clearly infeasible since $\tilde{\pi}$ is unknown at this stage.
Therefore, we must approximate the state distribution (replace $\tilde{\pi}$), which naturally leads to
$$L_ {\pi}(\tilde{\pi})=\eta(\pi)+\frac{1}{1-\gamma}\mathbb{E}_ {f\sim p_{\mathrm{train}}(\cdot),s\sim d^{\mu_f}(\cdot),a\sim\tilde{\mu}_f(\cdot|s)}[A^{\mu_f}(s,a)].$$
>I think the second point is more interesting---although DML itself is not new, to my knowledge, applying similar ideas to RL by simultaneously training multiple agents and letting them mutually regularize each other's policies to improve generalization is novel.
>In the original DML paper, different models are trained on the data with the _same_ distribution. Yet in this work, different agents mostly sample different MDPs with _different_ state distributions (this is also reflected in the motivating example in Appendix B). The authors may consider discussing this point in more detail.
Thank you for your insightful comments and suggestions—this is indeed the core motivation and a key distinction from the original DML. We will highlight this distinction in subsequent versions by further expanding Appendix B.
>What is the relation between "meta-representations" and invariant representations in the literature?
This is a good question. As you mentioned in the two papers [2, 3], similar concepts have indeed been explored. However, while these approaches typically decouple the generalization problem into robust representation learning (encoder $\phi$) and downstream policy learning, our method is **theoretically and empirically end-to-end.**
Note that our entire paper never introduces an upstream encoder $\phi$, and we find our approach both more elegant and simpler, as it removes the need to decouple the encoder $\phi$'s learning process from the reinforcement learning process, everything is end-to-end.
Ultimately, while meta-representations and invariant representations are conceptually similar, we argue that **the notion of meta-representations is more general**. This is because the agent does not need to explicitly learn a robust encoder; instead, the entire end-to-end policy only needs to improve robustness to irrelevant features. Consequently, components beyond the upstream encoder (such as downstream MLPs in the policy network's architecture) may also contribute to this robustness.
Best,
Authors
---
*Reference:*
[1] M Arjovsky et al. Invariant risk minimization.
[2] A Sonar et al. Invariant policy optimization: Towards stronger generalization in reinforcement learning.
[3] A Zhang et al. Learning invariant representations for reinforcement learning without reconstruction.
---
Rebuttal Comment 1.1:
Comment: Thank you for your response. I found the clarification on the theory part helpful.
However, honestly, I am not satisfied with the response regarding the comparison between "meta-representations" and invariant representation learning.
- As you mentioned, end-to-end training is appealing, yet it does not deny that these two terms are conceptually similar under your current definition---whether using an explicit encoder or not is only at an implementation level.
- This point appears to be quite important given that you have heavily emphasized the conceptual/philosophical value of "meta-representations" all over the paper.
- In fact, even if you add more discussion with the invariant representation learning methods to the related work section, I still feel that the overall presentation can be quite misleading to readers who are not familiar with the invariant representation learning literature, which I am not sure if it can be addressed without quite a bit rephrasing.
I will also raise this point in the reviewer-AC discussion phase.
Also, I noticed that you quoted my review in your response to Reviewer ByPb. It turns out that I indeed missed [1] as one of the closely related works. To avoid further misunderstanding, I will also leave a brief clarification there. Sorry for the inconvenience.
---
[1] Zhao, Chenyang, and Timothy Hospedales. Robust domain randomised reinforcement learning through peer-to-peer distillation. ACML, 2021.
---
Reply to Comment 1.1.1:
Comment: Dear Reviewer twjt,
Thank you for your additional comments. Below, we will provide a comprehensive response to your feedback.
>As you mentioned, end-to-end training is appealing, yet it does not deny that these two terms are conceptually similar under your current definition---whether using an explicit encoder or not **is only at an implementation level**.
Thank you for your response. However, the concept of meta-representation differs from invariant representation not only at the implementation level. To clarify this point, we refer to several papers on invariant representation learning [2, 3] and formally define the concept of invariant representation as follows:
In the framework of invariant representation learning, we define the policy as $\Delta_ {\mathcal{A}}=\pi(o_ t)$, where $o_ t$ is observation and $\Delta_ {\mathcal{A}}$ is the probability distribution over the action space $\mathcal{A}$, is obtained as a composition $\pi=h\circ g$.
We can regard $z=g(o_t)$ as a learned representation of $o_ t$, and a smaller mlp $\Delta_ {\mathcal{A}}=h(z)$, predicting probability distribution $\Delta_ {\mathcal{A}}$ given representation $z$, both of which are shared across domains.
Using this framework, we can strive to learn an "invariant" representation $z$ across the source domains, with the hope of achieving better generalization to the target domain. Therefore, invariant representation learning emphasizes the robustness of the upstream encoder $g$ across different domains, i.e.,
$\min_ {g}\Vert g(o)-g(\tilde{o})\Vert,$
where $o$ and $\tilde{o}$ represent observations of the same underlying state from different domains.
For meta-representations, formally, we do not decouple the policy $\pi$ to $h\circ g$. Instead, we directly emphasize the robustness of $\pi$ to $o$ and $\tilde{o}$, i.e.,
$\min_ {\pi}\Vert\pi(\cdot|o)-\pi(\cdot|\tilde{o})\Vert.$
In summary, meta-representation focuses on the invariance of the output (see the explanation of Definition 3.6 in our paper), while invariant representation learning mainly emphasizes learning an invariant representation $z$.
We acknowledge that meta-representations share conceptual similarities with invariant representations. However, to highlight the subtle distinctions between them (as discussed above), we introduced the term "meta-representation." We apologize for any confusion this may have caused.
>...I still feel that the overall presentation can be quite misleading to readers who are not familiar with the invariant representation learning literature...
Thank you for your valuable comments! To avoid any misleading implications for readers who are not familiar with invariant representation learning, we will definitely **highlight the subtle distinction** between meta-representation and invariant representation in the related work section.
>It turns out that I indeed missed [1] as one of the closely related works...
We sincerely appreciate your thorough review. Indeed, [1] is relevant to our work, and we will add it to the related work section in the revised version. We did read [1] and recognize some methodological similarities with our approach, yet we note **four** key differences:
- **Theoretical Contribution:** [1] primarily provides _empirical_ evidence for the effectiveness of mutual distillation, without theoretical analysis of _why_ it works. In contrast, we prove that generalization performance benefits from policy robustness to irrelevant features, which is a strong theoretical contribution.
- **A Stronger Insight:** In [1], the authors argue that mutual distillation facilitates knowledge sharing between students. However, we demonstrate that DML actually enhances the student's robustness to irrelevant features. We provide strong evidence for this statement using t-SNE and random CNNs.
- **Domain Sampling Mechanism:** In [1], the authors argue that training across multiple domains may lead to high variance, so in each iteration, each student $\pi_ i$ collects data only from a specific domain $\xi_ i$. However, we demonstrate that students can indeed be trained across multiple domains, with DML serving as a form of mutual regularization.
- **Harder Generalization:** In [1], the domain distribution is defined by the authors, whereas in our experiments, it is unknown, making generalization even more challenging.
In summary, we acknowledge the relevance of these two works, but we also emphasize the additional contributions our work makes to the generalization of reinforcement learning, particularly the non-trivial theoretical analysis.
Best,
Authors
---
*Reference:*
[1] C Zhao et al. Robust domain randomised reinforcement learning through peer-to-peer distillation.
[2] AT Nguyen et al. Domain invariant representation learning with domain density transformations.
[3] H Qi et al. Data-driven offline decision-making via invariant representation learning. | Summary: The paper deals with RL environments where the observations presented to an agent are noisy transformations of the true state via a rendering function that is drawn from an environment dependent distribution.
This paper first rigorously demonstrates how generalization performance of RL agents can suffer if the features they learn to use are not robust to noise. It is theoretically shown that the lower bound of the generalization performance can be improved by improving robustness.
The paper then proposes that Deep Mutual Learning can help introduce this robustness. This is based on intuition, and is then demonstrated empirically in various environments.
## Update after review
Rating unchanged. I believe this is a borderline accept. I believe the evaluation is not comprehensive enough for a higher rating.
Claims And Evidence: Claim 1:
The generalization performance of a policy under the specific setting of the randomly sampled rendering function (required to be a bijection) is affected by the robustness of the policy to changes in the rendering function.
This is proven theoretically.
Claim 2:
Deep Mutual Learning induces more robust features that help generalization.
This is supported by a variety of experiments that show how the policy's performance does not degrade as rapidly under noisy observations as it would without DML. The experiments cover a variety of environments.
The only concern I have here is that the evaluation is limited to only specific kinds of distributions of rendering functions.
Methods And Evaluation Criteria: Methods:
The proposed method is not novel - it is an existing method.
Evaluation:
The evaluation is sound and covers two key aspects:
1. Robustness - The primary metric is the divergence of the policy when the observations that the agent gets for the same state are changed by addition of noise.
2. Performance - The evaluation criteria also includes the average performance of the learned policies under different rendering functions, specifically under different addition of noise through randomized Gaussian filters.
Theoretical Claims: Did not find any issues in the theoretical results and their proofs.
Experimental Designs Or Analyses: The experiments and analyses are reasonably designed and are a good way to test the validity of the claims. However, I found the choice of rendering functions tested in the experiments to be very limited. See section on strengths and weaknesses for details.
Supplementary Material: Proofs in supplementary look correct.
Relation To Broader Scientific Literature: This paper is loosely related to the broader literature on meta-representations. The paper is more closely related to works on robust policy learning. The paper presents a proof of a widely held intuition that robustness to noisy observations improves performance. This is novel in my knowledge. There are no novel methods proposed in the paper based on the claim. However, an existing method (Deep Mutual Learning) is evaluated on the criteria shown in the paper.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: The paper does rigorously show how robustness to changes in the rendering function can affect performance, and why it is important to be tolerant to such changes. This is a useful result. The experiments also nicely show how DML can help tackle some of these changes. This evaluation is a good benchmark to check if an RL method is robust to some noise.
I, however, found that the evaluation in the paper is limited to a narrow set of rendering function changes. I believe this limits the significance of the experiments in the paper. Major changes in the rendering function are not considered. E.g. what if in a game the sprite is changed across episodes? In this sense, I find that the experiments are talking more about robustness to noise, rather than generalization across a wide variety of rendering functions. The paper does allude to generalization of this kind in all sections except the experiment section.
Other Comments Or Suggestions: N/A
Questions For Authors: 1. Can this be evaluated under a broader distribution of rendering functions?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Dear Reviewer Rz5E,
Thank you for your positive feedback on our paper. Below, we will address your concerns.
>The only concern I have here is that the evaluation is limited to only specific kinds of distributions of rendering functions.
>I, however, found that the evaluation in the paper is limited to a narrow set of rendering function changes. I believe this limits the significance of the experiments in the paper. Major changes in the rendering function are not considered. E.g. what if in a game the sprite is changed across episodes? In this sense, I find that the experiments are talking more about robustness to noise, rather than generalization across a wide variety of rendering functions. The paper does allude to generalization of this kind in all sections except the experiment section.
>Can this be evaluated under a broader distribution of rendering functions?
Thank you for your insightful comments. However, the observation that our experiments were evaluated under limited rendering functions might be a misunderstanding.
Please note that the Procgen environment samples from a nearly infinite pool of levels when testing generalization performance (each level can be considered as a specific rendering function, since the task semantics remain unchanged). We would like to quote the first paragraph of Section 2 in the original paper of Procgen [1]:
>_The Procgen Benchmark consists of 16 unique environments designed to measure both sample efficiency and generalization in reinforcement learning. These environments greatly benefit from the use of procedural content generation—the algorithmic creation of **a near-infinite supply** of highly randomized content. In these environments, employing procedural generation is far more effective than relying on fixed, human-designed content._
You may also refer to our anonymous website at https://dml-rl.github.io/. In the Coinrun environment specifically, the sprite do change across different episodes. Our generalization curves are indeed tested through sampling from a **near-infinite set of rendering functions:** during training, agents only have access to a limited set of rendering functions, i.e., the first 500 levels, while generalization performance is evaluated across an **infinite number of levels**. We hope this addresses your core concerns.
Best,
Authors
---
*Reference:*
[1] K Cobbe et al. Leveraging procedural generation to benchmark reinforcement learning. | Summary: The paper proposes to combine Deep Mutual Learning with RL. In Deep Mutual Learning, several learners learn independently but at the same try to minimize the KL between their predictive distributions. The paper hypothesizes that two RL policies can learn from different MDPs — where each MDP has its own randomly sampled observation function while the policies try to minimize the KL between them. This would lead to the learning of robust representation functions. The randomly perturbed observation function is a key aspect of the paper — in their paper they apply a CNN with random weights to the observation to map the true observation to a perturbed one. The paper tests this hypothesis via PPO and shows that Deep Mutual Learning is helpful for generalization on the Procgen Benchmark.
Claims And Evidence: Yes.
Methods And Evaluation Criteria: Yes.
Theoretical Claims: Yes, there are theoretical claims, but I have not checked them thoroughly due to my broader concerns about novelty.
Experimental Designs Or Analyses: Yes, the experimental design is sound.
Supplementary Material: I have looked at them briefly.
Relation To Broader Scientific Literature: See my comments in the "Cons" section below.
Essential References Not Discussed: [1] Zhao, Chenyang, and Timothy Hospedales. "Robust domain randomised reinforcement learning through peer-to-peer distillation."
Other Strengths And Weaknesses: ## Pros
1. Tackles an important problem about having a robust perception function for RL.
2. A positive thing is that the whole model is learned end-to-end via RL rather than separately learning a representation model.
## Cons
1. The idea of RL + DML appears to be not very novel as a similar thing is explored here [1]. Therefore I believe the key novelty is mainly about how one can get perturbed MDPs. However, I tend to think that the randomized CNN approach is a bit too simplistic. See my comment in the “Questions for Authors” section.
2. Only evaluates PPO. It could help to have a few other RL algorithms.
3. Why are existing representation learning approaches not worthy candidates for comparison as encoders? Just seeking clarification rather than asking for additional baselines. For instance, there are many representation learning methods that can be considered to learn robust features e.g., approaches like SimCLR [2, 3] use data augmentation by having jitter, distortions, etc.
4. It would be useful to analyze the informativeness of the meta-representation. It is possible that the representation is a lossy one. This isn’t necessarily a bad thing, just that some insight about it needs to be shared with the community — and how lossy this representation e.g., does it simply erase the textural information from the representation while retaining only edge features? If yes, then tasks that rely on textural information information might suffer.
5. More ablation could help. A simple ablation is to mix the MDPs during training without using mutual learning. I would be curious what effect that has or what difference that would have with the proposed one.
[1] Zhao, Chenyang, and Timothy Hospedales. "Robust domain randomised reinforcement learning through peer-to-peer distillation."
[2] Chen, Ting, et al. "A simple framework for contrastive learning of visual representations.”
[2] Agarwal, Rishabh, et al. "Contrastive behavioral similarity embeddings for generalization in reinforcement learning.”
Other Comments Or Suggestions: Resolve the Cons.
Questions For Authors: Are there ideas about how to go beyond just CNN-weight randomization for sampling the $f$s? The kind of variations we see in the real world are more systematic in nature: changes in lighting, camera angle, and shininess. Or it could be factor changes e.g., size or color changes. Many of these cannot be achieved by CNN-weight randomization. On a related note, are there any thoughts on how this kind of MDP variation can be obtained in real-world data?
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: Dear Reviewer ByPb,
Thank you for your careful evaluation on our paper. Below, we will address your concerns.
>The idea of RL + DML appears to be not very novel. Therefore I believe the key novelty is mainly about how one can get perturbed MDPs. However, I tend to think that the randomized CNN approach is a bit too simplistic.
The concept of DML is not novel and was used in supervised learning. However, although our core algorithm is based on existing methods, the DML used in this paper is **with strong motivation** and different from the original one. We would like to quote reviewer twjt's comment: "_Although DML itself is not new, to my knowledge, applying similar ideas to RL by simultaneously training multiple agents and letting them mutually regularize each other's policies to improve generalization is novel._"
Moreover, we conducted an in-depth analysis of why DML is effective and provided both theoretical and empirical evidence demonstrating its generalization benefits, thereby constituting our additional contribution.
>Only evaluates PPO. It could help to have a few other RL algorithms.
Thank you for your suggestion. We have added two additional baselines, SPO and PPG. We have the following generalization performance results:
| Algorithm | bigfish | dodgeball | fruitbot | starpilot |
|--------|-----|------|------|------|
| SPO | $1.16\pm1.03$| $1.74\pm1.0$| $2.21\pm1.82$ | $6.16\pm1.42$ |
| SPO with DML | $5.44\pm2.92$| $5.22\pm1.57$ |$1.12\pm1.02$ | $8.43\pm2.19$ |
Considering that PPG is an enhanced version of PPO that incorporates additional distillation strategies with relatively complex implementation, we specifically compare the generalization performance between standard PPG and PPG utilizing the frozen encoder obtained from PPO with DML:
| Algorithm | bigfish | dodgeball | fruitbot | starpilot |
|--------|-----|------|------|------|
| PPG (original) | $11.67\pm5.71$| $6.43\pm1.65$| $20.23\pm1.79$ | $11.97\pm3.2$ |
| PPG (DML encoder) | $30.0\pm4.95$| $9.28\pm2.5$ |$19.07\pm1.82$ | $18.97\pm4.27$ |
**More details:** https://anonymous.4open.science/r/meta-hypothesis-rebuttal-C70B/README.md
>Why are existing representation learning approaches not worthy candidates for comparison as encoders?
Thanks. Indeed, there are numerous works based on data augmentation. However, data augmentation introduces additional prior knowledge, which inevitably induces biases in the training data. These biases may be either beneficial or harmful to generalization, and they require human prior knowledge to guide the selection of appropriate data augmentation techniques for the given scenario.
Therefore, our approach emphasizes spontaneous learning of the underlying semantics by agents through mutual regularization, which is simple to implement, intrinsically unbiased, and generally applicable to a wide range of scenarios. More importantly, while prior works decouple the generalization problem into robust representation learning and downstream policy learning, our method is **theoretically and empirically end-to-end.**
>It would be useful to analyze the informativeness of the meta-representation... Does it simply erase the textural information from the representation while retaining only edge features? ...
Thank you for your constructive insights. This depends on specific scenarios. The total loss consists of both RL loss and KL regularization loss. If texture features are important for the current task, the agent will learn to preserve them, as removing such features would make the RL loss term harder to optimize, potentially resulting in suboptimal policy performance.
>More ablation could help. A simple ablation is to mix the MDPs during training without using mutual learning...
Thank you for your suggestion. However, directly mixing the training data from both agents may not be theoretically sound, as PPO's reinforcement learning loss requires data sampled from the old policy for computation, and the data distributions sampled by the two policies could differ. Therefore, we **have included an ablation study** with a PPO baseline that uses double the batch size and number of interactions. Due to response length limitations, please refer to the table in our response to reviewer bqXb and our link.
>Are there ideas about how to go beyond just CNN-weight randomization for sampling the $f$s?
We appreciate the insightful feedback. Indeed, the real-world variations are challenging to capture via CNN randomization alone. We also **tested the robustness of DML under different brightness, contrast, and hue conditions**, see https://anonymous.4open.science/r/meta-hypothesis-rebuttal-C70B/README.md
For real-world MDP variation, we could consider: (a) Vary factors (e.g., lighting/angle) in real-world datasets using robotic platforms, e.g., habitat. (b) Leverage physics-aware tools, e.g., Omniverse, to simulate plausible variations (e.g., shadows) on real data.
Best,
Authors | Summary: The paper tackles generalisation in reinfocement learning introducing the concept of "meta-representation", which is an abstract representation of a state shared by all instances with shared semantics, and separated from the details of a particular high-dimensional observation.
The paper brings two (almost separated) contributions:
1. A theoretical claim around a theory of generalization in reinforcement learning. By proving a couple of bounds, the authors make a formal argument for their claim that policy robustness to irrelevant features contributes to improved generalization.
2. A hypothesis that deep mutual learning helps learning more robust features, improving generalisation across environments sharing the same semantics. A set of experiments show better generalisation when DML is applied on top of a popular Deep RL algorithm (PPO).
Claims And Evidence: 1. The central hypothesis about DML helping learning meta-representations, threfore improving generalization performance is supported by experiments on top of a PPO baseline in the Procgen environment.
Two additional experiments further support the hypothesis:
1. random convolutional features to demonstrate the variance of a trained encoder to noisy observations
2. retraining policies on top of frozen encoders
Methods And Evaluation Criteria: ProcGen is an appropriate benchmark to measure generalisation in RL.
PPO represents a good baseline.
Theoretical Claims: I did check the correctness of the proofs (also reviewed the supplementary material) and found no errors.
Experimental Designs Or Analyses: Did you correct for the "actual" number of environment interactions?
Does the DML combo with two policies see double the states compared to the PPO baseline?
An ablation for the number of parameters would also make a more compelling argument.
Supplementary Material: Reviewed.
Relation To Broader Scientific Literature: Section 6 lists the relevant works, although discussing in more detail what each reference brings would be a better way to present them than just enumerating a long list.
Although it's understandable given the paper length constraints, section 6 could be expanded and would make the submission stronger.
Essential References Not Discussed: Not aware of anything major missing.
Other Strengths And Weaknesses: Strengths
1. Careful formalisation of the problem and the central claims.
2. Experiments clearly support the hypothesis in the context of PPO.
Weaknesses
1. Limited evaluation (a single algorithm as baseline, a single set of environments).
Other Comments Or Suggestions: I won't comment on the philosophical bits in the paper, but a process is not an insight. Maybe rephrase that.
Questions For Authors: 1. The theory assumes a bijection between the real state space and the observation space, which excludes many cases where partial observability collapses multiple states under the same observation. Could you comment on how your theory would extend to Partial observability, or how important the assumption of such a bijection is beyond formalising the problem?
2. Could you add an ablation for the number of parameters? PPO+DML trains two models (double the parameters) compared to the baseline, doesn't it?
3. Could you add an ablation for the number of steps (or just reuse the data to make a plot with the number of transitions performed on the x axis)?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Dear Reviewer bqXb,
Thank you for your constructive feedback on our paper! Below, we will address your concerns.
>Did you correct for the "actual" number of environment interactions? Does the DML combo with two policies see double the states compared to the PPO baseline?
Thanks. First, the two policies indeed double the actual number of interactions. However, when computing their respective losses, the two agents **cannot** directly access each other's training data for RL training. Specifically, assume that agent A (denote as $\pi_ A$) collects a batch of training data $\mathcal{D}_ A=\textbraceleft(o_ 1^A,a_ 1^A,r_ 1^A),\dots,(o_ k^A,a_ k^A,r_ k^A)\textbraceright$, agent B (denote as $\pi_ B$) collects a same batch of training data $\mathcal{D}_ B=\textbraceleft(o_ 1^B,a_ 1^B,r_ 1^B),\dots,(o_ k^B,a_ k^B,r_ k^B)\textbraceright$. Then, the total loss for agent A is
$\mathcal{L}_ {A}=\underbrace{\mathcal{L}_ {\mathrm{RL}}(\mathcal{D}_ A)}_ {\mathrm{\text{RL loss}}}+\underbrace{\frac{1}{k}\sum_ {i=1}^{k}D_ {\mathrm{KL}}(\pi_ B(\cdot|o_ i^A)\Vert\pi_ A(\cdot|o_ i^A))}_ {\mathrm{\text{DML loss}}}$
Here, agent A's total loss $\mathcal{L}_ {A}$ only involves agent A's **own** dataset $\mathcal{D}_ A$, while the DML loss serves as a regularization term. Therefore, from each agent's own perspective, the number of interactions remains consistent with the baseline.
>Could you add an ablation for the number of parameters?
>Could you add an ablation for the number of steps...?
**We have added the ablation experiments with double parameters.** To ensure fairness, we also doubled the batch size and total number of interactions for the PPO baseline. The table below shows the generalization performance across four environments:
| Algorithm | bigfish | dodgeball | fruitbot | starpilot |
|--------|-----|------|------|------|
| PPO (original) | $0.26\pm0.23$| $0.92\pm0.46$| $-0.5\pm0.81$ | $3.99\pm1.21$ |
| PPO (double parameters, batch size and interactions) | $3.99\pm4.06$| $1.94\pm0.81$ | $8.58\pm3.99$ | $3.18\pm1.33$ |
| PPO with DML (ours) | $16.11\pm4.63$| $5.66\pm1.98$ | $13.23\pm3.04$ | $11.28\pm3.04$ |
>Limited evaluation.
**We provided an additional RL baseline** with our method, please see Fig.2 in our link.
**For more results**: https://anonymous.4open.science/r/meta-hypothesis-rebuttal-C70B/README.md
>Section 6 lists the relevant works, although...
Thanks! We will definitely expand the related work in Section 6 in our extended paper.
>The theory assumes a bijection between the real state space and the observation space, which excludes many cases where partial observability collapses multiple states under the same observation. Could you comment on how your theory would extend to Partial observability, or how important the assumption of such a bijection is beyond formalising the problem?
Great question! Mathematically, the POMDP problem is consistent with the theoretical framework presented in this paper. Under the POMDP setting, $s$ represents the global information, while $f$ can be regarded as a masking function that obscures the global state $s$ into partial observations $o=f(s)$. Therefore, if we regard the *underlying state* $s$ in this work as *global information* and the *rendering function* $f$ as a *masking function*, then the generalization problem can be viewed as a POMDP problem.
However, for the POMDP problem, $f$ can only be guaranteed to be surjective but not bijective. For example, for two different global information states $s_ 1$ and $s_ 2$, after applying a certain masking function $f$, $f(s_ 1)=f(s_ 2)$ could happen. In this case, $|\mathcal{O}_ f|<|S|$. Just like two similar maze environments, the global states $s_1\neq s_2$. However, by masking the dissimilar parts of the mazes, the agent's observations become identical. This results in the policy being unable to truly distinguish between these two different global states, i.e., $\pi(\cdot|f(s_1))\equiv\pi(\cdot|f(s_2))$, thus potentially failing to learn the optimal policy.
As a result, the PODMP problem is more challenging than the generalization problem in this paper, as the policy may require additional structures to facilitate learning, such as using a recurrent neural network (RNN) to encode historical information, which inherently introduces **non-Markov property**.
Best,
Authors | null | null | null | null | null | null |
Taming Diffusion for Dataset Distillation with High Representativeness | Accept (poster) | Summary: This paper utilizes DDIM inversion to map the VAE latent space into a high-normality Gaussian space. Numerous subsets are then sampled from this Gaussian distribution. The final selection is determined by identifying the subset whose distribution has the smallest loss compared to the Gaussian distribution.
The results improve across different datasets.
**## update after rebuttal:**
The author has addressed my concerns regarding the theoretical aspects and the results on CIFAR-10/100 are also greater than the state-of-the-art. I will increase my current score to Accept.
Claims And Evidence: The claims made in the submission supported by clear and convincing evidence.
Methods And Evaluation Criteria: Proposed methods make sense. The domain mapping technique efficiently generates synthetic samples that accurately capture the underlying data distribution.
All benchmark datasets are used in the dataset distillation problem.
Theoretical Claims: About the Lemma A.1 in line 577-578, the author claim: for each class C containing m images, Zc is modeled as a discrete distribution, where the m latents are independently sampled from m distinct Gaussian distributions.
this statement is not necessarily true because it assumes independence between latent variables for each image within a class. However, in most cases, VAEs do not enforce such a strict assumption. The reason is latents are not independently sampled per image and their distributions are not necessarily distinct for each image. If the model captures class-level semantics well, the means of similar images may cluster together in the latent space. Also, In a standard VAE, the encoder learns a continuous latent space rather than modeling a discrete distribution for each class.
Thus, the claim about a multi-component Gaussian mixture distribution might be incorrect.
Experimental Designs Or Analyses: The current experimental designs or analyses are soundness and validity, but there are several issues can be discussed.
1. In table 1, the results on CIFAR-10 do not appear to be state-of-the-art, as multiple existing works have reported higher performance.
2. The author does not provide results for IPC = 1 on CIFAR-10 and CIFAR-100 to compare with state-of-the-art methods.
Supplementary Material: I review the whole supplementary material.
Relation To Broader Scientific Literature: The use of DDIM inversion in this work is closely related to recent advancements in generative modeling that focus on improving sampling efficiency and controllability within the latent space.
Essential References Not Discussed: The reference of dataset distillation and diffusion models are discussed.
The authors incorporate a pre-trained Diffusion Transformer (DiT) in their implementation details section line 302, but do not specify which VAE model is used. The described process appears to involve encoding input data, mapping the latent space, sampling new latent representations, and decoding back to the original data domain. However, the role of diffusion models in this framework remains unclear.
Other Strengths And Weaknesses: There are several strengths:
1. The approach demonstrates improved performance, particularly on large-scale datasets, by leveraging a structured latent space for effective sample generation
2. The method only needs a one-time generation cost, making it computationally efficient compared to iterative optimization-based distillation techniques.
Other Comments Or Suggestions: I have no other comments.
Questions For Authors: Why the author did not compare the results with other state-of-the-art methods.
The reason for ImageNet-1K can be they handle subsets, but most other approaches can be compared for small-scale datasets CIFAR10 and CIFAR100.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: **Q1: The concern about the multi-component Gaussian mixture distribution assumption.**
A1: Thank you for highlighting this. To clarify the assumption, we offer a more comprehensive explanation here.
For current diffusion-based methods and ours, the pre-trained VAE are not conditional VAE, so both the training and inference processes of the VAE are not conditioned on the class label C. In theory, each latent variable is encoded by independent statistical parameters (mean and variance), resulting in an N-component Gaussian mixture distribution for N images. In practice, as shown in Equation (10) (in Appendix), the VAE loss includes a KL divergence term, which pulls each latent distribution moderately toward N(0, I). This results in a Gaussian mixture with overlapping components, indicating that the overall mixture distribution can be well-approximated by M (< N) effective components.
We give the visualization of the VAE space in the first column in Appendix B.4-Figure A4. Although the number of components is smaller than N, it remains challenging to fit the distribution, which is not in conflict with our method. We will add the above analysis in the updated version.
**Q2: More comparison with other SOTA methods on CIFAR-10, CIFAR-100.**
A2: We did not include comparisons with more SOTA results on CIFAR because the methods adopt varying validation settings, making us unable to perform direct comparisons. **Since our method is geared towards more practical scenarios involving large-scale datasets**, we follow the validation setting commonly adopted by these methods that support large datasets—training for 400 epochs on CIFAR.
For completeness, we also provide a comparison with [a], which achieves SOTA results on CIFAR and is trained for 1000 epochs in their paper. We directly obtained the 10 and 50 IPC distilled subsets from their official GitHub repository and evaluated them using the same validation code as in our setting to ensure a fair comparison. Our results outperform theirs under the same setup. We will include this comparison in the updated version.
| Dataset | IPC |\[a\] (ResNet-18) | Ours (ResNet-18) | \[a\] (ResNet-101) | Ours (ResNet-101) |
|-|-|-|-|-|-|
| CIFAR10 | 10 | 36.4±0.3 | 41.3±0.1 | 30.4±0.6 | 35.8±0.6 |
| CIFAR10 | 50 | 55.4±0.4 | 70.8±0.5 | 41.9±0.6 | 63.9±0.4 |
| CIFAR100 | 10 | 46.6±0.1 | 49.4±0.2 | 31.9±0.5 | 46.0±0.5 |
| CIFAR100 | 50 | 61.0±0.2 | 65.7±0.3 | 57.5±0.5 | 66.6±0.2 |
**Q3: The experiment for IPC=1 on CIFAR-10 and CIFAR-100.**
A3: We provide a comparison with RDED in the table below, which achieves excellent results on CIFAR under the 1 IPC setting.
| Method| RDED (ResNet-18)| Ours (ResNet-18)| RDED (ResNet-101) | Ours (ResNet-101) |
|-|-|-|-|-|
| CIFAR-10 |22.9±0.4 | 24.2±0.3 | 18.7±0.1 | 21.6±0.2|
| CIFAR-100|11.0±0.3 | 11.8±0.1 | 10.8±0.1 | 10.4±0.2|
**Q4: The specific VAE model, and the role of diffusion models.**
A4: Thanks for pointing this out, We adopt the pre-trained DiT and VAE from [b].
The role of the VAE encoder in the framework is to encode the image to the latent space, while the DiT model is to inverse the latent for sampling new latent representation and then denoise the new latent representation to the VAE space. The VAE decoder is used to decode the sampled latents to pixels. Besides, as shown in Lines 149-155 left column, the motivation for using diffusion models lies in their ability to enhance realism and cross-model generalization, which are the key qualities of a high-quality distilled dataset. Based on this, as described in Lines 110–164 right column, our main motivation is that we identify three key limitations in current diffusion-based methods, primarily because of conducting optimization within the VAE latent space. This motivates us to explore a more effective optimization space, aiming to provide a better paradigm for diffusion-based methods.
We will include further clarification in the updated version.
[a] Shao, Shitong, et al. "Generalized large-scale data condensation via various backbone and statistical matching." CVPR. 2024.
[b] Peebles, William, and Saining Xie. "Scalable diffusion models with transformers." ICCV. 2023.
---
Rebuttal Comment 1.1:
Comment: The author has addressed my concerns regarding the theoretical aspects. However, the results on CIFAR-10/100 are significantly lower than the state-of-the-art. Given that this method is better suited for large-scale datasets like ImageNet-1K, I will maintain my current score.
---
Reply to Comment 1.1.1:
Comment: Thanks for your feedback! We would like to emphasize that **our method achieves state-of-the-art performance on the CIFAR datasets**. (i) As we mentioned in Q2, the evaluation settings on CIFAR datasets of different SOTA methods are different. Thus, it is unfair to copy their results from their papers and make direct comparisons, as the results are obtained in different settings. To make a fair comparison, we adopt a more common evaluation setting (such as train 400 epochs) from large-scale datasets to evaluate the performance on CIFAR datasets for our method and baselines, to ensure fairness and consistency in comparison. Due to the time limitation, we finished the experiments of some SOTA baselines and show the fair comparison under the same setting in Table 1 of the paper. Our method achieves non-marginal improvements on CIFAR than SOTA baselines including D$^4$M and RDED.
(ii) Following your suggestion, we further compare our method with the SOTA method G-VBSM[a] using our evaluation setting (including 400 epochs training) as discussed above in (i). The results are shown in the response to Q2, demonstrating our superior performance than G-VBSM[a].
(iii) To demonstrate the general performance of our method with a more comprehensive comparison, we further present the results of different methods using the evaluation setting and code (including 1000 epochs training) from G-VBSM[a] to **ensure a strictly fair comparison under all the same settings**. The missing values marked with ‘-’ are unavailable because the results are not reported in the paper. The following table shows that our method can still outperform all SOTA baselines in a different evaluation setting on CIFAR for all methods with fair comparisons.
R18: ResNet18; CW128: ConvNetW128; Conv: ConvNet
|Dataset|IPC|G-VBSM\[a\](R18)|ESFR\[b\](R18)|HMDC\[c\](R18)|Ours(R18)|G-VBSM\[a\](CW128)|ESFR\[b\](CW128)|HMDC\[c\](CW128)|Ours(CW128)|G-VBSM\[a\](Conv)|ESFR\[b\](Conv)|HMDC\[c\](Conv)|Ours(Conv)|
|-|-|-|-|-|-|-|-|-|-|-|-|-|-|
| CIFAR10 |10| 53.5±0.6 | 56.9±0.5 |69.8±0.4 |**69.8±0.5** | 46.5±0.7 | - | - |**55.2±0.5** |- |**59.9±0.2** |47.54±0.7 |57.3±0.4|
| CIFAR10 |50| 59.2±0.4 | 68.3±0.3 |75.8±0.6 |**85.2±0.4** | 54.3±0.3 | -| -|**66.8±0.4** | - | 69.0±0.2 |52.4±0.1 |**69.3±0.4** |
| CIFAR100 | 50 | 65.0±0.5 |-|-|**67.3±0.4** |45.7±0.4 | -|-|**52.1 ±0.5** |- |51.3±0.4 |-| **54.6±0.4** |
To summarize, our method achieves SOTA performance on CIFAR. In our evaluation setting, our method performs the best compared with SOTA baselines including RDED (shown in our paper) and G-VBSM[a] (shown in the rebuttal). In another evaluation setting following G-VBSM[a] with their code, our method can still perform the best compared with SOTA baselines including [b] and [c]. We will make this more clear in our paper revision.
[a] Shao, Shitong, et al. "Generalized large-scale data condensation via various backbone and statistical matching." CVPR. 2024.
[b] Deng, Wenxiao, et al. "Exploiting inter-sample and inter-feature relations in dataset distillation." CVPR. 2024.
[c] Moon J Y, Kim J U, Park G M. “Towards Model-Agnostic Dataset Condensation by Heterogeneous Models” ECCV. 2024. | Summary: This paper addresses limitations in diffusion-based dataset distillation methods and introduces D3HR, a novel framework that enhances the representativeness of distilled datasets. This paper reveal that current methods suffer from issues like inaccurate distribution matching, distribution deviation due to random noise, and separate sampling, leading to suboptimal performance. The proposed D3HR framework outperforms existing state-of-the-art dataset distillation methods across multiple datasets, including CIFAR-10, CIFAR-100, Tiny-ImageNet, and ImageNet-1K. It demonstrates better generalization across architectures like ResNet, MobileNet, and VGG.
## update after rebuttal
The authors' response has addressed my concerns, so I maintain my overall positive assessment.
Claims And Evidence: The claims are supported by clear and convincing evidence.
Methods And Evaluation Criteria: Yes.
Theoretical Claims: I have checked the correctness of the proofs for theoretical claims.
Experimental Designs Or Analyses: The experimental designs are reasonable.
Supplementary Material: Yes.
Relation To Broader Scientific Literature: D3HR advances the field by improving distribution alignment, reducing noise-induced artifacts, and enhancing dataset compression efficiency, making it a significant step forward in scalable dataset distillation methods.
Essential References Not Discussed: No.
Other Strengths And Weaknesses: Strengths:
- The proposed method improves distribution matching. Uses DDIM inversion to transform latents into a more Gaussian-like distribution, enhancing representativeness.
- The proposed method achieves state-of-the-art performance on different neural architectures.
- This work propose an efficient sampling strategy to reduce randomness in dataset generation and ensures that distilled samples align better with the original distribution.
Weaknesses:
- Figures 1 and 3 appear to be less informative. Even after carefully reading the paper, their meaning remains unclear. Additionally, in the caption of Figure 1, the "blue lines" mentioned cannot be found, which may cause confusion. Providing more detailed explanations or clearer visual indicators would improve their interpretability.
- This work highlights the issue of inaccurate distribution matching in the latent space found in previous methods. However, it is not clearly explained why the proposed method achieves better distribution alignment. A more in-depth discussion or empirical validation of how the mapping improves distribution matching would strengthen the argument.
- The paper lacks an ablation study on domain mapping and group sampling. Since these are key components of the proposed method, conducting and presenting ablation experiments would help validate their individual contributions to performance improvements.
- SRe2L relies on a large amount of soft labels to enhance dataset distillation performance. It would be valuable to evaluate the effectiveness of the proposed method using hard labels. This would provide a better measure of the quality of the generated images, independent of external supervisory signals.
Other Comments Or Suggestions: In Equation (2), the variable C is not explicitly defined, which may cause confusion for the reader. Clarifying its meaning within the equation or referring to its definition elsewhere in the text would improve clarity.
Questions For Authors: In Figure 5, the performance appears to be significantly influenced by the number of inversion timesteps. It would be helpful to discuss why this dependency occurs and whether there is an optimal range of timesteps that balances performance and computational efficiency.
Regarding storage in Section 6.6, does the proposed method also require storing the decoder D? If so, how does this affect the overall storage efficiency? Clarifying whether the decoder needs to be retained separately or if it can be reconstructed from stored parameters would provide a more complete picture of the method’s storage requirements.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: **Q1: Figure 1 and 3 less informative**
A1: Thanks for the suggestions. The “blue lines” are the “blue contour lines” which indicate the probability density of the distribution. We will revise the caption to clarify this.
Figure 1 is intended to convey two key messages: (1) The VAE latent space exhibits significantly lower normality compared to our mapped (inversion) space. The “blue contour lines” allow us to clearly observe the structure and concentration of the latents (blue dots). Denser and more centralized contours reflect regions with higher latent density, which are the areas we should pay more attention to. (2) We visualize representative latent points generated by our method. In Figure 1(b), we show the latents sampled in the mapped (high-normality) space, demonstrating that our sampling process closely matches the desired noise distribution. To further validate the fidelity of the mapping, Figure 1(a) presents the corresponding latents in the original VAE space after DDIM sampling. The blue contour lines help illustrate that our sampling process successfully captures the structure of the VAE latent space, and effectively concentrates in high-density regions.
Similarly, Figure 3 visualizes n latents in the VAE space—comparing those generated by the default DiT model and our proposed method. It demonstrates that our approach yields more representative and diverse latents.
We will provide more detailed explanations and clearer visual indicators to improve interpretability.
**Q2: Deep discussion or empirical validation on why better alignment can be achieved in the inversion space**
A2: The reason behind this is that a Gaussian mixture in the VAE space is more difficult to fit than a single Gaussian distribution in the inversion space. This is because compared to a Gaussian mixture with an uncertain number of components and unknown structure, a single Gaussian is a simpler and well-defined parametric form.
To prove our method achieves better distribution alignment, we visualize 10 generated latents in the VAE space for the same class ("Goldfish") using both D4M and ours, as shown in Appendix Figure A1 and Figure 1 in the main paper. The results show that D4M, which performs optimization directly in the VAE space, tends to select latents near the edges of the distribution. In contrast, our method produces a more representative and diverse set of latents, better capturing the overall structure of the distribution.
For the quantitative comparison of accuracy, we refer to three key results: the D4M in Table 1, the default DiT generation in Table 3 (row 1), and our method with domain mapping but without group sampling in Table 3 (row 2). Together, the last has the highest accuracy, which demonstrates the effectiveness and necessity of our domain mapping strategy.
Finally, to further support our claims, we also include a visual comparison of generated images for D4M, the default DiT, and ours. These qualitative results clearly illustrate the advantages of our approach in producing more representative samples.
**Q3: Ablation study on domain mapping and group sampling**
A3: We have the ablation studies in Section 6.1.
For the group sampling, we present the results in Table 3 (rows 2–9). These include **our method without group sampling (row 2)**, as well as ablations that include only partial components of $L_{T, C}$. This allows us to verify the importance of group sampling and to assess the individual contributions of each component in $L_{T, C}$.
For the domain mapping, as discussed in lines 366–374, left column, we use the results in Table 3 (rows 1–2) to verify its importance. We compare **the default DiT generation with DDPM (row 1)** and **domain mapping with DDIM (row 2)**, with the same configuration for all other steps. The results clearly demonstrate the advantages of domain mapping with DDIM (Line 375-384 left column).
We will give a more clear description and annotation.
**Q4: Performance on hard labels**
A4: Please refer to Q1 of the response for xaqL.
**Q5: Clarifying C for Equation 2**
A5: C denotes the class condition, which means the same as other equations. We will provide a clearer explanation of this in the updated version.
**Q6: Discussion of different Inversion Timesteps**
A6: As discussed in Lines 378–415, left column, there is a trade-off between maintaining the Gaussian assumption and preserving image structural information across different time steps t. Please refer to Q3 of the response for xB8L with more details.
The choice of inversion steps is guided by empirical observations. As shown in Figure 5, using 24–31 inversion steps consistently achieves SOTA accuracy, making it a reasonable and effective choice.
**Q7: Storage of decoder**
A7: In Appendix Figure A3, the decoder size has already been accounted for in our computation under “DiT weight.” The storage size of the VAE weights is 320MB. We will include this detail more clearly. | Summary: This article introduces the D³HR framework (Taming Diffusion for Dataset Distillation with High Representativeness) to tackle the issue of inaccurate distribution matching in existing diffusion-based dataset distillation methods. D³HR enhances distribution matching accuracy by utilizing DDIM inversion to transform the VAE latent space into a high-normality Gaussian domain. Additionally, it ensures thorough alignment of dataset distributions through a group sampling strategy that incorporates statistical constraints. Extensive benchmark experiments reveal significant performance improvements compared to previous approaches.
## update after rebuttal
This paper raises the issue of inaccurate distribution matching in existing diffusion-based dataset distillation methods and proposes a solid solution to it. The response answered my concerns on experiments. Thus, I keep my original rating of weak acceptance.
Claims And Evidence: Yes. The authors claim the efficient alignment of distribution of latent vectors, which is supported by results and visualization.
Methods And Evaluation Criteria: Yes. The proposed method is reasonable and the evaluation follows the common practice. Detailed ablation study is implemented to verify the effectiveness of the method.
Theoretical Claims: Yes, the authors provided the theoretical analysis about the VAE latent fitting and the latent distribution in DDIM inversion in the supplementary.
Experimental Designs Or Analyses: Yes. The experimental design follows the common practice. More diffusion-based DD methods should be included, for example minimax diffusion.
Supplementary Material: Yes. The supplementary contains theoretical analysis and additional experiments and visualization.
Relation To Broader Scientific Literature: D^3HR considers the overall distribution when generating distillation datasets, rather than sampling them individually, thus improving the representativeness of distillation datasets.
Essential References Not Discussed: No
Other Strengths And Weaknesses: Strengths:
1.The proposed method effectively resolves the issue of overall distribution deviation caused by individual sampling in previous diffusion-based dataset distillation approaches.
2.The experimental results demonstrate that the method is both effective in improving distillation quality and efficient in terms of computational performance.
Weakness:
1.The paper seems to focus more on selecting the optimal subset, i.e., choosing a subset from the original dataset that best matches the complete distribution. It seems that the method added an optimal input selection step to the diffusion-based image synthesis process.
Other Comments Or Suggestions: Please address the weaknesses.
Questions For Authors: 1. Does the DDIM inversion process introduce significant additional computational costs when mapping the latent space of the entire dataset to a Gaussian noise domain?
2. Section 6.2 highlights that performance degrades sharply when the DDIM inversion step count (T) is too high (e.g., T > 31). What is the root cause of this phenomenon?
3. In practice, is there potential for cross-selection between different candidate subsets in group sampling? The paper appears to select only one subset—could this lead to suboptimal global distribution alignment?
4. Does the loss function $\mathcal{L}_{T,\mathcal{C}}$ function more as a static evaluation metric rather than an optimizable loss?
5. How is the optimal number of candidate subsets (m) determined theoretically? For datasets of varying sizes, how should m be chosen?
6. The $\mathcal{L}_{T,\mathcal{C}}$ includes multiple hyperparameters (e.g., $\lambda_\mu$, $\lambda_\sigma$, $\lambda_{\gamma_1}$). Does this complexity complicate practical usage and reproducibility?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: **Q1: primarily focuses on optimal subset selection**
In line 027-044 right column, we identify three key limitations in diffusion-based methods due to their reliance on optimization in the VAE latent space. This motivates us to identify a more effective space by DDIM inversion, aiming to provide a better paradigm for diffusion-based methods. Our contribution lies in **the entire pipeline designed for dataset distillation, including DDIM inversion, distribution matching, group sampling, and generation**—not merely the sampling. Each component is carefully designed to cohesively operate in the pipeline to ensure that the distilled subset is both compact and highly representative.
**The process in the inversion space is not input selection. It is a principled generative procedure.** As discussed in Sec. 4.3, we first map the original latent distribution to a Gaussian distribution due to Lemma 4.1, enabling efficient sampling via its high-normality. We first generate latents that **probabilistically follow the distribution of the entire class**, as shown in line 260–266 left column. Building on this, group sampling then supports parallel generation of candidate subsets (each maintaining distributional alignment), from which we identify the most representative one. The whole process tightly integrates sampling and optimization, enabling effective and distribution-aware subset generation tailored for diffusion-based synthesis, and goes beyond simple input selection.
**Q2: The computation overhead for DDIM inversion**
Please refer to Q6 of the response for Reviewer VDRK.
**Q3: Extreme high T incur accuracy degradation**
As discussed in Line 378–415 left column, there is a trade-off between maintaining the Gaussian assumption and preserving image structural information across different steps t. When t is small (such as 20), the distribution is a mixture of Gaussians as shown in Figure A4, and our distribution matching with a single Gaussian (Sec. 4.3) is not able to accurately describe the Gaussian mixtures, leading to certain performance loss. When t becomes large such as 40, although our distribution matching can accurately represent the real distributions which becomes more normal (Figure A4), the real distributions suffer from more significantly structural information loss due to adding more noise, which in turn degrades the performance of DDIM inversion. Thus, it is a trade-off between maintaining the Gaussian assumption and preserving image structural information.
**Q4: Using cross-selection in group sampling**
To validate cross-selection effect, we experiment on Tiny-ImageNet using 10 representative subsets with 10 IPC (performing group sampling 10 times; average accuracy: 44.07; individual results shown in Figure A2). We randomly combine the subsets, as shown in the table below, all three combined results yield lower accuracy than individual subsets. As discussed in Line 240–244 right column, this is because our $L_{T,C}$ is designed to ensure that the entire subset aligns well with the desired distribution, rather than fitting individual latents. Cross-combining latents from different subsets breaks this design principle without any distribution alignments.
|Setting|Combined set1|Combined set2|Combined set3|
|-|-|-|-|
|Acc|42.3±0.4|42.0±0.4|41.9±0.5|
**Q5: The role of $L_{T, C}$, is $L_{T,C}$ complexity for usage and reproducibilit**
Indeed, $L_{T,C}$ is a static evaluation metric, which is easy to compute with basic mathematical operations, and the sampling process is efficient (Please refer to Q3-(1) of the response for xaqL). For $\lambda_\mu$, $\lambda_\delta$ and $\lambda_\gamma$, we set them to make the corresponding metrics on the same scale. We provide results for different $\lambda$ in Table below, which shows that the performance on $L_{T,C}$ is relatively robust to $\lambda$.
|Setting|1:1:0.5|1:1:1|1:1:2|1:0.5:0.5|
|-|-|-|-|-|
|Acc|44.2±0.1|44.0±0.4|43.6±0.3|43.4±0.2|
**Q6: Choice of m across the datasets with different sizes**
We empirically set the value of m. The table illustrates how accuracy varies with different m across datasets of different scales. As expected, increasing m improves accuracy, as a larger candidate pool offers greater diversity and a higher chance of including representative sets. However, when m becomes sufficiently large, the performance gains plateaus—indicating that the marginal benefit of adding more candidates diminishes, as the top-performing candidates become increasingly similar. We choose m at the saturation point, typically between 1e5 and 1e7, which can work well across different datasets.
Tiny-Imagenet, 10IPC:
|m|1|1e3|1e4|1e5|5e5|1e6|5e6|
|-|-|-|-|-|-|-|-|
|Acc|40.2±0.4|40.9±0.4|41.7±0.5|42.4±0.4|43.8±0.3|44.2±0.2|44.1±0.3|
CIFAR10, 10IPC:
|m|1|1e3|1e5|1e6|5e6|1e7|5e7|
|-|-|-|-|-|-|-|-|
|Acc|38.9±0.3|39.6±0.2|40.4±0.3|41.0±0.1|41.8±0.1|41.9±0.2|42.1±0.2|
**Q7: Comparison with Minimax**
Please refer to Q1 of the response for xaqL.
---
Rebuttal Comment 1.1:
Comment: Thanks for the response! My main concerns about the subset selection and experimental details have been addressed. I would like to keep my original rate. | Summary: This work proposes a novel diffusion-based dataset distillation solution. Based on the fact that previous methods suffer from inaccurate distribution matching, the authors propose to convert the images to latents with DDIM inversion and model it as Gaussian. Then, sample multiple subsets from the Gaussian and select the subset with the most similar distribution statistics. These latents are sent to DDIM for image generation. The proposed method achieves leading performance on regular DD benchmarks.
**Update after rebuttal**: I appreciate the authors' feedback and some concerns are addressed. So I still leans toward positive and would keep my initial positive score.
Claims And Evidence: The authors made three main claims (summarized in lines 21-44), which are reasonable and supported in the paper.
Methods And Evaluation Criteria: The method is constructed following the previous observations, which is sound.
The authors adopt regular benchmarks for dataset distillation, including small and large-scale image datasets, and also cross architecture protocol (appendix). The only concern is that they did not compare with MiniMax diffusion (Gu et al., CVPR 2024) which is also diffusion-based and may yield competitive performance (58.6\% on ImageNet-1K with IPC 50).
Theoretical Claims: The proofs are checked with no issue found.
Experimental Designs Or Analyses: The experiment design including the selection of teacher models, IPCs, and ablation study is sound.
Supplementary Material: I have read the supplementary material.
Relation To Broader Scientific Literature: N/A
Essential References Not Discussed: No missing references.
Other Strengths And Weaknesses: Other weaknesses:
1. The "group sampling" use sampling-reject paradigm to find the best latent subset, which seems be computationally heavy.
Other Comments Or Suggestions: No other comments
Questions For Authors: I summarize my concerns as follows, including these in the previous questions for the authors convienience:
1. The experimental comparison to MiniMax (Gu et al., CVPR'24) is missing, which might be a competitive baseline.
2. For Lemma 3.1: why the Gaussian mixture is "hard-to-fit"? This is concluded from which perspective?
3. For group sampling:
(1) It seems to be computationally heavy. Is the "2.6s per class" on 306 the time for group sampling?
(2) Why not sample $IPC-3$ latents and "solve" the other two latent based on the three constraints to avoid repeated sampling?
(3) This sampling method implies that the distribution of real samples is exactly the target of synthetic samples. However, this is not supported. It is possible that increasing/decreasing the variance yields a better target distribution.
(4) For low sample capacity (IPC), the distribution statistics may be biased.
I would tune my rating if my questions are well addressed.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: **Q1: Comparison to MiniMax with hard labels**
As noted in Lines 297–300 right column, we did not include Minimax in the main table as it focuses on small subsets of ImageNet-1K. For large datasets, it requires extra training of multiple diffusion models with high computational cost. They only report results for ResNet-18 on ImageNet-1K, and do not support the other three datasets and other architectures used in our table. For a fair comparison with their results, we give the comparison with Minimax using their main setting on ImageWoof. Minimax is the SOTA method with hard labels on ImageWoof. Our method with 224×224 resolution outperforms Minimax Diffusion with 256×256 resolution.
|IPC|model|Minimax|Ours|
|-|-|-|-|
|10|resnet18|37.6±0.9|39.6±1|
|10|resnetAP-10|39.2±1.3|40.73±1|
|50|resnet18|57.1±0.6|57.6±0.4|
|50|resnetAP-10|56.3±1.0|59.3±0.4|
|100|resnet18|65.7±0.4| 66.8±0.6|
|100|resnetAP-10|64.5±0.2|64.7±0.3|
**Q2: Why is Gaussian mixture "hard-to-fit"**
"hard-to-fit" means that a Gaussian mixture is much more difficult to fit than a single Gaussian, due to its uncertain number of components and unknown structure. In contrast, a single Gaussian is a simpler and well-defined parametric form. In addition, in Fig. A1, we present the visualization of fitting the Gaussian mixture using K-means clustering under the D4M setting. It can be observed that some outliers near the edges of the distribution are selected, indicating that the Gaussian mixture is not well captured by the clustering. This further supports our point that the Gaussian mixture is relatively hard to fit.
**Q3: About group sampling**
Thanks for the valuable feedback. We explain the group samping more clearly, and then address your comments.
**Rationality of group sampling**: We propose an efficient sampling design based on the mapped high-normality property. As discussed in Line 266-270 left column, the distribution of n latents (for n IPC) may still deviate from the desired distribution due to limited size n. To address this, we sample multiple subsets in parallel and choose the most representative subset with the closest distribution to the desired distribution, as detailed below.
**(1) Computational efficiency**: We report the runtime of the group sampling process in the table, demonstrating its simplicity and efficiency. As discussed in Lines 302-306 left column, this is because multiple subsets can be sampled in parallel on the GPU instead of sequential sampling, and the operations such as random sampling and mean/variance computations are very lightweight and efficient in current computation frameworks, making the entire process highly efficient.
m = 1e5, A100 40G:
|IPC|1|5|10|20|50|
|-|-|-|-|-|-|
|time(s)|0.3901±0.0057|1.0288±0.0092|1.8352±0.0012|3.506±0.0046| 8.5252±0.0055|
**(2) About analytical solutions**: Group sampling is straightforward and efficient, taking just a few seconds to sample millions of subsets and select the best one. The mentioned analytical method to sample N-3 and solve the rest for accurate distribution matching may require additional complex solvers with high computation cost. Furthermore, with the solved examples, although the statistics of the distribution may match perfectly, the overall distribution of all samples may not be a Gaussian distribution. It is possible that the designed examples are far away from the sampled examples to match the desired distribution which is in the middle between them.
**(3) Increasing/decreasing variance**: Our domain mapping (Sec. 4.2) and distribution matching (Sec. 4.3) try our best to build an easy-to-fit distribution of real data. Then we generate synthetic samples following the real data distribution, to ensure the training performance on synthetic samples. Changing the variance may lead to a distribution deviation with samples not similar to real ones and degraded training performance. We further perform the experiment to verify the influence of variance. As shown in the table, we adjust the variance of the distribution by ±50% in sampling. The results show that neither increasing nor decreasing the variance leads to higher accuracy.
|-50%|-30%|-10%|0|+10%|+30%|+50%|
|-|-|-|-|-|-|-|
|39.8±0.5|42.2±0.4|43.1±0.4|44.1±0.3|41.4±0.4|37.4±0.5|34.0±0.6|
**(4) Statistics may be biased for low IPCs**: As the law of large numbers suggests, smaller sample sizes indeed leads to higher statistical bias. This also provides a reasonable explanation for the observed drop in accuracy at low IPC. This is a general issue for dataset distillation works. To mitigate this, our group sampling generates m subsets and selects the most representative one with the closest distribution. Thus, although one subset may suffer from large statistical bias, it is possible to find another subset with smaller bias. The results in Table 3 show our best performance compared with baselines in low IPC, showing the effectiveness of our method in addressing the bias issue. | Summary: This paper proposes a diffusion-based dataset distillation method. The paper claims that the VAE space of the diffusion model is more difficult for distribution matching. To tackle this challenge, the core idea of the proposed method is to apply DDIM inversion to each sample in the original dataset and then model the distribution of the inverted samples. To obtain distilled samples, the method performs latent-space sampling for multiple times and select the sample group that yields the lowest loss. Experiments on some datasets validate the effectiveness of the method.
Claims And Evidence: The claims are not well supported. The authors claim that "distribution in the VAE space has low-degree of normality". However, there is no clear definition of "normality" or any reference. The visualization in Fig. 1 is not informative, either. One can hardly understand the difference between two plots. The only difference in the current version is that there are some offsets between the points.
Methods And Evaluation Criteria: I am not sufficiently sure that the proposed method makes sense. If the target is to find a space that can effectively matching the distribution, why not consider the embedding space before the final linear layer of a pre-trained classifier, where samples in various class are almost separable. Indeed converting to the feature space of inverted samples can reduce the difficulty of distribution matching, but I am not sure whether this strategy is optimal. Although I can find some motivation about architectural scalability between Line 149 and 155, this issue can be potentially addressed by including more structures during training [a].
Besides, why use sampling-based method to select sample groups instead of conducting gradient-based optimization ?
[a] Generalized Large-Scale Data Condensation via Various Backbone and Statistical Matching, Shao et al., CVPR 2024.
Theoretical Claims: I quickly go over the introduced lemma and the proof, and I find no issue within these parts.
Experimental Designs Or Analyses: The experiments are clear to validate the effectiveness of the proposed method over some baselines. But I am not sure if it is optimal.
Supplementary Material: I quickly go over the supplementary materials including proof and additional results, and I find no issue regarding these parts.
Relation To Broader Scientific Literature: NA
Essential References Not Discussed: Missing Reference:
[a] Generalized Large-Scale Data Condensation via Various Backbone and Statistical Matching, Shao et al., CVPR 2024.
[b] Teddy: Efficient Large-Scale Dataset Distillation via Taylor-Approximated Matching, Yu et al., ECCV 2024.
[c] Diversity-driven synthesis: Enhancing dataset distillation through directed weight adjustment, Du et al., NeurIPS 2024.
Other Strengths And Weaknesses: Strengths:
1. The experimental results are good and the method surpasses the diffusion-based methods.
2. The writing is generally clear.
Other Weaknesses:
1. I am afraid that the time efficiency may not be superior as claimed by the authors. First, we need to train a diffusion model on the original dataset, which can take multiple days especially on large-scale ones. Second, the DDIM inversion process for each sample is obviously non-trivial.
Other Comments Or Suggestions: There are no blue lines in Fig. 1.
Questions For Authors: I am also curious about the results of using hard labels, because this case can reflect the capacity of distilled samples best.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: **Q1: no clear definition of normality**
Thanks for pointing this out. In our context, normality refers to the degree of the latent space data conforms to a normal distribution. A higher level of normality indicates that the latent distribution more closely resembles a normal distribution. This usage is consistent with that in statistical normality test, which assess whether sample data is drawn from a normal distribution. We will add the clarification in the updated version.
**Q2: not informative Figure 1**
Please refer to Q1 of the response for phyT.
**Q3: Why not use the embedding space of a pre-trained model**
First, the scalability to multiple architectures in Lines 149-155 left column are the motivation why we use diffusion models. We agree with prior works (RDED, D4M, Minimax) that realism and cross-model generalization are key qualities of a high-quality distilled dataset, which can be effectively achieved with the help of diffusion models.
Based on this, as shown in Lines 110–164 right column, our main motivation is that we identify three key limitations in current diffusion-based methods, primarily because of conducting optimization within the VAE latent space. This motivates us to explore a more effective optimization space, aiming to provide a better paradigm for diffusion-based methods.
Certain previous approaches that rely on the embedding space of a pretrained model or a small set of pretrained models, can introduce architecture bias, which may limit their generalization capabilities in large scale datasets or different independent architectures. In contrast, we identify a better optimization space that is agnostic to any specific architecture, allowing a single distilled dataset to be directly used across a wide range of models for users. As shown in the Tabel A1 in the appendix, our method can achieve SOTA performance across various models just with one-time generation cost.
**Q4: Sampling-based method instead of gradient-based optimization for group sampling**
We propose an efficient and effective sampling design based on the mapped high-normality property. As discussed in Lines 260-266 left column, the n latents (corresponding to n IPC) probabilistically follows the distribution of the whole class C. Building on this, our group sampling method is simple and efficient to search the most representative subset. For computation overhead analysis, please refer to Q3-(1) of the response for xaqL. In contrast, the gradient-based optimization is computationally expensive and may compromise the probabilistic nature of the n latents.
**Q5: The missing references**
Regarding [c], we have already included the comparison in our paper under the name DWA in Table 1.
As for [a] and [b], we provide the comparison on ImageNet-1K below, and will include the corresponding reference in the next version.
Resnet 18:
|IPC|G-VBSM|Teddy(post)|Teddy(prior)|Ours|
|-|-|-|-|-|
|10|31.4±0.5|32.7±0.2|34.1±0.1|44.3±0.3|
|50|51.8±0.4|52.5±0.1|52.5±0.1|59.4±0.1|
|100|55.7±0.4|56.2±0.2|56.5±0.1|62.5±0.0|
Cross Resnet101:
|IPC|G-VBSM|Teddy(post)|Teddy(prior)|Ours|
|-|-|-|-|-|
|10| 38.2±0.4|40.0±0.1|40.3±0.1| 52.1±0.4|
|50|61.0±0.4|-|-|66.1±0.1|
|100|63.7±0.2|-|-|68.1±0.0|
**Q6: Time cost of a pre-trained diffusion model and DDIM inversion**
It is common to use pre-trained models in dataset distillation. Diffusion-based methods (D4M, Minimax) rely on a pre-trained diffusion model, while other methods often use pre-trained teacher models to guide the distillation process. Thus, we do not count the training of pre-trained models towards our time cost.
The DDIM inversion is effective without high computation cost. (i) As discussed in Sec. 5.3, we only need to perform DDIM inversion once with a one-time cost, to generate multiple distilled datasets for different model architectures under various IPC settings. This is different from other methods which need to run their whole algorithms one more time if the architecture or IPC setting changes. (ii) The results of DDIM inversion are easy to store with little storage requirement, as shown in Appendix-Figure A3. (iii) Moreover, the computation cost of DDIM inversion is affordable. Even for ImageNet-1K, our method only requires approximately 4.5 hours on a single node with 8 A100 GPUs. In comparison to the SOTA diffusion-based method Minimax, which requires fine-tuning 50 separate pre-trained DiTs for ImageNet-1K, our approach is significantly more efficient. In addition, if more efficient denoisers (e.g., DPM-Solver families) are used, our paradigm can be further accelerated. This may be an orthogonal improvement direction and not the focus of our work.
**Q7: Comparison with hard labels**
We give the comparison results with Minimax diffusion, which is the SOTA method with hard labels under their main evaluation setting on ImageWoof. Our method with 224×224 resolution outperforms Minimax Diffusion with 256×256 resolution. Please refer to Q1 of the response for xaqL.
---
Rebuttal Comment 1.1:
Comment: Thanks for the response. My concerns are partially addressed. Indeed the experiments show improvement over existing methods. On this basis, I am happy to increase my score. But I am still concerning the efficiency, the optimality, and the motivation of the sampling-based method, which can potentially be valuable for future research.
---
Reply to Comment 1.1.1:
Comment: Thanks for your comment about the sampling-based method. To better address your concern, we revise the explanation for clarity.
For **efficiency**, we report the runtime of the group sampling process in the table, demonstrating its simplicity and efficiency. As discussed in Lines 302-306 left column, this is because multiple subsets can be sampled in parallel on the GPU instead of sequential sampling, and the operations such as random sampling and mean/variance computations are very lightweight and efficient in current computation frameworks, making the entire process highly efficient.
m = 1e5, A100 40G:
|IPC|1|5|10|20|50|
|-|-|-|-|-|-|
|time(s)|0.3901±0.0057|1.0288±0.0092|1.8352±0.0012|3.506±0.0046| 8.5252±0.0055|
For **motivation**, we propose an efficient sampling design based on the mapped high-normality property. As discussed in Lines 260-270 left column, we need to generate n latents (corresponding to n IPC) probabilistically following the distribution of the whole class from Sec. 4.3. Therefore, Gaussian sampling is directly used to approximate the target distribution. Although each sample is randomly sampled following the target distribution, the overall distribution of all samples may still deviate from the target due to the limited number n of all samples. Thus, to mitigate this issue, we propose the group sampling method in Sec. 4.4. .
Specifically, as smaller sample sizes lead to higher statistical bias, we propose group sampling to generate multiple subsets and select the most representative one with the closest distribution to the target. Thus, although one subset may suffer from large statistical bias, it is possible to find another subset with smaller bias through our group sampling. The results of ablation study for group sampling in Table 3 and the discussions in Line 357-368 right column show our best performance compared with baselines, demonstrating the effectiveness of the sampling method. The motivation for our group sampling is straightforward and the performance is outstanding.
For **optimality**, as discussed above, the group sampling method is very efficient and effective. It only needs several seconds to sample 1e5 subsets and select the best one, and results in the best performance compared with SOTA baselines. Reviewer mentions a possible analytical solution to sample n-3 examples and solve the rest examples to match the target distribution accurately, achieving the optimality to some extent. However, it may require additional complex solvers with high computation cost. Furthermore, with the analytically solved examples, although the statistics of the distribution may match perfectly, the overall distribution of all samples may not be a Gaussian distribution. It is possible that the designed/solved examples are far away from the randomly sampled examples to match the target distribution which is in the middle between them. | null | null | null | null |
Diversified Flow Matching with Translation Identifiability | Accept (poster) | Summary: This paper proposed a flow matching model for diversified distribution matching, called DFM. The proposed method formulates a bilevel optimization problem to learn an interpolant and train a flow model on this interpolant. This paper demonstrates that the standard flow matching models fail in the DDM task. To address this, DFM proposes a method for learning a non-intersecting interpolant (Eq. 14) by leveraging the class label information. Intuitively, the objective encourages the trajectories of different classes to be well-separated. DFM model is evaluated on synthetic data, image-to-image translation, and swarm navigation (appendix).
Claims And Evidence: - DFM model is supported by the experimental results.
- However, there is concern regarding the novelty of Prop 3.4, as it is mainly a restatement of the assumption that $f_{1}^{\star}=g^{\star}$ and Thm 2.2.
Methods And Evaluation Criteria: - DFM aims to address the unsupervised domain traslation (UDT) problem. However, this model requires class labels for input-output data, raising concerns about whether this setting is also considered as UDT.
Theoretical Claims: - There is concern regarding the novelty of Prop 3.4 (See **Claims And Evidence**).
- "+ $1_{\mathcal{I}}$" in Equation 12 may need to be replaced with "* $1_{\mathcal{I}}$".
Experimental Designs Or Analyses: - DFM model is evaluated on synthetic data, image-to-image translation, and swarm navigation (appendix).
- The image translation experiment is conducted on a relatively non-standard benchmark of CelebAHQ-to-Bitmoji. For reference, see [1, 2].
- There are concerns regarding the presentation. Most of the experimental results comparing DFM with baseline methods are placed in the appendix, including Fig 9, 10, 11, and Tab2. Additionally, all swarm navigation results are placed in the appendix.
- While the main target task is diversified distribution matching, the image translation experiments only evaluate marginal distributions, not conditional distribution matching. For reference, DDM-GAN measured the LPIPS score on a similar experiment [3].
[1] De Bortoli, Valentin, et al. "Schrodinger Bridge Flow for Unpaired Data Translation." NeurIPS 2024.
[2] Liu, Guan-Horng, et al. "I $^ 2$ SB: Image-to-Image Schr\" odinger Bridge." ICML 2023.
[3] Shrestha, Sagar, and Xiao Fu. "Towards identifiable unsupervised domain translation: A diversified distribution matching approach." ICLR 2024.
Supplementary Material: I reviewed the experimental results in Appendix C and the proofs presented in Appendix E.
Relation To Broader Scientific Literature: This paper proposed a flow matching model for the diversified distribution matching (DDM) task.
Essential References Not Discussed: No
Other Strengths And Weaknesses: **Strengths**
- The paper is well-written and easy to follow.
- The motivation is well-supported by the experiments in Section 3.2.
**Weakness**
- There are concerns regarding the necessity of Thm 2.3.
- The motivation section presents results that are somewhat expected, as observed in [1].
- Additional concerns are included in other sections.
[1] Liu, Xingchao, Chengyue Gong, and Qiang Liu. "Flow straight and fast: Learning to generate and transfer data with rectified flow."
Other Comments Or Suggestions: No
Questions For Authors: No
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: **[Novelty of Proposition 3.4]**
The novelty lies in how to use FM-based losses to attain the same conclusion of Thm 2.2. Note that Thm 2.2 assumes that distribution matching is already attained. But Prop 3.4 specifically needs the distribution matching part to be realized by FM. How to achieve this while not violating the constraints in Thm 2.2 was very unclear before we came to the loss design of the bilevel objective. Coming to our design was entirely nontrivial and this constitutes the major novelty. We will articulate this point by adding a remark after Prop 3.4.
**[“$ \times 1_{\mathcal{I}}$” instead of “$+1\_{\mathcal{I}}$” ]**
Thank you for your careful reading. We seemed to have missed the definition of the identity function $1_{\mathcal{I}}$ leading to confusion. The operator should be $+$ when
$1_{\mathcal{I}}(x) = 0$ for $x \in \mathcal{I} $ and infinity otherwise. Whereas the operator should be $*$ when $1_{\mathcal{I}}(x) = 1$ for $x \in \mathcal{I} $ and infinity otherwise.
We will include the definition to avoid this confusion.
**[Presentation ]**
Some experiments were moved to the appendix due to space constraints. To alleviate the reviewer’s concerns, we will restructure the paper to include partial results from all experiments along with baseline comparisons in the main paper and move the rest to the appendix.
**[ LPIPS score ]**
Image similarity metrics were not presented because we observed that metrics such as LPIPS do not make sense when the images have large domain gaps, which is the case in the considered experiment. For example, DFM and CycleGAN achieved the same LPIPS score, despite DFM being clearly better than CycleGAN in terms of alignment. Also note that LPIPS score was still not presented for the CelebAHQ to Bitmoji translation task in DDM-GAN .
Nonetheless, to alleviate the reviewer’s concern, we evaluate the DreamSim [R1] score in the table below, which was shown to better align with human judgement than LPIPS score. Although the metric can provide some rough idea, it still cannot capture some obvious issues (e.g., DDM-GAN has diversity issues as seen in Fig. 7, last two rows, in the manuscript).
*[R1] Fu, Stephanie, et al. "Dreamsim: Learning new dimensions of human visual similarity using synthetic data."*
------------------------------
Method $\quad\quad$ Mean (Std)
------------------------------
DFM $\quad\quad\quad~~$ 0.59 (0.05)
DDM-GAN $\quad$ 0.58 (0.05)
CycleGAN $\quad~$ 0.63 (0.06)
FM $\quad\quad\quad~~~~$ 0.66 (0.06)
FM-OT $\quad\quad~~$ 0.66 (0.06)
FM-cond $\quad~~$ 0.60 (0.06)
SDEdit $\quad\quad~~$ 0.62 (0.06)
------------------------------
We will add the above result in the revised version.
**[Standard Benchmark Dataset]**
Note that standard benchmark datasets (CelebAHQ Male to Female and AFHQ) can actually be considered as easy cases because the domain gap is relatively small. Hence, the issue of content misalignment was not observed by the existing methods [1,2]. For this reason, we intentionally did not include them, as they did not help make our point.
However, in the case of CelebAHQ-to-Bitmoji, the content misalignment issue is clear, and therefore helps to prove our point.
**[Necessity of Thm 2.3]**
Indeed, we presented Thm 2.3 for showing the robustness of Thm 2.2. As Theorem 2.3 is not the contribution of this work, we only presented the theorem to provide sufficient context. However, we understand the reviewer’s concerns that Theorem 2.3 was not used explicitly in any of our own theoretical analysis, so might not be necessary to present it.
We will move the theorem to the appendix to save space for other important revisions to the paper.
[**Comparison with (Liu et al., 2023)**]
Note that the example in the motivation is not claimed to be the contribution of our work. It is merely to illustrate the issue with using linear interpolants to the readers. Hence, we believe that a similar example showing reflecting trajectories does not undermine our work. Nonetheless, we understand that the example might be obvious for some readers familiar with the work. Hence we will cite [1] before elaborating on the example.
**[ UDT terminology ]**
The work can be considered unsupervised in that no paired data is required at all. However, we understand the reviewer’s concern and will consistently use “unpaired domain translation” for UDT instead of “unsupervised domain translation” in the revised version.
---
Rebuttal Comment 1.1:
Comment: Initially, I submitted an official comment that was not visible to the authors, so I am reposting it here:
I appreciate the authors for the response and the additional experiments. Those have been helpful in addressing my concerns. Therefore, I will raise my rating to 3.
---
Reply to Comment 1.1.1:
Comment: Thank you for your response and valuable feedback to further refine our work. | Summary: The paper introduces Diversified Flow Matching (DFM), a novel unsupervised domain translation (UDT) framework that extends ODE-based Flow Matching (FM) from linear to nonlinear interpolants, addressing the critical limitation of translation identifiability.
Key Contributions:
Overcoming Linear Flow Matching Limitations
- Prior FM approaches fail when distribution modes overlap, leading to incorrect mappings due to linear interpolants.
- The authors explicitly demonstrate this failure case with synthetic Gaussian mixtures where mode overlaps disrupt proper translation trajectories.
Advancing Nonlinear Flow Matching for Identifiability
- Builds on prior learnable flow models that incorporate nonlinear interpolants to improve flow-based translation.
- While previous works in metric-based flow modeling and Schrödinger bridge methods introduced learnable transport functions, they did not explicitly guarantee translation identifiability.
- The authors extend this concept by introducing higher-order non-intersecting nonlinear interpolants to explicitly enforce identifiability in domain translation.
Bilevel Optimization Loss for Enforcing Identifiability
- A novel bilevel learning loss is proposed, ensuring a unified, non-intersecting translation trajectory across different domain conditions.
- This approach is a unique theoretical and practical advancement, correcting mode overlap issues seen in prior FM methods.
Claims And Evidence: (1) Claim 1: Linear Flow Matching Fails for Translation Identifiability
Evidence:
- Synthetic Gaussian mixture experiments clearly demonstrate incorrect trajectory mappings when using linear interpolants.
- Prior FM methods fail in mode-overlapping settings, leading to poor translation accuracy.
Limitation:
- Needs real-world validation in high-dimensional datasets.
(2) Claim 2: Bilevel Learning Loss Ensures Identifiability
Evidence:
- Proposition 3.4: Provides formal proof that the bilevel loss enforces translation identifiability by learning non-intersecting interpolants.
- Empirical results:
(a) Synthetic data: DFM avoids trajectory conflicts where FM-cond fails.
(b) Image translation: FID scores demonstrate improvements, but more qualitative analysis is needed to attribute gains specifically to translation identifiability.
(c) Swarm navigation: DFM preserves transport trajectories where standard FM methods fail.
Limitation:
- Table 1 lacks clarity → Needs explicit quantitative and qualitative validation that the observed FID improvements are due to translation identifiability rather than other architectural enhancements.
- Real-world experimental results lack qualitative and quantitative ablation studies on the effect of the bilevel optimization loss.
(a) No direct comparison is made between DFM with and without the bilevel loss in a real-world scenario.
(b) Translation identifiability should be evaluated explicitly in real-world tasks, particularly in structured medical or multimodal datasets where domain shifts are crucial.
(3) Claim 3: DFM Achieves Superior Content Alignment Over FM-cond and GAN-based DDM
Evidence:
- Face-to-Bitmoji translation experiments show better content alignment than FM-cond and GAN-based DDM.
- Table 2 (synthetic results) shows clear performance improvements, suggesting the effectiveness of DFM’s nonlinear flow matching.
Limitation:
- Table 1’s performance improvements require stronger justification.
- Need further ablation studies → Testing whether DFM’s gains persist without nonlinear interpolants.
- More real-world experiments needed to confirm generalization beyond synthetic tasks.
Methods And Evaluation Criteria: Technical Approach's Contribution :
- Introduces a custom bilevel optimization loss with nonlinear, non-intersecting interpolants to explicitly enforce translation identifiability.
- Unlike prior FM-based methods, the bilevel optimization ensures that each interpolant follows a unified translation trajectory, avoiding trajectory conflicts.
- Simplifies the bilevel optimization problem by leveraging non-overlapping conditional distributions, making it computationally efficient.
Evaluation Metrics
- FID Scores → Measure image translation quality.
- Earth Mover’s Distance (EMD) → Assesses distribution transport accuracy.
- Translation Error (TE) → Evaluates content alignment precision.
Strengths:
- Clear synthetic data evaluations that visualize trajectory correctness.
- Shows that the bilevel loss improves identifiability beyond prior GAN/FM-based methods.
Weaknesses:
- Table 1’s performance gains need further explanation → Whether the gains stem from translation identifiability or other factors is unclear.
- Table 2 (synthetic) provides stronger validation than Table 1 → More real-world experiments should match this clarity.
- Ablation studies are missing for:
(a) Alternative nonlinear interpolants.
(b) Computational efficiency trade-offs.
(c) Real-world experimental validation of the bilevel optimization loss's effect on translation identifiability.
Theoretical Claims: I have no comments on that.
Experimental Designs Or Analyses: I recommend that the author review and supplement the following parts:
(1) Ablation Study: Effect of the Bilevel Optimization Loss on Translation Identifiability
- Ablation experiments should test DFM with and without the bilevel loss to show how much it contributes to translation identifiability.
- Qualitative trajectory comparisons should illustrate the effect of the bilevel loss on mode separation and content preservation.
- Quantitative experiments should assess domain translation accuracy and alignment differences with and without the bilevel loss.
(2) Real-World Verification of Bilevel Learning Loss Effectiveness
- Demonstrate a real-world use case where translation identifiability affects model performance.
- Quantify performance improvement using classification accuracy, error reduction in domain adaptation tasks.
(3) Addressing Ambiguity Between Table 1 and Table 2 Results
- Table 2 (synthetic experiments) shows clearer performance improvements than Table 1, strongly supporting DFM’s effectiveness.
- Table 1’s real-world results, however, remain ambiguous, particularly regarding:
(a) Whether the observed performance difference between DFM and FM-cond is due to translation identifiability or other confounding factors. (b) Lack of qualitative trajectory visualizations and structured ablation to confirm that the bilevel optimization loss directly improves translation identifiability.
(4) Other suggestions
- Additional experiments aligning real-world results (Table 1) with synthetic evaluations (Table 2).
- Qualitative trajectory comparisons in real-world settings to explicitly visualize translation improvements.
- Ablation study breaking down the exact contributions of translation identifiability in Table 1 results.
- If real-world dataset expansion is infeasible, at least include additional qualitative and quantitative results in the appendix.
Supplementary Material: I have reviewed the supplementary material and have no comments on that.
Relation To Broader Scientific Literature: Additional Clarifications Needed:
- Clarify how DFM differs from prior work in nonlinear flow matching, particularly in handling mode overlaps and enforcing identifiability.
- More discussion on real-world applications where identifiability is a critical bottleneck.
Essential References Not Discussed: I have no clear reference to mention, but please refer to my comment on Relation to Broader Scientific Literature.
Other Strengths And Weaknesses: There are some weaknesses that could limit the paper’s broader impact.
- Empirical validation remains narrow, as the evaluation focuses on controlled synthetic settings and simple image translation tasks, without testing on real-world, high-dimensional structured datasets.
- Real-world validation of the bilevel loss is missing → Needs qualitative & quantitative ablation studies.
- Table 1 results require stronger interpretation to confirm that improvements arise from translation identifiability rather than other confounding factors.
- Computational trade-offs remain unexplored → Scalability to larger datasets needs further analysis.
- The lack of open-source implementation raises reproducibility concerns, which should be addressed before the camera-ready submission.
====
I will assess the authors' incorporation of feedback, along with other overall considerations, and determine whether to adjust or maintain the score accordingly.
Other Comments Or Suggestions: Some mathematical derivations (e.g., Proposition 3.4) could be more clearly structured for better readability, and a summary table comparing DFM to existing methods would help contextualize its contributions.
Questions For Authors: - What is the computational overhead of DFM compared to these baselines?
- Does the bilevel optimization framework introduce significant training inefficiencies?
- How sensitive is DFM’s performance to the specific choice of nonlinear interpolant?
- Have alternative nonlinear functions been tested, and if so, how do they affect stability and identifiability?
- Have you tested runtime performance across different dataset sizes or on high-dimensional data?
- Would the method perform well in cases where conditional distributions have overlapping supports, which may occur in real-world applications?
- Do you plan to release code before the camera-ready submission?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal:
**Anonymized URL**: (https://drive.google.com/file/d/1U4gdB5qy1d98AJ1YWxR2v3fzDQp167nt/view?usp=sharing)
**[Limitations of Claim 2: Bilevel Loss implies Identifiability]**
To clarify, the proposed DFM and the baselines FM, FM-OT, and FM-cond do use the same architecture, and are trained using the same hyperparameter settings. Therefore, the only difference between these methods is in the loss design. Hence, the qualitative and quantitative performance gain can be attributed to the translation identifiability rather than architectural differences. We will add a remark for clarification.
Regarding real-word scenario: in this work, our interest lies in a theoretically sound FM approach for realizing DDM and retaining translation identifiability. Translation identifiability’s effectiveness in real-world applications is indeed important, but a bit beyond the scope. Nonetheless, we noticed that there have been recent works using DDM and translation identifiability for medical imaging [R-1]. They did not use FM, but clearly showed the usefulness of translation identifiability. We will point readers to such references.
We will make the above points clearer in the revised version.
[R-1] Song, Jiahui, et al. "Translation Identifiability-Guided Unsupervised Cross-Platform Super-Resolution for OCT Images." IEEE SAM, 2024.
**[Limitations of Claim 3: DFM achieves superior content alignment ]**
We should mention that Table 1 is not meant to show performance improvement. Table 1 only shows that FID of the proposed method being comparable to the best baseline. This ensures that the image quality of the translated images is not compromised. Whereas, the qualitative results accompanying Table 1 in Fig. 7 is used to show that the proposed method has better content alignment than all other baselines. We have now quantified the content alignment result using DreamSim scores. This can be used together with Table 1 and the figure to assess the performance of the methods. Overall, a good method in our context should have low DreamSim scores and reasonable FID scores. Only having FID scores does not mean good performance.
Note that we provided two real-world experiments with image translation and swarm navigation to show generalization beyond synthetic tasks.
**[Table 1: Translation identifiability gains]**
As mentioned, Table 1 is not used to show performance gain. Table 1 shows the image quality (measured by FID) is not compromised when we establish translation identifiability. The translation identifiability is shown in Fig. 7.
The DFM does not retain identifiability if the nonlinear interpolants are not used. We have included linear interpolant in this experiment. One can see that the performance is not promising.
**[Ablations]**
**[Alternative non-linear Interpolants]** In fact, we did not use any specific design for the nonlinear interpolant. Our understanding is that as long as it satisfies the regularity condition and is a learnable interpolant, it can serve our purpose. To address the reviewer’s concern, we have conducted experiments on different nonlinear interpolant parametrization, which is shown in R-Fig. 1. In R-Fig. 1, we use two other parametrization of the nonlinear interpolant (i,e., $(1-t) x + ty + f(t) \gamma_{\theta}(x, y, t)$ with different $f(t)$, namely, (i) $ (1-t) x + t y + {\rm sin}(\pi t) \gamma_{\theta}(x, y, t)$ (ii) $ (1-t) x + t y + \sqrt{t (1-t) } \gamma_{\theta}(x, y, t)$. One can see that DFM is robust to different parametrization of the nonlinear interpolant.
**[Computational efficiency]** R-Table 1 in the URL shows the training and inference time of all methods. The proposed method does not incur significant training time overhead compared to other FM based methods. Whereas, there is no overhead at all during inference.
**[Real-world validation]** Note that our implementation did not directly optimize the bilevel loss. We exploited the non-overlapping structure of conditional distribution to obtain a simplified loss. We have provided two real-world validations as discussed previously.
**[Overlapping supports]**
R-Fig. 3 in the anonymized PDF link shows the result of overlapping supports of the conditional distribution. The figure shows that small overlaps do not significantly harm the translation. Further, note that non-overlapping supports naturally occur in applications as demonstrated in our experiments. That said, very large overlaps can indeed be detrimental to the proposed method.
**[Code Submission]**
Note that we have already provided demo code in the supplemental materials along with our manuscript. We will release the complete code along with pre-trained models before the camera-ready submission.
---
Rebuttal Comment 1.1:
Comment: Thank you for the author's response. However, it fell slightly short of my expectations, so I have adjusted the score to 3. While I acknowledge the study's contribution, I recommend that additional key experiments be conducted and included in the main paper to more effectively support and strengthen it.
---
Reply to Comment 1.1.1:
Comment: We thank the reviewer for the time and effort devoted to reviewing our work.
We believe that we have addressed the reviewer’s concerns with further experiments or clarifications in our rebuttal (also, please see the attached PDF). These new experiments, along with clarifications, will be incorporated in the revised version.
The additional experiments include:
1. Nonlinear interpolants,
2. Computational efficiency,
3. Overlapping supports,
4. More quantitative results for image translation (including DreamSim score and additional baselines).
We have also addressed the following clarifications:
1. Table 1 (FID) should not be directly compared with Table 2. We use qualitative results, as shown in Fig. 7 of the manuscript, alongside the DreamSim score to assess translation performance. We will also expand the discussion of quantitative results, including responses to reviewer dKp3’s comments on the LPIPS score.
2. The image translation experiment is inherently high-dimensional and is a standard approach used in existing FM-based methods for validating real data. | Summary: The paper introduce Diversified Flow Matching (DFM), an FM-based framework for DDM. They design a custom loss function and nonlinear interpolant to ensure translation identifiability, addressing the limitations of conventional FM methods that use linear interpolants. By leveraging the non-overlapping property of conditional distributions, they reformulate the bilevel optimization problem into a two-stage approach, simplifying computation. The method is tested on synthetic data and real-world applications, demonstrating its effectiveness in maintaining translation identifiability and improving trajectory information.
Claims And Evidence: YES
Methods And Evaluation Criteria: The proposed methods and evaluation criteria in the paper are appropriate for the problem of diversified distribution matching (DDM).
Theoretical Claims: The paper presents two main theoretical claims: Proposition 3.4 (translation identifiability of DFM) and Fact 3.3 (failure of the sum-of-LS formulation).
Proposition 3.4 relies on idealized assumptions (e.g., existence of diffeomorphisms) but is logically sound within the theoretical framework.
Fact 3.3 is rigorously supported by both synthetic examples and formal reasoning.
Experimental Designs Or Analyses: The paper evaluates DFM through three experiments: synthetic data, image translation, and swarm navigation. While the experiments demonstrate DFM’s effectiveness, several design and analysis choices warrant discussion:
1. Synthetic Data Experiment
Design:
Tests on 2D/3D Gaussian mixtures with ground-truth translation y=-x.
Metrics: Earth Mover’s Distance (EMD) and Translation Error (TE).
Validity:
Strengths: EMD and TE are appropriate for distribution matching and identifiability. The use of multiple trials (10 runs) adds statistical robustness.
2. Image Translation Experiment
Design:
Translates CelebAHQ faces to Bitmoji using FID for distribution matching and visual checks for content alignment.
Trains on Stable Diffusion’s latent space (not raw pixels).
Validity:
Strengths: FID is standard for generative models. Including CycleGAN and DDM-GAN baselines contextualizes performance.
Issues:
Content Alignment: Relies on qualitative visual checks without quantitative metrics (e.g., SSIM, LPIPS, or user studies). This risks overlooking subtle misalignments.
3. Swarm Navigation Experiment
Design:
Tests on LiDAR data of Mt. Rainier with Gaussian swarm sources/destinations.
Metric: Surface Adherence (SA) to measure trajectory proximity to terrain.
Validity:
Strengths: SA is a meaningful metric for terrain adherence.
Issues:
Oversimplified Scenario: Swarms have non-overlapping paths (per Assumption 3.5), ignoring real-world complexities like intersecting trajectories or dynamic obstacles.
General Issues:
Baseline Scope:
Omission of recent flow-based UDT methods (e.g., Rectified Flow, Schr̈odinger Bridges).
Supplementary Material: The supplementary material was thoroughly reviewed, with focus on Appendices B (method details), C (additional experiments), D (hyperparameters), and E (proofs).
Relation To Broader Scientific Literature: The key contributions of the paper are deeply rooted in addressing gaps and building upon advancements in unsupervised domain translation (UDT), distribution matching, and flow-based generative models. Here’s how they relate to prior work:
1. Bridging Flow Matching (FM) and Diversified Distribution Matching (DDM)
Prior Work:
DDM (Shrestha & Fu, 2024): Introduced translation identifiability via GANs by matching multiple conditional distributions.
Flow Matching (Lipman et al., 2022): Provided stable training and trajectory modeling via ODEs but focused on single distribution pairs.
Contribution:
The paper unifies these frameworks by adapting FM to DDM, enabling translation identifiability (a GAN-based DDM strength) with trajectory information (a flow-based advantage). This resolves GANs’ instability and trajectory limitations while extending FM to multi-conditional settings.
2. Addressing Translation Non-Identifiability in Flow Models
Prior Work:
CycleGAN (Zhu et al., 2017): Highlighted content misalignment due to non-unique transport maps.
Optimal Transport (OT) in UDT (Liu et al., 2022; De Bortoli et al., 2021): Assumed OT maps as solutions but lacked guarantees for general translations.
Contribution:
By enforcing DDM’s sufficiently diverse condition (SDC) through FM, the paper guarantees identifiability for non-OT maps. This directly addresses the non-uniqueness issue in prior UDT methods, aligning with theoretical insights from Shrestha & Fu (2024) but in a flow-based framework.
3. Introducing Bilevel Optimization and Nonlinear Interpolants
Prior Work:
Linear Interpolants in FM (Albergo et al., 2023): Used linear paths (e.g., \(z_t=(1-t)x+ty\)) but failed for multi-conditional DDM due to conflicting trajectories.
Conditional FM (Atanackovic et al., 2024): Learned separate flows per condition but lacked unified transport functions.
Contribution:
The paper proposes nonlinear interpolants (Eq. 17) and bilevel optimization (Eq. 12) to harmonize trajectories across diverse conditional pairs. This extends FM’s applicability to DDM, resolving conflicts inherent to linear interpolants and enabling a unified velocity field.
4. Exploiting Structural Constraints for Efficiency
Prior Work:
Non-Overlapping Supports in OT (Villani et al., 2009): Leveraged distribution separation for tractable transport.
Contribution:
By assuming non-overlapping supports (Assumption 3.5) and designing non-intersecting interpolants (Eq. 14), the paper simplifies bilevel optimization into a tractable two-stage process. This aligns with structural insights from OT but tailors them to FM-based DDM.
Essential References Not Discussed: Deep Momentum Multi-Marginal Schrödinger Bridge:
The proposed DFM framework aims to unify multiple conditional distribution pairs under a single flow, which inherently aligns with multi-marginal SB formulations. Including this reference or related paper is critical to contextualize DFM’s bilevel optimization strategy against state-of-the-art SB advancements, especially since DFM implicitly addresses multi-marginal coupling.
Other Strengths And Weaknesses: Strengths:
1. Originality:
The integration of FM with DDM is a novel contribution. While DDM was previously restricted to GANs, this work creatively adapts FM to enforce identifiability via bilevel optimization and learnable nonlinear interpolants.
The design of private interpolants for each conditional distribution pair and the reformulation under non-overlapping structural assumptions demonstrate innovative problem-solving.
2. Significance:
Translation identifiability is a critical issue in UDT, and DFM provides a principled solution with theoretical guarantees.
The ability to recover transport trajectories has practical implications for applications like robot navigation and single-cell analysis, where path information is essential.
3. Technical Soundness:
Theoretical results (e.g., Proposition 3.4) rigorously connect DFM to the DDM criterion, ensuring identifiability under sufficiently diverse conditional distributions.
Experiments on synthetic data, image translation, and swarm navigation validate the method’s effectiveness. The improved FID scores (Table 1) and avoidance of GAN instability (Fig. 6) highlight empirical advantages.
4. Clarity:
The paper is well-structured, with clear explanations of challenges in adapting FM for DDM (e.g., pitfalls of linear interpolants in Fig. 3). Visualizations (e.g., trajectories in Fig. 5, 9–11) enhance understanding.
Weaknesses:
1. Restrictive Assumptions:
The efficient implementation relies on non-overlapping supports of conditional distributions (Assumption 3.5), which may not hold in many real-world scenarios. While acknowledged as a limitation, potential workarounds for overlapping cases are not explored.
2. Experimental Scope:
Image translation experiments operate in a latent space rather than raw pixels, which may understate challenges in high-dimensional settings. Testing on more diverse modalities (e.g., text-to-image) could strengthen claims.
Other Comments Or Suggestions: No.
Questions For Authors: No.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal:
**[Quantitative Metrics for Image to Image Translation]**
Image similarity metrics were not presented because we observed that metrics such as LPIPS do not make sense when the images have large domain gaps (i.e., when the geometric representations of the feature spaces are largely different like in photos and bitmoji). For example, DFM and CycleGAN achieved the same LPIPS score, despite DFM being clearly better than CycleGAN in terms of alignment.
Nonetheless, to alleviate the reviewer’s concern, we evaluate the DreamSim score [Fu et al, 2023]. This score serves for similar purposes of LPIPS but was shown to better align with human judgement [Fu et al., 2023]. Although the metric can provide some rough idea, it still cannot capture some obvious issues (e.g., DDM-GAN has diversity issues as seen in Fig. 7, last two rows, in the manuscript):
------------------------------
Method $\quad\quad$ Mean (Std)
------------------------------
DFM $\quad\quad\quad~~$ 0.59 (0.05)
DDM-GAN $\quad$ 0.58 (0.05)
CycleGAN $\quad~$ 0.63 (0.06)
FM $\quad\quad\quad~~~~$ 0.66 (0.06)
FM-OT $\quad\quad~~$ 0.66 (0.06)
FM-cond $\quad~~$ 0.60 (0.06)
SDEdit $\quad\quad~~$ 0.62 (0.06)
-------------------------------
**[Swarm Navigation Issue]**
We should mention that our learned paths are time-space nonoverlapping. This means that the swarms can use the overlapped space as long as they do not reach the same spatial point at the same time. This was actually reflected in Fig. 10 (**please note the colorbar**). We believe that such learned path plans are reasonable as they avoid collision and allow the swarms to use the same space at different times. We realize that we did not articulate this point in the simulations. We will clarify in the revision.
**[Additional Baselines]**
**Anonymized URL**: (https://drive.google.com/file/d/1U4gdB5qy1d98AJ1YWxR2v3fzDQp167nt/view?usp=sharing)
To alleviate the reviewer’s concern, we have conducted experiments with additional baseline SDEdit which is based on diffusion. The new table and figure can be found in the anonymized pdf link. One can see that SDEdit suffers from misalignment as well as has higher FID.
**[References]**
Thank you for the relevant reference. We will discuss this work in our related work section.
**[Non-overlapping support assumption]**
In fact, we found that the non-overlapping support assumption is not very hard to be met in practice, as the partitioning according to $u^{(q)}$ is controlled by the system designers. For example, in photo to cartoon translation, one can pick black/non-black hairs as $u^1$ and $u^2$, which naturally lead to non-overlapping clusters. Of course, partitioning data would reduce the amount of data in each cluster, which might make learning its corresponding $v_t$ harder. This is a tradeoff that system designers should pay attention to when splitting the data.
**[Experimental Scope]**
The reviewer’s comment is related to an open challenge for diffusion and FM-type methods; that is, scalability with large dimension data has not been solved in general. Note that diffusion and flow matching in latent space of VAE rather than raw pixels is common practice [R1, R2] . Further, the latent space is of dimension 32 x 32 x 4, which is still quite high dimensional.
We agree that diverse modalities like text-image is a very interesting scenario. However, applying any diffusion/FM models in the raw data space remains an open problem, and solving this challenge is out of scope of this work. We will add some remarks in “limitations” to draw attention to this open challenge.
*[R1] Kapusniak, Kacper, et al. "Metric flow matching for smooth interpolations on the data manifold." NeurIPS 2024.*
*[R2] Tong, Alexander, et al. "Improving and generalizing flow-based generative models with minibatch optimal transport.* | Summary: This paper aims to address the unpaired domain translation problem with conditional information. The previous method is based on GAN. However, GAN training may not be stable; this paper proposes a Flow Matching-based method. However, the naive FM method may not work because conditional distributions may be mismatched, as shown in the synthetic experiments in the paper. The authors proposed a novel bilevel optimization loss to address this problem. One level of the loss optimizes the flow for each condition, and the other level optimizes the global flow and the interpolant between source and target distributions. The authors conducted experiments on synthetic data, Human face data, and Swarm Navigation data.
Claims And Evidence: Yes.
Methods And Evaluation Criteria: Not sufficient. The toy examples should include the case that different conditions have overlaps. The authors need to compare with stronger baselines on more datasets.
Theoretical Claims: I roughly checked the proof of Proposition 3.4, and didn't find issues.
Experimental Designs Or Analyses: Yes, important baselines are missing, and experiments on more datasets on which domain translation methods are commonly tested should be included.
Supplementary Material: Yes, I reviewed C.1 Synthetic Data Experiment and E.1 proof of Proposition 3.4.
Relation To Broader Scientific Literature: The key contribution of this paper is to propose a Flow Matching method to address the domain translation problem with additional conditional information. The previous method proposed by Shrestha and Fu 2024 was based on GAN.
Essential References Not Discussed: Several existing image-to-image translation methods are missing:
- Zhao et al, EGSDE: Unpaired Image-to-Image Translation via Energy-Guided Stochastic Differential Equations, NeurIPS 2022.
- Gazdieva et al., Extremal Domain Translation with Neural Optimal Transport, NeurIPS 2023.
- Kornilov et al., Optimal Flow Matching: Learning Straight Trajectories in Just One Step. NeurIPS 2024.
Other Strengths And Weaknesses: ### Strength:
The authors proposed a Flow Matching method to address the unpaired domain translation problem with conditional information. The authors proposed a bilevel optimization loss. One level of the loss optimizes the flow for each condition, and the other level optimizes the global flow and the Interpolant between source and target distributions.
### Weakness:
The experiments in this paper are not strong.
1. The authors should compare with stronger baselines:
- Zhao et al, EGSDE: Unpaired Image-to-Image Translation via Energy-Guided Stochastic Differential Equations, NeurIPS 2022.
- Gazdieva et al., Extremal Domain Translation with Neural Optimal Transport, NeurIPS 2023.
- Kornilov et al., Optimal Flow Matching: Learning Straight Trajectories in Just One Step. NeurIPS 2024.
2. The authors should do experiments on more datasets, such as CelebA/CelebA-HQ, AFHQ, on which domain translation methods are commonly tested.
3. In the synthetic experiments, the authors should include data with overlapping condition distributions, such that we can evaluate how effective Eq. 12 is.
4. The improvement of the proposed method is minor compared to using the naive baseline FM-cond: 22.21 vs 22.65 in terms of FID.
Other Comments Or Suggestions: No.
Questions For Authors: In Fig. 3 (b), the authors drew intended trajectories. However, I am not sure whether the blue and green trajectories are really achievable or not. The blue and red lines cross. At each cross point of one blue line and one red line, the final velocity v will be the average of the two velocities of the red and green lines. So, the blue and red lines cannot cross on the 2-d plane. I have similar concerns for Fig. 5 (a) and Fig. 10 DFM. The authors need to clarify this in case my understanding is wrong.
The authors did synthetic experiments showing Eq. 10 sometimes works and sometimes doesn't work, to motivate their own formulation Eq. 12. However, the authors didn't explain why Eq. 10 doesn't work. Is the network complexity not enough, or is the initialization not good, or other reasons? How do you parametrize $I^{(q)}$ in Eq. 10 and 12? Eq. 12 is also difficult to optimize, and Eq. 12 could also sometimes fail. The authors need to justify that the optimal solution of Eq. 12 can be achieved in the experiments.
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: **[Intersecting trajectories in figures]**
Note that Fig. 3(b) does **not** show the velocity field but the interpolant $I^{\rm linear}(x, y, t)$ where $x, y \sim \rho(x, y | u^{(q)})$. The wording was meant to imply that interpolants guide the learning of the vector field. Our term “intended trajectories” could be confusing; we will change it to “interpolant trajectories.”
In Fig. 5(a) and Fig. 10, the trajectories do not cross each other (**please note the time colorbar**). This is because the two conditional populations travel at different speeds. Hence the intermediate transported distributions are not at the same location at the same time, although they pass via the same location, avoiding collision. This was briefly discussed in Sec. 5.1 (2D Gaussian blobs). We will make this clearer in the revised version.
**[About Eq (10) and (12)]**
This is an important but nuanced point worth clarifying. We briefly discussed why Eq. (10) fails in Lines 244–268, with a more rigorous explanation in the proof of Fact 3.3. Essentially, when $I^{(q)}$ is learnable and $Q > 1$, Eq. (11) may not hold for all $q$, even though it is needed for $\widehat{v}$ to transport $p_{x|u^{(q)}}$ to $p_{y|u^{(q)}}$. Changing $I^{(q)}$ alters the minimum of the flow matching loss $L_{\rm FM}^{(q)}$, and since $v_t$ is coupled with all $L_{\rm FM}^{(q)}$, minimizing Eq. (10) may not achieve the minimum for every loss. However, since $v_t$ is coupled with all $L_{\rm FM}^{(q)}$’s, it is not guaranteed that minimum of all $L_{\rm FM}^{(q)}$ is reached by minimizing Eq. (10).
$I^{(q)}$ is also parameterized as in Eq. (17).
Note that Eq. (12) does not “fail” like Eq. (10); unlike Eq. (10), which is theoretically flawed (therefore fails sometimes) as shown in Fact 3.3, Eq. (12) is theoretically sound per Prop. 3.4. However, as the reviewer correctly noted, Eq. (12) is hard to optimize due to its bilevel nature. To address this, we proposed to exploit the structural constraint in Section 3.4.
We will add a remark to summarize these nuances and clarify this discussion.
**[More Experiments]**
**Anonymized URL**: (https://drive.google.com/file/d/1U4gdB5qy1d98AJ1YWxR2v3fzDQp167nt/view?usp=sharing)
We should mention that the baselines FM-OT and MFM are strong, recent methods. Nonetheless, to address the reviewer’s concerns, we experimented with two additional diffusion-based baselines—EGSDE (provided by the reviewer) and SDEdit [Meng et al., 2022]—both using the same diffusion model trained on the Bitmoji domain based on DDIM.
In URL, we include these baselines and test them on the CelebAHQ-to-Bitmoji experiment (note that standard datasets, e.g., CelebAHQ Male-to-Female and AFHQ, are actually easier cases since the domain gap is smaller; hence, content misalignment rarely appears even for methods (such as MFM, EGSDE) without identifiability guarantees).
R-Fig. 3 shows that translations by the new baselines differ significantly from Bitmoji images, leading to high FID despite setting the reverse diffusion repeats (K) to 3. Thus, although the ^DreamSim score [Fu et al., 2023] is relatively low, the translations are not meaningful due to high FID. In comparison, our method yields superior translations, as shown by qualitative results, FID, and DreamSim scores.
*^Note that DreamSim appears to be insensitive to small but perceptible differences in translation fidelity (c.f. DFM and DDM-GAN qualitative results)*
**[References]**
Thank you for the relevant references. We will include them in the revised version.
**[Overlapping Cases]**
R-Fig. 3 shows the case where the source and target conditional distributions have some overlap. The overlap is created by increasing the variance of the Gaussian components from Fig. 3 in the manuscript. One can see that small overlaps have a marginal effect on the performance of the proposed method. However, since the proposed implementation exploits the property of disjoint supports, larger overlaps can be detrimental to its performance.
We should remake that, as the partitioning of the conditional distribution is **controlled by the system designer,** the available data can always be split in a support-disjoint way. Hence, the harm brought by overlapping support is avoidable in many cases.
**[About FID]**
**In the context of identifiability-guaranteed translation, a good method retains source content while maintaining a reasonable FID (image quality).** Thus, minimizing FID is not our primary goal; we use it to show that our method does not compromise quality. Note that low FID alone does not ensure transport identifiability. Even if some baselines have similar FID scores, it does not mean they could attain content alignment.
R-Table 1 shows that our method does not compromise image quality (measured by FID) while ensuring content alignment (see R-Fig. 2 and Dreamsim score), unlike baselines that often lose content despite similar FID scores.
---
Rebuttal Comment 1.1:
Comment: Thank the authors for the response! However, the improvement of the proposed method is still marginal compared to the FM-cond from results in the main paper and the additional results in the rebuttal regarding the Dreamsim score (0.59 vs 0.60). Also, more stronger baselines (e.g. Kornilov et al. 2024) I mentioned in the review were not compared, more datasets and standard domain translation tasks were not tested. I would still consider experiment part a week point of this paper.
---
Reply to Comment 1.1.1:
Comment: Thank you for the time and effort devoted to reviewing our work.
We believe that we have addressed these concerns in our rebuttal. To further clarify:
1. We selected a baseline from the list provided by the reviewer, identified as one of the “strong baselines.” Kornilov et al., 2024, was not chosen because it requires training ALAE before the flow matching can be trained—a process that would be challenging to complete within the rebuttal period given our current resource and time constraints. We do plan to include it in the revised version.
2. We acknowledge that the Dreamsim score offers only a rough indication of performance. It does not capture several nuances in translation quality (for example, DDM-GAN has a lower Dreamsim score but exhibits noticeable translation and diversity issues compared to DFM). We have provided additional explanations in our response to Reviewer dKp3 under the [LPIPS score] section, and we will add more qualitative results to the appendix in the revised version.
3. We provided clarifications regarding standard domain translation tasks such as CelebA-HQ male-to-female, where existing methods are already capable of producing content-aligned translations. Our method specifically addresses content-misalignment issues observed in other approaches. However, it is important to note that standard datasets (e.g., male-to-female, AFHQ) do not exhibit these issues to begin with.
We hope these explanations clarify our approach and thank you for your valuable feedback. | null | null | null | null | null | null |
Gradient-based Explanations for Deep Learning Survival Models | Accept (poster) | Summary: The paper benchmarks previously proposed gradient-based explanation methods across three previously proposed deep survival analysis methods. Experimental results on synthetic and real-world datasets highlight differences in performance across scenarios.
Claims And Evidence: - The paper claims an extension of previously proposed GradSHAP to GradSHAP(t) as a key contribution. However, it seems like a straightforward application of GradSHAP to survival outcomes. It is unclear what the actual contributions or challenges unique to survival time GradSHAP(t) address.
- The paper claims that GradSHAP(t) offers a better balance in computational efficiency and accuracy. However, only Figure 6 is provided to support this claim, and the definition of local accuracy is not provided in the paper. Additionally, it is unclear why alternative approaches such as SurvLIME are not discussed.
- The paper claims that gradient-based explanation methods effectively identify prediction-relevant features. Unfortunately, most experiments are based on synthetic data, with only Grad(t) and Grad(t) × Input(t) benchmarked on preselected instances. It is unclear why comprehensive evaluations of all gradient-based approaches, including GradSHAP(t), are not provided, with evaluations summarized across all instances.
Methods And Evaluation Criteria: - The proposed approach, GradSHAP(t), is a straightforward extension of the previously proposed GradSHAP to survival outcomes.
- The evaluation criteria on synthetic data is based on two preselected instances, which do not comprehensively capture the variance across test examples. Additionally, it is unclear what local accuracy in survival outcomes entails (Figure 6).
- The comparisons are not consistent across the deep survival methods and the gradient-based approaches across experimental settings.
Theoretical Claims: N/A
Experimental Designs Or Analyses: - Given that this is a benchmarking paper, the experimental results are underwhelming. The experimental comparisons are not consistent and seem cherry-picked. I encourage the author(s) to provide extensive analysis and results across all experiments, where all methods are included and results are summarized across all instances.
Supplementary Material: N/A
Relation To Broader Scientific Literature: - Gradient-based explanations for deep survival models are an important research area for clinical decision-making
Essential References Not Discussed: - The paper should also discuss other non-time-varying survival explanation approaches, e.g., Kovalev et al. (2021) and Utkin et al. (2022).
Other Strengths And Weaknesses: The writing could be improved to focus on key contributions. Also, the experimental section is difficult to follow given the inconsistency in the experimental setup.
Other Comments Or Suggestions: **Minor**
- Eqn 4: Should be $\ln$ instead of $\log$
Questions For Authors: - Could you provide comprehensive results for all experiments?
Code Of Conduct: Affirmed.
Overall Recommendation: 1 | Rebuttal 1:
Rebuttal: Thank you for your valuable and insightful feedback. Before addressing your concerns in detail, we want to clarify a few crucial aspects and potential misunderstandings:
* This is **not** a benchmark paper.
* We do provide the definition and explanation of local accuracy in the appendix.
* We do provide comprehensive results (as far as meaningful) for **all experiments** and **all methods** and for **aggregated** metrics.
* We do compare with SurvLIME (contrary to the point you raised).
**R4A1) What is the objective of this paper?**
The objective of our paper is explicitly stated to **not** be a benchmark paper comparing different gradient-based explanation methods for survival DNNs (see XAI benchmark papers by Liu et al., 2021 and Agarwal et al., 2022 for classic prediction models). Instead, we adapt these methods for survival DNNs, provide method-specific visualizations and interpretations (addressing the recent disagreement problem), and compare GradSHAP(t) as a flexible model-specific version to SurvSHAP(t), making the calculation of Shapley values for survival DNNs possible (see **R1A3 and R3A1**).
**R4A2) Why no comprehensive (aggregated) evaluations for all experiments? Only synthetic data?**
A comprehensive evaluation across all methods is not feasible because XAI methods pursue different goals and lack definitive "correct" explanations. For gradient-based methods, this disagreement problem (Sturmfels et al., 2020; Krishna et al., 2023) origins from varying implicit or explicit baselines, making direct comparisons on a local level unreliable (e.g., Grad(t) measures output-sensitivity, GradxInput(t) attributes implicitly against a zero baseline, etc.). We evaluate the methods as local explanation techniques and highlight their characteristics using the introduced visualizations (see Appendix A.1 and A.2 for our comprehensive results). A meaningful aggregation of results across all instances is only possible for Shapley-based methods (as we did for two measures in Sec. 5.2). However, aggregation compromises the local nature of the explanations as it leads to global measures.
Additionally, we mainly used synthetic data for the comprehensive evaluation since it is the only reliable way to verify – in a controlled environment – if the model identifies truly prediction-relevant local effects based on the method's goal. Instead, a benchmark would focus on comparing methods against each other.
**R4A3) Marginal technical contribution?**
Please refer to the detailed response for **Reviewer 3 R3A1)**.
We acknowledge that we may not have effectively communicated our intended contributions (adoptions for survival including challenges, visualizations and package implementation). In the final paper, we will emphasize and explain these contributions better.
**R4A4) Concerns about local accuracy and advantage of GradSHAP(t)**
The local accuracy measure for survival outcomes is defined and explained in detail in Appendix A.3.1. We acknowledge the importance of this metric and will incorporate it into the main text. It measures the average decomposition quality of the local attributions of SHAP-based methods (i.e., decomposing $\hat{S}(t|x)-E(\hat{S}(t|x))$). The primary advantage of our approach (GradSHAP(t)) lies in its drastically improved runtime efficiency compared to SurvSHAP(t). In addition to the results provided in our paper in Sec. 5.2. Fig. 6 and Appendix A.3.2., we now conducted an additional runtime comparison between SurvSHAP(t) and GradSHAP(t) as discussed in responses to **Reviewer 1: R1A1 and R1A3)**.
**R4A5) Comparison to SurvLIME and other non time-varying methods.**
We compared GradSHAP(t) with SurvLIME in terms of global feature importance ranking (see Sec. 5.2, Fig. 7, and A.3.3). While SurvLIME estimates local feature importance values, SurvSHAP(t) and GradSHAP(t) provide local attributions. A direct comparison is therefore only meaningful by evaluating the resulting feature ranking across all instances.
In the related work, we purposefully only explicitly mention survival XAI methods, which are comparable to the gradient-based explanations discussed in the paper. Other survival explainability methods which do not provide time-dependent, local feature attributions are beyond the scope of our paper, including Kovalev et al. (2021) and Utkin et al. (2022), but are discussed in great detail in the referenced comprehensive review by Langbein et al. (2024).
---
Rebuttal Comment 1.1:
Comment: Thank you for your rebuttal and for clarifying some of my concerns. Unfortunately, most of my concerns remain unaddressed, namely:
**Marginal Technical Contribution**
GradSHAP(t) appears to be a straightforward extension of GradSHAP to survival analysis. Could you clarify what the technical contributions of the paper are?
**Underwhelming Experimental Results**
Given the limited technical contributions, I would expect the experimental results to be rigorous enough to justify the paper's acceptance. However, there are several issues:
1) The results seem cherry-picked in terms of examples, survival models, and gradient-based explanation methods (Figures 3–8). The non-time varying methods should be included as well, since the estimate should just be constant over time. Also the plots are difficult to interpret. Given than the effect of the covariates is known for synthentic data, an agregated quantitavie metric, e,g., RMSE comparing different methods should also be provided.
2) Given that SurvSHAP(t) is a comparable baseline to the proposed approach, it is unclear why SurvSHAP(t) is not consistently benchmarked against GradSHAP(t) in all these instances.
3) *Local Accuracy*: Thank you for pointing me to the definition. Could you clarify why local accuracy is directly tied to the specific gradient explanation method used?
4) *Global Importance Ranking Tasks (Figure 7)*: The paper should also benchmark against non-gradient-based methods, such as the Cox proportional hazards model, to provide a more comprehensive comparison. Additionally, could you clarify the expected ground-truth feature ranking? Unfortunately, the proposed plot is difficult to interpret without actual ground-truth information. This is another instance where summarizing the results with a quantitative metric would be helpful.
---
Reply to Comment 1.1.1:
Comment: Thank you for your time and effort in reviewing our responses. We regret that some of your concerns remain unaddressed, and we appreciate the opportunity to clarify these further.
**Marginal Technical Contribution?**
As already noted in our rebuttal, we have addressed this point in the response to Reviewer 3 under **R3A1** and kindly refer you to that response, where we provide a detailed explanation.
**Underwhelming Experimental Results?**
**1) Cherry-picked examples**
* Our paper focuses on **local post-hoc** attribution methods, specifically adapting gradient-based methods for survival neural networks (SNN). While this choice may appear selective, it covers the most common SNN and gradient-based attribution methods, and thus clearly defines the paper's scope. Additionally, since the paper is about local gradient-based methods, it is essential to show the results instance-wise (Fig. 3-5), even though it seems cherry-picked, but is the nature of the methods discussed in the paper.
* Including experiments on non-post-hoc or non-attribution methods (e.g., inherent explanations or counterfactuals) would blur our contribution scope as we explain a single prediction of an already trained SNN and not (directly) the survival data. While the mentioned non-time-varying methods may be of interest in the broader context of survival XAI, they do not align with our focus on post-hoc feature attribution methods and thus fall outside the scope of our detailed examples.
* In our simulations, we aimed to showcase the different local behavior of the methods and highlight the "Disagreement Problem" in the survival context, which can only be effectively demonstrated in a simulated setting on an instance-wise level. We acknowledge that this motivation may not have been made clear enough in the current version and will improve this in the final revision.
* As already mentioned, the methods pursue different decompositional objectives – also depending on the baselines – we are unsure how the methods could be meaningfully compared using RMSE, but would gratefully appreciate clarification. While correlation-based comparisons are possible, such analyses have already been performed for standard models. Instead, we compare methods where a shared objective and model-agnostic counterparts exist, such as GradSHAP(t) and SurvSHAP(t).
**2) SurvSHAP(t)} vs. GradSHAP(t)**
It is unclear which instances you are referring to where GradSHAP(t) was not compared to SurvSHAP(t). Sec. 5.1 is not intended as a benchmark, but rather as a proof of concept to demonstrate that explanations align with model-learned feature effects and provide guidance for correct interpretation. Sec. 5.2 then uses an equivalent data-generating process to benchmark GradSHAP(t) and SurvSHAP(t) – the only directly comparable methods – **across all instances in the simulated datasets** using three global evaluation metrics: local accuracy, runtime, and global importance ranking.
**3) Local Accuracy**
We use the time-dependent local accuracy criterion $M:T\to R_{>0}$ (plotted over the survival time $t$):
$$
M(t)=\sqrt{\frac{E_{x}\left[\left(f(t|x)-E_{\tilde{x}}[f(t|\tilde{x})]-\sum_{j=1}^p R_j(t |x)\right)^2\right]}{E_{x}\left[f(t|x)\right]}}.
$$
Both GradSHAP(t) and SurvSHAP(t) are (marginal) Shapley-based attribution methods, aiming to decompose the difference between a single and the expected survival predictions $f(t|x)-E_{\tilde{x}}[f(t|\tilde{x})]$, thus quantifying feature contributions (see Fig. 2 and Sec. 4.2). The other gradient-based methods instead:
* Grad(t) and SG(t) are output-sensitivity methods (no decomposition goal),
* Grad x Input(t) decomposes $\approx f(t|x)$,
* IG(t) decomposes $f(t|x) - f(t|\tilde{x})$.
Only for IG(t) exist mathematical guarantees for an exact approximation, i.e., an equivalent *local accuracy* measure could be defined. However, there is no (implemented) model-agnostic counterpart for IG(t).
**4) Global importance rankings**
The ground truth feature ranking is given by the feature indices ($x_1<x_2<x_3<x_4<x_5$) as highlighted in the plot legend ("Features (increasing importance)") and discussed in Sec. 5.2. We will further clarify the feature order in description and legend of Fig. 7 in the final version. We agree that a summary metric would improve clarity, so we will compute and include the rank correlation between the ground truth and observed feature rankings. While we can also fit a CoxPH model and compute its FIs $\beta_j x_j^{(i)}$, the focus of our study is to compare XAI methods for NN-based models. Introducing a CoxPH comparison would shift the goal to evaluating model quality rather than the performance of XAI methods, which is beyond the scope of this paper. As discussed in **R4A4**, SurvLIME, SurvSHAP(t), and GradSHAP(t) are the only relevant local XAI methods for survival analysis in this context. | Summary: This paper shows a comparative study on various explanation methods for survival analysis. While there are several model-agnostic methods to interpret models for survival analysis, this paper considers gradient-based methods. The applicability of the gradient-based methods is limited to models that can compute gradients (e.g., neural network models), but this paper shows its effectiveness compared to the other methods.
Claims And Evidence: Yes.
Methods And Evaluation Criteria: Yes.
Theoretical Claims: No theoretical claims are presented in this paper.
Experimental Designs Or Analyses: Yes.
Supplementary Material: Yes, many graphs referred from the main body of this paper are shown in the appendix.
Relation To Broader Scientific Literature: While Langbein et al. (2024) review many methods to interpret survival models, gradient-based methods are briefly discussed in this review. This paper focuses more on gradient-based methods, and the contribution of this paper can be seen as extensive experiments on comparative study of gradient-based methods for survival models.
Essential References Not Discussed: None.
Other Strengths And Weaknesses: A weakness of this paper is that the technical contribution is marginal. While there are many methods to interpret $y=f(x)$ for the standard regression analysis where $x$ is a feature vector and $y$ is a target value, this paper shows only adaptations of these methods to interpret $p=S(t|x)$ where $t$ is a time point and $p$ is a probability and the adaptations are almost straightforward. In other words, this paper does not show any novel idea associated with applying the interpretation methods for the standard regression analysis to survival analysis. (This is in contrast with (Krzyzinski et al., 2023), which proposes a modification of an evaluation metric specifically designed for survival analysis. The modification is described in the appendix of this paper: from Equation (9) for the standard regression analysis to Equation (10) for survival analysis.)
A strength of this paper can be seen as explicitly providing the adaptations (as summarized in Figure 2) and shows effectiveness of these adapted methods. The results reported in the experiments (in Section 5) are reasonable and convincing. For example, this paper shows the effectiveness of using the gradient-based method, GradShap(t), compared with existing model-agnostic methods SurvSHAP(t) and SurvLIME.
Other Comments Or Suggestions: None.
Questions For Authors: None.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your careful evaluation and suggestions. We acknowledge that our contributions may not have been communicated clearly enough in the original submission. To address this, we will revise the manuscript to better clarify these key contributions:
* Our work follows adaptations common in survival XAI but tackles key challenges beyond straightforward mathematical extensions. E.g., a naive application of these methods on CoxTime is not possible.
* We introduce tailored visualizations and post-hoc interpretations for gradient-based survival outputs and exemplify the impact of implicit vs. explicit baselines, addressing the recent debate on the disagreement of gradient-based explanations.
* As a novel contribution, we provide a software package implementing all described gradient-based XAI methods for DeepSurv, DeepHit, and CoxTime.
In the following, we provide a detailed explanation regarding your feedback:
**R3A1) Marginal technical contribution?**
Our primary contribution is extending six standard gradient-based explanation methods to time-dependent survival analysis, addressing a crucial gap in survival XAI research. The extensions are far from trivial from both a technical implementation and post-hoc interpretation perspective. For instance, in the CoxTime model time is an input feature, allowing for complex relationships between the artificially created time feature and other features. Thus, applying gradient-based methods naively to the survival function $S(t|x)$ separately at each time point $t$ is not feasible, as time-expanded instances are no longer independent, leading to accumulated gradients from earlier time points. This computational difficulty is not captured in the formal mathematical adaptions. Similar methodological adaptations are standard practice in survival interpretability research (see Kovalev et al., (2020), Krzyzinski et al., (2023); even the time-dependent local accuracy metric in Krzyzinski et al., (2023) follows a similar extension from the original Shapley value axiom.
Furthermore, another major contribution of our work are effective visualization and interpretation techniques for functional outputs tailored to different methods. This is particularly important given the ongoing debate and disagreement regarding gradient-based methods (Sturmfels et al., 2020; Krishna et al., 2023; Koenen et al., 2024). Our work contributes to this discussion by clarifying how implicit or explicit baselines in these methods influence survival explanations and provides practical guidance on selecting appropriate techniques based on their interpretability characteristics.
Finally, we highlight our `R` package, `Survinng`, as an additional contribution. Existing libraries like `Captum` and `innsight` do not natively support survival DNNs, necessitating custom implementations. Our package, which includes all described gradient-based XAI methods for DeepSurv, DeepHit, and CoxTime, will be made available with the final version of this paper. | Summary: The authors introduce GradSHAP(t), an extension of SurvSHAP(t) that analyzes the gradients to better explain the model’s predictions. The authors also propose extensions of other gradient-focused XAI methods to align with the survival task.
Claims And Evidence: Yes.
Methods And Evaluation Criteria: GradSHAP(t) (and the other proposed methods) clearly align with the application at hand. Explainability of survival models is critical due to their applications in fields such as healthcare. The temporal aspect creates additional complexity, which motivates the exploration of time-dependent explainability analysis.
Theoretical Claims: The authors do not provide theoretical claims.
Experimental Designs Or Analyses: This article relies on synthetic data for a bulk of its experiments. However, given that real world data is often difficult to explain (due to lack of domain knowledge), this is necessary for the purpose of this paper. These results are reinforced by a single real-world dataset, which contains known features of interest.
The experimental setup is well documented. Also, the motivation for the design decisions made when constructing the synthetic dataset are clearly stated and understandable.
The authors provide rigorous and convincing analysis of all experiments.
Supplementary Material: Yes, A.1, A.3.1
Relation To Broader Scientific Literature: The paper is related to both the survival analysis literature and the explainability research literature.
Essential References Not Discussed: While the paper considers GradSHAP(t) with respect to proportional hazard (DeepSurv, CoxTime) and discrete time (DeepSurv) models, I would be interested in an additional analysis of Accelerated Failure Time (AFT) model such as DART (Lee et al, 2023).
Other Strengths And Weaknesses: The extension of gradient based XAI to survival analysis is novel and has clear potential for future impact. The article is overall written well and all figures are visually digestible.
Other Comments Or Suggestions: N/A
Questions For Authors: N/A
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We appreciate the suggestion to include semiparametric AFT-based survival deep learning models, such as Deep AFT Rank-regression for Time-to-event prediction model (DART). It is an interesting approach, which estimates the survival function in similar fashion to a non-Cox-based version of the DeepSurv model. However, the pre-trained baseline hazard function additionally depends on the output of the base neural network, as highlighted in Eq. 9 in the paper by Lee et al. (2023). Unlike Cox-based methods, such as DeepSurv and CoxTime, this formulation allows for gradient computation on the baseline hazard, which could provide further insights into the differences between Cox and non-Cox methodologies. Given its potential, we aim to explore its integration and explanations in future research.
Our current focus is on methods that are readily accessible to practitioners, particularly those implemented in widely used libraries such as Pycox (Python) and survivalmodels (R). Expanding these packages or developing more comprehensive survival analysis software to also include AFT models such as DART is an important direction, and we are actively working toward addressing this gap.
More broadly, extending gradient-based XAI methods to AFT-based deep learning models like DART is an exciting avenue for future work. We will highlight this in the paper's future work section.
We would also like to take the opportunity to highlight that we conducted additional comparisons of SurvSHAP(t) and GradSHAP(t) on real data. In the multi-modal model (Sec. 5.3), SurvSHAP(t) was aborted after 10 hours (256 threads, 700GB RAM) with only two reference samples, while GradSHAP(t) completed in ~8 minutes using 100 reference and 20 integration samples. See our response to Reviewer 1 (**R1A3**) for details.
Thank you very much for the positive feedback! | Summary: This paper addresses the challenge of interpreting "black box" deep learning models used for survival analysis, which predict time-to-event outcomes. The authors introduce a framework for gradient-based explanation methods to capture the time-dependent influence of various features, including those from multi-modal data like medical images and tabular information. They introduce GradSHAP(t), a gradient-based, model-specific counterpart to the model-agnostic SurvSHAP(t). Using both synthetic and real-data experiments, it is shown to be computationally efficient while maintaining accuracy compared to existing approaches.
Claims And Evidence: The primary claims for novel contributions in the paper are
1. using existing gradient-based methods to explain survival predictions (specifically, capturing the time-dependence of features)
2. introducing GradShap(t) and showing that it is computationally efficient while maintaining accuracy with its main competitor SurvShap(t) from a previous work
Prior work has already established the importance time-dependent attribution of features to survival predictions. Claim 1 extends this specifically for gradient-based explanations.
For Claim 2, the evidence seems preliminary. We seem to lose in terms of the local accuracy (Fig 6). Moreover, I'm not sure how important the corresponding gains in runtime even are, since this is a post-hoc task, not an inference task where runtime is critical. The in-depth evaluation is done on 2 examples presented in Fig 6, and I'd have liked to additionally see aggregate metrics over the dataset. In the end, I'm left thinking it might provide marginal benefits over the existing method SurvShap(t), if at all.
Methods And Evaluation Criteria: - The synthetic experiments make sense in that they give us an idea of potential benefits and pave the way for real-data experiments.
- The real-data experiments are lacking in that the gains relative to the main baseline, SurvShap(t), are unclear. The authors chose 2 examples but even on those, I see gains in runtime (which is not too important for a post-hoc task) but a loss in local accuracy (which is arguably more important for interpretation). I am also unable to parse Fig. 8 to judge whether what the model tells us is indeed sensible.
Theoretical Claims: N/A
Experimental Designs Or Analyses: I have pointed out the issues with the evaluations used, especially for the real-world data. I think the manuscript should contain not just 2 in-depth examples but also aggregate metrics over the dataset. It should also clearly compare with SurvShap(t) on the same examples and identify where the gains of GradShap(t) are coming from. As a reviewer it is hard for me ascertain based on the limited results here whether GradShap(t) works significantly better and what its benefits over SurvShap(t) are.
Supplementary Material: Yes, I review the supplementary material (both the experimental setup and the figures with the results).
Relation To Broader Scientific Literature: The work extends interpretability of survival models from model-agnostic methods to gradient-based methods. The hope here is that while model-agnostic methods only deal with the model outputs, the gradient-based methods use the model's "internals" to get a better view into how the model is using its features.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: Strengths: I really enjoyed reading the paper, it is very well written.
Weaknesses: I'd like to see more of
- explanation of SurvShap(t) and how exactly GradShap(t) gains relative to it
- experiments with real data that illustrate the above
Other Comments Or Suggestions: N/A
Questions For Authors: N/A
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We are grateful for your constructive feedback. In response, we conducted additional experiments on the feasibility and computational efficiency of GradSHAP(t) and SurvSHAP(t) on the multi-modal real data example, which we will include in the final paper. Here, GradSHAP(t) took 5 minutes to compute, while we had to abort the computation of SurvSHAP(t) after 10 hours (details below). In light of these results, we argue that runtime is one of the most crucial aspects for post-hoc Shapley value approximation, which is supported by previous literature. Additionally, we want to highlight that local accuracy and importance ranking are already aggregated metrics. The following summarizes all your concerns in-depth:
**R1A1) Limited gain of GradSHAP(t) relative to SurvSHAP(t)?**
The objective behind GradSHAP(t) is not merely to propose a "better" method, but rather a practical one that balances flexibility and computational feasibility. Although differences in local accuracy are visible due to the log scale, they are practically negligible, whereas the runtime improvement of GradSHAP(t) is substantial. This becomes particularly apparent in our additional experiments, including image data, which demonstrate that SurvSHAP(t) quickly becomes computationally infeasible without substantial resources, whereas GradSHAP(t) remains efficient and can be computed on a standard laptop (for further details refer to **R1A3**). Computational runtime is a well-established criterion in post-hoc XAI methods, particularly for SHAP explanations. It is frequently used as a key selling point in the scientific literature when introducing new estimation methods, see e.g., TreeSHAP (Lundberg et al., 2020), FastSHAP (Jethani et al., 2021) or various other SHAP algorithms such as in Ancona et al. (2019) or Chen et al. (2018) and runtime is included as a comparison metric in their SHAP benchmarking suite (Python SHAP package, Lundberg and Lee, 2017).
**R1A2) Limited number of examples/lack of aggregated metrics?**
Our comparison of SurvSHAP(t) and GradSHAP(t) was performed for all three survival DNN classes (see Appendix A.3 for full plot) with varying numbers of input features, averaged over 20 trained models per case. In spite of its name, local accuracy is already a dataset-wide aggregated measure (see Eq. 10, Appendix A.3.1.), which we plot for $p=30$ over the survival time in Fig. 6. Additionally, Figure 7 presents a comparison of global feature importance, particularly importance rankings, which are also aggregated over survival time. Could you clarify if you were referring to something beyond these analyses?
**R1A3) Real data?**
We performed additional comparisons of SurvSHAP(t) and GradSHAP(t) on real data. On the multi-modal model (including images) for explaining a single instance (Sec. 5.3), we had to abort the computation of SurvSHAP(t) after 10 hours (using 256 threads and 700GB of RAM) with only two reference samples. In contrast, GradSHAP(t) completes in around 8 minutes with 100 reference and 20 integration samples. As an additional comparison, we conducted the same experiment (but ResNet18) on downscaled images (32×32) using a standard ML workstation (48 threads, 256GB RAM). As shown in the table below, SurvSHAP (with 50 samples) takes more than 41 times longer than GradSHAP (n = 25, samples = 50), which is nearly 25 minutes for just a single explanation compared to 36 seconds. GradSHAP achieves this not only faster but also with better instance-wise local accuracy (averaged over survival time $t$, i.e., no aggregation over all instances).
We agree that this is crucial information for the readers and we will include discussions and visualizations of the computational efficiency of both methods on real data in the final version of the paper.
| Method | Runtime | "Instance local accuracy" (avg. over $t$) |
|----------------------------------------|-------------------|---------------------------------|
| GradSHAP(t) (n = 10, samples = 10) | 2.96 sec | 0.00108 |
| GradSHAP(t) (n = 25, samples = 50) | 36.07 sec | **0.00023** |
| GradSHAP(t) (n = 50, samples = 50) | 1 min 18.05 sec | **0.00021** |
| SurvSHAP(t) (samples = 5) | 2 min 45.30 sec | 0.00230 |
| SurvSHAP(t) (samples = 25) | 12 min 34.78 sec | 0.00044 |
| SurvSHAP(t) (samples = 50) | 24 min 45.93 sec | 0.00027 |
We are also happy to provide further clarification on Figure 8, if you further specify which aspects remain unclear from the figure and/or text. | null | null | null | null | null | null |
ShapeEmbed: a self-supervised learning framework for shape quantification | Reject | Summary: This paper presents a self-supervised method for learning object shape, given a binary segmentation mask, that by construction is invariant to translation/scaling/rotation/reflection/outline-point-indexing. This method, ShapeEmbed, consists of extracting a normalized distance matrix from points sampled along the outline of the object, and using this as input to a VAE, where the encoder is modified to use circular padding for convolutions, maintaining equivariance to shifts in the choice of origin for the point indexing. Additionally, several loss terms are added - reconstruction loss of the distance matrix, and regularization terms enforcing a valid reconstructed distance matrix.
The proposed method is tested on several datasets - MNIST, shape matching, and two biological datasets. Results show improvements over alternative baselines, and ablation studies demonstrate the contribution of individual components such as the circular padding and index-invariant loss.
## update after rebuttal
After reading the rebuttal and other reviews/discussions, I will maintain my original rating. The data sets that were studied, combined with the need for the correct foreground segmentation to be provided, feel more like an initial proof of concept. In my view the paper would be greatly strengthened by the inclusion of the type of analysis alluded to in the rebuttal, to validate the real-world applicability of the proposed method.
Claims And Evidence: Yes, the experiment findings support the claims made regarding the properties and benefits of the proposed method.
Methods And Evaluation Criteria: I'd consider the experiment results on the studied datasets to be "proof of principle" - useful as an initial test of the proposed method, but not at the level of an dataset demonstrating the utility of the method on a real application. For instance, it seems that if one were interested in doing classification on BBBC010, the attainable accuracy is 94% (Wählby et al., Nat Meth, 2012).
The studied datasets seem to be both simple in terms of the structure of the shapes, and in terms of the foreground segmentation being provided. I think the paper would be greatly strengthened by showing an application on a more complex dataset where the segmentation was automatically inferred, and where the shape component gave some improvement to the overall performance as compared with what could be obtained without explicitly considering shape in this manner.
Theoretical Claims: Checked over the discussion of the construction of the method/encoder and loss to verify invariance claims.
Experimental Designs Or Analyses: Useful ablation studies provided, in paper and supplementary pdf.
Supplementary Material: Yes, looked over full provided supplementary pdf.
Relation To Broader Scientific Literature: As noted above, one potential weakness of the proposed method is that it currently seems to only be tested on cases where the correct foreground segmentation is provided. In practice, I imagine the segmentation problem itself will often be difficult and give noisy results. One potential interesting avenue would be whether this method could be leveraged to quality of automatic segmentation, by providing a learned prior over the shape distribution for the given class of images.
Essential References Not Discussed: n/a
Other Strengths And Weaknesses: n/a
Other Comments Or Suggestions: Could be useful to provide sample image/shape from MEF dataset, seems to be only one that is omitted as far as visualizations.
Questions For Authors: As discussed above, my key concern is with benefit of the proposed method to real world applications. This is somewhat discussed in the penultimate sentence of the paper, but can the authors describe in more specifics how they see this method being applied to specific biological imaging datasets?
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: # Envisioned use of the method in biological imaging
Morphological features extracted from 2D images serve as phenotypic fingerprints to reveal cell identity, cell states, and response to chemical treatments (see 10.1038/s41592-024-02241-6 for a recent example). Shape, as captured in 2D contours, is one of the most information-rich phenotypic characteristics and provides insights into a range of biological phenomena. Many methods have been proposed to characterize 2D shape in biological imaging (see 10.1111/j.1365-2818.2007.01799.x for a review) and unsupervised methods that include geometric invariances have recently gained traction as illustrated by O2VAE, our main competitor (10.1038/s41467-024-45362-4). This can be explained by the following: as an exploratory science, biology operates without knowing what to look for a priori, making unbiased data exploration invaluable. While experiments aim to uncover "biological labels" (e.g., cell type, cell state), living systems don't come with annotations and researchers only have access to "experimental labels" (e.g., treated vs untreated samples). Using these experimental labels as proxies for the underlying biological labels is inherently problematic due to individual variability: two samples treated identically may respond differently because of natural variations. Self-supervised approaches are especially valuable as they enable the investigation of biological labels independently of experimental categories. We demonstrate one such use-case in the BBBC010 dataset, where ShapeEmbed identifies distinct shape populations of C. elegans nematodes without supervision and reveals instances where experimental labels do not align with biological reality (Figure 4).
Having methods that allow such an unbiased exploration of the distribution of biological shapes can be valuable in many settings, from assessing the efficacy of drug treatments to analyzing biopsies, where cell type identification must ideally be carried out without prior knowledge or potentially biased manual annotation. Although we cannot provide specific details for confidentiality reasons, we are already using ShapeEmbed in such contexts in ongoing collaborations with experimental colleagues.
# Complexity of the biological datasets considered
The biological datasets we use in our experiments were chosen to 1) provide results on a relatively simple and well-characterized biological benchmark (BBBC010), and 2) demonstrate performance on a harder, real-life example where the shape component is known to be essential (MEF).
BBBC010 is indeed not a “pure” shape dataset. Although the authors report a classification accuracy of 97% and a precision of 83% (see 10.1038/nmeth.1984, note that 94% accuracy is for object detection, not classification), this comparatively better performance over ShapeEmbed (87% accuracy and 87% precision, see response to Reviewer HCmb) is likely due to the use of intensity and texture features. We do not use BBBC010 to demonstrate that we provide the best results when it comes to classification, but instead to show that we can learn, without any supervision, a good representation of biological shape in a way that allows unbiased exploration of the data. This also motivates not comparing our results with those reported by Wählby et al., but with a corresponding shape-only baseline (called Region Properties in Table 5). Further investigation of the representation space (Figure 4) illustrates that classification performance alone is not a good indicator of the ability to distinguish between biological states in this dataset, as some nematodes labeled live appear to be dead and vice-versa.
The MEF dataset contains images of cells that were cultured on fibronectin micropattern surfaces to enforce cell shape constraints (as described in 10.1242/jcs.091231). This real use-case illustrates the challenge of untangling individual biological variability vs experimental variability and has been used in recent papers proposing unsupervised frameworks for biological shape analysis (10.1038/s41596-020-00432-x, 10.1038/s41467-024-45362-4). We regret not including visual examples from the MEF dataset illustrating the complexity of the data and would like to do so in the supplementary material of the final version. Until then, we refer to the original publication to get a better sense of the data complexity.
# Other remarks
We indeed rely on existing segmentation masks as we focus on the task of learning a representation of shape information. We agree with the idea of using ShapeEmbed to construct a learned shape prior to help with segmentation, which could either be pre-trained on unpaired segmentations or learned on-the-fly together with a future segmentation architecture to improve quality. Both approaches would be exciting future work but are beyond the scope of this paper. | Summary: Authors introduce a network for 2D shape analysis (silhouettes of objects in images). It works as follows: shape outline is interpolated via spline curve with fixed number of points N across all data samples; pairwise distance matrix is constructed based on those points and normalized to unit Frobenius norm; resulting adjacency matrix is treated as image and passed to convolutional auto-encoder. Proposed approach is translation/scaling/rotation invariant by design. Re-indexing invariance (distance matrix depends on starting point choice) is achieved via loss term that evaluates all valid perturbations of distance matrix. Method shows very strong performance compared to baselines across a diverse set of data.
POST-REBUTTAL UPDATE
I have read other reviews and agree with them on the following points:
+ that method also might not be able to handle noise in segmentation well and noise in segmentation can produce non simply connected shapes. To me, it is another practical concern about application of proposed niche method.
+ method seem to work really well for particular niche of biological data (even without comparison to PointNets and subsequent works).
To me, final decision boils down to potential changes we think are necessary for the paper to be accepted. Below are things that I think need to be changed for the paper to be accepted:
+ Positioning right now is too broad for actual contribution. I think it should be named "ContourEmbded:... " instead of "ShapeEmbed". In the rebuttal authors suggested the following change: “ShapeEmbed: a self supervised learning framework for 2D contour quantification”. For me, it is too minor -- this paper is not about shape embeddings.
+ All discussion about method assumptions: simply connected shapes, non-noisy segmentation of silhouettes (?) should be added with examples (supplement is okay).
+ Additional evaluation should be added to paper or supplement as well.
For me those changes are too major to be accepted without revision, so I keep my rating.
Claims And Evidence: - Proposed shape descriptors are invariant to scaling, translation, rotation, reflection and re-indexing (theoretical; see corresponding section).
- Proposed shape descriptors significantly outperform baselines (O2VAE, EFD - Elliptical Fourier Descriptors) for 2D shape classification tasks on diverse set of data: handwritten digits(MNIST); general shapes (MPEG-7); cell data (MEFs); nematodes data (BBBC010).
- Proposed method can be used in a generative setting to sample 2D outlines from latent feature vectors which is demonstrated qualitatively in supplement.
Methods And Evaluation Criteria: - Classification methods are evaluated via F-Score and log-loss (in supplement).
- For all datasets authors report metrics based on 5-fold cross-validation: mean and std across folds.
- Generative models are only evaluated qualitatively.
I find evaluation limited, especially for biological data. F-score is a good balanced measure for overall performance and results are convincing in that regard. However, additional metrics (e.g. precision, recall) might be helpful to better understand how exactly the proposed method outperforms baselines. I recommend including them in supplement.
Theoretical Claims: - Proposed method by design is invariant to translation, rotation and reflection since it relies on distance matrix of shape silhouette approximation. Scaling invariance is achieved by normalization of the distance matrix by matrix norm. This claim sounds solid to me.
- Authors also claim re-indexing invariance (method depends on order of rows/columns of distance matrices). This is achieved by loss that takes into account all possible distance matrices based on choice of initial point and orientation of the silhouette (overall 2N variants). Thus, this approach is not truly invariant to re-indexing but rather it is enforced via loss. This claim is justified empirically via ablation of this part of the loss (Table 2).
I find the last claim theoretically problematic. To me, it looks like the authors assume that all 2D shapes are simply connected when they derive 2N variants. For non-simply connected shapes this does not seem to hold. Let’s consider 2D donut (O-shape). Let’s assume that external and internal contours have N/2 points each (overall N). It means that indexing of internal and external contours have N variants each. But their interactions have N^2 variants (each external contour indexing can be matched with any internal contour indexing)! And if we assume 2D double donuts (8-shape) with N/3 points per contour, the number of variants becomes (2N/3)^3. I think the proposed method still works because most of the shapes in data are simply connected but this theoretical issue requires clear discussion in the paper and, ideally, ablation.
Another theoretical issue is related to contour traversal. To me, it looks like authors assume no loops in contour. Let’s consider two circles that touch at a single point. Authors assume 2 possible orientations of such a contour but in fact there are four: 2 traversals of one circle until we hit second and after that there are also two traversals. I consider this example to be more rare compared to non simply-connected 2D shapes but this still needs to be discussed.
Experimental Designs Or Analyses: - Experimental design for classification is solid for in-distribution setting but does not show how well the method generalizes across datasets.
- Generative experiments design is lacking because evaluation is only qualitative.
- Choice of baselines is very limited and ignores a large body of work on rotation-invariant point networks that can be utilized for this problem.
Supplementary Material: I have checked the full supplement and I refer to it throughout the review.
Relation To Broader Scientific Literature: Proposed method introduces 2D shape surface representation based on the distance matrix of silhouette points and convolutional network that processes distance matrix as image. This has following relations:
- The fact that 3D (and 2D shapes) can be thoroughly characterized via distribution of pairwise distances of surface points is well known in the 3D vision/graphics community (see essential references).
- Shape analysis in the form of surface point clouds is also a well-studied topic in the 3D vision community and can be applied for this problem as well (see essential references).
Essential References Not Discussed: Paper largely ignores point based networks that can be leveraged for 2D shape analysis: 2D shapes can be represented as 2D point clouds and then processed via point networks (original PointNet paper has experiments on MNIST, for example). Point networks are usually indexing invariant by design; translation/scaling invariance is achieved by normalization; and rotation invariance is achieved by certain architectural modifications (see some references below):
[1] Li X, Li R, Chen G, Fu CW, Cohen-Or D, Heng PA. A rotation-invariant framework for deep point cloud analysis. IEEE transactions on visualization and computer graphics. 2021 Jun 25;28(12):4503-14.
[2] Zhang Z, Hua BS, Yeung SK. Riconv++: Effective rotation invariant convolutions for 3d point clouds deep learning. International Journal of Computer Vision. 2022 May;130(5):1228-43.
[3] Li F, Fujiwara K, Okura F, Matsushita Y. A closer look at rotation-invariant deep point cloud analysis. InProceedings of the IEEE/CVF International Conference on Computer Vision 2021 (pp. 16218-16227).
Paper also ignores a large body of work on shape descriptors (see reference below and follow-up works).
[1] Osada R, Funkhouser T, Chazelle B, Dobkin D. Shape distributions. ACM Transactions on Graphics (TOG). 2002 Oct 1;21(4):807-32.
Other Strengths And Weaknesses: + Empirical results are very strong. If combined with proper discussion of method assumptions and limitations, this might be useful work for practitioners.
Other Comments Or Suggestions: - Legends in some figures (Fig. 3, Fig. 4) are hard to read. I recommend larger font for them.
Questions For Authors: My decision is mostly based on re-indexing theoretical issues and limited comparison to point-based approaches. Can authors kindly clarify the following:
1) Does the method assume that 2D shapes are simply-connected? If yes, how does the method extend to non-simply connected shapes?
2) If the method does not assume simply connected 2D shapes, what is wrong with examples that I have provided in theoretical claims (O- and 8-shapes; touching circles)?
3) If the method assumes that shapes are simply connected, how often this is observed in evaluated data?
4) Are there any insights how the proposed method would work in comparison with rotation-invariant 2D point networks?
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: # ShapeEmbed assumptions on 2D shapes connectedness
We thank you for your insightful questions and hereafter answer them one by one.
**Does the method assume that 2D shapes are simply-connected?** Yes, ShapeEmbed operates with contours that are simply connected and described by a sequence of ordered points (i.e., the contour can be recreated by linking points that follow each other). If accepted, we will adjust the wording in the method description to make this clearer.
**If yes, how does the method extend to non-simply connected shapes?** Our model architecture and loss rely on the fact that points in simply-connected contours can be unambiguously ordered (up to the choice of origin and direction of travel) to learn a representation that ignores reparameterization. For non-simply connected shapes, there is no obvious way to “concatenate” them into a single distance matrix as you rightfully pointed out. Dealing with this would require a model that is invariant to point ordering altogether (similar to point clouds). We are interested to explore this in future work, but it goes beyond the scope of ShapeEmbed.
**If the method does not assume simply connected 2D shapes, what is wrong with examples that I have provided in theoretical claims (O- and 8-shapes; touching circles)?** Although ShapeEmbed assumes simply-connected 2D shapes as described above, it can still handle 0- and 8-shapes (see MNIST dataset) and touching circles. 0- and 8- shapes can be described as a simply-connected contour relying either on a ridge detector (which will provide a midline, ignoring the width) or on their outer edge. Touching circles, like 8-shapes, can be described by a simply-connected sequence of points either like drawing a flower with two petals or like drawing an 8 with a self intersection, and then traversed either clockwise or counterclockwise. We have encountered this in currently unpublished biological data (see response to Reviewer MfnJ) and can confirm that our method is able to describe such structures successfully.
**If the method assumes that shapes are simply connected, how often this is observed in evaluated data?** We have so far not encountered a case in which the simply-connected assumption breaks. We expect this to hold true especially for biological imaging data, where objects do not have holes (e.g. cells) and can be described as a ridge when self-intersecting (e.g. filaments).
# Literature on rotation-invariant point networks
Thank you for pointing us to related works on 3D point cloud analysis. We agree that 2D contours can also be expressed as 3D point clouds (with all contour points lying on a plane). We however identify two major differences in the problem addressed by (10.1109/TVCG.2021.3092570, 10.1007/s11263-022-01601-z, 10.1109/ICCV48922.2021.01591) and our method.
**1. Supervised versus self-supervised learning:** While (10.1109/TVCG.2021.3092570, 10.1007/s11263-022-01601-z, 10.1109/ICCV48922.2021.01591) present invariant architectures that can be trained for classification, segmentation or shape retrieval in a supervised fashion (using ground truth labels), we consider the problem of learning a shape representation purely from contour data without any labels. This distinction (see response to Reviewer MfnJ) is essential when it comes to biological data exploration, which is the primary motivation for our work.
**2. Point clouds versus contours:** Processing point clouds (in 2D or 3D) differs from processing contours, defined in our case as ordered sequences of points. Point clouds are in contrast unordered. Using an ordered sequence is critical for us as it allows maintaining a fixed neighborhood structure and straightforwardly reconstructing outlines for visualisation, even when parts of the contour come into close proximity or if the contour self-intersects.
While we believe that a direct comparison with rotation-invariant 2D point networks is not warranted for the reasons above, we do agree that it would be valuable to integrate this discussion in our related work section and will do so in the final version of the paper if accepted.
# Literature on shape descriptor methods
Thank you for pointing us to the line of work explored in (10.1145/571647.571648). Despite its focus on 3D polygonal models and not 2D contours, similar concepts could be potentially applied in our case in future works. We propose to add this reference and discuss it in the “Statistics-based methods” paragraph of our related work section in the final version of the paper.
# Other remarks
* Following your suggestion, we will add new tables with accuracy, precision, and recall for all experiments in the supplementary materials of the final version if accepted. The results provided in our response to Reviewer HCmb already include these additional metrics.
* We will increase the font size to make the legend of Figures 3 and 4 easier to read in the final version if accepted.
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Rebuttal Comment 1.1:
Comment: I very much appreciate significant effort that authors put into rebuttal comments for me and other reviewers. I agree with authors that method shows very strong performance on biological data and might be of potential interest for the community.
However, there are important remaining concerns that prevent me from rising my rating:
- I think that the paper title is too broadly positioned. To me, the current title implies more general method than one being proposed. To me, the proposed method seems to be well-design solution that tackles problem of analysis of simply-connected 2D silhouettes of biological objects (i.e. cells). Current title "ShapeEmbed" implies more general approach for shape quantification and should be compared to more general shape analysis approaches (e.g. PointTransformers, PointNets, DGCNN etc). All of these approaches are inherently applicable to 2D shapes. For example, PointNet (2016 paper) runs experiments on MNIST as well. If comparison to more general methods is not included, I think that the title should be something like "2DShapeEmbed: a self-supervised learning framework for 2D silhouette quantification" to reflect this particular nature of the method. Can authors comment on that?
- Authors addressed my theoretical concern about method being applicable to only simply connected shapes. However, it is not clear whether proposed heuristics are implemented for the current iteration of the method. Can authors clarify whether they are currently used or not?
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Reply to Comment 1.1.1:
Comment: ## The paper title is too broadly positioned and the current title implies a more general method than being proposed
To clarify the scope of our method and taking into account your suggestion, we propose to revise the title to “ShapeEmbed: a self supervised learning framework for 2D contour quantification” in the final version. We consider this modification to be an appropriate consensus that preserves our original method’s name (ShapeEmbed) while clarifying its applicability to 2D contours. We prefer the term “contour” over “silhouette” as the latter is often understood as a “filled contour” (akin to a mask) and our approach really only relies on the points at the border of the object.
## It is unclear whether the proposed heuristics are implemented in the current version of the method
We are not sure if “heuristics” here refer to the pre-processing steps required to extract an ordered sequence of points from self-intersecting object outlines, or to the processing (encoding and decoding) of these ordered sequences of points. As far as the processing is concerned, no heuristics need to be implemented - as long as an object outline is provided as an ordered sequence of points, it can be encoded and decoded successfully with ShapeEmbed regardless of whether it self-intersects or not. As mentioned in our response to reviewer MfnJ, we have observed this on biological imaging data that present such patterns but that we are not currently at liberty to disclose.
If your questions concerns _how_ one can extract ordered sequences of points from masks of self-intersecting objects, this can be achieved for relatively simple datasets relying on classical image processing operations as demonstrated for instance for MNIST in this blog post: https://edwin-de-jong.github.io/blog/mnist-sequence-data/. More refined solutions have been proposed in the context of biological imaging, where complex object (self-)intersections may occur, see for instance https://doi.org/10.1007/978-3-642-15711-0_79. In our codebase, our pre-processing step is a standalone module, that isn’t part of the ShapeEmbed model per se (since the model takes as an input distance matrices, not masks), and that implements a simple contour extraction step relying on classical Python libraries. It can easily be modified or replaced by more refined and dataset-specific operations such as the two examples provided earlier.
In summary, we do not claim that ShapeEmbed solves the problem of extracting ordered sequences of points from outlines _in general_, but can confirm that, provided with outlines described as ordered sequence of points, our method appropriately handles self-intersecting objects. We propose to make this point clearer with an additional sentence in Section 3.1 of the revised manuscript. | Summary: The paper proposes a novel self-supervised framework for shape embedding, which is invariant to translation, scale, and outline pixel-indexing. The learned shape representation is used in a classification task and outperforms all previous works.
## update after rebuttal
My final rating is accept.
Claims And Evidence: N/A
Methods And Evaluation Criteria: N/A
Theoretical Claims: N/A
Experimental Designs Or Analyses: N/A
Supplementary Material: N/A
Relation To Broader Scientific Literature: N/A
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: Strength
1. The proposed method is novel and insightful.
2. The motivation and underlying principles of the proposed method are clearly explained.
3. The experiments are solid and can support the claims of the work.
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 positive comments on the strengths of ShapeEmbed and for your appreciation of the way we describe and evaluate the method. | Summary: This work presents ShapeEmbed, a new approach for representation learning of 2D shapes (represented as contours/outlines). The main desiderata for such a representation are invariance to translation, rotation, scaling, reflection, and indexing.
The key ideas behind the design of this approach build upon using the distance matrix representation of a 2D shape outline as input to a convolutional neural net-based VAE. Distance matrices can be easily made invariant to everything other than indexing (what point we start from when we encode the curve). The main observation is that there is an equivalence between indexing invariance and translation invariance if the distance matrix is treated as an image. To take advantage of this, the authors implement circular padding in all convolution and pooling operations of the ResNet18 encoder, and propose a variety of reconstruction loss functions to achieve indexing invariance and regularize the training.
Comparisons are made against two classical algorithms and the state-of-the-art O2VAE on the MPEG7 and MNIST shape datasets, and on biological datasets MEF and BBBC010, by training logistic regression on top of the learned latent spaces. ShapeEmbed has a clear performance advantage.
** Post-rebuttal update **
After the rebuttal, reviewing the responses and other reviews, I have decided to maintain my initial rating.
Claims And Evidence: The main claims are
1. Superior performance for shape quantification over a range of natural and biological images.
- this is demonstrated well by the strong performance over the recent O2VAE
2. Capturing variability both across and within experimental conditions in biological images
- this is qualitatively shown using a tSNE-based figure and quantitative results in the main text and the supplement
3. Indexing invariance matters and results in significant performance improvements
- Table 4 clearly shows that removing indexing invariance (no circular padding, no indexing invariance loss) significantly reduces performance.
Based on this, I conclude that these claims are supported by clear and convincing evidence. Given that the biological task of dead vs. alive C. elegans, is a bit simple (curved vs straight shapes), the significance might be limited.
Methods And Evaluation Criteria: The chosen classical baselines and SOTA O2VAE make sense. Having two "natural" datasets and two biological datasets is sufficient for showing the general applicability of the approach.
Theoretical Claims: This work does not make theoretical claims, but I thoroughly checked the motivation for how to build out indexing invariance and the equivalence to translation invariance makes sense.
Experimental Designs Or Analyses: The main experimental premise is simple: Four datasets and four methods. Each method, including the proposed one, produces a feature descriptor without using any class labels. Then, a logistic regression classifier is trained on these features following 5-fold cross-validation.
The ablations cover evaluating the effect of index invariance, rotation, and translation and the effect of learning an encoding vs using distance matrices directly.
Supplementary Material: I reviewed the supplementary material in its entirety. It adds helpful detail to the main draft, which is already well written and easy to follow.
Relation To Broader Scientific Literature: The key contribution of the paper is figuring out how to use the distance matrix representation to add additional indexing invariance for encoding 2D shapes represented as contours. The paper empirically shows that adding this indexing invariance makes a positive impact. The main learning-based baseline O2VAE implements invariance less explicitly and has weaker performance.
Essential References Not Discussed: Essential references that should be included are self-supervised computer vision algorithms like MAE, SimCLR, MoCo, DINO etc. These algorithms are also important baselines that are excluded.
Other Strengths And Weaknesses: Strengths:
- The work is well presented, motivated and well executed. The proposed approach has good performance
Weaknesses:
- Significance: the application domain appears to be quite limited. It is not clear why it is important to learn how to encode 2D silhouettes of objects in a self-supervised way, and the impact of driving this innovation forward. The intro can be revised to include this information.
- Significance: there have been significant efforts in self-supervised learning in computer vision through a variety of contrastive learning techniques like MAE, SimCLR, MoCo, DINO etc. These are not discussed at all, and can potentially serve as powerful baselines -- just because they do not target silhouette images does not make them not applicable to this task.
- Empirical evaluation: It would be helpful to include the biological datasets in Table 3 of the supplement to ensure that the VAE encoding makes a significant difference over just the distance matrix.
Other Comments Or Suggestions: The table captions should be revised. For example, Table 1 is described as having biological imaging data, while it shows results on MNIST and MPEG-7
Questions For Authors: My main concerns are with the clear communication of the significance of self-supervised learning of 2D silhouettes and why the prevailing self-supervised learning techniques from computer vision have not been included at all both in the discussion and experiments. The work is well executed, but the lack of reference or comparison to methods like MAE or SimCLR makes my current rating a significantly borderline accept.
If the authors can provide clarification on the significance of investigating self-supervised learning of 2D silhouettes, and why a lot of mainstream computer vision self-supervised learning algorithms are not discussed, I will be more confident in my positive weak accept rating.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: # Significance of investigating self-supervised learning of 2D silhouettes
We refer to our reply to Reviewer MfnJ, where we clarify how we envision the method to be used in biological imaging.
# Comparison with prevailing computer vision self-supervised learning algorithms
We hereafter provide clarifications on how ShapeEmbed compares against a ViT model (MAE) and a contrastive learning framework (SimCLR) trained on binary masks as input (as we did for the other methods we compare against).
* Masked AutoEncoders (MAE). We benchmarked against the 3 “off-the-shelf” MAE ViT (https://github.com/facebookresearch/mae) configurations (“base”, “large”, and “huge”). We resized the masks to 224x224, the input size expected by MAE by default. We used a batch size of 16 (as in the original MAE paper) and 200 epochs (as ShapeEmbed).
* SimCLR. We created a SimCLR model with a ResNet18 backbone with 128 output dimensions relying on the original codebase (https://github.com/sthalles/SimCLR/). We trained for 200 epochs (as ShapeEmbed) using the default configuration and set of transforms to create positive pairs.
## MNIST
|Method|acc|prec|recall|F1|Log loss|
|:-:|:-:|:-:|:-:|:-:|:-:|
|mae_vit_base|0.953±0.003|0.953±0.003|0.952±0.004|0.953±0.026|0.062±0.020|
|mae_vit_large|0.840±0.009|0.841±0.009|0.840±0.009|0.840±0.009|0.520±0.021|
|mae_vit_huge|0.921±0.004|0.919±0.003|0.921±0.004|0.923±0.005|0.369±0.018|
|simCLR_rs18|0.598±0.011|0.594±0.012|0.598±0.011|0.593±0.011|1.188±0.033|
|**ShapeEmbed**|**0.963 ± 0.005**|**0.963 ± 0.005**|**0.963 ± 0.005**|**0.963 ± 0.007**|**0.187 ± 0.020**|
## MPEG-7
|Model|acc|prec|recall|F1 score|Log loss|
|-|:-:|:-:|:-:|:-:|:-:|
|mae_vit_base|0.675±0.024|0.660±0.016|0.675±0.024|0.646±0.001|1.471±0.071|
|mae_vit_large|0.654±0.037|0.637±0.037|0.654±0.037|0.627±0.040|1.465±0.112|
|mae_vit_huge|0.633±0.166|0.615±0.001|0.601±0.045|0.600±0.010|1.767±0.079|
|simCLR_rs18|0.141±0.016|0.145±0.022|0.141±0.016|0.128±0.020|3.502±0.522|
|**ShapeEmbed**|**0.763±0.037**|**0.716±0.002**|**0.763±0.036**| **0.751±0.024**|**1.158±0.206**|
## MEF
|Method|acc|prec|recall|F1|Log loss|
|-|:-:|:-:|:-:|:-:|:-:|
|mae_vit_base|0.537±0.031|0.539±0.030|0.546±0.029|0.537±0.030| 0.895±0.024|
|mae_vit_large|0.535±0.019|0.534±0.020|0.535±0.018|0.532±0.019 |0.885±0.028|
|mae_vit_huge|0.549±0.023|0.552±0.024|0.549±0.023|0.549±0.023| 0.830±0.034|
|simCLR_rs18|0.444±0.0292|0.451±0.032|0.444±0.0292|0.434±0.0316| 1.019±0.0203|
|**ShapeEmbed**|**0.745±0.006**|**0.751±0.006**|**0.745±0.005**|**0.746±0.006**|**0.640±0.016**|
## BBBC010
|Model|acc|prec|recall|F1 score|Log loss|
|-|:-:|:-:|:-:|:-:|:-:|
|mae_vit_base|0.628±0.105|0.633±0.107|0.6285±0.105|0.597±0.119|0.7161±0.156|
|mae_vit_large|0.720±0.580|0.723±0.058|0.721±0.060|0.514±0.072|0.632±0.082|
|mae_vit_huge|0.657±0.081|0.671±0.090|0.657±0.081|0.718±0.059|0.649±0.083|
|simCLR_rs18|0.567±0.115|0.569±0.119|0.567±0.115|0.562±0.117|0.762±0.125|
|**ShapeEmbed**|**0.872±0.015**|**0.866±0.009**|**0.866±0.009**|**0.866±0.008**|**0.509±0.136**|
We hypothesize that the sub-par performance of MAE is due to ViT not being suited to the problem we study: we seek to encode the shape of individual objects in small images coming from small datasets (by ViT standards). We believe that the poor performance of SimCLR is due to the construction of positive pairs, here defined as an image and an augmented version of itself. To achieve rotation, scaling, and positional invariance with SimCLR, we would need to define an alternative way of creating positive pairs of masks that would comprehensively cover all the transformations we normalize for in ShapeEmbed, which is beyond the scope of a direct comparison. We are interested in exploring ways to use a contrastive framework on a distance matrix input in future works, but doing so requires further investigation and is out of scope for this paper.
We did not manage to benchmark against MoCo and DINO in the rebuttal period, but anticipate that we would reach similar conclusions as the challenge of using contrastive learning and ViT models for our task would apply as well.
If accepted, we will add the following results to Tables 1 and 4, and include the discussion in a new section of our supplementary material.
# Other remarks
* Following your suggestion, we will include the new results below on the two biological datasets (BBBC010 and MEFs) in Supplementary Table 3 in the final version if accepted.
Dataset|Distance matrices|||||ShapeEmbed|||||
|-|:-:|:-:|:-:|:-:|:-:|:-:|:-:|:-:|:-:|:-:|
||acc|prec|recall|f1|log|acc|prec|recall|f1|log|
|BBBC010|0.737±0.025|0.737±0.025|0.734±0.026|0.737±0.026|2.889±0.686|**0.872±0.015**|**0.866±0.009**|**0.866±0.009**|**0.866±0.008**|**0.509±0.136**|
|MEF|0.343±0.007|0.452±0.024|0.343±0.007|0.299±0.006|1.202±0.066|**0.745±0.006**|**0.751±0.006**|**0.745±0.005**|**0.746±0.006**|**0.640±0.016**|
* Thanks for flagging the typo in the caption of Table 1, we will revise it in the final version.
---
Rebuttal Comment 1.1:
Comment: Thank you for the effort in performing these additional comparisons, I believe they will be a valuable addition to this paper. | null | null | null | null | null | null |
Subgroups Matter for Robust Bias Mitigation | Accept (poster) | Summary: This paper studies how the definition of subgroups affects the efficacy of bias mitigation techniques for spurious correlations. A causal graph approach is introduced to formalize correlations between classes, attributes, and subgroups, which are then manipulated to study AUC with respect to an ERM baseline on two semi-synthetic image datasets. The results show that subgroups have a large impact on bias mitigation, including leading to worse outcomes than ERM, and that increasing granularity has no significant effect on performance. Finally, the paper proposes the distance from an unbiased distribution achieved by resampling as an effective generalization measure.
## Update after rebuttal
Although I initially recommended rejection, the authors provided a very detailed and comprehensive rebuttal which addressed all of my critiques. Most importantly, the paper is substantially improved with the addition of more challenging datasets across a variety of domains, as well as a reduction in theoretical overclaims and situation of the theory within established generalization results. Therefore, I now recommend a weak accept.
Claims And Evidence: Overall, the presented evidence supports the paper’s empirical claims on the two datasets studied. My main concerns are a limited scope of evaluation (discussed in Methods and Evaluation Criteria) and overclaimed theoretical results (discussed in Theoretical Claims).
Methods And Evaluation Criteria: 1. My main concern regarding evaluation is the lack of challenging datasets across a variety of evaluation domains. This paper focuses on semi-synthetic versions of the MNIST and CheXPert datasets. The simplicity of MNIST lends itself to more of a sanity check than a benchmark. Moreover, while CheXPert is a good real-world dataset, the paper downsamples it to only 2330 training images (originally 200K+). Overall, the evaluation in this paper is below the standard in spurious correlations literature of at least 3-4 datasets across both vision and language tasks (e.g., [2, 3, 4, 7]), making it difficult to assess the generality of its conclusions.
2. This paper provides results on resampling, but does not mention the downsampling method (wherein data from larger groups is removed prior to training) proposed by [1] (cited by the authors). Downsampling is often superior to resampling, as resampling WGA may collapse over training [1, 5, 6]. In particular, it’s not clear whether the poor performance of resampling in Figure 2 is due to group definitions or the suboptimality of resampling as a technique.
[1] Idrissi et al. Simple data balancing achieves competitive worst-group-accuracy. CLeaR 2022.
[2] Izmailov et al. On Feature Learning in the Presence of Spurious Correlations. NeurIPS 2022.
[3] Kirichenko et al. Last Layer Re-Training is Sufficient for Robustness to Spurious Correlations. ICLR 2023.
[4] Koh et al. WILDS: A Benchmark of in-the-Wild Distribution Shifts. ICML 2021.
[5] LaBonte et al. The Group Robustness is in the Details: Revisiting Finetuning under Spurious Correlations. NeurIPS 2024.
[6] Stromberg et al. Robustness to Subpopulation Shift with Domain Label Noise via Regularized Annotation of Domains. TMLR 2024.
[7] Zhou et al. Examining and Combating Spurious Features under Distribution Shift. ICML 2021.
Theoretical Claims: 1. The statement from the introduction that this paper “[provides] a theoretical explanation for the differences observed based on the minimum distance between the group-weighted biased distribution and the unbiased test distribution” is overclaimed. While Pearson coefficients are provided, no theoretical result is proven which connects the proposed distance metric to model performance (i.e., a generalization bound).
2. The proposed distance metric is insufficiently justified independently of [1]. It makes intuitive sense -- the lower the distance metric, the better the “optimal” resampling will be. However, the distance from the resampling distribution to $\mathcal{P}_{unbiased}$ is chosen to be the mean absolute error without justification. Why not mean squared error, the absolute or squared error on the worst group only, or a probability divergence such as KL divergence?
[1] Zhou et al. Examining and Combating Spurious Features under Distribution Shift. ICML 2021.
Experimental Designs Or Analyses: The experimental design, particularly with respect to the subgroup generation step, is clearly explained and well-justified. The additional specifications and results in the Appendix are welcomed.
Supplementary Material: No supplementary material is provided.
Relation To Broader Scientific Literature: Multiple other works have proposed rethinking the definitions of spurious correlations (e.g., [5]) as well as the definitions of subgroups [2, 3]. However, to my knowledge this is the only paper to evaluate subgroup definitions in the context of the causal learning literature (e.g., [1, 4]).
[1] Jones et al. Rethinking fair representation learning for performance-sensitive tasks. ICLR 2025.
[2] Kim et al. Improving Robustness to Multiple Spurious Correlations by Multi-Objective Optimization. ICML 2024.
[3] Li et al. A Whac-A-Mole Dilemma: Shortcuts Come in Multiples Where Mitigating One Amplifies Others. CVPR 2023.
[4] Schrouff et al. Mind the graph when balancing data for fairness or robustness. NeurIPS 2024.
[5] Yang et al. Change is Hard: A Closer Look at Subpopulation Shift. ICML 2023.
Essential References Not Discussed: 1. Figure 3 of this paper studies performance of gDRO and resampling under noise in subgroup labels. A recent paper which should be discussed in this section is [3], which provides evidence of degradation of the WGA of resampling (called upweighting by [3]) under noise in the subgroup labels (called domain labels by [3]). Overall, the novelty of the experiments in Figure 3 is somewhat limited in comparison to [3].
2. It would also be beneficial to discuss references which study definitions of subgroups across spurious features. For example, [1] examine a dataset with multiple spurious correlations and show that defining subgroups with respect to bias type (e.g., age or gender) has a large impact on robustness method performance. Moreover, both [1] and [2] show that mitigating spurious correlation with respect to one subgroup definition may actually exacerbate bias with respect to a different definition.
[1] Kim et al. Improving Robustness to Multiple Spurious Correlations by Multi-Objective Optimization. ICML 2024.
[2] Li et al. A Whac-A-Mole Dilemma: Shortcuts Come in Multiples Where Mitigating One Amplifies Others. CVPR 2023.
[3] Stromberg et al. Robustness to Subpopulation Shift with Domain Label Noise via Regularized Annotation of Domains. TMLR 2024.
Other Strengths And Weaknesses: One strength of the paper is its comprehensiveness in investigating as many as 15 different types of subpopulation groupings. The granularity and random groupings are particularly interesting.
One weakness (as noted by the authors in the Limitations section) is that the paper focuses on the influence of subgroup definition within bias mitigation methods that utilize group annotations, which is a somewhat unrealistic setting. Nevertheless, since understanding methods that utilize group annotations is likely a prerequisite for understanding methods that infer subgroups, the study is still worthwhile.
Other Comments Or Suggestions: I have a minor issue with the paper’s assertion that “approaches [which do not utilize group annotations] often fail to consistently outperform traditional subgroup-based methods and are not
widely adopted” (line 121-122). The references cited in this paragraph are somewhat outdated, and the statement minimizes the progress made by more recent methods. For example, [1, 5, 9] are competitive with gDRO [8] and [4, 7] are competitive with DFR [2]. As far as adoption of such methods, at least [6] (cited in this paper) is considered widely adopted, though nowadays far from state-of-the-art.
Regarding the granularity discussion in Section 5.2, an interesting case study may be the CivilComments dataset [3]. There are two versions of this dataset in the literature: one with four groups, where the identity categories (male, female, LGBT, black, white, Christian, Muslim, or other religion) are collapsed into a single spurious feature, and one which uses the un-collapsed identity categories. It would be interesting to see if the granularity findings hold across these two versions of CivilComments, and whether results in the literature are consistent.
Below, I’ve included a list of typos or sentences where more clarification is needed. Also, the plots are pixelated and sometimes hard to read; it would be helpful to increase the DPI.
1. Line 88: Subgroup typo.
2. Line 135: $\mathbb{E}\_P$ should be $\mathbb{E}_{\mathcal{P}}$?
3. Equation 2: $\mathcal{G}$ is not defined; I assume it is the set of groups.
4. Equation 3: The average over $m$ is meaningless here as one is already taking the expectation over $\mathcal{P}_{train}$; the index $i$ is unused within the sum.
5. Equation 3: $P_{train_G}$ should be $P_{train_g}$?
6. Lines 205-206: =0 and =1 should be in math mode.
7. Section 5.3 and 5.5: \mid should be used for conditional probabilities.
[1] Han et al. Improving Group Robustness on Spurious Correlation Requires Preciser Group Inference. ICML 2024.
[2] Kirichenko et al. Last Layer Re-Training is Sufficient for Robustness to Spurious Correlations. ICLR 2023.
[3] Koh et al. WILDS: A Benchmark of in-the-Wild Distribution Shifts. ICML 2021.
[4] LaBonte et al. Towards Last-layer Retraining for Group Robustness with Fewer Annotations. NeurIPS 2023.
[5] Liu et al. Avoiding spurious correlations via logit correction. ICLR 2023.
[6] Liu et al. Just train twice: Improving group robustness without training group information. ICML 2021.
[7] Qiu et al. Simple and Fast Group Robustness by Automatic Feature Reweighting. ICML 2023.
[8] Sagawa et al. Distributionally Robust Neural Networks for Group Shifts: On the Importance of Regularization for Worst-Case Generalization. ICLR 2020.
[9] Zhang et al. Correct-N-Contrast: A Contrastive Approach for Improving Robustness to Spurious Correlations. ICML 2022.
Questions For Authors: As mentioned in the “Theoretical Claims” section, why was mean absolute error chosen for the minimum distance metric instead of mean squared error, a worst-group metric, or KL divergence?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank the reviewer for their thoughtful and comprehensive review. We agree with the comments and feel they have helped us substantially improve the paper. We have made clarifications to the manuscript and run >200 additional experiments. We include details of our changes below and share all results in this [folder](https://rb.gy/xebqmp). We hope this will give the reviewer confidence to raise their score.
**1. Lack of challenging datasets across domains**
We agree that expanding the scope of evaluation would strengthen the results. To address this, **we have expanded our evaluation to include two additional datasets**: civil_comments (text), and CelebA (natural images). Encouragingly, these datasets show consistent trends and help to bolster the generalisability of our conclusions. Please see details on the updated setup in Tab A3 and key results in Figs 2 and 5.
**2. Downsampling** is often superior to resampling. Is resampling’s poor performance due to group definitions or its suboptimality?
We should clarify we do not think the takeaway should be that resampling performs poorly, but that it performs *variably* depending on the subgroups used. In Fig 2, we observe that it performs quite well for some subgroups (e.g. it increases AUC by >0.10 relative to ERM on MNIST with $YAS$ groups and by >0.04 on CXP with $AY_8$ groups).
However, we agree that given the literature it would be interesting to see whether similar results hold for downsampling. **We implement downsampling** as described in [1] and find that results are closely aligned for CXP, CelebA, and civil_comments (Fig C2). Downsampling actually underperforms on MNIST, so we maintain resampling for its consistency.
**3. Granularity findings across two versions of civil_comments**
We agree this would be a very interesting case study. As we were unable to find this in the literature, we did this experiment by splitting the attribute $A$ (any mention of gender) into two more subgroups (mentions male/does not) and likewise for $S$ (religion) into Christian/non-Christian. We found that performance was very similar across the granular and coarse groupings, in line with our results on synthetic granular groups (Fig 3). We are grateful for this suggestion and think this is a nice real-world and practical insight to strengthen our paper.
**4. Downsampling CheXPert dataset**
This is a fair point, however, we note that pacemaker annotations are only available for 4862 images, and we have to further downsample the dataset to make it balanced with respect to disease ($Y$) and sex ($S$). Despite the size, we found that by starting with a pre-trained model we were able to get good convergence behaviour.
In addition, we modified our setup to use the full 60k MNIST images, and, to better understand scaling behaviour with respect to dataset size, we compared the performance of the model trained on the full dataset to the one trained on the downsampled 6k variant. As expected, models trained on the larger variant performed better on average, however trends across subgroups were very similar (Figs D2,3). We thus believe our results are not an artifact of the small dataset size on CheXPert (further supported by our observation of the same trends on CelebA and civil_comments).
**5. Overclaimed theoretical section**
We have reworded the appropriate sections (please see reply 1 to Reviewer mP4g).
**6. Choice of distance metric**
After further consideration we changed the metric to KL divergence. We still see a strong correlation between the divergence of the weighted biased distribution to the target distribution and unbiased generalisation (Fig 5). We note that KL divergence and MAE produce quite similar results, in particular in subgroup ordering (Tab 2).
**7. Limited novelty of Fig 3 in comparison to [2]**
We acknowledge those experiments share similarities with [2], and we appreciate how their findings align with ours, reinforcing both conclusions. We now mention [2] in our manuscript. However, our evaluations differ in scope, as we consider a broader set of methods, including GroupDRO, CFair, and DomainInd, and focus on full fine-tuning rather than last-layer retraining.
**8. Discuss references which study definitions of subgroups across spurious features**
We appreciate this suggestion and have added a discussion about this type of study in our related work. Their findings complement ours by exploring how subgroup choice impacts mitigation in a setting where there are multiple SCs, while we focus on a simpler setting where there is only one SC but multiple additional variables (e.g. possible mitigation targets).
**9. Minor issue with the paper’s assertion l.121**
We have adjusted our statement accordingly and incorporated more citations. We further elaborate in response 2 to Reviewer 86pJ.
**10. Minor edits**
We thank the reviewer for noting these and have edited the manuscript.
[1]Idrissi et al, CLeaR (2022)
[2]Stromberg et al, TMLR (2024)
---
Rebuttal Comment 1.1:
Comment: Thank you for the very detailed response. I greatly appreciate the substantial effort you put into running 200+ experiments in a short rebuttal timeframe. I found the additional experiments interesting, especially the CivilComments/CelebA and downsampling experiments, and their inclusion significantly improves the submission.
I apologize for the lack of clarity on where the granular/coarse versions of CivilComments may be found in the literature. The version with four groups is used by, e.g., [1, 4], while the version with many groups is used by, e.g., [3, 5]. (They are the same dataset, from the WILDS benchmark [2], but one version collapses the identity categories). Nevertheless, your version is also a nice experiment.
Based on the new empirical evidence, I have raised my score. I am prevented from raising it higher due to my outstanding concerns about the theoretical claims (though I appreciate the rewording of the theoretical overclaims and additional KL divergence experiments). Specifically, as mentioned in my review, the results are weakened by the lack of theoretical connection between the proposed metric and model performance, and the choice of distance (i.e., MAE vs KL) is insufficiently justified.
[1] Kirichenko et al. Last layer re-training is sufficient for robustness to spurious correlations. ICLR 2023.
[2] Koh et al. WILDS: A benchmark of in-the-wild distribution shifts. ICML 2021.
[3] Liu et al. Just train twice: Improving group robustness without training group information. ICML 2021.
[4] Sagawa et al. Distributionally robust neural networks for group shifts: On the importance of regularization for worst-case generalization. ICLR 2020.
[5] Zhang et al. Correct-n-contrast: A contrastive approach for improving robustness to spurious correlations. ICML 2022.
---
Reply to Comment 1.1.1:
Comment: We thank the reviewer for raising their score and for recognising that the extra experiments have significantly improved the submission. We apologise for not further elaborating on the theoretical sections and our choice of distance metric in the initial rebuttal, this was due to the strict character limit for the rebuttal.
Below, we provide additional clarifications on our choice of KL divergence along with some intuition on the theoretical connections between our metric and model performance. In light of these additional explanations, we hope the reviewer would consider further raising their score.
**1. Choice of distance metric**
We eventually chose the KL divergence to quantify the difference between the weighted biased training distributions and the target test distribution because it is more consistent with the literature. We noted similar uses of the KL divergence to compare train and test distributions in many recent works such as [1,2,3,5,6]. This allows our findings to be more easily compared to and extended to other settings, in contrast to our initial metric, MAE. We calculate it by comparing train and test discrete probability distributions of the 8 events corresponding to sampling each $(Y,A,S)$ combination.
**2. Theoretical connection between proposed metric and model performance**
While we agree that a complete proof explaining why the divergence between the weighted training distribution and the test distribution is correlated with test performance would be nice to have, we think this is out of scope for our current work. However, we would encourage future research to further explore this direction. In the meantime, **we provide additional intuition for this connection by framing our findings within established results in generalisation**.
There is a broad consensus that “train/test distribution matching” through methods like data balancing can improve test set generalisation when the train and test distributions are not independent and identically distributed [4,7,9]. For example, a well known result by Ben David et al. [8] shows that for a model $h$ where the labelling function is the same across both source and target distributions:
$$\mathcal{L_{test}}(h) \le \mathcal{L_{train}}(h) + D(\mathcal{P_{train}},\mathcal{P_{test}})$$
where $D(\cdot,\cdot)$ represents the total variation divergence (TV).
In our case, Pinsker’s inequality gives us $TV(\mathcal{P},\mathcal{Q}) \le \sqrt{\frac{1}{2}*KL(\mathcal{P} \parallel \mathcal{Q})}$. Since our labelling function does not change across distributions, we can show that the test error is upper bounded by:
$$\mathcal{L_{unbiased}}(h) \le \mathcal{L_{train}}(h) + \sqrt{0.5*KL(\mathcal{P_{train}} \parallel \mathcal{P_{unbiased}})}$$
We also note that in practice, since all our models reach a similar train error close to 0, the differences in upper bound are largely driven by the divergence between both distributions. In our setting we assume that the divergence between both distributions is attributable to differences in probabilities of sampling each $(Y,A,S)$ subgroup. This aligns with our findings showing that by reweighting the training distribution (through gDRO or resampling) and thus reducing the divergence to the test distribution, a lower generalisation error can be achieved.
We further note other papers which similarly give expected generalisation error upper [2,3,5,6] and lower bounds [3] involving the KL divergence between training and test distributions. However, directly estimating generalisation under distribution shift is a difficult task which requires very strong assumptions [10].
We believe that framing our findings within this theoretical line of work gives important context and further supports our observation that decreased KL divergence between the weighted training distribution and the test distribution results in improved unbiased generalisation. **We have incorporated this discussion into Section 5.3 of our paper.**
[1] He et al., Information theoretic generalisation bounds for DNNs. InfoCog @ NeurIPS (2024)
[2] Aminian et al., Learning algorithm generalization error bounds via auxiliary distributions. IEEE (2024).
[3] Masiha et al., Learning under distribution mismatch and model misspecification. ISIT (2021).
[4] Mansour et al., Domain adaptation: learning bounds and algorithms. COLT (2009).
[5] Wu et al., On the Generalization for Transfer Learning: An Information-Theoretic Analysis. IEEE (2024).
[6] Nguyen et al., KL guided domain adaptation. ICLR (2022).
[7] Dong et al., How Does Distribution Matching Help Domain Generalization: An Information-theoretic Analysis. IEEE (2024).
[8] Ben-David et al., A theory of learning from different domains. Machine Learning (2010).
[9] Wang et al., Causal balancing for domain generalization. ICLR (2023).
[10] Estimating generalization under distribution shifts via domain-invariant representations. ICML (2020). | Summary: The authors investigate the impact of group definitions on the performance of bias mitigation methods using semi-synthetic experiments on binary classification of images. Specifically, the authors introduce a spurious correlation into the training datasets by selecting examples based on two attributes and a label and then apply subgroup-based bias mitigation methods (gDRO, resampling, DomainInd, and CFair) using different subgroup definitions. Their evaluation reveals that subgroup definitions play a crucial role in model performance: the subgroup should capture the spurious correlation in the data to perform well. The authors quantify this finding using the minimum distance metric evaluated between the train dataset divided by subgroups and the unbiased test dataset. This metric seems to correlate well with bias mitigation performance, potentially revealing theoretical mechanisms behind the impact of subgroup definitions.
## update after rebuttal
The authors addressed all my questions. I will keep my evaluation.
Claims And Evidence: I mostly have comments on positioning and writing.
1. Observing the correlation between the minimum distance metric and performance does not constitute a theoretical analysis. I think this finding should be positioned as a potential mechanism or explanation.
2. I think the paper should more clearly state that it focuses on the worst group accuracy and does not consider different wide-spread fairness criteria (e.g., demographic parity or equalized odds) and methods that enforce fairness constraints.
3. Additionally, while the authors acknowledge that they focus on spurious correlations in Section 5.6, I believe the paper should also clearly state that it only analyzes one specific model of spurious correlation.
Methods And Evaluation Criteria: The datasets and models seem reasonable. However, evaluating models on the dataset with "reversed" spurious correlation could be interesting: it would show whether the models leaned generalizable correlations or simply balanced accuracy across groups.
Theoretical Claims: I have briefly looked at calculations in Appendix A.6.
Experimental Designs Or Analyses: I think the chosen bias mitigation methods (gDRO, resampling, DomainInd, and CFair) are reasonable. Many more recent modifications to these methods exist. However, the analysis of more established versions may be suitable for the exploratory study.
Supplementary Material: I looked at Appendices A.1, A.2, and A.5 in detail and briefly looked at the rest of the supplementary material.
Relation To Broader Scientific Literature: The paper investigates an important question for group-based bias mitigation methods. These methods are fairly popular in the literature on fairness, robustness, and OOD generalization.
Essential References Not Discussed: I do not have additional suggestions for the references.
Other Strengths And Weaknesses: The paper is well-written, the findings seem original.
Other Comments Or Suggestions: I do not have any suggestions.
Questions For Authors: 1. How do you explain the success of subgroups based on $A$ paired with model-based methods (given that these subgroups perform poorly with reweighting-based methods)?
2. Could you argue why the results for your model of spurious transfer to more sophisticated scenarios?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We thank the reviewer for their insightful comments, and we are glad to hear they appreciate the paper and the originality of our findings. We respond to the comments raised in the review below, and refer to additional results, which are all presented in this [folder](https://drive.google.com/drive/folders/1N5Fpf8VK41awBIYireIoaAjQES_i8xtV?usp=sharing).
**1. Observing the correlation between the minimum distance metric and performance should be positioned as a potential mechanism**
We agree with the reviewer’s comment and have changed the wording of this in the relevant sections, for instance in the introduction: “We provide a potential explanation for the differences observed based on the KL divergence between the optimal group-weighted biased distribution and the unbiased test distribution.”
**2. Evaluating models on the dataset with "reversed" spurious correlation** could be interesting
We are grateful for this suggestion, and performed the suggested evaluation to further probe the generalisation abilities of our different models. We find that for most datasets, bias mitigation methods, and subgroups, the performance suffers a small decrease on the dataset where the SC is “reversed” compared to the balanced unbiased test dataset (average of $-0.01$), as shown in Tab D1. We also see very similar trends across subgroups to the unbiased test dataset, as shown in Fig D1.
**3. How do you explain the success of subgroups based on $A$ paired with model-based methods** (given that these subgroups perform poorly with reweighting-based methods)?
We thank the reviewer for this question and agree that it is an important point to discuss. We touched on this briefly in the main text (“For model- based methods, a similar pattern is evident, with the added requirement that the subgroups contain both positive and negative classes”), but agree that this point deserves a more thorough and clear explanation.
We came to the conclusion that to “map” a subgrouping from a reweighting-based method to a model-based method, the $Y$ component should be removed (e.g. each subgroup should contain both positive and negative classes). This is because methods like DomainInd and CFair learn representations for each subgroup separately. DomainInd trains a separate classifier for each subgroup, so it would not make sense to train a separate classification head for positive and negative classes. Similarly, CFair seeks to align subgroup representations, so it would not make sense to align representations of one subgroup containing only positive images to another subgroup containing only negative images, as this would defeat the point of training a discriminative classifier. On the other hand, for data-reweighting based methods, including the $Y$ in the subgroups helps to balance the final reweighted dataset with respect to class, and therefore improves results, especially in our case where the spurious correlation involves the class $Y$.
This explains why we find that the subgroups which work well for DomainInd and CFair (e.g. $A$) are just a merged version of the ones which work well for gDRO and resampling (e.g. $AY$). To the best of our knowledge, **no papers have explicitly discussed this distinction despite its practical importance**. We have now elaborated on this in the main body of the paper and included a full discussion in the Appendix.
**4. The paper should more clearly state that it focuses on worst group accuracy** and does not consider different wide-spread fairness criteria and methods that enforce fairness constraints
We agree that this is an important point and have modified the manuscript to state this more clearly. In addition to the original sentence in the problem setup section “we frame the task according to the fairness paradigm described in Jones et al. (2025), whereby the objective is to generalise from a biased training distribution to an unbiased testing distribution”, we have added an extra sentence in the experimental setup to explicitly state that we are evaluating models based on overall performance on the unbiased dataset and worst-group performance. We selected these measures for their directness and simplicity compared to other fairness criteria.
**5. The paper should clearly state that it only analyzes one specific model of spurious correlation**
We have clarified this in the problem setup section.
**6. Could you argue why the results for your model of spurious transfer to more sophisticated scenarios?**
We believe the reviewer is asking if our results transfer to more complex datasets/tasks. We think that in more sophisticated scenarios there may be more complex SCs and causes for bias, so trends may vary on *which* specific subgroup is best, but we think our key point, that **subgroup definition impacts mitigation effectiveness**, holds across scenarios.
We hope we have addressed the reviewer’s questions, but please let us know if there are additional points we could further clarify.
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Rebuttal Comment 1.1:
Comment: Thanks for the response!
I will keep my score due to my internal evaluation of the significance of the findings.
---
Reply to Comment 1.1.1:
Comment: We thank the reviewer for their quick reply! | Summary: The paper investigates how subgroup definition impacts the effectiveness of bias mitigation methods in machine learning, hypothesizing that inconsistent success stems from this often-overlooked factor. Through experiments on semi-synthetic image classification tasks with varied subgroup definitions (coarse, fine-grained, intersectional, and noisy), the authors show that subgroup choice significantly influences outcomes, sometimes worsening fairness. Theoretical analysis reveals that the best subgrouping for bias mitigation is not always the one directly aligned with fairness objectives. Key contributions include introducing a novel setting with spurious correlations, demonstrating subgroup-dependent performance patterns, and providing theoretical insights into optimal grouping strategies, challenging conventional fairness assumptions.
## update after rebuttal
I believe the authors have put significant effort into the rebuttal, providing many new figures and tables in their shared folder. If these are integrated into the final camera-ready version, I believe the paper will be above the acceptance threshold and will make a strong contribution with meaningful results to the field. Therefore, I have raised my score accordingly.
Claims And Evidence: 1. **Overlap between first and fourth key contributions**: The claim that subgroup choice impacts disparities (first contribution) appears closely related to the finding that the best way to achieve fairness for a subgroup is not necessarily using it in bias mitigation (fourth contribution). Since both findings seem to be discussed in Section 5.4, the distinction between them is unclear. The authors should clarify how these two contributions differ or consolidate them if they are essentially the same.
2. **Empirical support for optimal grouping strategies (second contribution)**: While the authors suggest an optimal grouping strategy (A, Y, S), their evidence is primarily based on Colored MNIST, a synthetic dataset. This raises concerns about generalizability to real-world settings. More experiments on diverse datasets would strengthen the claim.
3. **Theoretical explanation (third contribution)**: The theoretical analysis is currently relegated to the appendix without clear integration into the main text. A more structured discussion in the main sections, with problem formulation and intuition, would improve clarity and support the claim more convincingly. Better section organization in A.5. and A.6. would also make the theoretical insights more accessible.
Overall, while the findings are interesting, clarifying overlapping claims, expanding empirical validation, and improving theoretical discussion would strengthen the paper’s contributions.
Methods And Evaluation Criteria: The proposed evaluation framework is well-structured and relevant for analyzing the impact of subgroup choice on bias mitigation. The subgroup generation strategy is comprehensive, covering various realistic scenarios, including noisy annotations, coarse vs. fine-grained groupings, and intersectional subgroups. The use of Colored MNIST (synthetic) and CXP (real-world chest X-ray dataset) ensures both controlled and practical evaluations. However, some areas could be improved:
1. Evaluation Metrics: While AUC is a valid metric, it is not widely used in this literature. Including Worst-Group Accuracy (WGA) would provide better insights, making results more comparable to prior work.
2. Baseline Comparisons: The paper lacks comparisons with key existing methods, such as Whac-a-Mole (which accounts for both known and unknown spurious correlations) and approaches like DFR (Kirichenko et al.), AFR (Qiu et al.), EVaLS (Ghaznavi et al.), and SELF (LaBonte et al.). Many of these do not rely on group labels for debiasing or model selection, making them highly relevant benchmarks. Their inclusion would clarify the relative effectiveness of subgroup selection in bias mitigation.
3. Generalizability & Real-World Validation: While the paper includes a real-world dataset (CXP), additional benchmarks from other domains would strengthen the findings. This is particularly important given the reliance on Colored MNIST for some subgrouping insights, which may not always translate to real-world settings.
Overall, the methodology is well-motivated, but incorporating WGA, broader baselines, and additional real-world benchmarks would enhance the study’s impact and comparability.
Theoretical Claims: Yes I have checked the theoretical claims and proofs but it was not so easy to follow and understand for me.
Experimental Designs Or Analyses: Yes, the experimental design and analyses are generally valid. The subgroup generation strategy is comprehensive, and the evaluation setup is well-structured. Theoretical insights align with empirical findings, supporting the study’s conclusions. However, adding key baselines and alternative metrics like Worst-Group Accuracy (WGA) would further enhance validity.
Supplementary Material: Yes all of the parts.
Relation To Broader Scientific Literature: The paper builds on existing work in fairness and bias mitigation by challenging the assumption that the best way to improve fairness for a specific subgroup is to use that subgroup in mitigation. This aligns with prior findings in Whac-a-Mole (Sagawa et al.), which showed that bias mitigation can shift bias rather than eliminate it. It also relates to DFR (Kirichenko et al.), AFR (Qiu et al.), and SELF (LaBonte et al.), which explore debiasing without explicit group labels, suggesting alternative ways to approach fairness. Additionally, the paper’s theoretical analysis on subgroup weighting connects to prior work like EVaLS (Ghaznavi et al.), which examines model selection in biased settings. By emphasizing subgroup choice, the paper provides a novel perspective on why bias mitigation often fails, complementing and extending these prior studies.
Essential References Not Discussed: Yes, several relevant works are missing that would provide important context for the paper’s key contributions:
1. Whac-a-Mole (Sagawa et al.) – This work examines spurious correlations and the unintended consequences of bias mitigation, particularly in cases where debiasing one issue exacerbates another. It directly relates to the paper’s argument that subgroup choice can lead to worse outcomes.
2. DFR (Kirichenko et al.), AFR (Qiu et al.), EVaLS (Ghaznavi et al.), and SELF (LaBonte et al.) – These methods focus on fairness interventions that do not rely on explicit subgroup labels for debiasing or model selection. Since the paper critiques subgroup definition as a bottleneck, these works provide alternative solutions that should be acknowledged.
Citing and discussing these works would provide a more comprehensive view of the challenges in bias mitigation and situate the paper’s findings within the broader literature.
Other Strengths And Weaknesses: One of the key strengths of the paper is its novel approach to identifying optimal subgroups for bias mitigation, as well as its thorough benchmarking across various subgroup combinations. This is a meaningful contribution that can help guide future work on improving fairness in machine learning models. The systematic evaluation and detailed subgroup generation strategy are well-executed, providing valuable insights into how subgroup choices can affect model performance.
However, the paper could benefit from more evidence or case studies demonstrating how this optimal subgroup identification can be applied in a real-world pipeline. While the theoretical analysis and experimental results are strong, additional practical examples or a clearer link to real-world applications would further solidify the significance and applicability of the approach.
Other Comments Or Suggestions: L222 “drops the on unbiased test set” → “drops on the unbiased test set”
Questions For Authors: 1. Clarity of First Key Contribution: Could you please clarify the distinction between the first and fourth key contributions?
2. Empirical Results for Optimal Grouping Strategies: Can you provide more empirical results or case studies demonstrating how the optimal subgroup strategies perform in real-world datasets, beyond the synthetic or semi-synthetic examples (e.g., coloured MNIST)?
3. Theoretical Insights: The theoretical discussion in the appendix feels somewhat disconnected from the main text. Could you summarize the key theoretical insights more explicitly in the main body of the paper to help readers better understand the underlying mechanics of your findings?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank the reviewer for their detailed review and helpful suggestions. We summarise the >200 supplementary experiments and edits we have made to address them below. All extra results are shared in this [folder](https://rb.gy/xebqmp). We hope this will give the reviewer confidence to raise their score.
**1. More experiments on diverse datasets** and additional practical examples or a clearer link to real-world applications would further solidify the significance
We agree with the reviewer's suggestion and have **expanded our analysis to two more datasets** with different modalities and complexity: civil_comments (text) and CelebA (natural images). We find that results closely align across the four datasets. They show similar patterns on the impact of subgroups on mitigation effectiveness with performance strongly correlating to the ability to restore the unbiased distribution. Please see details on the updated setup in Tab A3 and key results in Figs 2 and 5. We believe this strengthens the papers’ claims.
We have clarified the link to real-world applications by further discussing practical examples like differences in the proportion of chest drains causing sex disparities and by including real results on the effect of granularity of subgroups in civil_comments as discussed in response 9 to Reviewer 6xGC.
**2. Lacks comparisons** with key existing methods, many of these do not rely on group labels
We thank the reviewer for their comment and relevant references. We have added them to our related work section, and have in particular expanded our discussion on methods which do not require subgroup labels as they do provide important context for our work.
For our experiments, we focus on a select few established and simple methods as a foundation since many newer approaches (like DFR or AFR) share core principles with resampling and GroupDRO. A recent benchmark also showed no significant performance differences between mitigation techniques [1].
We initially restricted our experiments to methods with subgroup labels because (a) it is important to understand how subgroups affect mitigation as even methods which do not rely on labels often infer these subgroups (as Reviewer 6xGC noted), and (b) many methods which do not require subgroup labels often actually require some labels on the validation data (e.g. for hyperparameter selection), as discussed in [2], and hence subgroup definition remains an important question, and finally (c), methods with labels are often the upper bound [3-5], though recent exceptions exist [6,7].
However, we do agree they could provide an interesting comparison, and so conducted additional experiments on Just Train Twice (JTT) [8], which does not use subgroup labels for training (but requires some for model selection). As shown in Fig C1 and Tab C1, we find that with validation subgroup labels to guide model and hyperparameter selection JTT performs mostly on par with our other methods, however, **performance is again highly dependent on the choice of subgroups**. When no subgroup annotations are used (i.e. model selection is done by overall validation accuracy), the method does not improve over ERM (except for on MNIST where JTT works remarkably effectively, most likely due to the simplicity of the task). We have devoted a new section in our Appendix to these results.
**3. Overlap between first and fourth key contributions**
The second contribution demonstrates broadly how subgroup choice impacts mitigation effectiveness, while the fourth contribution highlights a specific counterintuitive finding: that achieving fairness between two particular groups may require using different groups for mitigation rather than those groups themselves. We've clarified this distinction in the manuscript, as we believe this specific insight represents an important and non-obvious result.
**4. Structure of theoretical section**
We thank the reviewer for their comment and have modified the manuscript to improve the clarity of this section by including key intuition, examples, and restructuring A5 and A6. We believe this should significantly help readers better understand the mechanics of our findings.
**5. While AUC is a valid metric, it is not widely used in this literature**. Including WGA would provide better insights
We include WGA in Tables 2 and 4. For the other results, we use overall AUC for consistency with [1]. Moreover, since we frame the objective as generalisation to an unbiased test set (as in [9]), overall AUC is a useful measure of generalisation performance. AUC is also threshold-independent, which helps give confidence that our results are not simply a side-effect of poor/biased threshold selection.
[1]Zong et al, ICLR (2023)
[2]Pezeshki et al, ICML (2024)
[3]Taghanaki et al, NeurIPS (2022)
[4]Bayasi et al, MICCAI (2024)
[5]Han et al, ICML (2024)
[6]Liu et al, ICLR (2023)
[7]Pezeshki et al, NeurIPS (2021)
[8]Liu et al, ICML (2021)
[9]Jones et al, ICLR (2025)
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Rebuttal Comment 1.1:
Comment: I would like to thank and congratulate authors for their amazing efforts on the rebuttal. I have adjusted my score accordingly. All the best.
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Reply to Comment 1.1.1:
Comment: We thank the reviewer for their very prompt reply and are happy to hear we have addressed their concerns! | null | null | null | null | null | null | null | null |
Correlation Clustering Beyond the Pivot Algorithm | Accept (poster) | Summary: The paper studied a variant of the pivot algorithm for correlation clustering and gave a dynamic implementation with polylog(n) update time and 2.997 approximation. Correlation clustering is a classical problem in TCS and machine learning. Here, we are given a labeled complete graph $G=(V, E^+ \cup E^-)$, and the goal is to partition the vertices such that the total number of $(+)$ edges crossing clusters and $(-)$ edges inside the same clusters is minimized.
It is well known that the pivot algorithm could achieve a 3-approximation for correlation clustering in expectation. At a high level, the pivot algorithm samples a uniform permutation $\pi$ for the set of vertices and recursively merges the yet-to-be-clustered neighbors of the lowest-ranked vertices to create clusters.
This paper follows a recent line of work that tries to break the 3-approximation barrier with combinatorial algorithms (e.g., CHS [SODA’24]; CLPTYZ [STOC’24]). The paper follows the framework of the pivot algorithm but additionally introduced some ideas in agreement decomposition as explored by, e.g., CLMNPT [ICML’21]; AW [ITCS’22]. In particular, the paper identifies the tackled the issues in the pivot algorithm of $i).$ merging neighbors with high disagreement neighborhoods and $ii).$ fails to merge non-neighbors with low disagreement neighborhoods. In this way, the paper obtained a $2.997$-approximation algorithm with much better empirical performances.
Claims And Evidence: Yes. The theoretical results are with proofs, and the algorithm design is reasonable.
Methods And Evaluation Criteria: Yes, the comparison of average and worst-case costs against the vanilla pivot algorithm shows the advantage of the modified pivot algorithm.
Theoretical Claims: At a high level, the main technique of the paper resembles a blend of the pivot algorithm and the agreement decomposition algorithm. As discussed in the paper, the vanilla pivot algorithm suffers from the problem of clustering neighbors with a high disagreement and not being able to merge with non-neighbors with low disagreement. The intuitive fix of these problems would be to artificially add some of such vertices to the clustering formed by the vanilla pivot algorithm. Formally proving the approximation guarantee, on the other hand, requires some quite involved techniques in fractional triangle packing. I did not get time to carefully check the quantities in the charging argument, but the design makes sense to me in general.
Experimental Designs Or Analyses: Yes, for the most part. However, from the experiment section, it is unclear whether the paper ran multiple experiments with different random seeds, especially given that the pivot algorithm is known to have a large variance for different choices of random seeds. See my comments in the criticism for details.
Supplementary Material: The appendix contains proofs for the approximation guarantees and the efficient implementation. I briefly checked the proof of efficiency, and it looks good to me.
Relation To Broader Scientific Literature: Correlation clustering is an important problem in machine learning with broad applications. I believe the algorithm designed in this paper is quite practical.
Essential References Not Discussed: No missing essential references. On a side note, the cited work of CLMNPT [ICML’21] and AW [ITCS’22] did not use the pivot algorithm but instead used agreement decomposition. The current discussion on the right column of page 1 appears to allude that those results were also based on the pivot algorithm. Furthermore, there are some more recent results for correlation clustering in dynamic settings that are related to this work (e.g, ‘Dynamic Correlation Clustering in Sublinear Update Time’ [ICML’24] and ‘Fully Dynamic Adversarially Robust Correlation Clustering in Polylogarithmic Update Time’ [AISTATS’25]).
Other Strengths And Weaknesses: I’m in general supportive of the paper: correlation clustering is an important problem, and getting algorithms with both better theoretical bounds and empirical performances is an important direction to pursue. To the best of my knowledge, this is the first algorithm that achieves $<3$ approximation for dynamic correlation clustering in poly-logarithmic update time. Furthermore, compared to the combinatorial algorithm in CLPTYZ [STOC’24], the algorithm in this paper is much more practical. The paper also appears to be well-written, and the concepts are explained relatively well despite the charging argument being intrinsically involved.
I do not see any major weaknesses in the work. However, I do think the paper could benefit from reporting the average cost for multiple runs of the pivot algorithm. This algorithm often suffers from instability and demonstrates very high costs in the worst case (see the experiments in, e.g., CLMNPT [ICML’21]; CLMP [ICML’24]; BDPSW [AISATS’25]). Therefore, comparing the pivot algorithm with multiple random seeds looks more reasonable. (Maybe the paper already did so, but it’s unclear to me in the paper.)
Other Comments Or Suggestions: I think $2.997$ is sufficiently smaller than $3$, so maybe writing this number out directly in Theorem 1.1 is better. $3-\Omega(1)$ makes me think the $\Omega(1)$ is some number like $10^{-10}$.
Questions For Authors: N/A, I do not have additional questions.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We appreciate your recommendation to run multiple experiments using different random seeds, especially since the Pivot algorithm is known to have instability. To clarify, Figures 1 and 2 already show both average and worst-case outcomes, based on multiple random seeds per dataset. As illustrated, our Modified Pivot algorithm demonstrates notably less instability compared to the pivot algorithm. We will emphasize this point more clearly in the revision.
We agree that writing the approximation number (2.997) explicitly in Theorem 1.1 improves readability. We will apply this change into the final version.
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Rebuttal Comment 1.1:
Comment: Thanks for the clarification of the experiments. I have no further questions. I'll keep my score as it is. | Summary: This paper presents a modification of the standard 3-approximation Pivot algorithm for correlation clustering (select a node in a graph, cluster it with its neighbors, and remove it) called ModifiedPivot, which avoids the worst-case errors of Pivot by clustering some its neighbors as singletons (if their neighborhood doesn't overlap well with the pivot's neighborhood), and by adding some of the pivots non-neighbors to the cluster (if they overlap well enough with the pivot's neighborhood). A careful analysis based on the bad triangle charging technique shows that the method has an approximation guarantee that is strictly better than 3, a barrier that standard pivot cannot overcome. Furthermore, modifiedPivot can be implemented in the fully-dynamic model with log^{O(1) n update time, providing the first better-than-three algorithm with such an update time in this model (previously, there was not even an O(n) update time for better-than-three approximation algorithms). In practice, the modified pivot algorithm leads to empirical improvements on a suite of real-world graphs and stochastic block models.
## Update post rebuttal
Thanks for the reply and clarification. I maintain my positive view of the paper.
Claims And Evidence: Yes, the explanation of the algorithm itself at a high level is very sensible, and the main proof techniques and why they should be expected to work are outlined clearly. Several figures and discussions of the main techniques are provided throughout to help the reader. Empirical results also support the theoretical findings. Detailed proofs are provided to accompany the theoretical results, which are the main contribution of the paper.
Methods And Evaluation Criteria: The paper is primarily about theoretical results. The numerical experiments accompanying the theory are sensible and are performed on a standard collection of graphs used previously for correlation clustering experiments.
Theoretical Claims: I followed the detailed explanation of the proof techniques that are provided at a high level throughout the text. The bad triangle charging scheme is standard in correlation clustering analysis and is a very sound approach. I confirmed at a high level that the pieces of the proof fit together and seem sound. However, the main technical results are contained in the dense 16 page appendix, and I did not check these for correctness.
Experimental Designs Or Analyses: The experimental setup is sound.
Supplementary Material: No
Relation To Broader Scientific Literature: The text does a good job placing the paper within its broader context in the literature. In particular, there was previously no fully dynamic algorithm with even a linear update time that maintained a better than three approximation. Aside from settling this question in the fully dynamic setting, having a modified pivot algorithm that is practical and has a better than 3 approximation is a useful breakthrough result for correlation clustering. While better than 3 approximation algorithm exist, they are largely impractical. Meanwhile, there are many different practical methods that can achieve a 3-approximation or worse, but improving on factor 3 is a significant barrier.
Essential References Not Discussed: None.
Other Strengths And Weaknesses: The key results of this paper is significant and has the potential to lead to other methods that break the factor-3 approximation barrier while actually being practical. It's also nice that the author have complemented their theoretical analysis with some experiments on real world graphs.
One small potential weakness in the experiments section is that it's unclear how many different epsilon and delta parameters were tried out in order to obtain the improved results. If in order to get good results, many parameter values need to be tested, then there is a runtime tradeoff to consider since standard pivot does not need to compute these. Thus, a more accurate comparison may be to run Pivot many times (with different permutations) and take the best result, if you are going to run to run ModifiedPivot many times (on the same permutation) with different choices of epsilon and delta. This is not a huge issue, as the main contributions of the paper are theoretical. However, depending on how many times parameter settings you need to try for epsilon and delta, there could be some weaknesses in the empirical results.
Other Comments Or Suggestions: In Algorithm 1 you state "We emphasize that even though vertices in $A_v$ get clustered here, they are not removed from $V$ in this step and so can be picked as pivots later."
I'm confused by this and it seems contradictory. Saying that a node is already clustered (in this case as a singleton) suggests that in the final output clustering, the node will indeed just be in a singleton cluster. But saying that it could later be chosen as a pivot suggests that it could later be clustered with some of its neighbors (and significantly overlapping non-neighbors). I'm confused then as to how a node can simultaneously clustered already while possibly being a pivot later. I may have missed something, but I'm not sure how to reconcile this apparent contradiction.
Questions For Authors: How many choices of epsilon and delta do you have to test in your numerical experiments?
Can you help me reconcile the apparent contradiction mentioned above in the "other comments and suggestions" section of my review?
Code Of Conduct: Affirmed.
Overall Recommendation: 5 | Rebuttal 1:
Rebuttal: Thanks for pointing out the confusion regarding Algorithm 1, we will make sure to clarify this in the next version of the paper. To clarify this, the vertices in $A_v$ will be allowed to be picked as pivots later on, but even if they start clusters they won't themselves be added to those clusters and will be put in singleton clusters. This makes the algorithm easier to implement in the dynamic setting and elsewhere, because its output can be viewed as the output of the PIVOT algorithm which is then post-processed and locally improved. We will clarify this further in the text of the paper in its next version.
In our experiments, we tested at most 8 choices for each of epsilon and delta in all the runs, which adds up to at most 64 combinations. We will clarify this in the next version of the paper. | Summary: This paper studies the classic correlation clustering problem, where the objective is to partition objects into clusters while minimizing disagreements with given similarity and dissimilarity labels. The PIVOT algorithm by Ailon et al. (STOC’05) provides a 3-approximation for this problem, but its analysis is tight, and improving this bound has remained an open challenge.
The authors introduce MODIFIEDPIVOT, an extension of PIVOT that locally adjusts the clustering by moving vertices to different or new clusters. Their theoretical analysis proves that MODIFIEDPIVOT achieves an approximation ratio of 3 − Ω(1), improving prior results in dynamic settings. In particular, they show that in a fully dynamic environment, the algorithm maintains this improved approximation while handling updates in polylogarithmic time per operation (Theorem 1.1).
Additionally, the authors implement MODIFIEDPIVOT and evaluate it on real-world datasets, demonstrating that it makes less than 77% of the mistakes made by PIVOT on average, further validating its practical effectiveness.
Claims And Evidence: The theoretical claims are supported by proofs while the benefit of the proposed algorithm over the standard pivot is supported by the conducted experiments.
Methods And Evaluation Criteria: Yes, both the proposed method and evaluation criteria make sense for the problem at hand.
Theoretical Claims: Yes, they seem correct, although I did not check in detail.
Experimental Designs Or Analyses: No issue found.
Supplementary Material: Yes, I reviewed all of it.
Relation To Broader Scientific Literature: The main contributions of this paper are closely tied to the classic PIVOT algorithm for correlation clustering, introduced by Ailon et al. (STOC’05), which is known to achieve a 3-approximation for the problem. The analysis of PIVOT is traditionally conducted through a charging scheme based on analyzing “bad triangles.”
In this paper, the authors introduce MODIFIEDPIVOT, an algorithm that improves upon the original PIVOT by achieving an approximation ratio of 3 − ε₀ for some absolute constant ε₀ > 0. This result is obtained through a novel charging scheme. MODIFIEDPIVOT provides a better-than-3 approximation in the dynamic setting with polylogarithmic time per update, improving the 3-approximation previously achieved by Behnezhad et al. (FOCS’19) and Dalirrooyfard et al. (ICML’24).
Essential References Not Discussed: Since the proposed MODIFIEDPIVOT algorithm relies on relocating certain nodes to new or alternative clusters compared to the standard PIVOT, it would be valuable for the authors to discuss related works (e.g., [1, 2]) that have applied local search optimization to the correlation clustering objective, starting from the solution provided by PIVOT. These studies have demonstrated the effectiveness of such an approach, aligning with the findings of this paper. While the authors provide a thorough characterization of cases where PIVOT fails, incorporating a discussion of related works would further strengthen the contextualization and significance of the proposed method.
[1] An Efficient Local Search Algorithm for Correlation Clustering on Large Graphs. COCOA 2023.
[2] In and out: Optimizing overall interaction in probabilistic graphs under clustering constraints. KDD 2020.
Other Strengths And Weaknesses: Strengths:
S1) The paper effectively demonstrates, through examples and figures, where the standard PIVOT algorithm fails, which helps in clarifying the understanding of Algorithm 1.
S2) The paper addresses an open problem in the literature: whether it is possible to maintain a 3 − Ω(1) approximation of correlation clustering in polylogarithmic time per update.
S3) The charging scheme used to analyze the approximation factor of the proposed algorithm introduces some novel elements compared to the standard charging scheme applied to analyze the PIVOT algorithm.
S4) The experiments empirically show that the MODIFIEDPIVOT algorithm leads to improvements in all cases across the datasets considered.
Weaknesses:
W1) The approximation factor of MODIFIEDPIVOT (2.997) is very close to that of the standard PIVOT (3). While there is an improvement, it appears to be quite marginal.
W2) The time complexity overhead introduced by MODIFIEDPIVOT (in non-dynamic settings) compared to the standard PIVOT is not sufficiently addressed in the paper. Given that the improvement in the approximation factor (see W1) is relatively small, the additional computational cost may not be justified. A more detailed discussion of this trade-off would be valuable.
W3) The description of the charging scheme algorithm (Algorithm 2) is not clear in the main paper. It would be beneficial to either move the pseudocode and the detailed explanation to the supplementary material, leaving only the intuition of the scheme in the main text, or provide a clearer and more detailed description within the main paper.
W4) There is a need for a baseline that uses local search starting from the solution of PIVOT. If the such local search algorithm accepts only improvements, this would trivially preserve the 3-approximation of PIVOT, allowing for a clearer comparison and understanding of the potential benefits of the proposed modifications.
Other Comments Or Suggestions: The explanation of the PIVOT algorithm before “Problem 1” repeats information already provided in the introduction, leading to some redundancy. It may be beneficial to streamline this section to avoid unnecessary repetition.
On page 2: “The figure below illustrates this. On the top, we have the optimal clustering. On the bottom, we have the output of PIVOT.”
On page 3, some edges in the first figure appear to be obscured by the blue shape representing the cluster. Clarifying or adjusting the visualization could improve readability and ensure all edges are clearly visible.
Questions For Authors: Q1) Could the authors clarify the time complexity overhead introduced by MODIFIEDPIVOT (in non-dynamic settings) compared to the standard PIVOT? Given that the improvement in the approximation factor (see W1) is relatively small, is the additional computational cost justified? A more detailed discussion of this trade-off would be appreciated.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank the reviewer for thoughtful comments. We note that while indeed the improvement from 3 to 2.997 in the approximation ratio is rather small *quantitatively*, it breaks a longstanding barrier of 3-approximation for combinatorial algorithms and has an important *qualitative* value. Additionally, our experiments show that the improvement in the approximation ratio is much more drastic than this theoretical guarantee.
It is also worth pointing out that to break the 3-approximation analysis, our analysis deviates significantly from that of the original pivot algorithm and has to incorporate several new ingredients such as charging non-local triangles and fractional charges. Our hope is that these techniques prove useful in the future for providing analyses that go much below 3 or 2.997 approximations.
The time complexity of our Modified Pivot algorithm and the Pivot algorithm are the same once the parameters of the algorithm are fixed. We'll make sure to clarify this in the next version of the paper.
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Rebuttal Comment 1.1:
Comment: Thank you for the clarifications. Emphasizing that the proposed method has the same complexity as the original PIVOT is valuable, even though it can be inferred from the paper.
The fact that the experiments show an improvement in the approximation ratio beyond the theoretical guarantee is not surprising, as the proposed algorithm allows for relocating certain nodes to new or alternative clusters compared to the standard PIVOT. This approach has already been shown to be beneficial in related works (see essential references not discussed), which have applied local search optimization to the correlation clustering objective starting from the solution provided by PIVOT. I believe referencing these works would further strengthen the contextualization of the proposed method.
I agree with the authors that the new techniques introduced for the theoretical analysis of the proposed algorithm could be valuable in future studies to improve the theoretical understanding of related algorithms. After also reading the other reviews, I have decided to raise my score to a weak accept.
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Reply to Comment 1.1.1:
Comment: We appreciate this. We’ll make sure to include more references about local search methods in the next version of the paper. | null | null | null | null | null | null | null | null |
BiAssemble: Learning Collaborative Affordance for Bimanual Geometric Assembly | Accept (poster) | Summary: This paper proposes a framework for learning collaborative affordance in bimanual geometric assembly. The task is assembling fractured parts into complete objects, which is a long-horizon task requiring pick-up, alignment, and assembly. The paper tackles this task through predicting collaborative affordance and gripper actions for bimanual geometric shape assembly. A real-world benchmark for re-assembling broken parts is created. Evaluations demonstrate the effectiveness of the approach and shows generalizability to unseen object categories in both simulated and real-world environments.
## update after rebuttal
The paper addresses a novel and useful task of bimanual geometric assembly. The authors also provide additional experimental results applying the method to other tasks (e.g., a bottle opening task). However, the concerns of relatively low real-world performance and many assumptions such as imagined assembly shapes, floating grippers, relying on pose trackers, etc. remain unaddressed. I will maintain my original score.
Claims And Evidence: The paper claims to provide an effective solution for bimanual geometric assembly, but the reported success rates in experiments are low (20-30%), which does not support the reliability and practicability of the approach.
Methods And Evaluation Criteria: The integration of collaborative affordance prediction with geometric reasoning demonstrates potential for advancing bimanual assembly tasks.
The method has many assumptions. It assumes the availability of an ideal "imaginary assembled shape". Also, the task setup mainly considers objects with two fragments, however, in reality there could be an arbitrary number of fragments with multimodal contacts involved. Three-fragment assembly task results are shown in the supplementary material, but the success rate is quite low and cannot fully validate the scalability of the approach to multi-fragment assembly.
A real-world benchmark on geometric assembly is created, which paves way for future research on this direction.
Theoretical Claims: The equations in the paper are correct.
Experimental Designs Or Analyses: Thorough evaluations in both simulation and real-world environments are carried out to demonstrate the effectiveness of the approach. The model is generalizable to shapes from unseen categories.
The proposed ablations validate the role of individual components, such as disassembly prediction and SE(3)-equivariant representations in the obtained performance.
For real-world experiments, only qualitative results are presented, there is a lack of quantitative results on more object shapes and comparisons to other baselines. There is also a lack of more detailed sim2real transfer analysis, for example, side-by-side assembly comparison of an exact same set of shapes in simulation and the real world.
The evaluations in simulation are carried out with floating grippers. It would be more realistic to control grippers mounted on bi-manual arms, as there could be singularity and arm-table collision issues that are not being taken into account with the floating grippers.
Supplementary Material: Yes.
Relation To Broader Scientific Literature: The paper addresses a useful task that has been under-explored in previous robotics works, and provides an effective approach to solve this challenging task.
Essential References Not Discussed: No.
Other Strengths And Weaknesses: The paper addresses an underexplored but important task in robotics and provides a novel solution to tackle it. However, it relies on many assumptions (e.g., the availability of an "imaginary assembled shape" and the restriction to mostly two-part assemblies) and has low success rates and robustness. It is also not thoroughly validated in real-world environments of its effectiveness and scalability.
The failure analysis is helpful in categorizing errors but did not provide actionable insights or detailed solutions to address the low success rates.
Other Comments Or Suggestions: See above.
Questions For Authors: Why is the success rate so low? Which component is the most brittle part?
How would the accuracy of the pose estimator affect the performance? If the pose estimation is a bit off due to occlusions or sensor noises in the real world, would the model be robust to it and still manage to succeed?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your thoughtful review and questions. We have carefully addressed them below.
> W1. Low reported success rates
The relatively low scores across all models and baselines stem from the highly diverse and complex nature of geometric shape assembly task. As detailed in Appendix G, our dataset contains varied fracture patterns, including many flat or minimal parts that are extremely difficult to grasp and assembly. We intentionally chose this challenging dataset to set a benchmark for future improvements. For instance, future methods could involve pre-grasp operations like moving flat parts to the table edge to make them graspable.
While we demonstrate the effectiveness of our method in this complex task, our approach is also applicable to a broader range of bimanual tasks. Due to space limitations, we kindly refer the reviewer to our response to Reviewer3 (KY79m), W3, where we provide a detailed clarification that our method can be adapted to tasks like bottle cap closing, and has good performance (67% accuracy).
> W2. Assumption of imaginary assembled shape. Two-fragment task setup. Three-fragment task' success rate.
For **(A) imagined assembled shape**, we kindly refer the reviewer to our response to Reviewer1 (z3UB), W1, for a detailed clarification.
For **(B) multi-fragment assembly**, our experiments show that our method can handle multiple parts (Appendix E.1). The relatively low success rate is mainly due to the presence of more minimal parts that are nearly impossible to grasp or assemble. Rather than excluding these highly challenging cases from test dataset, we intentionally include them for an honest evaluation. We recognize that multi-fragment assembly introduces additional challenges, we will explore pre-grasp and pre-orientation operations to handle such complexities and improve multi-fragment assembly.
> W3. Quantitative results for real-world experiments. Sim2real transfer analysis.
For (A) real-world experiments, we tested our model on each category with 10 trials, without any fine-tuning. The success rates are as follows: Bowl: 3/10, Mug: 2/10, BeerBottle: 3/10, WineGlass: 2/10. For mug, in some trials, we intentionally place it with the handle facing downward, making it ungraspable, so the gripper must grasp mug's top edge. This leads to collisions when both grippers grasp the top edges, due to mug's small diameter. For wineglass, its glasswork is prone to slipping, even when gripper successfully grasps it, it may tip during manipulation.
For (B) sim2real transfer analysis, we load the object meshes (acquired from our real-world benchmark) into simulation. We observe better results in simulation, primarily due to discrepancies in joint constraints. For instance, when picking up a flat fragment on a table, gripper in simulation can move parallel and close to the table surface, whereas real robot encounters joint limitations that restrict its movement. This comparison highlights the need to incorporate bimanual joint constraints into simulation framework to better reflect real-world scenarios and improve transferability.
> W4. floating grippers
In this work, following [Paper 9-11], we focus on learning collaborative affordance, abstracting away the robot arm control. While our real-world experiments show the proposed actions work with real arms using motion planning (MoveIt!), we acknowledge that incorporating arm control would enhance the system’s realism. In future work, we will address these challenges including arm singularities and collision issues, integrating cuRobo for motion generation for bimanual manipulators.
> W5. failure analysis and actionable insights
In our failure analysis, we provided potential solutions for future works, including (1) incorporating pre-grasp operations like moving flat part to the table edge to make it graspable, (2) performing a series of pick-and-place operations to adjust object' pose. More details are available in Appendix G.
> W6. Which component is the most brittle part?
We have conducted additional ablation studies, with results and analysis in Table 4,5 of Appendix E.3.
> W7. Is model robust to occlusions or noise?
As described in Equation 2 of our paper, the pose estimator does not need to precisely predict the absolute object pose. Instead, it only needs to estimate the relative pose between two frames, which significantly simplifies the task. Beisdes, our empirical results show that FoundationPose, the SOTA model we use, performs well in continuous manipulation scenarios, maintaining accuracy and robustness even with occlusions (e.g., gripper occlusion after grasping) or sensor noise.
**References**
[9] Eisner, et al. Flowbot3d: Learning 3d articulation flow to manipulate articulated objects. RSS, 2022.
[10] Xu, et al. UMPNet: Universal manipulation policy network for articulated objects. RAL, 2022.
[11] Zhao, et al. Dualafford: Learning collaborative visual affordance for dual-gripper manipulation. ICLR, 2023. | Summary: In this paper, the authors present a framework for bimanual geometri assembly. They formulate the task into 3 steps: pick-up, alignment and assembly. For pick-up, a point-level affordance prediction module is trained and used; For alignment, a SE(3) transformation is predicted; For assembly, a collision-free direction is predicted.
The authors also introduce a real-world benchmark featuring geometry variety and global reproducibility.
The authors evaluate their method in simulation and on real data. The results outperform previous affordance-based and imitation-based methods.
Claims And Evidence: The claims are well supported by the comparison and ablation studies results.
Methods And Evaluation Criteria: The authors use the assembly success rate as the evaluation criteria, which can be reasonable. But the thresholds of distance and rotation angels are not given. It is very important for real applications. And according to the figure and video, there are still a large gap between the two parts after assembly.
Theoretical Claims: There are no theoretical claims.
Experimental Designs Or Analyses: The authors compare their approach using three methods: ACT, a manually designed heuristic strategy, and a modified version of the existing affordance prediction method, DualAfford. However, they do not include comparisons with existing works on geometric assembly. The authors justify this omission by stating that these prior works do not account for robot execution. While this reasoning has merit, it would strengthen the study if the authors had adapted these geometric assembly methods to the current setting and included them in the comparison. Such an approach could provide a more comprehensive evaluation of their method’s performance relative to established baselines.
Additionally, the authors perform ablation studies to assess their design choices, which are reasonably constructed.
Supplementary Material: The supplemetary explains their framework and shows the real-world experiment results, which is helpful for understanding the paper.
Relation To Broader Scientific Literature: The contribution of this work is very specific to this task, and may not contribute much to the broader community.
Essential References Not Discussed: NA
Other Strengths And Weaknesses: The proposed framework is designed specifically to the task. However, its technical novelty is quite limited and does not meet the standards expected for ICML.
The paper is well-written, and the style of the figures is visually appealing. That said, the logic of Figure 2 is convoluted and difficult to follow.
Additionally, the method relies on complete reconstruction from multi-view images,which may be impractical for real-world applications.
Other Comments Or Suggestions: NA
Questions For Authors: NA
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We sincerely appreciate your thoughtful questions. We've addressed them in detail below.
**For detailed paper references, please refer to our response to Reviewer1 (z3UB).**
> W1. Thresholds of distance and rotation. There is a gap between two parts after assembly.
Thank you for the suggestion. The threshold for distance is set to 2 unit-length in the simulation, and threshold for rotation is 30 degrees. While we are not permitted to make revisions during rebuttal, we will include this information in the final paper. Geometric shape assembly is a particularly challenging task due to the diversity of object categories, complex geometries, and the significant generalization required. In fact, even humans find it difficult to assemble shapes based solely on visual information. In this paper, we have taken a successful first step toward addressing this challenge. Moving forward, we plan to incorporate tactile information into our method, as it is especially valuable in contact-rich tasks and may help achieve more precise assembly of fractured parts.
> W2. Comparisons with existing works on geometric assembly.
We conducted a comparison with an existing geometric assembly method [Paper-5]. Although this method only considers the geometries and ideal assembled poses of fractured parts, without taking the robotic assembly process into account, we adapted it as a baseline by: (1) using a heuristic method to generate the robots' pick-up actions (detailed in Appendix B), (2) denoting the predicted SE(3) pose for part i as $q_{i}^{asm}$, and using Equation 1 in our paper, we calculate the gripper’s target pose $g_{i}^{asm}$ for assembly. The average accuracy of this baseline is 3.00% on the training categories, which is significantly lower than our method. The main reason for this performance gap is that prior visual assembly methods neglect the robotic execution process. Specifically, these methods do not determine where to grasp the fragments, not only for successful pickup but also to avoid the seam region for subsequent assembly. They also lack the capability to align the fragments properly at the seam, which is crucial for avoiding collisions when the two parts are brought together. On the contrary, our method integrates the considerations of part geometry, shape assembly with robotic coordination and execution in the proposed affordance learning framework.
> W3. The contribution of this work is specific to this task.
Thank you for this constructive comment. Our framework focuses on learning bimanual collaborative and geometry-aware affordances to generate long-horizon action sequences for robotic manipulation tasks. While we demonstrate the effectiveness of our method in geometric shape assembly task, which involves diverse object categories, complex geometries, and significant generalization challenges, the learned affordance is applicable to a broader range of bimanual tasks that require coordinated manipulation.
For other tasks requiring bimanual coordiniation, such as peg insertion, bottle cap closing, and furniture assembly (which are relatively easier than geometric shape assembly), our method can be easily adapted. For instance, in the bottle cap closing task, the process can be formulated into three steps: (1) The two arms pick up the bottle and cap from the table. (2) The two arms align the cap with the bottle opening. (3) The two arms place and secure the cap onto the bottle. We conducted experiments on this task, and results show that after training on a few bottle shapes, our method generalizes to novel bottle shapes, achieving an average accuracy of 67%. Visualizations of the predicted affordance maps and manipulation process are available on project website (Rebuttal-Figure3) [https://sites.google.com/view/biassembly/ ] .
> W4. Figure 2 is convoluted
In the paper, Figure 1 introduces the intuition behind our proposed framework, while Figure 2 provides a more detailed illustration. Based on your feedback, we have revised and simplified Figure 2 to make it clearer and easier to follow. The updated version is on our website (Rebuttal-Figure2).
> W5. The method relies on reconstruction from multi-view images, which may be impractical for real-world applications.
Reconstructing unknown objects (such as fractured parts) with robotic manipulators is a well-established research area. A feasible approach involves using two robotic arms with wrist camera to capture the images of fractured part and applying the method in Sec. 5.2 for reconstruction. The process and results are available at project website (Rebuttal-Figure1). Additionally, alternative approaches have been explored in previous works [Paper 1-3], including allowing the robot to re-orient the object while collecting visual observations to facilitate the reconstruction of unknown objects. Therefore, object reconstruction in real-world scenarios is both feasible and not inherently difficult, given the available techniques and tools.
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Rebuttal Comment 1.1:
Comment: Thank the author for the detailed and careful responses. They have conducted additional experiments, including new baseline and extension to other tasks. Most of my concerns have been addressed in the rebuttal. I'd like to raise my score to ``weak accept''. However, the technical novelty needs futher clarification in the final version.
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Reply to Comment 1.1.1:
Comment: Dear Reviewer,
We sincerely thank you for your thoughtful comments and for considering raising your score to "weak accept". We are pleased to hear that our responses have addressed most of your concerns. Following your suggestion, we will include further clarifications regarding the technical novelty (including our response to W3) and other discussions in the final version of the paper.
We truly appreciate your positive recognition of our work. We would be very grateful if you could consider adjusting your score through the "edit" option on the original review if you find it appropriate.
Once again, thank you for your valuable feedback and for your positive consideration. | Summary: This work focuses the shape assembly task aimed at reconstructing broken objects. A multi-stage BiAssembly framework is put forward to carry out this task. Initially, the BiAssembly framework utilizes SOTA techniques to obtain an imagined assembled shape. Subsequently, it forecasts the disassembly direction, alignment pose transformation, pick-up affordance, and ultimately, the gripper alignment and assembly poses. Moreover, a real-world framework is introduced in this paper. The experimental outcomes demonstrate that the BiAssembly framework outperforms previous approaches.
Claims And Evidence: Yes
Methods And Evaluation Criteria: Yes
Theoretical Claims: Yes
Experimental Designs Or Analyses: Yes
Supplementary Material: Yes
Relation To Broader Scientific Literature: This work is related to shape assemble perdition task. And it focus on the execution policy.
Essential References Not Discussed: Yes
Other Strengths And Weaknesses: Strengths
Overall, the paper is written well. Technical details and experiments are clearly explained. The framework for shape assembly seems to work. According to the paper's results, it does better than old heuristic or policy - based methods.
Weaknesses
The multi-stage framework has some assumptions. For example, it assumes the object has two broken parts, the imagined assembled shape can be got early, and the robot follows a set alignment and assembly process.
Other Comments Or Suggestions: Overall, this paper presents a viable framework for shape assembly, which is beneficial for this field. However, the framework in this paper is limited by its single-task-oriented design. This makes such methods less general and less likely to inspire a wider readers. I tend to accept this paper. Meanwhile, I hope that the author can strive for greater generality in the design of the model in the feature.
Questions For Authors: None
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your valuable questions. We've addressed each of your concerns below.
**For detailed paper references, please refer to our reply to Reviewer1 (Reviewer z3UB).**
> W1. The multi-stage framework has some assumptions. For example, it assumes the object has two broken parts, the imagined assembled shape can be got early, and the robot follows a set alignment and assembly process.
For **(A) multiple broken parts**. We have conducted experiments to demonstrate that our method can handle multiple broken parts in **Appendix E.1**. And both the quantitative and qualitative results demonstrate that our proposed method can be effectively adapted to multi-fragment assembly tasks. We also provide a detailed explanation of how our method can be adapted for multi-fragment assembly in this section.
For **(B) imagined assembled shape**. The assumption of "imaginary assembled shape" is justified based on two well-established research areas that together ensure both adaptability and autonomy in real-world scenarios: (1) the reconstruction of broken parts, and (2) the prediction of target assembled shapes from those broken parts:
1. Reconstructing unknown objects (broken parts) with robotic manipulators is a well-studied problem [Paper 1-3]. A feasible approach involves using two robotic arms to capture images of the fractured part and applying the method in Sec. 5.2 for reconstruction. The process and results are available at project website (Rebuttal-Figure1) [ https://sites.google.com/view/biassembly/ ] . Additionally, alternative approaches have been explored in [Paper 1-3].
2. Predicting the imaginary assembled shape from multiple fractured parts is also a well-studied vision problem [Paper 4-8]. Prior works have demonstrated the ability to predict precise fragment poses and shown strong generalization capability to unknown parts and shapes, enabling the construction of an imaginary assembled shape. Furthermore, our experiments (Appendix E.2) show that our method is robust to imperfect imaginary assembled shapes, even without fine-tuning.
These supporting works and empirical results demonstrate the adaptability and autonomy of our framework in real-world scenarios.
For **(C) alignment and assembly process**. The alignment and assembly process mirrors the natural approach humans take when assembling fragments. Humans typically align the fragments along the seams first and then gradually move them together for precise fitting. Furthermore, when decomposing the assembly process into multiple frames, there is usually a stage where the two fragments are aligned but separated by a small distance. This intermediate step is captured in our formulation as the alignment step, which generalizes well to most shape assembly scenarios.
Thanks for your valuable comments! We will add the above discussions in our paper and make it more clarified.
> W2. Overall, this paper presents a viable framework for shape assembly, which is beneficial for this field. However, the framework in this paper is limited by its single-task-oriented design. This makes such methods less general and less likely to inspire a wider readers. I tend to accept this paper. Meanwhile, I hope that the author can strive for greater generality in the design of the model in the feature.
Thank you for this constructive comment. Our framework focuses on learning bimanual collaborative and geometry-aware affordances to generate long-horizon action sequences for robotic manipulation tasks. While we demonstrate the effectiveness of the proposed method in geometric shape assembly task, which involves diverse object categories, complex geometries, and significant generalization challenges, the learned affordance is applicable to a broader range of bimanual tasks that require coordinated manipulation.
For other tasks requiring bimanual coordiniation, such as peg insertion, bottle cap closing, and furniture assembly (which are relatively easier than geometric shape assembly), our method can be easily adapted. For instance, in the bottle cap closing task, the process can be formulated into three steps: (1) The two arms pick up the bottle and cap from the table. (2) The two arms align the cap with the bottle opening. (3) The two arms place and secure the cap onto the bottle. We conducted experiments on this task, and the results show that after training on a few bottle shapes, our method generalizes to novel bottle shapes, achieving an average accuracy of 67%. Visualizations of the predicted affordance maps and the manipulation process are available on our project website (Rebuttal-Figure3) [ https://sites.google.com/view/biassembly/ ] .
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Rebuttal Comment 1.1:
Comment: Thank you for the author's response. I will maintain my initial rating to support the acceptance of this paper.
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Reply to Comment 1.1.1:
Comment: Dear reviewer,
We are pleased that our clarifications have addressed your concerns. Thanks for your positive rating and recommendation to acceptance! | Summary: This paper addresses the challenges in the observation space and action space by proposing the BiAssemble framework to solve the collaborative problem of bimanual robots in geometric assembly tasks. Specifically, the task is decomposed into three steps: pick-up, alignment, and assembly, which are addressed by progressively predicting the affordance maps and the gripper actions of the two parts of the object. Additionally, this paper establishes a real-world benchmark for assembling broken objects and conducts extensive experiments in both simulation and real-world environments, demonstrating the superiority of the proposed algorithm and its ability to generalize to unseen object categories.
Claims And Evidence: clear
Methods And Evaluation Criteria: yes
Theoretical Claims: yes
Experimental Designs Or Analyses: yes
Supplementary Material: yes
Relation To Broader Scientific Literature: none
Essential References Not Discussed: no
Other Strengths And Weaknesses: Strengths:
• The paper proposes a novel geometric assembly task focusing on bimanual robot collaboration to repair broken objects, addressing the research gap in the field of geometric assembly for complex shapes and long-horizon action sequences.
• The idea of introducing point-level affordance is both interesting and highly significant, as it not only predicts the feasibility of grasping points but also simultaneously considers the collaborative requirements of subsequent alignment and assembly steps.
• The construction of a real-world benchmark bridges the gap between simulation and real-world environments.
• The article is well-written, with a clear structure, well-defined motivations, and comprehensive experiments.
Weaknesses:
• The algorithm relies on predefined assembly shapes, and I suspect that it is unable to autonomously infer the correct assembly of unknown objects, thus limiting its applicability and reducing its adaptability and autonomy in real-world scenarios.
• The paper assumes that the relative pose between the gripper and the object remains stable, but in real environments, the relative attitude between the gripper and the object may change due to external perturbations. Does this perturbation significantly affect the robustness of the model? If so, in what ways? If the perturbation significantly affects the model performance, in what ways are subsequent plans to address this issue?
• For the implementation of the methodology mentioned in the authors' supplementary material that can be extended to handle multi-piece assemblies, how does the accumulation of iterative errors affect the results, and will an end-to-end approach be considered for efficient completion in multi-piece tasks?
Other Comments Or Suggestions: none
Questions For Authors: see Strengths And Weaknesses
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We sincerely appreciate your valuable questions, and we have provided detailed responses below.
> W1. The algorithm relies on predefined assembly shapes...
The assumption of "imaginary assembled shape" is justified based on two well-established research areas that together ensure both adaptability and autonomy in real-world scenarios: (1) the reconstruction of broken parts, and (2) the prediction of target assembled shapes from those broken parts:
1. Reconstructing unknown objects (broken parts) with robotic manipulators is a well-studied problem [Paper 1-3]. A feasible approach involves using two robotic arms to capture images of the fractured part and applying the method in Sec. 5.2 for reconstruction. The process and results are available at project website (Rebuttal-Figure1) [https://sites.google.com/view/biassembly/ ]. Additionally, alternative approaches have been explored in [Paper 1-3].
2. Predicting the imaginary assembled shape from multiple fractured parts is also a well-studied vision problem [Paper 4-8]. Prior works have demonstrated the ability to predict precise fragment poses and shown strong generalization capability to unknown parts and shapes, enabling the construction of an imaginary assembled shape. Furthermore, our experiments (Appendix E.2) show that our method is robust to imperfect imaginary assembled shapes, even without fine-tuning.
These supporting works and empirical results demonstrate the adaptability and autonomy of our framework in real-world scenarios.
> W2. The relative attitude between gripper and object may change due to external perturbations. Does it affect the robustness of model?
If external perturbations cause the relative pose between the gripper and the object to change, a pretrained pose estimation model (we used FoundationPose) can track the updated object pose in real-time performance. Consequently, as shown in Equation 2 of our paper, we only need to update the previous gripper pose $ q_{i}^{pick} $ with the perturbed pose $ \hat{q_{i}^{pick}} $, allowing us to compute the correct gripper pose $ \hat{g_{i}^{asm}} $ for assembly. Furthermore, since Equation 2 holds at any time step, our approach remains robust throughout the manipulation process. Specifically, at each time step $ t $, we update $ q_{i,t}^{pick} $ (obtained from FoundationPose) and $ g_{i,t}^{pick} $ (obtained from the robot control interface) to compute the appropriate gripper pose $ g_{i,t+1}^{pick} $ for the next step. This ensures that our method can dynamically adapt to perturbations without compromising assembly accuracy. We appreciate this insightful question and will incorporate this explanation into our paper after rebuttal.
> W3. How does the accumulation of iterative errors affect the results of multi-piece task? Will an end-to-end approach be considered for efficient completion in multi-piece tasks?
To evaluate the impact of iterative error accumulation in multi-piece assemblies, we conduct a comparative experiment with (a)(b) settings in the first iteration: (a) the two parts are assembled by the robot, (b) the two parts are perfectly assembled using ground-truth alignment. Then, we evaluate the accuracy of the second-iteration assembly ''to assemble the third parts to'' under (a)(b) conditions: 21.20% accuracy for setting (a), and 24.80% accuracy for setting (b). These results indicate that iterative errors affect assembly accuracy, as misalignments in earlier steps can propagate and influence the integration of new parts.
We appreciate the suggestion regarding an end-to-end approach. While our current method is effective for multi-piece assembly, we will explore an end-to-end approach in future work. This would not only consider the geometry of the parts being assembled in each iteration but also optimize the overall assembly sequence based on the geometry of all parts, leading to more efficient and accurate multi-piece assembly.
**References**
[1] Nicholas Pfaff, et al. Scalable Real2Sim: Physics-Aware Asset Generation Via Robotic Pick-and-Place Setups. 2025
[2] Saptarshi Dasgupta, et al. Uncertainty-aware Active Learning of NeRF-based Object Models for Robot Manipulators using Visual and Re-orientation Actions. IROS, 2024.
[3] Zhizhou Jia, et al. An Efficient Projection-Based Next-best-view Planning Framework for Reconstruction of Unknown Objects. 2025.
[4] Silvia Sellán1, et al. Breaking bad: A dataset for geometric fracture and reassembly. Neurips, 2022.
[5] Ruihai Wu, et al. Leveraging SE-(3) equivariance for learning 3d geometric shape assembly. ICCV, 2023.
[6] Jiaxin Lu, et al. Jigsaw: Learning to Assemble Multiple Fractured Objects. Neurips, 2024.
[7] Theodore Tsesmelis, et al. Re-assembling the past: The RePAIR dataset and benchmark for real world 2D and 3D puzzle solving. Neurips, 2024.
[8] Gianluca Scarpellini, et al. DiffAssemble: A Unified Graph-Diffusion Model for 2D and 3D Reassembly. CVPR, 2024. | null | null | null | null | null | null |
Differential Coding for Training-Free ANN-to-SNN Conversion | Accept (poster) | Summary: In this work, the authors proposed differentiable neural coding. Based on the proposed coding, the authors provided differential graded units, differential spiking neurons, and differential coding for linear layer. According to the authors’ experiments, they could achieve state-of-the-art accuracy on image classification tasks.
Claims And Evidence: The proposed methods are theoretically supported well. Experimental evidence should be added to improve the paper.
Methods And Evaluation Criteria: The most important limitation of the SNN model is its applicability to neuromorphic hardware. SNNs must operate on event-based neuromorphic hardware to ensure low-power operation. From this perspective, the method proposed in this study has major concerns. There are great doubts about whether the proposed differentiable neural coding can be applied to neuromorphic hardware. There are also concerns about the feasibility of implementing the proposed differential graded units, differential spiking neurons, and differential linear layers derived from neural coding on neuromorphic hardware. The proposed method is expected to be difficult to implement on neuromorphic hardware.
MT neurons are more complex to implement than LIF-series neurons. In particular, 2n subtract (x-\lambda_p) operations are required to obtain the argmin of Equation 6. This computational overhead not only offsets the advantages of SNNs operating on neuromorphic hardware, but may also make implementation impossible. How can MT neurons be implemented on neuromorphic hardware? - How can it be applied to LIF?
Theoretical Claims: The biggest difference between the existing rate coding (Equation 7) and the proposed coding (Equation 14) is described in the manuscript as “differential coding only updates the encoded activation value when an output spike occurs, rather than decay at each time-step in rate coding.” (line 205~). However, this is based on an incorrect fact. Equation 7 is only an equation to explain the ANN-to-SNN conversion of rate coding, and the actual output of the SNN is a binary spike train. Therefore, as the authors mentioned, the firing rate is not calculated at every time point in the spiking neuron, but binary spike output is generated only when a spike is fired. In this regard, there is no difference between the proposed coding and rate coding. Based on the authors’ claim, it seems that the authors did not use binary spike activation. If so, this greatly worsens the advantages of SNN for event-based computing. If binary spike activation is not used, how can it be utilized in neuromorphic hardware? If it is difficult to utilize in neuromorphic hardware, it seems reasonable to consider the proposed model as a DNN with a new activation function.
- Equation 15 - How can the membrane potential (m^l[t]) and the firing rate (r^(l-1)[t]) of the previous layer be the same?
- Equation 16 - It is not reasonable to use non-linear activation (F) to approximate spiking neurons. It is reasonable to simulate only the behavior of spiking neurons that can be supported by neuromorphic hardware without non-linear activation.
Experimental Designs Or Analyses: Ablation studies on proposed methods are required.
From the experimental results in Table 1, it is judged that the CNN model using ReLU does not need minus vth. Why did MT neurons also use these models?
Analysis of overheads such as proposed methods and MT neurons is required. Also, these overheads should be considered in comparing energy consumption.
In addition to image recognition, the experimental results of object detection, segmentation, etc., if added, will be able to highlight the utility of the proposed method.
Supplementary Material: Yes, I reviewed it along with the manuscript.
Relation To Broader Scientific Literature: It will help advance neuromorphic computing.
Essential References Not Discussed: None
Other Strengths And Weaknesses: Please refer to the above comments.
Other Comments Or Suggestions: - It would be better to add synapse part to Figure 1.
- For convenient comparisons, It would be better to present the accuracy of ANN for each experimental result in Table 1. (Even if it is also in the supplementary)
Questions For Authors: Please refer to the above comments.
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: Thank you for your thoughtful and very detailed feedback. We are delighted that you find our paper theoretically supported well and the results state-of-the-art. We would like to address your concerns and answer your questions in the following:
### 1. Answer to "MT neurons are more complex to implement than LIF-series neurons. In particular, 2n subtract ($x-\lambda_p$) operations are required to obtain the argmin of Equation 6." and "Analysis of overheads such as proposed methods and MT neurons is required."
Thank you for raising these concern. Equation 6 in the article is presented for ease of understanding. In hardware implementation, the argmin module is not used. We have developed a hardware-friendly version of the MT neuron model, which can efficiently map the appropriate threshold using the potential's sign bit and exponent bits at an extremely low cost. **The detailed implementation of MT neuron can be seen in our response to Reviewer Yuhw.** We look forward to your review.
### 2. Answer to "It seems that the authors did not use binary spike activation." and explanation of "differential coding only updates the encoded activation value when an output spike occurs, rather than decay at each time-step in rate coding."
We use binary spike activation between neurons, as shown by Equation 6 and the red line in Figure 3a.
Equations 7 and 12 respectively represent the encoding of the information sequence $x^l[1:t]$ in layer $l$ under rate coding and differential coding. Here, $x$ can be the weighted spike according to Equation 4. In rate coding, even though no spike is fired at a given time step and no explicit additional computation is performed, the meaning $r[t]$ encoded by the sequence $x^l[1:t]$ changes due to the increase in $t$, as Equation 7. Conversely, differential coding ensures that when no spike occurs at time-step $t$, the sequence $x^l[1:t]$ retains the same meaning as $x^l[1:t-1]$.
### 3. From the experimental results in Table 1, it is judged that the CNN model using ReLU does not need minus vth. Why did MT neurons also use these models?
Does the term " minus vth" in your question refer to negative thresholds? Negative thresholds help minimize excessive spikes, which reduce unevenness errors[1] in conversion error. When converting a CNN model with ReLU, Differential Graded Units are not utilized. Instead, the ReLU activation function is replaced with a specific MT Neuron, which uses an additional mask to dynamically disable certain negative thresholds, ensuring the total output remains positive. Detailed implementation will be included in the appendix.
[1] Optimal ANN-SNN Conversion for High-accuracy and Ultra-low-latency Spiking Neural Networks.
### 4. Explain Equation 15 - How can the membrane potential ($m^l[t]$) and the firing rate ($r^{l-1}[t]$) of the previous layer be the same?
To unify the representation, we consider the linear layer as an independent layer, rather than just weights between layers. When layer $l-1$ is a linear layer, the actual previous layer should be $l-2$. In this case, $x^{l-1}[t]= W^lx^{l-2}=\sum_iW^l\lambda^ls^{l-2}$. Here, $r^{l-1}[t]$ represents the rate obtained by converting differencial coding back into a rate coding after linear layer.
In Equation 15, we define $m^l[t]=r^{l-1}[t]$ and further derive $m^l[t]=m^l[t-1]+\frac{x^{l-1}[t]}{t}$.
### 5.Explain Equation 16 - It is not reasonable to use non-linear activation (F) to approximate spiking neurons. It is reasonable to simulate only the behavior of spiking neurons that can be supported by neuromorphic hardware without non-linear activation.
We consider the non-linear activation as a part of the neuron's internal dynamics, separate from the communication between neuron layers. This design ensures that spike communication between neuronal layers remains uninterrupted, making our method feasible for hardware implementation. Furthermore, our Equation 16 specifies the expected output, which can also be approximated using multiple IF neurons to achieve hardware implementation[2].
[2] Spatio-temporal approximation: A training-free snn conversion for transformers.
### 6. Ablation studies on proposed methods are required. And the experimental results of object detection, segmentation, etc., if added, will be able to highlight the utility of the proposed method.
The ablation studies comparing differential coding and rate coding, as well as threshold iteration and the 99% large activation method, are detailed in Section 5 and Appendices K and M. If there’s anything further you’d like us to add, please let us know.
**In response to Reviewer Kt6R, we have added new experiments and ablation studies on object detection and semantic segmentation tasks.** We look forward to your review.
### 7. Refine Figure 1 and Table 1.
Thank you for your suggestion. We will revise Figure 1 to make it more biologically explainable and update Table 1 to ensure it is easier for comparisons. | Summary: This paper introduces a novel differential coding scheme for training-free ANN-to-SNN conversion. The authors propose using time-weighted spikes as incremental updates rather than direct rate representations, significantly reducing energy consumption and spike counts. They detail an algorithmic framework integrating multi-threshold spiking neurons, differential coding for various layers (convolutions, fully connected, Transformers), and a threshold iteration method that optimally sets neuron thresholds under a normal distribution assumption.
Claims And Evidence: The authors claim that differential coding reduces the spike rate and preserves high accuracy in converted SNNs. They support this claim with extensive experiments demonstrating both reduced energy consumption and competitive accuracy compared to baseline methods.
Methods And Evaluation Criteria: The proposed methods—differential coding and threshold optimization—are well-suited to ANN-to-SNN conversion tasks. The chosen evaluation criteria (accuracy and energy-related metrics) are appropriate and align with typical benchmarks for spiking networks.
Theoretical Claims: The authors provide proofs and derivations in the supplemental material. The mathematical steps appear sound.
Experimental Designs Or Analyses: The experimental designs—using multiple CNN and Transformer benchmarks—are comprehensive. The analysis is carefully presented, with comparisons to standard baselines and ablation studies showing how each component (e.g., differential coding vs. threshold tuning) contributes to overall performance.
Supplementary Material: Yes, the supplementary material was reviewed. It clarifies proofs for the threshold iteration method, detailed derivations, and provides code references.
Relation To Broader Scientific Literature: The paper builds on established ANN-to-SNN conversion methods but improves them through more efficient coding strategies.
Essential References Not Discussed: The paper covers the main works on ANN-to-SNN conversion and multi-threshold neurons. However, Adaptive Calibration [AAAI 2025] is also a training-free and multi-threshold neuron framework. I think it should be included.
Adaptive Calibration: A Unified Conversion Framework of Spiking Neural Network [AAAI 2025]
Other Strengths And Weaknesses: Strengths:
1. The proposed differential coding framework is novel and well-explained.
2. The threshold iteration method is carefully justified with theoretical derivations.
3. Empirical results are thorough, showing gains in both accuracy and energy efficiency.
Weaknesses:
1. While the authors do address threshold tuning, more empirical comparisons (e.g., grid-based calibration [1]) would help quantify speed and accuracy trade-offs.
2. Discussions on hardware implementation are relatively brief—expanding on how differential coding would map to neuromorphic hardware (especially regarding memory overhead and potential short-time “explosive” accumulations) would clarify practical feasibility.
[1] A free lunch from ann: Towards efficient, accurate spiking neural networks calibration.
Other Comments Or Suggestions: 1. It would be beneficial to include a small ablation experiment on threshold selection methods (e.g., comparing the threshold iteration method to a grid search or calibration-based approach) to show how quickly and accurately each method converges.
2. A dedicated subsection on hardware aspects—whether differential coding might exacerbate or mitigate “burst-like” spiking under certain time scales—would strengthen the paper’s real-world applicability.
Questions For Authors: See Suggestions and Weaknesses
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your positive and thoughtful comments. We are encouraged that you find our method novel and well-explained, and our empirical results thorough. We would like to address your concerns and answer your questions in the following.
### 1. Hardware implementation of MT Neuron and discussion about memory overhead and the relationship between differential coding and "burst-like" spiking behavior.
Thank you for your suggestion. We will first show how to implement a hardware friendly MT neuron, and then discuss the relationship between differential coding and "burst-like" spiking behavior.
**Hardware implementation of MT Neuron**:
Compared with previous ANN2SNN methods, the MT neuron is required to transmit an extra index $i$ for the threshold. When implementing the MT neuron on GPUs, two implementations can be considered:
1. Sent $V_{th}[i] \cdot S[t]$ to the next layer
2. Add an external threshold dimension with $2n$ elements to $S[t]$, set $S[t][i]=1$ and $S[t][j]=0$ for all $j \neq i$. At the same time, an external threshold dimension is added to the weight of the next layer, whose elements are the multi-level thresholds.
For simplicity, we use implementation 1 on GPUs, which is not pure binary but equivalent to implementation 2 with binary outputs. The MT neuron is also compatible with asynchronous computing neuromorphic chips because its outputs are still sparse events. Take the speck chip [1] as an example. The LIF neuron in the convolutional layer in speck chip outputs $(c,x,y)$ to the next layer (refer to Fig S4). When using the MT neuron, the only modification is adding a threshold index, i.e., $(c,x,y, i)$. The computations of the next layer should also be changed with a bit-shift operation on weights (because the threshold is the power of 2 and the multiplication is avoided). After the above modifications, the computation is still asynchronous and event-driven.
The implemention to avoid argmin in Equation 6 in hardware can be desctibed in the following two steps.
**Step1:** Set all the base threshold $\theta^l=1$ and get SNN weights by using the weight normalization strategy[2]. So, all thresholds in MT neuron are:
$$\lambda^l_i=\begin{cases}
\frac{1}{2^{i-1}},&1<i\leq n,\\\\
\frac{-1}{2^{i-n-1}},&n<i\leq 2n.
\end{cases}$$
**Step2:**
We define $\frac{4}{3}m^l[t]=(-1)^{S}2^{E}(1+M)$ with $1$ sign bit ($S$), $8$ exponent bits ($E$), and $23$ mantissa bits ($M$).
Since the median of $\frac{1}{2^{k-1}}$ and $\frac{1}{2^k}$ is $\frac{3}{4}\frac{1}{2^{k-1}}$, we can easily select the correct threshold index $i$ using $E$ and $S$ of $\frac{4}{3}m^l[t]$, without performing $2n$ subtractions to calculate the argmin in Equation 6 :
$$\text{MTH}_{\theta,n}(m^{l}[t],i)=\begin{cases}1,&\text{if }\begin{cases}
i<n,\text{ S}=0\text{ and }i=1-\text{E},\\\\
i\geq n,\text{ S}=1\text{ and }i-n =1-\text{E},\end{cases}\\\\
0,&\text{otherwise}.\end{cases}$$
The detailed implementation will be included in the final version.
For differential neurons, the memory overhead compared to initial neurons, such as IF or MT neurons, only includes an additional membrane potential. This extra potential is used to adjust the input current as described in Theorem 4.4.
**The relationship between differential coding and "burst-like" spiking behavior**:
In this paper, due to the MT neurons, which select an appropriate threshold index to fire spikes, there is no short-time "explosive" accumulation problem. However, this does not prevent us from discussing the effects of using differential coding and burst coding on other neurons that have at least one negative threshold.
Using differential coding can significantly reduce the short-time "explosive" accumulation problem. Since the goal of ANN-to-SNN conversion is to approximate the activation values of an ANN, for neurons that initially suffered from this problem, the differential information diminishes over time. This gradual reduction ultimately eliminates the accumulation issue.
[1] Spike-based Dynamic Computing with Asynchronous Sensing-Computing Neuromorphic Chip
[2] Conversion of Continuous-Valued Deep Networks to Efficient Event-Driven Networks for Image Classification
### 2. Disscussion on comparision with grid search and calibration-based approach.
Thank you for your suggestion. Due to time constraints, we plan to refine the code for the grid search and calibration-based methods in future work to conduct a more detailed comparison of their accuracy. However, **from a speed perspective**, our method calculates the theoretically optimal thresholds for all network modules—whether at the layer-wise, channel-wise, or neuron-wise level—within seconds after computing the mean and variance. We believe this represents a significant improvement in speed compared to grid search and calibration-based methods.
### 3. Incomplete related works.
Thank you for your suggestion. We will cite {Adaptive Calibration [AAAI 2025]} and discuss this article in the final version | Summary: ANN-to-SNN conversion has been known to produce so-called ‘conversion’ errors. Recent studies proposed methods that can reduce conversion errors, and in this study, the authors propose to improve the earlier studies with a novel algorithm named ‘differential coding’. Specifically, they focus on preventing the decay of the early spikes’ influences on spiking neurons’ outputs and show that a new encoding variable in spiking neurons can prevent neurons forgetting early spikes. The analytical analyses on neurons’ behaviors with differential coding makes this study’s objective clear, and the empirical evaluations are compelling. Given the novelty and potential influence of this newly proposed idea, I think this study may be of great interest to our readers.
Claims And Evidence: The paper proposes novel and interesting algorithms, which are well explained. Further, the empirical evaluations clearly support the utility of the "differential coding" proposed by the authors.
Methods And Evaluation Criteria: The authors tested differentiable coding on only ImageNet. Since ImageNet is a golden standard for image classification, this may not be a critical issue, but it would be great to see evaluations on a few more datasets to strengthen this study’s message.
Theoretical Claims: I did not find any issues with their description.
Experimental Designs Or Analyses: Experimental designs and analyses are all sound.
Supplementary Material: I read them and did not find any issues.
Relation To Broader Scientific Literature: They described earlier studies sufficiently well.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: N/A
Other Comments Or Suggestions: In lines 426-427, the authors write "As shown in Table3, detailed results can be found in Appendix". I think the authors may want to rephrase it for better readability.
Questions For Authors: N/A
Code Of Conduct: Affirmed.
Overall Recommendation: 5 | Rebuttal 1:
Rebuttal: Thank you for your positive and constructive comments. We are delighted that you find our idea novel, interesting and well explained. We would like to address your concerns and answer your questions in the following.
## 1. It would be great to see evaluations on a few more datasets to strengthen this study’s message.
Thank you for your suggestion to evaluate our method on more tasks to strengthen the message. We added the test results of our method on object detection and semantic segmentation tasks.
### 1.1 Evaluation results of object detection task on the COCO dataset
We evaluated the performance of our approach for object detection task on the COCO dataset using three different models provided by torchvision in various parameter settings, along with ablation studies, as shown in the table below. The result shows that both differential coding and Threshold Iteration method improves the network's performance.
**Table R1: Accuracy and energy efficiency of DCGS(Ours) across different models for object detection task on the COCO dataset.**
| Architecture | ANN mAP%\[IoU=0.50:0.95\] \/energy ratio | n | T=2 | T=4 | T=6 | T=8 |
| -------- | -------------- | ----- | ----- | ----- | ----- | ----- |
| FCOS_ResNet50| mAP%: 39.2| 2 | 0.0 | 0.2 | 1.6 | 6.3 |
| | energy ratio| 2 | 0.12 | 0.24 | 0.35 | 0.47 |
| FCOS_ResNet50 | mAP%: 39.2 | 4 | 21.0 | 33.9 | 36.7 | 38.2 |
| | energy ratio | 4 | 0.16 | 0.31 | 0.43 | 0.55 |
| FCOS_ResNet50 | mAP%: 39.2 | 8 | 30.5 | 38.5 | 39.2 | 39.2 |
| | energy ratio | 8 | 0.22 | 0.42 | 0.61 | 0.75 |
| Retinanet_ResNet50| mAP%: 36.4| 8 | 25.6 | 33.9 | 35.8 | 36.0 |
| | energy ratio| 8 | 0.23 | 0.44 | 0.63 | 0.78 |
| Retinanet \_ResNet50_v2| mAP%: 41.5| 8 | 19.7 | 32.6 | 37.9 | 39.7 |
| | energy ratio| 8 | 0.22 | 0.43 | 0.64 | 0.84 |
**Table R2: Ablation Study of DCGS(Ours) on FCOS_ResNet50 model for object detection task on the COCO dataset.**
| Coding Type | Threshold Searching method | mAP% \/energy ratio | n | T=2 | T=4 | T=6 | T=8 |
| -------- | -------------- | ----- |----- | ----- | ----- | ----- | ----- |
| Differential| Threshold Iteration |mAP%| 8 | 30.5 | 38.5 | 39.2 | 39.2 |
| | |energy ratio| 8 | 0.22 | 0.42 | 0.61 | 0.75 |
| Rate| Threshold Iteration |mAP%| 8 | 21.8 | 31.5 | 34.3 | 35.5 |
| | |energy ratio| 8 | 0.22 | 0.44 | 0.66 | 0.88 |
| Differential| 99.9% Large Activation |mAP%| 8 | 25.8 | 36.2 | 38.4 |39.0 |
| | |energy ratio| 8 | 0.22 | 0.43 | 0.62 | 0.78 |
### 1.2 Evaluation results of Semantic segmentation task on the PascalVOC dataset
Additionally, we evaluated our method for semantic segmentation task on the PascalVOC dataset using two different models provided by torchvision in various parameter settings, also conducting ablation experiments, as presented in the table below. The result shows that both differential coding and Threshold Iteration method improves the network's performance.
**Table R3: Accuracy and energy efficiency of DCGS(Ours) across different models for semantic segmentation task on the PascalVOC dataset.**
| Architecture | ANN mIoU% \/energy ratio | n | T=2 | T=4 | T=6 | T=8 |
| -------- | -------------- | ----- | ----- | ----- | ----- | ----- |
| FCN_ResNet50| mIoU%: 64.2 | 2 | 4.0 | 10.1 | 19.8 | 36.0 |
| | energy ratio| 2 | 0.03 | 0.10 | 0.15 | 0.22 |
| FCN_ResNet50 | mIoU%: 64.2 | 4 | 51.8 | 60.5 | 62.7 | 64.0 |
| | energy ratio | 4 | 0.10 | 0.20 | 0.27 | 0.35 |
| FCN_ResNet50 | mIoU%: 64.2 | 8 | 61.0 | 64.3 | 64.6 | 64.5 |
| | energy ratio | 8 | 0.18 | 0.34 | 0.50 | 0.63 |
| Deeplabv3_ResNet50| mIoU%: 69.3 | 8 | 66.6 | 69.1 | 69.3 | 69.3 |
| | energy ratio| 8 | 0.08 | 0.32 | 0.46 | 0.58 |
**Table R4: Ablation Study of DCGS(Ours) on FCN_ResNet50 model for semantic segmentation task on the PascalVOC dataset.**
| Coding Type | Threshold Searching method | mIoU% \/energy ratio | n | T=2 | T=4 | T=6 | T=8 |
| -------- | -------------- |----- | ----- | ----- | ----- | ----- | ----- |
| Differential| Threshold Iteration |mIoU%| 8 | 61.0 | 64.3 | 64.6 | 64.5 |
| | |energy ratio| 8 | 0.18 | 0.34 | 0.50 | 0.63 |
| Rate| Threshold Iteration |mIoU%| 8 | 58.2 | 62.9 | 63.7 | 63.9 |
| | |energy ratio| 8 | 0.18 | 0.37 | 0.54 | 0.71 |
| Differential| 99.9% Large Activation |mIoU%| 8 | 61.2 | 64.3 | 64.5 | 64.4 |
| | |energy ratio| 8 | 0.18 | 0.35 | 0.51 | 0.64 |
## 2. In lines 426-427, the authors write "As shown in Table3, detailed results can be found in Appendix". I think the authors may want to rephrase it for better readability.
Thank you for your suggestion. We will revise this sentence to "The partial results are presented in Table 3, with a more detailed table provided in Appendix L.". What's more, in the final version, we will reshape Table 3 and Table 5 into line charts to more intuitively compare the different methods. | null | null | null | null | null | null | null | null |
Staged and Physics-Grounded Learning Framework with Hyperintensity Prior for Pre-Contrast MRI Synthesis | Accept (poster) | Summary: This paper is about using post-contrast MRI to create pre-contrast MRI via deep learning. Physics principles are built into the model. To tackle the complexity in setting up the model and its training, a two-stage approach is presented, which alleviates the challenge in handling the complexity. The approach is set up as an inpainting process that first learns about a mask in post-contrast MRI and then rebuilds the pre-contrast MRI.
Claims And Evidence: Yes
Methods And Evaluation Criteria: Yes
Theoretical Claims: Yes
Experimental Designs Or Analyses: Yes
Supplementary Material: Not applicable, no supplementary material.
Relation To Broader Scientific Literature: The paper is well related to the broader scientific literature and presents a method for reconstructing a missing modality in MRI.
Essential References Not Discussed: No
Other Strengths And Weaknesses: The strength can be found in two aspects. One is to construct pre-contrast MRI from post-contrast MRI, which is not well covered in existing research. The other is the inclusion of physics-based principles into the reconstruction model, but please see comments below.
Weaknesses are
1. Why dS_pre/dS_post appeared on both sides of Eq. (15)?
2. It is not clear how Eq. (19-20) derive the brightness prior H. By prior, it generally means the information known beforehand, for example, before MRI is acquired. But from Eq. (19-20), it seems the prior is derived from post-contrast MRI via auto-encoder and softmax, in this sense, it is unclear if that qualifies as prior information, unless I am missing something here.
Furthermore, is the prior H calculated slice-by-slice for a post-contrast MRI, or is it calculated only once for the whole post-contrast MRI series?
3. Why is there a need to use a regularization term in Eq. (22)?
4. How is \tau determined in Eq. (22)?
5. It is not clear how the deep learner in Stage 2 works or gets trained? Does it somehow incorporate the form of Eq. (11) in the deep learning model? Or is it just a deep learning model trying to mimic Eq. (11)?
6. How is the regularization term, Eq. (23), used in the loss function of Stage 1? This should be given in the main text instead of the appendix.
7. The practical applicability is a concern, as there are large number of weight parameters to tune, as given in Eq. (31) and (34). These many weight parameters may pose a difficult for users to select a good combination.
8. The relationship between Eq. (34) and Eq. (31) is confusing. It seems Eq. (34) includes the loss term given in Eq. (31), the inpainting+ loss, but according to the main text, an advantage of the paper is to separately train the masking step and inpainting step, then why does Eq. (34) involve Eq. (31)?
Other Comments Or Suggestions: Please refer to Strengths and Weaknesses.
Questions For Authors: Please refer to Strengths and Weaknesses.
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: Thank you for taking time and efforts to review our paper, your opinon is really appreciated. Thank you for acknowledging our work’s theoretical contribution, motivation and usage of the physcis principles. The goal of this project is to leverage the power of AI4Science to tackle unsolved challenges in MRI applications, which we believe is as equally important to achieving a higher score on well-studied tasks. For each weakness item, our response is listed as below.
1.The left is derivative, the right is partial derivative, which is minorly different.
2.Yes, we agree that ‘prior’ generally refers to information known beforehand, but it does not necessarily imply a temporal sequence in MRI scans. A more precise definition is: prior knowledge refers to any information about the problem beyond the training data. In our study, the prior is the assumption that contrast uptake regions typically appear hyperintense compared to non-enhanced areas [Line 201]. Equations 19–20 are designed to enforce this prior in a differential manner. The prior is preset for all training images.
3.Eq 22 defines the psudo ground truth for Stage 1, there is no regularization on it. But for the output of stage 1, we use regularization to ensure the model effectively learns the true hyperintensity prior like in [1]. The regularizer is assigned a low learning rate to avoid ruining the overall latent learning process.
4.The initial selection of τ is 0.1. This subtraction imaging technique, $\mathbf{S}{\text{post}} - \mathbf{S}{\text{pre}}$, is widely used in clinical practice [2] to capture contrast enhancement, with τ applied just to suppress background noise. Although τ is chosen empirically, its practical range is narrow (e.g., 0.08–0.12). A simple grid search on a few representative cases (e.g., τ ∈ [0.08, 0.10, 0.12]) is typically sufficient. We also explored different τ values in the ablation study (Reviewer 2, Item 1).
5.You are right! basically, the proposed model is trained to mimic Eq. 11. In our work, we disentangle the whole learning process to two stage learning. Different losses are designed to facilitate end-to-end model training. Similar to item 3, a light regularization term is applied to constraint the model to adapt to the physcis law.
6.Please refer to Item 3.
7.Thank you for raising this important question regarding the applicability of our model given the presence of nine weighting parameters (from Eq. 31 and 34). We offer two practical solutions:
(1) Use of Predefined Weights:
These weights were set based on the intrinsic properties of each loss function, not on specific data modalities or anatomies, and have yielded satisfactory results across scanners, sites, and anatomical regions. Below is the rationale for each:
* $\lambda_{\text{L1}} = 1$: Standard for pixel-wise accuracy.
* $\lambda_{\text{SSIM}} = 10$: SSIM ranges [0, 1], so we boost its contribution.
* $\lambda_{\text{perceptual}} = 0.5$: Operates on high-dimensional feature space, typically yielding larger values; thus, we scale it down.
* $\lambda_{\text{adv}} = 1$: Realism is equally important to pixel similarity.
* $\lambda_{\text{Inpaint+}} = 1$: We treat segmentation and inpainting as equally critical.
* $\lambda_{\text{ae}} = 1$: Autoencoder output should match L1-level fidelity.
* $\lambda_{\text{bce}} = 10$: BCE loss yields small values over binary masks; we scale it up for balance.
* $\lambda_{\text{hyper}} = 0.1$: Physics prior should guide but not dominate learning.
* $\lambda_{\text{psyn}} = 0.01$: Regularization terms are generally weighted lower to avoid over-constraining.
(2) Use of Normalized Loss Weighting:
Alternatively, we can apply a simple approach by setting$\lambda_{i} = \frac{1}{\mathcal{L}_i}$ for each loss term $\mathcal{L}_i$, allowing all objectives to converge uniformly.
These options support the generalizability and practical utility of our method without the need for extensive manual tuning.
8.While each stage has its own loss function, the model is trained end-to-end, similar to multi-task learning [3]. We apologize for the confusion and will clarify the separation of stage and final losses in future revisions.
Thank you again for your detailed and extensive comments, we are sorry our current manuscript might cause some confusion and misunderstanding, Hope our response can address the confusions. In later revision, we will update our manscript to make it clearer according to your comments. Feel free to let us know if there is any questions. Thank you!
Reference:
[1] Myronenko, Andriy. "3D MRI brain tumor segmentation using autoencoder regularization." Springer International Publishing, 2018.
[2] Hubbard, C., et al. The use of MRI digital subtraction technique in the diagnosis of traumatic pancreatic injury. Radiology Case Reports, 14(5), 639-645.
[3] Zhang, Y., & Yang, Q. (2018). An overview of multi-task learning. National Science Review, 5(1), 30-43. | Summary: This work discusses a deep learning method for recovering pre-contrasted MRI from post-contrasted MRI. The authors propose to first estimate a thresholded map as a mask indicating contrast agent update. This mask is then fed as an additional conditioning signal for recovering the pre-contrast image. The authors also discussed an artifact removal approach for enhancing pre-contrast images. The proposed framework is evaluated against several other types of basic feed forward neural network architectures.
## update after rebuttal
I would like to thank the authors for the efforts especially for the additional comparisons and clarifications.
With that being said, I still find the manuscript suffers somehow from unjustified claims / design choices and flaws in writing structures that are very unlikely to be addressed in a revision (and it may not be of the best practice to first introducing two heavy components: AE and a complicated artefact removal framework which had led to quite a lot confusions and then suddenly claiming they are not essential or are just for extension purpose). Also, the huge amount of hyper-parameters (as pointed out by Reviewer `pkvY`) render the proposed framework very difficult to be applied to other datasets by readers. I would therefore keep my current rating.
Claims And Evidence: Claim: Line 095 left: The proposed work "present a significant advancement in MRI image by developing a method capable of generating high-quality pre-contrast images"
Fact check: This claim cannot be substantiated unless being compared with commonly used medical image translation / quality enhancement methods such as [1-6]. Given the similar mathematical formulation (pixel to pixel mapping), even some of them are originally designed for slightly different purpose, re-purposing them to the pre-contrast recovery should be straightforward.
Claim: Line 058 right: The proposed methods are extensively evaluated on two real-world datasets we collected from two hospitals, demonstrating their robustness.
Fact check: Robustness are normally characterized by stable performance against OOD data or adversarial samples at test time. Unlikely to be the case described in the Experiment section.
Claim: Training a simple image-to-image synthesis network to map Post-Contrast to Pre-Contrast images often fails to balance the synthesis of the structural and contrast information in the image.
Fact check: Line 158 left: M is still a function of S_{post} though.
Claim: Line 195 left: "...a conventional deep segmentation model to guarantee model precision and robustness ..."
Fact check: convolutional segmentation models alone cannot guarantee model precision and robustness without proper training data / training approach.
Claim: Eq. 16 The proposed method reduced the complexity from multiplicative to additive.
Fact check: It is unclear how Eq. 16 is reached given the sequential nature of Eq. 11 and 12.
Claim Line 265 right: "these methods represent the golden standard approaches in image enhancement, segmentation, and synthesis."
Fact check: No evidence. E.g. for image enhancement and synthesis there exists much more advanced methods such as [1-6].
1. Adaptive latent diffusion model for 3d medical image to image translation: Multi-modal magnetic resonance imaging study
2. Unsupervised Medical Image Translation With Adversarial Diffusion Models
3. DuDoDR-Net: Dual-domain data consistent recurrent network for simultaneous sparse view and metal artifact reduction in computed tomography
4. Target-guided diffusion models for unpaired cross-modality medical image translation
5. Cascaded multi-path shortcut diffusion model for medical image translation
6. A generic deep learning model for reduced gadolinium dose in contrast‐enhanced brain MRI
Methods And Evaluation Criteria: The evaluation metrics are relevant. However, given that most experiments are performed on two in-house datasets, the reproducibility of the proposed work is unclear.
Theoretical Claims: The proposed work is mostly empirical. Please find my additional comments in `Claims And Evidence` section.
Experimental Designs Or Analyses: The claimed superiority cannot be substantiated without systematic comparisons with recent medical image enhancement / modality translation / artifact removal works, such as [1-6]. Given the similar mathematical formulation (pixel to pixel mapping), even some of them are originally designed for slightly different purposes, applying them to pre-contrast recovery should be straightforward.
Supplementary Material: The supplementary material discusses evaluation metrics, training losses (which should be put into main text), gradient dynamics, in addition to discussions on some design choices.
Relation To Broader Scientific Literature: This work falls into the categories of medical image quality enhancement / modality translation / artifact removal, given the similar mathematical formulations.
Essential References Not Discussed: Works on medical image enhancement / modality translation / artifact removal, such as [1-6] should be discussed, given the similar mathematical formulations (learning pixel to pixel mappings in image intensity domain).
Other Strengths And Weaknesses: Strengths:
- The authors have presented the mathematical model for image contrast enhancement.
- Improved performances are shown compared with experimented neural networks.
Weaknesses:
- The paper suffer from a lack of rationale for many design choices: E.g., Why do the authors process S_{post} with an autoencoder?
Sec. 2.3 can be distracting as it is not closely centered at the pre-contrast recovery problem.
- The motivation for processing S_{post} with AE is unclear.
- The threshold \tau is subject to manual choice and it is critical for defining M_{true}. Given the heterogeneity in real-world MRI acquisition and its non-quantitative nature choosing a proper \tau can be difficult in real world.
- Artifact removal: It is related but not centered on the pre-contrast recovery. It should instead be put as a standalone work and carefully assessed alone. Also, little information about the rationale behind and the methodology is presented in the main text.
Other Comments Or Suggestions: N/A
Questions For Authors: Given that most experiments are performed on two in-house datasets, how would the reproducibility of the proposed work be assessed?
Ethical Review Concerns: N/A, given the claims in line 236-237 right.
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: Thank you for your in-depth review of our manuscript. Your comments are constructive and will help improve the quality of our work. In this manuscript, we propose a novel MRI theory-driven method to address a challenging problem in MRI imaging. Please find our detailed responses to your comments below:
Claim:
1.(Comparison to other methods such as {1-6}): Thank you for raising this point. Per your suggestion, we conducted three additional comparative experiments using models No. 2, 3, and 6 from your recommended list. For No. 3 and 6, we adapted them to the same pipeline used by SPHERE. For the Syn-Diff model (No. 2), we trained it for 40 epochs, which took approximately 80 hours on two A100 GPUs. The quantitative results are summarized as follows:
Tab 5. Additional Comparasions
| Models | PSNR ↑ | SSIM ↑ | CNR ↓ | LPIPS ↓ | GMSD ↓ | CFS ↑ | IRC ↑ | EIS ↑ |
|------------------|---------|--------|--------|--------|--------|--------|--------|--------|
| DuDoDR-Net | 32.6218 | 0.7974 | 0.1078 | 0.0738 | 0.0404 | 0.6854 | 0.8143 | 0.2222 |
| Dose Reduction | 34.8808 | 0.8665 | 0.0804 | 0.0492 | 0.0358 | 0.8450 | 0.7847 | 0.3941 |
| Syn-Diff | 35.7180 | 0.8961 | 0.0728 | 0.0337 | 0.0325 | 0.7068 | 0.8633 | 0.5434 |
| SPHERE* | 36.8244 | 0.9026 | 0.0628 | 0.0313 | 0.0315 | 0.9181 | 0.8684 | 0.5364 |
Please also refer to Fig 3. in https://anonymous.4open.science/r/ICML25_rebuttal-63F3 for qualitative evaluation. DuDoDR-NET and Dose Reduction perform significantly worse, while Syn-Diff indicates somewhat closer results. However, it overemphasizes background regions and fails on pathological structures. These outcomes further support our claim that existing models struggle to balance structural fidelity and contrast enhancement. In contrast, our model provides the most effective solution to this challenging task.
2.(Line 058 right): We totally agree with you on this, Sorry for this mistake.
3.(M is still a function of S_{post}), we will add one more equation of M in terms of S_{post} to make it clearer.
4.(Line 195 left): Yes, the output of the arbitrary segmentation model is combined with the Hyperintensity branch to make a fused prediction, the loss function is applied on the fused prediction for training. We will refine the wording in revision.
5.(Unclear how Eq. 16 is reached): Yes, as noted, our task inherently involves a sequential combination of segmentation and inpainting+ subtasks. With our dual stage learning, the complexity is additive with modular training [1]. However, directly modeling these together with a single network needs to encode all segmentation-to-inpainting mappings simultaneously. This multiplicative complexity arises naturally from the fact that the model needs encode every possible combination of segmentation-to-inpainting mappings. We will explicitly clarify this rationale in our revision.
6.[Evaluation in-house datasets] In this study, we tried our best to evaluate our model more extensively like across multiple datasets, sites, anatomies, and downstream tasks. But I am sorry we cannot disclose datasets due to license constrait. In future, we plan to apply our model to public datasets to further support reproducibility.
Weakness:
1,2. The autoencoder is a marginal component of our model. It works with a scaling factor to adjust image intensity, which mgiht also be handled by raw input. We keep it to subtly suppress non-structural noise, making hyperintensity extraction more robust. Though not explicitly designed for denoising, the AE learns compressed bottleneck representations that capture structural and semantic manifold, naturally reducing inconsistent noise or redundancy [2]. We apologize for missing this rationale and will include it in the next revision. An ablation study on the AE is also provided in Fig 4. in Link for details. Overall, we find AE marginally beneficial.
3.Please refer to Reviewer #4 Item 4.
4.The artifact removal component is included to extend our model’s applicability to scenarios with corrupted images. The current implementation serves as a proof of concept, and we plan to explore it further in future work.
Thank you again for taking the time to rigorously review our paper! Your comments will undoubtedly enhance the overall quality of our work like on the model rationale. We sincerely appreciate your thoughtful feedback. Please feel free to reach out if you have any further questions.
Reference
[1] Leung, K. H., et al (2020). A physics-guided modular deep-learning based automated framework for tumor segmentation in PET. Physics in Medicine & Biology, 65(24), 245032.
[2] Bartlett, O. J., et. al (2023). Noise reduction in single-shot images using an auto-encoder. The Royal Astronomical Society, 521(4), 6318-6329. | Summary: This paper proposes SPHERE, a staged and physics-grounded learning framework for synthesizing Pre-Contrast MRI images from Post-Contrast MRI scans. The key innovation lies in incorporating MRI physics principles and a hyperintensity prior into a two-stage deep learning model. The framework consists of segmentation and inpainting. Extensive experiments on multi-site MRI datasets demonstrate that SPHERE outperforms existing deep learning methods across multiple metrics and generalizes well to spine and breast MRI applications. The method also extends to artifact removal for corrupted Pre-Contrast images. The approach has potential clinical significance by reducing the need for additional imaging sessions, cost, and patient risk.
Claims And Evidence: Claim 1: SPHERE synthesizes clinically viable Pre-Contrast MRI images from Post-Contrast scans.
Evidence:
The method is tested on two large, real-world MRI datasets from multiple sites and scanners. It achieves higher PSNR, SSIM, and CNR compared to baseline models, supporting the claim of high-fidelity image synthesis.
Claim 2: The two-stage learning framework improves synthesis quality over direct image-to-image translation.
Evidence:
The paper provides a mathematical derivation of the complexity reduction and gradient stability benefits of the two-stage approach. Empirical results show that SPHERE outperforms state-of-the-art methods, which struggle with contrast preservation and structural accuracy.
Claim 3:
The hyperintensity prior improves contrast segmentation and Pre-Contrast reconstruction.
Evidence: The segmentation results demonstrate that incorporating a hyperintensity prior enhances contrast region detection. Comparative experiments indicate improved structural and contrast preservation.
Claim 4: SPHERE generalizes to other medical imaging tasks.
Evidence:
The model is fine-tuned on spine and breast MRI datasets, achieving strong quantitative results, demonstrating adaptability beyond brain MRI.
Weaknesses in evidence:
Weakness 1: The effectiveness of the hyperintensity prior is mentioned, but an explicit ablation study isolating its impact is missing.
Weakness 2: While the results indicate strong performance, validation with radiologists or clinical usability studies would further substantiate the claim of clinical applicability.
Methods And Evaluation Criteria: The proposed MRI physics guided SPHERE framework is well-aligned with the problem of Pre-Contrast MRI synthesis. The two-stage learning approach, incorporating a hyperintensity prior, is a well-motivated methodological choice. The formulation effectively addresses the limitations of direct image-to-image translation by improving contrast segmentation and synthesis accuracy.
The evaluation criteria are appropriate for assessing image synthesis quality. The authors use standard image quality metrics, including PSNR, SSIM, CNR, and LPIPS, which are widely accepted for medical image analysis. The inclusion of multi-site, multi-scanner datasets enhances the robustness and generalizability of the findings. Additionally, downstream tasks (e.g., low-dose contrast simulation, spine and breast MRI applications) provide further validation of clinical utility.
Theoretical Claims: Yes
Experimental Designs Or Analyses: Yes
Supplementary Material: Yes
Relation To Broader Scientific Literature: This paper builds on existing work in medical image synthesis, MRI reconstruction, and physics-informed deep learning while introducing a novel two-stage, physics-grounded approach for Pre-Contrast MRI synthesis.
Medical image synthesis:
Prior works, such as UNet-based image-to-image translation and transformer-based synthesis models, have been applied to MRI reconstruction but often fail to preserve contrast details when synthesizing missing sequences.
The proposed SPHERE framework extends these efforts by explicitly modeling MRI physics to improve synthesis quality.
Physics-Guided deep learning in MRI:
The paper aligns with trends in physics-informed learning. Unlike purely data-driven approaches, SPHERE incorporates MRI signal equations to constrain the learning process, similar to prior work in quantitative MRI reconstruction.
Essential References Not Discussed: No
Other Strengths And Weaknesses: Strengths
1. The paper presents a novel two-stage physics-grounded approach for Pre-Contrast MRI synthesis, integrating MRI signal modeling with deep learning, which is an innovative contribution beyond purely data-driven synthesis methods.
2. The method addresses a practical problem in medical imaging, reducing the need for additional scans, which could lead to cost savings and reduced patient risk. The evaluation on real-world multi-site datasets enhances its potential clinical impact.
3. The experiments are rigorous and diverse, including:
Comparisons with strong baselines (UNet, SwinIR, UKAN).
Multiple quantitative metrics (PSNR, SSIM, CNR, LPIPS).
Downstream clinical applications (spine, breast MRI, and low-dose contrast simulation).
4. The paper is generally well-structured with detailed methodological explanations.
Weaknesses
1. While the paper presents intuitive justifications for the hyperintensity prior and two-stage framework, an explicit ablation study quantifying their contributions is missing.
2. The two-stage design is claimed to be computationally more efficient, but there are no runtime comparisons or training time analyses to support this claim.
3. While the method performs well quantitatively, there is no validation by radiologists to confirm the clinical realism and usability of the synthesized Pre-Contrast images.
Other Comments Or Suggestions: No
Questions For Authors: No
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your meticulous and comprehensive review. We appreciate your recognition of our work on quantitative performance, mathematical support, prior knowledge incorporation, and model generalizability. Regarding the identified weaknesses, we provide the following responses:
1.Yes, the hyperintensity prior and two-stage framework are two critical components of our model, and quantifying their contribution to performance is important. We have added ablation studies on key components such as the Hyperintensity Prior, the Arbitrary Segmentation Branch, the Autoencoder module, the Dual Learning stage, and selection of τ.
Tab 3. Ablation study on different modules and τ selection.
| Configuration | PSNR ↑ | SSIM ↑ | CNR ↓ | LPIPS ↓ | GMSD ↓ | CFS ↑ | IRC ↑ | EIS ↑ |
|----------------------------|---------|--------|--------|--------|--------|--------|--------|--------|
| W/o Hyperintensity | 35.7608 | 0.8842 | 0.0729 | 0.0434 | 0.0356 | 0.8970 | 0.8252 | 0.4041 |
| W/o Abitrary Seg | 36.3764 | 0.8951 | 0.0666 | 0.0346 | 0.0337 | 0.9068 | 0.8558 | 0.4703 |
| W/o AE | 36.6764 | 0.9006 | 0.0635 | 0.0321 | 0.0328 | 0.9119 | 0.8585 | 0.5075 |
| W/o Dual Step | 34.5522 | 0.8580 | 0.0836 | 0.0479 | 0.0362 | 0.8462 | 0.8454 | 0.3746 |
| SPHERE* | 36.8244 | 0.9026 | 0.0628 | 0.0313 | 0.0315 | 0.9181 | 0.8684 | 0.5364 |
| **τ selection** | | | | | | | | |
| τ = 0.06 | 35.7835 | 0.8990 | 0.0651 | 0.0366 | 0.0320 | 0.9109 | 0.8560 | 0.5366 |
| τ = 0.08 | 36.8841 | 0.9034 | 0.0628 | 0.0298 | 0.0315 | 0.9179 | 0.8676 | 0.5319 |
| τ = 0.10 | 36.8244 | 0.9026 | 0.0628 | 0.0313 | 0.0315 | 0.9181 | 0.8684 | 0.5364 |
| τ = 0.12 | 36.8759 | 0.9035 | 0.0624 | 0.0299 | 0.0317 | 0.9176 | 0.8687 | 0.5333 |
| τ = 0.14 | 36.7256 | 0.9008 | 0.0635 | 0.0313 | 0.0320 | 0.9097 | 0.8702 | 0.5246 |
Above quantitative and qualitative results in Fig. 4 on https://anonymous.4open.science/r/ICML25_rebuttal-63F3 shows that the key component such as Dual stage learning, Hyperintensity, and arbitrary seg are all beneficial to the model performances to different extents. For the τ selection, values in the range of 0.08–0.14 generally yield consistent performance with minimal variation. This suggests that our model is not highly sensitive to exact choice of τ, indicating robustness and fewer constraints on hyperparameter tuning.
2.We actually do not intend to claim the computational efficency, Instead, we aim to highlight that the learning complexity or difficulty of the dual-stage learning method is lower than that of direct learning, as shown in Eq. 17. This does not necessarily imply faster model runtime. We apologize for any misunderstanding this may have caused. In terms of inference time, we added an runtime analysis per your request. Two metrics including throughput and latency are employed to measure the model runtime. Results are shown as below:
Tab 4. Runtime Analysis
| Runtime Metric | UNet | Att-UNet | UNet++ | SwinIR | UKAN | MambaIR | BICEPS | SPHERE* | SPHERE* (FP16) |
|----------------------|------|----------|--------|--------|------|---------|--------|---------|----------------|
| Throughput (I/s) | 1.12 | 1.06 | 0.97 | 1.04 | 1.10 | 1.33 | 1.06 | 0.45 | 0.59 |
| Latency (s/I) | 0.89 | 0.94 | 1.03 | 0.96 | 0.91 | 0.75 | 0.94 | 2.20 | 1.69 |
As shown in the table, the model speed of the proposed method is approximately 2× slower than other methods due to the dual-stage design. From an application perspective, we consider post-processing of a DICOM series within or ~ 5 minutes to be clinically viable. The current runtime of SPHERE (FP16) roughly meets this criterion (~177 slices in 5m). If further acceleration is needed on high resolution 3D scan, we can refer to TensorRT or Triton for faster inference on deployment. For training on a single A100 GPU, the time required for a direct learning model such as UNet++ is 2.02h, while SPHERE requires 6.10h due to its dual-stage optimization. We have also benchmarked the training time on different hardware platforms including V100, A100, and H100. Our latest setup enables training completion in 3.1 hours, significantly accelerating model development. Please refer to Fig. 5 in the external link for more details. So, we can conclude that our dual design may need more runtime for training/inference, but within the clinically acceptable range. Thank you for raising this valuable point. We will include it in the main text in a later revision.
3. Please refer to Reviewer #1 item 1, thanks.
Thank you again for your careful review of our paper, your acknowledegement of our work is really inspiring to us, and we hope we addressed your concerns, if there is any other questions, feel free to let us know! Thank you! | Summary: This paper proposes a novel staged, physics-grounded learning framework with a hyperintensity prior to synthesize Pre-Contrast images directly from Post-Contrast MRIs. The proposed method can generate high-quality Pre-Contrast images, thus, enabling comprehensive diagnostics while reducing the need for additional imaging sessions, costs, and patient risks. The authors claim it is the first Pre-Contrast synthesis model capable of generating images that may be interchangeably used with standard-of-care Pre-Contrast images. Extensive evaluations across multiple datasets, sites, anatomies, and downstream tasks demonstrate the model’s robustness and clinical applicability, positioning it as a valuable tool for contrast-enhanced MRI workflows.
## Update after rebuttal:
I appreciate the authors’ responses to my questions, especially involving experts to assess the quality of the synthesized pre-contrast images. I have updated my score accordingly.
However, I'd like to point out that if you use a t-test to check the significance of the 'Reader Scores', you will find no significant differences between them, for example, 4.00 ± 0.00 vs. 3.89 ± 0.31. You might need to reformulate your words instead of claiming 'consistently outperform', which doesn't impact your conclusion, though.
Claims And Evidence: Yes
Methods And Evaluation Criteria: Yes
Theoretical Claims: N/A
Experimental Designs Or Analyses: Yes. The whole experimental sections.
Supplementary Material: Kind of. The evaluation metric and loss funciton.
Relation To Broader Scientific Literature: The paper can be used to deal with the real-world MRI generation problem.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: Strengths:
1. The two-stage training paradigm (initial physics-based augmentation followed by deep-learning-based synthesis) seems innovative.
2. The proposed model achieves better results (quantitatively and qualitatively) compared to prior work, indicating the success of integrating domain knowledge into the learning process.
3. The proposed approach has the potential to reduce the need for multiple MRI scans while maintaining diagnostic quality.
Weaknesses:
1. It is unclear how well the generated synthetic pre-contrast images preserve pathology-related features in conditions like tumors, multiple sclerosis, or stroke. I am expecting to see more in-depth clinical validations as this paper focuses on real-world problems
2. How can the proposed method be generalized to different MRI sequences and modalities?
3. I am also wondering how each component of the proposed method benefic the performances. Could you please provide a more detailed ablation study to explicitly evaluate the impact of individual components?
Other Comments Or Suggestions: N/A
Questions For Authors: N/A
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for reviewing our manuscript from the clinical application perspective, your comments are truly constructive for us. We appreciate your recognition of our novelty, integration of domain knowledge, and potential clinical applicability. The motivation of our study is to provide a theoretically supported AI solution to address an unsolved application problem in MR imaging. Regarding the weakness, we provide the responses as below: (an External Link for Results Visualization: https://anonymous.4open.science/r/ICML25_rebuttal-63F3)
1.Thank you for raising this concern about clinical validation. We have invited two independent radiologists to comprehensively assess the quality of the synthesized pre-contrast images in comparison to the SOC pre-contrast images. Reader #1 has over 15 years of clinical experience in radiology, and Reader #2 has over 10 years. A total of 15 cases were reviewed. The pathologies included tumors, GBM (glioblastoma), lymphoma (CNS and Hodgkin’s-related), anaplastic astrocytoma, meningioma, oligoastrocytoma, Von Hippel-Lindau disease, and fungal/parasitic infection. Five metrics were used: Perceived Image Quality, Anatomical Alignment, Tissue Visualization (Usability with Post), Diagnostic Value (when +Post), and Imaging Artifacts. All metrics were scored using a 1–4 Likert scale. Please refer to Table 1 in the link for more metric details. The results from both readers are summarized as follows (see Fig. 1 and Fig. 2 in the link for additional statistical analysis and visualized results):
Tab 2. Reader Scores
| Metric | Syn-Pre Mean ± SD, | Syn-Pre Quartiles, | SOC-Pre Mean ± SD, | SOC-Pre Quartiles |
|-------------------------------|-------------------|-------------------|-------------------|-------------------|
| Perceived Image Quality | 3.96 ± 0.19 | 4.00, 4.00 | 3.64 ± 0.49 | 3.00, 4.00 |
| Anatomical alignment | 3.96 ± 0.19 | 4.00, 4.00 | 3.75 ± 0.52 | 4.00, 4.00 |
| Tissure Visualization | 3.68 ± 0.43 | 3.50, 4.00 | 3.86 ± 0.30 | 4.00, 4.00 |
| Diagnosis Value | 3.68 ± 0.55 | 3.00, 4.00 | 3.86 ± 0.36 | 4.00, 4.00 |
| Imaging Artifacts | 4.00 ± 0.00 | 4.00, 4.00 | 3.89 ± 0.31 | 4.00, 4.00 |
As demonstrated by the results, the Syn-Pre images consistently perform better or comparable to SOC-Pre in several important aspects. Specifically, Syn-Pre achieved higher scores in perceived image quality (3.96 ± 0.19 vs. 3.64 ± 0.49), anatomical alignment with post-contrast (3.96 ± 0.19 vs. 3.75 ± 0.52), and imaging artifacts (4.00 ± 0.00 vs. 3.89 ± 0.31), suggesting superior visual clarity, structural coherence, and reduced noise. While visualization of tissue (3.68 ± 0.43 vs. 3.86 ± 0.30) and diagnostic value when paired with post-contrast (3.68 ± 0.55 vs. 3.86 ± 0.36) scored slightly lower for Syn-Pre, the difference remains minimal and clinically acceptable. Specifically, 12 out of 15 cases were rated equivalent to SOC-Pre in these two metrics, with only 3 cases showing slight degradation. To further quantify this, one-sided Wilcoxon signed-rank tests were conducted under the null hypothesis that Syn-Pre underperforms SOC-Pre by ≥0.16 points. The resulting P-values are 0.0159 for tissue structure and 0.0003 for diagnostic value. Therefore, we reject this null hypothesis and confirm that Syn-Pre is not meaningfully worse. Together, these reader study results together with the extensive evaluations reinforce the strong performance and the practical viability of Syn-Pre as a reliable substitute when SOC-Pre images are unavailable or suboptimal.
2.For the common MRI sequences or modalities such as T1, T2, T2FLAIR, T2STAR, TOF, TRICKS, ADC, ASL, DWI, LOC, SSFP, and SWI, gadolinium-based contrast agents (GBCAs) are predominantly used in T1-weighted imaging, which serves as the clinical standard for contrast enhancement [1]. We acknowledge that contrast agents have limited but notable applications in other sequences such as T2-STIR, TOF, and SWI. The fundamental prerequisite for applying our method is the presence of hyperintense in the post-contrast images, which are not visible in the pre-contrast images. When this condition is met, our dual-stage learning framework which is driven by hyperintensity priors, can theoretically be extended to other sequences beyond T1. In future work, we plan to explore the generalizability of our approach to additional modalities.
3.Please refer to Reviewer #2 item 1.
Thank you again for taking time and efforts to review our paper, please feel free to raise a question if there is any confusion. Thank you!
Reference
[1] Lohrke, Jessica, et al. "25 years of contrast-enhanced MRI: developments, current challenges and future perspectives." Advances in therapy 33 (2016): 1-28. | null | null | null | null | null | null |
Enhancing Adversarial Robustness with Conformal Prediction: A Framework for Guaranteed Model Reliability | Accept (poster) | Summary: This paper studies adversarial robustness of Conformal Prediction. Specifically, this paper develops an attack method that does not require coverage guarantees and integrates it with a conformal training-based defense strategy by minimizing the size of the prediction sets under adversarial perturbations while maintaining high coverage probabilities. Experimental evaluations on the CIFAR10 and CIFAR-100 datasets show that the attack method induces greater uncertainty compared to baseline approaches, while the defensive model significantly enhances robustness against various adversarial attacks for most cases.
Claims And Evidence: Yes.
Methods And Evaluation Criteria: Yes.
Theoretical Claims: The proof is not checked.
Experimental Designs Or Analyses: Yes.
Supplementary Material: Not attached.
Relation To Broader Scientific Literature: The proposed adversarial training method is tailored for conformal prediction.
Essential References Not Discussed: NA
Other Strengths And Weaknesses: Strength:
1. The paper is well-written and easy to follow.
Weaknesses:
1. The effectiveness of the proposed adversarial training method is not clearly evident in the experimental results. Regarding attacks, the proposed attack method indeed achieves the largest set size as it’s designed to maximize the set size. However, in terms of defense, in cifar100, the proposed OPSA-AT only achieves the best set size against 50% attacks (3 out 6). Note that the authors only experiment on cifar10 and cifar100 datasets (50% datasets) and OPSA-AT is trained to maintain a small set size against attacks, showing that the effectiveness of the proposed method is not adequate. Additionally, in terms of another metric, SSCV, the dominance of the proposed method is also not clear on cifar10 dataset.
Other Comments Or Suggestions: 1. In eqn 13, there is no $\delta$ but $\delta $ is mentioned below.
2. The definition of eqn 16 is not clear. It denotes a scaler, or a vector, or a set? $k$ is mentioned above but not appears in the equation.
3. In Eqn 19, what is $B_{\pi(1)}$ ?
4. Table 1 and table 2 are really hard to understand and parse. It is recommended to enhance the presentation to make key information clear.
Questions For Authors: 1. In Table 1,2, why is the most effective attack method to increase SSCV the clean images themselves? It seems that the designed attack methods are unnecessary and meaningless as clean image is the best one.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We appreciate the recognition of our paper’s clarity and thank the reviewer for their careful attention to detail. While we share many points of agreement, the main misunderstanding lies in the interpretation of outcomes, which we would like to clarify.
**Tabular Data Interpretation**:
We will expand the text explanations to provide more detail on Table 1 and Table 2 from the paper. Both tables follow a similar structure, with each row representing a specific metric for different defense models under a particular attack on the test set. To compare defense methods, focus on each row, where coverage is approximately the same (ideally around 90%), with slight variations due to sampling differences. For the 'Size' metric, smaller values are better, and the same applies to SSCV—lower values are preferred. To compare attack methods, look at each column. Unlike the defense metrics, a larger size and SSCV indicate a more effective attack method.
**Experimental Outcome Interpretation**:
First, we must clarify that we utilized the **complete** CIFAR-10 and CIFAR-100 datasets, with training sets for model training and test sets split (20% for calibration, 80% for testing).
Second, in conformal prediction, a key research question is how to minimize uncertainty (prediction set size) while maintaining equivalent coverage probability. Indeed, Coverage and SSCV results show some instability in measuring attacks, with clean images exhibiting higher SSCV than attacks. As with the accuracies ([A, B, C]), this outcome is expected. The inherent trade-off between adversarial robustness and SSCV naturally leads to this phenomenon. Similar to TRADES and MART, SSCV is not maximized on the clean dataset because the training process specifically accounts for clean data.
Third, in terms of defense, OPSA-AT achieves the best set size at 3/6 on CIFAR-100 but achieves 5/6 on CIFAR-10. Even when OPSA-AT is not the best on some attacks, it achieves the second-best performance. No other defense reaches such good performance on CIFAR-10 and CIFAR-100. Considering overall performance, we still believe our defense is effective. To further support our arguments, we carry out experiments on ImageNetMini, where OPSA-AT outperforms other defenses on Size (see Table 2 of response to Reviewer uZo5)
**Formula Issues**:
Typo in Equation 13: We apologize for incorrectly changing "$\delta$" to "p" in Equation 13 and have corrected this error.
Definition issue of Equation 16: Equation 16 is central to conformal training, constructed as a differentiable loss function to approximate a hard threshold. It is similar to Equation 13 but differs in that, for defensive purposes, we need to consider coverage, so Equation 16 subtracts the calculated tau value over B_cal.
Clarification for Equation 19: $\mathcal{B}_{\pi(1)}$ is simply the mini-batch that appears in the first position after a permutation $\pi$ is applied to the indices of the mini-batches. The exchangeability property ensures that the statistical properties of the mini-batches remain unchanged under any reordering (as in [D]).
[A] Zhang, Hongyang, $et$ $al$. ''Theoretically principled trade-off between robustness and accuracy." International conference on machine learning. PMLR (2019).
[B] Dobriban, Edgar, $et$ $al$. ''Provable tradeoffs in adversarially robust classification." IEEE Transactions on Information Theory (2023).
[C] Robey, Alexander, $et$ $al$. ''Adversarial Training Should Be Cast as a Non-Zero-Sum Game." The Twelfth International Conference on Learning Representations. ICLR (2024).
[D] Li, Yangyi, et al. "Data Poisoning Attacks against Conformal Prediction." International Conference on Machine Learning. PMLR (2024).
---
Rebuttal Comment 1.1:
Comment: Thanks for the author's efforts. Some of my concerns have been addressed and I agree to raise the score to weak accept. However the concern about empirical performance still exists as "OPSA-AT achieves the best set size at 3/6 on CIFAR-100 but achieves 5/6 on CIFAR-10" is not satisfactory considering the method targets the set size metric.
---
Reply to Comment 1.1.1:
Comment: # Response to Concerns About Empirical Validation
Thank you for further elaborating on your concern regarding empirical validation. We would like to address this point in more detail.
Our method was trained for only 10 epochs; however, if we increase the number of training epochs, **our approach continues to improve in performance, whereas the performance of other defenses tends to degrade**. This is because our method incorporates adversarial training within a non-zero-sum game framework, similar to methodologies in [A], which **effectively mitigates model overfitting**.
Due to time constraints, as shown in Table 6, we trained both TRADES and OPSA-AT models for 20 epochs; these defenses were previously among the top two on CIFAR-100 when trained for just 10 epochs. Our defense outperforms TRADES with 20-epoch training under PGD10, PGD40, and OPSA attacks, where TRADES performs better with 10-epoch training. Furthermore, **TRADES began to overfit, with its metric Size increasing 10%, whereas our method continued to improve and achieved the smallest metric Size under OPSA attacks**. We are confident that with 50 or 100 epochs of training and selecting the best model for each defense approach, our OPSA-AT would outperform the others completely. However, due to computational resource constraints and our intention to adhere to the protocols of related work, we did not perform this additional training at the beginning.
The key message here is that **our defense, OPSA-AT, has a stronger learning capacity: it continues improving with extended training, whereas other defenses tend to plateau or degrade.** We acknowledge that this point was not addressed in the current version and will ensure it is included in the final revision.
## Table 6: Mean and Standard Deviation of Coverage, Size, and SSCV for CIFAR100
| **Attacks** | **Indicator** | **TRADES²⁰** | **OPSA-AT²⁰** |
|-------------|---------------|--------------|---------------|
| **PGD¹⁰** | Coverage (%) | 89.99 ± 0.33 | 90.15 ± 0.34 |
| | Size | 42.49 ± 0.28 | 33.68 ± 0.32 |
| | SSCV | 0.03 ± 0.01 | 0.06 ± 0.00 |
| **PGD⁴⁰** | Coverage (%) | 89.94 ± 0.33 | 90.10 ± 0.33 |
| | Size | 42.46 ± 0.29 | 33.56 ± 0.31 |
| | SSCV | 0.03 ± 0.01 | 0.06 ± 0.00 |
| **OPSA¹⁰** | Coverage (%) | 90.10 ± 0.34 | 90.50 ± 0.32 |
| | Size | 43.20 ± 0.28 | 31.43 ± 0.29 |
| | SSCV | 0.06 ± 0.01 | 0.03 ± 0.00 |
Furthermore, we aim to highlight that our defense's learning capability also extends to larger datasets. As shown in Table 7, even with just 5 training epochs on the ImageNet-Mini dataset, our model exhibited superior parameter efficiency across all evaluated attacks. We acknowledge the limitation of only 5 epochs in the current setting, but under this shortened training period, OPSA-AT already achieves strong performance, and we expect significantly enhanced robustness upon completing the full 10-epoch training.
In summary, these results collectively support the effectiveness of our proposed defense framework, and we will include them in the final version of the paper.
## Table 7: Mean and Standard Deviation of Coverage, Size, and SSCV for ImageNetmini
| **Attacks** | **Indicator** | **TRADES⁵** | **MART⁵** | **OPSA-AT⁵** |
|-------------|---------------|-------------|-----------|--------------|
| **Clean** | Coverage (%) | 89.64 ± 0.50 | 89.69 ± 0.50 | 89.69 ± 0.48 |
| | Size | 18.55 ± 0.11 | 20.62 ± 0.12 | 17.01 ± 0.18 |
| | SSCV | 0.08 ± 0.01 | 0.07 ± 0.01 | 0.10 ± 0.01 |
| **FGSM** | Coverage (%) | 89.48 ± 0.50 | 90.34 ± 0.50 | 89.51 ± 0.49 |
| | Size | 39.01 ± 0.12 | 48.88 ± 0.11 | 30.41 ± 0.23 |
| | SSCV | 0.07 ± 0.11 | 0.10 ± 0.00 | 0.08 ± 0.02 |
| **PGD¹⁰** | Coverage (%) | 89.38 ± 0.49 | 90.44 ± 0.46 | 89.66 ± 0.49 |
| | Size | 38.11 ± 0.12 | 50.35 ± 0.10 | 34.88 ± 0.24 |
| | SSCV | 0.05 ± 0.01 | 0.01 ± 0.00 | 0.14 ± 0.03 |
| **OPSA¹⁰** | Coverage (%) | 89.71 ± 0.48 | 90.47 ± 0.46 | 89.95 ± 0.46 |
| | Size | 40.92 ± 0.12 | 50.52 ± 0.09 | 35.63 ± 0.02 |
| | SSCV | 0.23 ± 0.24 | 0.10 ± 0.00 | 0.11 ± 0.04 |
[A] Robey, Alexander, $et$ $al$. ''Adversarial Training Should Be Cast as a Non-Zero-Sum Game." The Twelfth International Conference on Learning Representations. ICLR (2024). | Summary: The paper proposed a conformal prediction based adversarial attack and training method. To enable computationally tractable implementations, the authors propose a smoothed surrogate loss. The attack and defense methods are tested on CIFAR10 and CIFAR100.
## update after rebuttal
I believe the authors have sufficiently addressed the comments and concerns raised and so I have increased my score to a 4: Accept.
Claims And Evidence: The experiments largely support the claims made by the authors. It would be helpful if the authors compared the computational cost of the various attacks and defenses.
Methods And Evaluation Criteria: The method and evaluation criteria make sense for the application.
Theoretical Claims: I did not check the proofs.
Experimental Designs Or Analyses: I checked the CIFAR10 and CIFAR100 experiments and found no issues.
Supplementary Material: No supplementary materials were included.
Relation To Broader Scientific Literature: The adversarially robust conformal prediction method proposed here naturally integrates adversarial training. In contrast with the recent approach of Liu et al. (2024), a key novelty of the present work is the attack-agnostic manner in which it frames the problem.
Essential References Not Discussed: I am not aware of any key missing references.
Other Strengths And Weaknesses: I find the core idea to be original and the paper to be well written.
Other Comments Or Suggestions: Equations 16 and 22 are missing a comma at the end.
Questions For Authors: 1) On page 8 the authors write “Notably, OPSA surpasses PGD, even when PGD is given four times more iterations.” It would be helpful here, and for the other of the comparisons, if the authors could comment on the computational cost of their attack and defense methods, as compared to the other methods in tables 1 and 2. Without this information, it is difficult to truly compare the effectiveness of the new attack/defense with the competing methods.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We appreciate the recognition of the novelty and clarity of our work. Thanks for your valuable feedback on addressing the effectiveness problem. We would like to address your concern.
**Time Consumption**:
Table 4 reports the time (in seconds) per epoch for each adversarial training model on 100 batches. Table 5 presents the execution time (in seconds) of attacks, including three additional methods: APGD (100), AutoAttack (default), and Square Attack (black-box, 1000 queries). These results were derived from 8 batches of tests conducted on 100 images randomly sampled from the CIFAR-100 test set.
# Table 4: Adversarial Training Model Time
| Dataset | FGSM | PGD$^{10}$ | TRADES$^{10}$ | MART$^{10}$ | BETA-AT$^{10}$ | OPSA-AT$^{10}$ |
|-------------|----------|------------|---------------|-------------|----------------|----------------|
| CIFAR-10 | 65 | 655 | 321 | 445 | 469 | 1642 |
| CIFAR-100 | 70 | 1398 | 342 | 742 | 1190 | 1689 |
| IMAGENETmini| 81 | 1766 | 452 | 881 | 1805 | 2024 |
# Table 5: Attack Execution Time
| Attacks | FGSM | PGD$^{10}$ | TRADES$^{10}$ | MART$^{10}$ | BETA-AT$^{10}$ | OPSA-AT$^{10}$ |
|-----------|----------|------------|---------------|-------------|----------------|----------------|
| FGSM | 18.5176 | 15.3600 | 17.2783 | 15.7824 | 18.5751 | 20.8580 |
| Auto | 1595.8604| 2275.8080 | 2017.4780 | 2125.3660 | 669.0256 | 2543.7452 |
| Square | 272.9225 | 342.7212 | 336.6973 | 321.6511 | 107.9474 | 432.7322 |
| PGD$^{10}$ | 20.0746 | 18.3247 | 18.7224 | 19.7636 | 21.3279 | 21.5170 |
| PGD$^{40}$ | 27.1290 | 24.2051 | 24.0342 | 25.5516 | 29.1992 | 28.5025 |
| APGD$^{100}$ | 37.0082 | 39.8945 | 35.6490 | 35.7549 | 33.0879 | 35.6442 |
| BETA$^{10}$ | 32.7680 | 27.5900 | 27.1002 | 26.5268 | 29.0277 | 31.3223 |
| OPSA$^{10}$ | 25.9038 | 24.1116 | 25.4911 | 25.3905 | 27.2531 | 27.4187 |
Our defense requires more computation than others, but experiments show its complexity does not scale significantly with dataset or model size. In attacks, our method outperforms FGSM and PGD$^{10}$ in speed, runs slightly faster than PGD$^{40}$ and APGD, and is 100 times faster than AutoAttack. Notably, it consistently generates the largest adversarial perturbations, inducing the highest model uncertainty across all defenses.
**Formula problem**: Thank you for noticing that there were no commas in Equations 16 and 22; we have now added them.
---
Rebuttal Comment 1.1:
Comment: Thank you for addressing my questions and comments. | Summary: This paper introduces a novel approach that integrates Conformal Prediction (CP) with Adversarial Training (AT) to enhance the adversarial robustness of deep learning models. The authors frame adversarial robustness as a bi-level optimization problem, where an attacker maximizes the uncertainty by enlarging the CP prediction set, while a defender minimizes this uncertainty while maintaining statistical coverage guarantees.
Key contributions of the paper include:
- Optimal Size Attack (OPSA) – A differentiable adversarial attack that increases the CP prediction set size to introduce uncertainty.
- Adversarially Robust Conformal Prediction (OPSA-AT) – A defense mechanism that integrates CP with adversarial training to maintain small and reliable prediction sets.
- Experimental validation on CIFAR-10 and CIFAR-100 – Showing OPSA outperforms baseline attacks like FGSM, PGD, and BETA in increasing uncertainty, while OPSA-AT provides superior robustness compared to other adversarial training methods.
The results demonstrate that the proposed approach provides a stronger defense against adversarial attacks while preserving prediction set efficiency, making it relevant for safety-critical applications.
Claims And Evidence: The claims in the paper are largely well-supported by experiments and theoretical discussions.
- The paper claims that OPSA induces greater uncertainty than existing adversarial attacks. This is well-supported by quantitative results, showing that OPSA consistently produces larger prediction sets compared to PGD and BETA.
- The authors argue that OPSA-AT reduces uncertainty while maintaining coverage guarantees. Their experimental results show that OPSA-AT achieves the smallest prediction sets while keeping classification coverage above 1-α, providing clear evidence of effectiveness.
- The bi-level optimization formulation is justified with mathematical derivations and an algorithmic implementation, making the claims about the framework’s validity credible.
Methods And Evaluation Criteria: - The paper evaluates robustness using coverage probability, prediction set size, and size-stratified coverage violation (SSCV). These are relevant metrics for assessing adversarial robustness in CP.
- The choice of CIFAR-10 and CIFAR-100 is reasonable for a first demonstration, as they are standard benchmarks in adversarial robustness research.
- Only ResNet-34 has been used.
- The comparisons against FGSM, PGD, BETA, TRADES, and MART are comprehensive and provide a solid baseline for evaluating OPSA and OPSA-AT.
A potential improvement would be to test the methods on other datasets and larger networks where adversarial robustness is crucial.
Theoretical Claims: The theoretical claims in the paper appear to be correct and well-founded.
- The bi-level optimization framework is mathematically well-posed and follows existing formulations from adversarial training literature.
- The adversarial attack formulation (maximizing prediction set size) is a logical extension of conformal prediction principles.
- The proofs in Appendix A and C support the convergence and correctness of the adversarial robustness guarantees.
One aspect that could be clarified is whether the theoretical guarantees hold under more general adversarial threat models (e.g., different norm constraints or black-box attacks).
Experimental Designs Or Analyses: The experimental setup is well-structured and follows best practices in adversarial robustness evaluation.
- The attack and defense methods are evaluated across multiple adversarial perturbation levels.
- The results include statistical confidence intervals (mean ± standard deviation), which adds credibility.
-The boxplot visualizations in Appendix D provide useful insights into attack and defense effectiveness.
However, there are some areas for improvement:
- Ablation Studies – It would be useful to show how OPSA-AT performs under different hyperparameters (e.g., $\lambda$, T1, T2) to understand its sensitivity.
- Computational Overhead – The paper does not discuss how much extra training/inference time OPSA-AT introduces.
Supplementary Material: The supplementary material (Appendices) contains:
- Proofs of key theoretical claims (Proposition 1, Theorem 1).
- An illustrative example of the attack formulation.
- Additional experimental results and visualizations (boxplots for CIFAR-10 and CIFAR-100).
Relation To Broader Scientific Literature: The paper builds upon and extends three key areas of machine learning research:
Adversarial Robustness
- Traditional adversarial training methods (e.g., Madry et al., 2017; TRADES (Zhang et al., 2019); MART (Wang et al., 2019)) focus on minimizing classification errors but do not address uncertainty.
- This work extends adversarial training to the uncertainty estimation domain by integrating CP, which is a novel perspective.
Conformal Prediction
- CP methods (e.g., Vovk et al., 2005; Ghosh et al., 2023) provide distribution-free coverage guarantees but struggle under adversarial conditions.
- This paper proposes a way to defend CP models against adversarial perturbations, which is a valuable contribution.
Bi-Level Optimization in Machine Learning
- The bi-level optimization framework aligns with recent advances in min-max adversarial training (Nouiehed et al., 2019; Robey et al., 2024).
- Unlike previous work, the authors frame prediction set size minimization as a key objective, which is a fresh take on the problem.
Essential References Not Discussed: - CertViT: A method for achieving certified robustness in pre-trained Vision Transformers, presented at the ICML 2023 Workshop. It employs the Douglas-Rachford splitting algorithm to ensure both robustness and sparsity simultaneously.
- Shrink & Cert: A bi-level optimization approach for enhancing certified robustness while maintaining sparsity constraints, also presented at the ICML 2023 Workshop.
Other Strengths And Weaknesses: Strengths:
- Novelty – The integration of CP with adversarial training is original and impactful.
- Strong theoretical foundation – The framework is mathematically sound with rigorous proofs.
- Comprehensive experiments – The study provides strong empirical validation using diverse attack/defense comparisons.
- Practical implications – The approach is useful for safety-critical applications where robustness matters.
Weaknesses:
- Limited dataset diversity – Experiments are only on CIFAR-10/100, which may not generalize to real-world settings.
- Limited networks - Experiments are only on ResNet-34 network.
- No evaluation of computational efficiency – OPSA-AT might be computationally expensive, but the paper does not discuss it.
- No discussion on transferability – How well does the defense hold up against black-box attacks?
Other Comments Or Suggestions: - Consider additional datasets (e.g., ImageNet) to show broader applicability.
- Consider additional networks. Possibly larger networks. If large networks are not feasible computationally then mention that.
- Analyze the time complexity of OPSA-AT to ensure practical feasibility.
- Investigate black-box attacks to check whether OPSA-AT generalizes to unseen adversarial strategies.
Questions For Authors: - How does OPSA-AT perform on larger-scale datasets like ImageNet? This would provide a better sense of real-world applicability.
- How does OPSA-AT perform on larger-networks like ResNet-50, ViT, etc.
- What is the computational overhead of OPSA-AT compared to standard adversarial training? Understanding the trade-off between robustness and efficiency is crucial.
- Does OPSA-AT maintain robustness against black-box or transfer attacks? The current experiments focus on white-box settings, so it’s unclear if the defense generalizes.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for recognizing the novelty, strong theoretical foundation, comprehensive experiments, and practical implications of our work. We appreciate your valuable suggestions and feedback. Below, we address your concerns.
**Time Consumption**: See response to Reviewer 7J63.
**Experimental Diversity**: Our paper is theoretically supported and has demonstrated efficiency in experiments, confirming the effectiveness of our method. However, we agree that more experimental validation is beneficial. To strengthen our evaluation, we conducted additional experiments on the ImageNetMini dataset (80% training, 20% split for calibration and testing) using a ResNet50 trained for five epochs. Due to time constraints, we tested our top defenses (TRADES, MART, OPSA-AT) against strong attacks (Clean, FGSM, PGD, OPSA). As shown in Table 2, our attack and defense achieve state-of-the-art performance on Size (the most reliable metric) and deliver near-best results on SSCV, outperforming all baselines.
# Table 2: Mean and Standard Deviation of Coverage, Size, and SSCV for imagemini
| **Attacks** | **Indicator** | **Training Algorithm** | | |
|-------------|---------------|------------------------|----------------------|----------------------|
| | | **TRADES$^5$** | **MART$^5$** | **OPSA-AT$^5$** |
| Clean | Coverage (%) | 89.64 ± 0.50 | 89.69 ± 0.50 | 89.69 ± 0.48 |
| | Size | 18.55 ± 0.11 | 20.62 ± 0.12 | 17.01 ± 0.18 |
| | SSCV | 0.08 ± 0.01 | 0.07 ± 0.01 | 0.10 ± 0.01 |
| FGSM | Coverage (%) | 89.48 ± 0.50 | 90.34 ± 0.50 | 89.51 ± 0.49 |
| | Size | 39.01 ± 0.12 | 48.88 ± 0.11 | 30.41 ± 0.23 |
| | SSCV | 0.07 ± 0.11 | 0.10 ± 0.00 | 0.08 ± 0.02 |
| PGD$^{10}$ | Coverage (%) | 89.38 ± 0.49 | 90.44 ± 0.46 | 89.66 ± 0.49 |
| | Size | 38.11 ± 0.12 | 50.35 ± 0.10 | 34.88 ± 0.24 |
| | SSCV | 0.05 ± 0.01 | 0.01 ± 0.00 | 0.14 ± 0.03 |
| OPSA$^{10}$ | Coverage (%) | 89.71 ± 0.48 | 90.47 ± 0.46 | 89.95 ± 0.46 |
| | Size | 40.92 ± 0.12 | 50.52 ± 0.09 | 35.63 ± 0.02 |
| | SSCV | 0.23 ± 0.24 | 0.10 ± 0.00 | 0.11 ± 0.04 |
**Additional Attacks**: We further tested our defense against APGD, Black-box (Square), and AutoAttack—an advanced ensemble of black-box and white-box attacks. As outlined in our response to Reviewer 2dn3 (Table 1), our method consistently demonstrates robustness across these attack scenarios. Notably, all attacks generated smaller prediction set sizes than OPSA, while our defense remained effective.
**Ablation Studies**: Regarding the hyperparameters $\lambda$ and $T_{2}$, we refer to the detailed analysis in [A], where these parameters were rigorously analyzed. For $T_{1}$, its core function is to calibrate the sigmoid function to approximate the Threshold Response (THR) method [B], enlargement of prediction Interval. As shown in Table 3, systematic variations of $T_{1}$ on CIFAR-100 reveal a critical threshold effect: as randomly sampled $T_{1}$ values increase, the prediction set size expands progressively before plateauing at approximately 10.
# Table 3: The effectiveness of OPSA attacks at different T₁ values
| **$T_{1}$** | **OPSA** | **OPSA-AT$^{10}$** |
|--------|----------|----------------|
| 0.001 | Coverage (%) | 89.62 ± 0.35 |
| | Size | 22.06 ± 0.20 |
| | SSCV | 0.03 ± 0.01 |
| 0.1 | Coverage (%) | 89.76 ± 0.34 |
| | Size | 29.35 ± 0.26 |
| | SSCV | 0.03 ± 0.01 |
| 1 | Coverage (%) | 89.95 ± 0.35 |
| | Size | 33.30 ± 0.27 |
| | SSCV | 0.03 ± 0.01 |
| 10 | Coverage (%) | 89.88 ± 0.34 |
| | Size | 33.50 ± 0.25 |
| | SSCV | 0.03 ± 0.01 |
| 100 | Coverage (%) | 89.90 ± 0.33 |
| | Size | 33.50 ± 0.26 |
| | SSCV | 0.03 ± 0.01 |
| 1000 | Coverage (%) | 89.91 ± 0.34 |
| | Size | 33.50 ± 0.26 |
| | SSCV | 0.03 ± 0.01 |
**Others**: We have incorporated discussions of the following two papers [C][D] into our analysis to provide a more comprehensive theoretical foundation.
Reference:
[A] Stutz, David, $et$ $al$. '' Learning optimal conformal classifiers." arXiv preprint arXiv:2110.09192. (2021).
[B] Sadinle, Mauricio, $et$ $al$. ''Least ambiguous set-valued classifiers with bounded error levels." Journal of the American Statistical Association (2024).
[C] Kavya, Gupta, $et$ $al$. ''CertViT: Certified Robustness of Pre-Trained Vision Transformers." https://arxiv.org/abs/2302.10287. (2023).
[D] Kavya, Gupta, $et$ $al$. ''Shrink \& Cert: Bi-level Optimization for Certified Robustness." The Second Workshop on New Frontiers in Adversarial Machine Learning. (2023). | Summary: The paper proposes a framework that integrates adversarial training with conformal prediction (CP) to enhance model robustness against adversarial attacks while maintaining reliable uncertainty estimates. It formulates adversarial training within the CP framework as a bi-level optimization problem, where an attacker seeks to maximize uncertainty while a defender aims to minimize it. The paper introduces a novel attack method that increases uncertainty without requiring coverage guarantees and develops a conformal training-based defense strategy that minimizes the size of prediction sets under adversarial perturbations. Experiments on CIFAR-10 and CIFAR-100 demonstrate that the proposed attack increases uncertainty more than existing methods, while the defense improves robustness against various adversarial attacks.
Claims And Evidence: Claim 1: The proposed method "minimizes the size of the prediction sets under adversarial perturbations while maintaining high coverage probabilities: evidence given in the experimental section."
Claim 2: "The defensive model significantly enhances robustness against various adversarial attacks and maintains reliable prediction intervals": NO EVIDENCE GIVEN
Claim 3: The "findings highlight the effectiveness of integrating adversarial training with conformal prediction to develop trustworthy and
resilient deep learning models for safety-critical domains": Only partial evidence is given in the experimental section.
Methods And Evaluation Criteria: The methods and evaluation criteria are reasonable and required.
However, some essential evaluations and methods are missing.
Methods missing: APGD and AutoAttack; these are stronger attacks, and it would be interesting to see if the proposed adversarial training method still performs reasonably against these stronger attacks.
Evaluations missing: It is unclear what the performance of the model is in terms of accuracy or what the performance of the attack is in terms of attack efficacy.
Theoretical Claims: The theoritical claims in the paper seem to be reasonable and are proved.
Experimental Designs Or Analyses: The experimental design is not clear; some key information required to truly understand the experiments is missing.
This information is:
1. The l-p norm used, while the method section says that any l-p norm can be used, the attack norm used is not specified in the evaluations.
2. The epsilon value used.
Supplementary Material: Yes, I checked the box plots and glanced over the theoretical proofs.
Relation To Broader Scientific Literature: The proposed idea in the paper is certainly very interesting and relevant to a broader scientific community.
Essential References Not Discussed: The related works that I am aware of are cited in the paper already.
Other Strengths And Weaknesses: Strengths:
To the best of my knowledge, the idea is novel, and the work has the potential to be very impactful and to pave the way towards safety-criticality.
Weakness:
Certain claims made are not proved in the paper, as written above in the "claims" section.
While the work has the potential to pave the way towards safety-criticality, this work itself does not work towards safety-criticality.
No safety-critical application has been pursued in this paper. Therefore the lines 036-040 are an overclaim in my opinion.
Some critical evaluations are missing in terms of performance against the current SotA adversarial attacks like APGD and AutoAttack.
Some metrics, such as model performance in terms of accuracy under attack, are also missing.
Lastly, it is unclear what the increased time requirement for the adversarial training and the adversarial attack is in comparison to the other known adversarial attacks and training methods.
Other Comments Or Suggestions: This work has the potential to be very impactful.
However, as mentioned in the responses above, some key components are missing in terms of evaluations, metrics, and experimental details.
Including these would be very helpful.
Questions For Authors: Knowing the experimental details of the proposed attack would be very helpful.
Additionally, knowing the time taken for the proposed attack and defense method (training) in comparison to the others attacks and training methods (respectively) would also be very helpful.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We truly appreciate your recognition of the novelty and potential impact of our work. Your comments on clarifying the missing experimental details and time consumption are greatly appreciated. Below, we address your points and provide further explanations.
**Experimental Setup**: In principle, any $\ell_p$ norm could be used, but all experiments use the $\ell_\infty$ norm, with $\epsilon=0.03$, following prior work ([A]). We will clarify this in the final version.
**Additional Experiments**:
We included accuracy results for different defenses under various attacks (Tables 1 and 2), including three additional methods: APGD (100), AutoAttack (default), and Square Attack (black-box, 1000 queries). Our defense achieves the highest overall accuracy, while our attack produces the largest adversarial perturbations.
# Table 1: Detailed Results for Attack Methods (Square, APGD$^{100}$, Auto, OPSA$^{10}$)
## Square Attack [B]
| Indicator | FGSM | PGD$^{10}$ | TRADES$^{10}$ | MART$^{10}$ | BETA-AT$^{10}$ | OPSA-AT$^{10}$ |
|---------------|----------|------------|---------------|-------------|----------------|----------------|
| Coverage (%) | 88.98 ± 0.36 | 88.99 ± 0.35 | 90.86 ± 0.32 | 89.79 ± 0.34 | 90.65 ± 0.32 | 89.31 ± 0.34 |
| Size | 28.14 ± 0.20 | 33.03 ± 0.18 | 11.61 ± 0.09 | 11.60 ± 0.10 | 73.59 ± 0.27 | 13.81 ± 0.27 |
| SSCV | 0.05 ± 0.01 | 0.08 ± 0.01 | 0.04 ± 0.01 | 0.10 ± 0.03 | 0.46 ± 0.15 | 0.03 ± 0.01 |
## APGD$^{100}$ Attack [C]
| Indicator | FGSM | PGD$^{10}$ | TRADES$^{10}$ | MART$^{10}$ | BETA-AT$^{10}$ | OPSA-AT$^{10}$ |
|---------------|----------|------------|---------------|-------------|----------------|----------------|
| Coverage (%) | 89.06 ± 0.36 | 88.99 ± 0.35 | 90.22 ± 0.32 | 89.11 ± 0.37 | 90.64 ± 0.33 | 90.04 ± 0.34 |
| Size | 32.00 ± 0.21 | 33.06 ± 0.18 | 13.54 ± 0.11 | 13.48 ± 0.12 | 73.93 ± 0.26 | 16.73 ± 0.20 |
| SSCV | 0.06 ± 0.01 | 0.08 ± 0.01 | 0.04 ± 0.01 | 0.10 ± 0.00 | 0.60 ± 0.17 | 0.09 ± 0.00 |
## Auto Attack [C]
| Indicator | FGSM | PGD$^{10}$ | TRADES$^{10}$ | MART$^{10}$ | BETA-AT$^{10}$ | OPSA-AT$^{10}$ |
|---------------|----------|------------|---------------|-------------|----------------|----------------|
| Coverage (%) | 89.03 ± 0.36 | 88.99 ± 0.35 | 90.31 ± 0.33 | 89.11 ± 0.35 | 90.65 ± 0.31 | 90.50 ± 0.31 |
| Size | 32.04 ± 0.21 | 33.06 ± 0.18 | 12.69 ± 0.22 | 13.58 ± 0.12 | 74.00 ± 0.26 | 11.31 ± 0.22 |
| SSCV | 0.06 ± 0.01 | 0.08 ± 0.01 | 0.06 ± 0.01 | 0.10 ± 0.00 | 0.61 ± 0.18 | 0.09 ± 0.01 |
## OPSA$^{10}$ Attack
| Indicator | FGSM | PGD$^{10}$ | TRADES$^{10}$ | MART$^{10}$ | BETA-AT$^{10}$ | OPSA-AT$^{10}$ |
|---------------|----------|------------|---------------|-------------|----------------|----------------|
| Coverage (%) | 90.75 ± 0.32 | 89.78 ± 0.34 | 90.31 ± 0.33 | 90.46 ± 0.32 | 89.29 ± 0.35 | 89.95 ± 0.35 |
| Size | 65.48 ± 0.22 | 39.14 ± 0.20 | 32.31 ± 0.19 | 35.28 ± 0.23 | 75.22 ± 0.20 | 33.30 ± 0.27 |
| SSCV | 0.10 ± 0.00 | 0.07 ± 0.01 | 0.08 ± 0.01 | 0.06 ± 0.01 | 0.10 ± 0.00 | 0.03 ± 0.01 |
**Time Consumption**: See response to Reviewer 7J63.
**Missing Evidence**: We acknowledge that our defense may not excel in all metrics under certain attacks. However, it prioritizes size minimization under equivalent coverage constraints, which is crucial for conformal prediction. On CIFAR-10, our model consistently achieves the smallest size, while on CIFAR-100, it remains competitive with state-of-the-art defenses.
AutoAttack combines black-box and white-box strategies, and a key observation is that stronger defenses require longer attack times. This highlights two points:
1. **Defense Strength**: The extended attack duration indicates our defense's resilience, as adversaries need more effort to breach it.
2. **Training Time**: Longer training is necessary due to the defense's complexity and optimization goals, enhancing its robustness.
We have conducted additional experiments on the ImageNet-Mini dataset, where the model sizes of both our attack and defense methods consistently outperform baseline approaches. Due to page limits, we summarize that our defense achieves state-of-the-art performance across all adversarial attack scenarios. For detailed results and analysis, please refer to our response to Reviewer uZo5.
References:
[A] Robey, Alexander, $et$ $al$. ''Adversarial Training Should Be Cast as a Non-Zero-Sum Game." The Twelfth International Conference on Learning Representations. ICLR (2024). (from paper)
[B] Maksym, Andriushchenko, $et$ $al$. ''Square Attack: a query-efficient black-box adversarial attack via random search." https://arxiv.org/abs/1912.00049.
[C] Francesco, Croce, $et$ $al$. ''Reliable evaluation of adversarial robustness with an ensemble of diverse parameter-free attacks." https://arxiv.org/abs/2003.01690.
---
Rebuttal Comment 1.1:
Comment: Thank you for the rebuttal. I will respond to the specifics shortly.
For now, I have a quick question: Are the accuracies of the models after attacks when using different training methods reported anywhere? Did I happen to miss those?
Best
Reviewer 2dn3
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Reply to Comment 1.1.1:
Comment: Thank you for your inquiry. While we did evaluate the accuracy of various models, space limitations prevented us from presenting all results. Below are the accuracy metrics of our defense models against different adversarial attacks on the CIFAR-100 dataset, demonstrating that our proposed defense method consistently achieves superior performance compared to others.
# Table 1: Accuracy Results for Different Attack and Defense Methods
| **Attacks** | **FGSM** | **PGD$^{10}$** | **TRADES$^{10}$** | **MART$^{10}$** | **BETA-AT$^{10}$** | **OPSA-AT$^{10}$** |
|-------------|----------|------------|---------------|-------------|----------------|----------------|
| Clean | 43.65% | 24.15% | 51.55% | 52.10% | 6.09% | 55.65% |
| FGSM | 16.14% | 20.74% | 30.20% | 30.24% | 24.27% | 37.04% |
| PGD$^{10}$ | 12.84% | 20.47% | 26.80% | 25.36% | 5.24% | 29.06% |
| PGD$^{40}$ | 12.83% | 20.46% | 26.75% | 25.30% | 4.89% | 28.94% |
| BETA$^{10}$ | 17.94% | 24.69% | 38.26% | 39.79% | 25.90% | 43.79% |
| Square | 10.91% | 20.03% | 28.99% | 28.90% | 2.36% | 33.04% |
| APGD$^{100}$ | 9.86% | 19.46% | 25.45% | 24.23% | 1.19% | 27.73% |
| Auto | 9.46% | 18.73% | 24.34% | 23.12% | 0.95% | 26.65% |
| OPSA$^{10}$ | 13.15% | 20.90% | 27.59% | 26.30% | 4.78% | 29.99% | | null | null | null | null | null | null |
ExPLoRA: Parameter-Efficient Extended Pre-Training to Adapt Vision Transformers under Domain Shifts | Accept (poster) | Summary: The authors show that continued pre-training (with PEFT) on the target domains before supervised fine tuning is an effective methodolofy for adapting natural-image foundation models to non-natural image target tasks. They show particular gains on RGB tasks, but also show some benefit on multi-spectral imagery.
Claims And Evidence: * Claim: Continued pre-training on target domain, with peft, unlocks peft finetuning for specialized tasks.
This is supported in Table 1 and other results tables. However, the question of whether PEFT is needed in either stage is useful (beyond memory savings) is not answered.
Methods And Evaluation Criteria: Broadly, the method and evaluations both make sense.
Theoretical Claims: There are no theoretical claims in this paper.
Experimental Designs Or Analyses: Reading the paper, the experimental design mostly makes sense, with a few caveats:
Table 2 shows results for both Dinov2 and MAE, but Table 4- 9 don't always show both. Does it still work there?
There is no comparison that I can find for a model which has continued pre-training and finetuning on the same dataset with full finetuning (not ScaleMAE or SatMae), so the performance charachteristics of using PEFT are not well developed.
Supplementary Material: I reviewed the supplementary (appendix)
Relation To Broader Scientific Literature: This paper builds on the idea of "finetuning like you pretrain"[1] and "Self-supervised pretraining improves self-supervised pretraining."[2], and adds a PEFT component. They verify this works for adapting natural image models to OOD data domains like sattelite imagery.
[1] Goyal, Sachin, et al. "Finetune like you pretrain: Improved finetuning of zero-shot vision models." Proceedings of the IEEE/CVF Conference on Computer Vision and Pattern Recognition. 2023.
[2]. Reed, Colorado J., et al. "Self-supervised pretraining improves self-supervised pretraining." Proceedings of the IEEE/CVF Winter Conference on Applications of Computer Vision. 2022.
Essential References Not Discussed: [1] and [2] are relevant and not discussed.
[1] Goyal, Sachin, et al. "Finetune like you pretrain: Improved finetuning of zero-shot vision models." Proceedings of the IEEE/CVF Conference on Computer Vision and Pattern Recognition. 2023.
[2]. Reed, Colorado J., et al. "Self-supervised pretraining improves self-supervised pretraining." Proceedings of the IEEE/CVF Winter Conference on Applications of Computer Vision. 2022.
Other Strengths And Weaknesses: Strenghts:
Empirically, it works!
Relatively easy to read.
Weaknesses:
In principle, this modernizes "Self-supervised pretraining improves self-supervised pretraining." with a stronger backbone and peft finetuning, which is not very novel.
Other Comments Or Suggestions: My main suggestions for improving are discussing the missed references, demonstrating that PEFT is truly needed (not just full finetune), and sure to show both Dino and MAE results in Table 4-9 for consistency.
Questions For Authors: Here are the points which would lead me to the a higher score.
* Demonstrating that one can't do the proposed two stage finetuning with no PEFT, since PEFT mechnaism is one of the key innovation . I believe this to be true, since it is difficult to not catastrophically forget, but it is the key innovation in the paper, so important to verify
* Show additional evidence in Table 4 ,5 for D -[L}-r32 and M-[L]-r32 in Tables 7-9.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your feedback and recognition of the empirical performance and novelty of using parameter-efficency for pre-training in ExPLoRA. Here are our responses:
**Q: Is PEFT needed in either pre-training or fine-tuning beyond memory savings?**
Our primary motivation for parameter-efficient techniques is _efficiency_:
* Reduced memory footprint provides significant compute savings with larger batch sizes and/or fewer GPUs, and since gradients for <10% of parameters need to be stored and propagated. This makes ExPLoRA much faster than full pre-training (see [revised Table 1](https://imgur.com/a/iMjgOHv) and [response to reviewer W3i1](https://openreview.net/forum?id=OtxLhobhwb¬eId=AapZp7BqgM))
* Memory savings enable using models such as ViT-L or ViT-G, otherwise inaccessible with constrained GPU budgets
* While not our main motivation, constraining the parameter space mitigates catastrophic forgetting from the natural image domain. ExPLoRA outperforms fine-tuning from MAE/DinoV2 or domain-specific SatMAE models by >1% in Table 1, and full continual pre-training methods (eg: GFM) by 5-7%. For linear probing, this gap widens to 8%, suggesting benefits from both original and extended pre-training.
We've included a baseline for fully pre-training a ViT-L from scratch on fMoW-RGB with DinoV2 objective in our [revised Table 3](https://imgur.com/a/tWdN4xU). This shows full pre-training cannot match ExPLoRA while requiring >10x compute and >16x parameters.
Lastly, our parameter-efficient pre-training is orthogonal to fine-tuning method choice. ExPLoRA preserves the ViT architecture, enabling any fine-tuning approach. While we primarily use PEFT for efficiency, ExPLoRA also outperforms fully fine-tuned SatMAE and ScaleMAE models by 1.4% (Table 1).
**Q: Are there baselines that fully fine-tune natural-image pre-trained models on the domain of interest?**
We use PEFT primarily for efficiency. At your request, we've included fully fine-tuning DinoV2 and ExPLoRA models on fMoW-RGB alongside the SatMAE paper's fully fine-tuned MAE result in our [expanded Table 1](https://imgur.com/a/iMjgOHv).
Full fine-tuning is viable with sufficient resources. ExPLoRA models benefit from it just as well as other baselines and outperform them. However, LoRA-r8 PEFT is much cheaper and equally effective. Table 4 includes a comparison where MAE is directly fully fine-tuned on fMoW-Sentinel, showing poor performance (>9% gap) due to the large domain shift.
We reiterate that we don't aim to replace full or PEFT fine-tuning, both complementary to ExPLoRA. Instead, we provide an efficient alternative to _full, domain-specific pre-training_.
**Q: Relation to “self-supervised pre-training improves...” (HPT)**
We will update our paper to include this reference. Key differences between ExPLoRA and HPT:
* HPT uses two full backbone pre-training phases on different datasets. ExPLoRA uses a single efficient extended pre-training phase that generalizes to multiple downstream tasks.
* While HPT offers tuning only batch norm layers in the second phase, it centers around full-rank pre-training, like GFM. ExPLoRA uses parameter-efficient techniques that **reduce compute by >10x and parameters by >16x** while achieving similar or higher performance.
* HPT studies MoCo with ResNet-50. ExPLoRA addresses ViTs with different SSL objectives (DinoV2, MAE), demonstrating broader applicability.
ExPLoRA goes beyond "modernizing HPT" by demonstrating parameter-efficient extended pre-training's value via strong performance at reduced costs across diverse datasets, SSL objectives, and tasks.
**Q: Relation to “Finetune like you pretrain...” (FLYP)**
We agree this reference is also valuable. As above, there are important differences with ExPLoRA:
* FLYP is a fine-tuning technique while ExPLoRA is a pre-training technique
* FLYP focuses on contrastive SSL methods with ResNet. ExPLoRA is compatible with any ViT SSL objective (as we show with DinoV2, MAE).
FLYP does further justify continuing pre-training with the same loss function (eq. 5). We'll update our final manuscript to include this reference.
**Q: Show additional evidence in Table 4 ,5 for D -[L}-r32 and M-[L]-r32 in Tables 7-9.**
We have now included MAE results in tables 7-9, [linked here](https://imgur.com/a/lx4TaLZ), which underperforms our SoTA Dino-ExPLoRA.
For tables 4-5, we use MAE SSL from SatMAE. There's no DinoV2 modification for multi-spectral/temporal data in prior work. Creating one would require modifying the ViT and Dino SSL mechanism for non-RGB temporal/multi-spectral sequences, which is out of scope. Our goal is to use the SatMAE SSL architecture with MAE weights, showing ExPLoRA matches/outperforms full pre-training (0.67%) and vastly outperforms full MAE fine-tuning on multi-spectral data by 8.54% (Table 2).
---
We hope these answers address your questions. If your main concerns are resolved, we kindly request you reconsider your score.
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Rebuttal Comment 1.1:
Comment: I am satisfied witht the rebuttal, and therefore raise my score. However, I still view this as very closely related to HPT, and encourage a careful poistioning of your work as it relates to this reference for the camera ready.
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Reply to Comment 1.1.1:
Comment: Thank you for your time in reviewing our work and for your helpful suggestions! We are glad to know our rebuttal has resolved your main concerns. For the camera-ready, we will make sure to include a discussion on HPT as related work. We appreciate that you have increased your rating. | Summary: This paper proposes a continual pre-training method with a parameter-efficient fine-tuning (PEFT) module such as LoRA (Hu et al. 2021) to improve the adaptability of visual foundation models on specific domains. By inserting and training the PEFT module inside the general-domain pre-trained backbone model with the same learning objective that the backbone model was trained, the proposed ExPLoRA induces meaningful initialization for adaptation with labeled data, resulting in somewhat better classification accuracy on downstream tasks compared with the full fine-tuning approach.
Hu et al. 2021, LoRA: Low-Rank Adaptation of Large Language Models
Claims And Evidence: The authors claim extended pre-training with LoRA (and a few unfreeze model blocks) via self-supervised learning (SSL) objectives can induce better initialization for specific domain datasets. This claim was well-validated through the conventional evaluation protocol of SSL, i.e., evaluation with linear probing and fine-tuning performance on detection and calibration tasks across diverse domains.
**However**, there is a point that can be further improved.
* The author explains the rationale of continual pertaining with LoRA based on weight decomposition, i.e., the desired target weight vector $W_{T}^{(\tau)}$ is the summation of pre-trained weight vector $W_{S}$ on source domain (general knowledge), a vector contains general knowledge on the target domain, $\Delta_{T}$, and the vector represent the task-specific knowledge on target domain $\Delta^{(\tau)}$.
* If the author can provide some qualitative analysis that illustrates the difference (maybe in the embedding space) between pre-trained weight and ExPLoRA-extended pre-trained weight, this design motivation of ExPLoRA will become more convincing.
Methods And Evaluation Criteria: The proposed method is reasonable to address the stated problem -- developing domain adaptable foundation models, and the adopted metric follows the standard of literature.
Theoretical Claims: There are no formal theorems.
Experimental Designs Or Analyses: Overall the amount and range of experiments are extensive and well-design, but it would be better if the authors could (1) add some qualitative analyses such as embedding visualization, and baseline for the test-time adaptation method
- Wang et al. 2020, Tent: Fully Test-time Adaptation by Entropy Minimization
- Zhang et al. 2023, DomainAdaptor: A Novel Approach to Test-time Adaptation
Supplementary Material: Take a closer look at training details and runtime-performance tradeoff plots
Relation To Broader Scientific Literature: The authors claim that the proposed paradigm can indeed contribute to developing the domain-adaptable foundation models by reducing the development cost compared with the from-scratch training approach. However, as shown in Figure 7 of the appendix, the proposed method requires a non-trivial amount of additional training compared with the vanilla pre-trained model for the marginal improvement of downstream performance. Thus the contribution seems not significant.
Essential References Not Discussed: I would recommend the author mention test-time adaptation (TTA) approaches (especially the PEFT-based TTA method) somewhere in the main body of the paper. In terms of the goal -- enabling efficient adaptation of backbone model to target domain -- and design of the learning algorithm, TTA approaches are well-aligned with the position of this work.
- Wang et al. 2020, Tent: Fully Test-time Adaptation by Entropy Minimization
- Gao et al. 2022, VISUAL PROMPT TUNING FOR TEST-TIME DOMAIN ADAPTATION
- Zhang et al. 2023, DomainAdaptor: A Novel Approach to Test-time Adaptation
- Tsai et al. 2023, Convolutional Visual Prompt for Robust Visual Perception
Other Strengths And Weaknesses: Although the proposed method consistently shows strong results across diverse downstream tasks and domains (`strength`), it requires a non-trivial amount of additional training hours, e.g., 200 hours to achieve marginally improved downstream performance (`weaknesses`).
Other Comments Or Suggestions: See the above reviews.
# Post-rebuttal
> I appreciate the authors' professional rebuttal. For now, I will adhere to my rating because I do not agree with authors' statements on the benefits of the proposed method from the perspective of computational efficiency <-> accuracy improvement trade-off. I will go through other rebuttals as well to reconsider my recommendation (if necessary) through the remaining discussion period.
Questions For Authors: See the above reviews.
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: Thank you for your valuable feedback. We appreciate your recognition of our extensive, well-designed experimental validation and for ExPLoRA’s improved performance over baselines. Here are our responses:
**Q: Can you provide qualitative analysis that illustrates the difference between pre-trained vs ExPLoRA pre-trained embedding spaces?**
Section 7 contains our analysis of patch embeddings output by ViT blocks across different models (ExPLoRA, DinoV2, MAE, SatMAE), revealing important quantitative differences. Please also see our response to reviewer Fy1r [linked here](https://openreview.net/forum?id=OtxLhobhwb¬eId=JMCCQ90U3c).
Figure 9 (appendix B.8) also qualitatively analyzes attention maps across different ViT blocks of these models. ExPLoRA concentrates attention more tightly on central objects, especially in final layers. This correlates with lower mean eigenvalues and higher positional/classification accuracies from linear probing.
**Q: Include discussion of test-time adaptation (TTA) methods.**
Thank you for mentioning these methods. We have updated our related work section to include these references which will be present in our camera-ready revision. Our work has key differences with TTA methods:
* TTA methods make a critical assumption: the label space Y is shared between the source and target domains. This makes [1,2,3] incompatible with unsupervised pre-trained backbones when domains have different label sets (common in many settings, including ours). Unsupervised pre-training techniques like DinoV2 or ExPLoRA don't assume specific downstream label sets, requiring some supervised adaptation (linear-probing/PEFT) to parameterize $p^{(\tau)}_T(y|x)$ for downstream task $\tau$ in target domain $T$. TTA methods could then be applied on top of ExPLoRA backbones just as with any ViT. This means that ExPLoRA is complementary with TTA methods rather than a competing method.
* [3,4] are tailored for CNNs, not applicable to our work with ViTs, which consistently outperform CNNs on our datasets (eg: fMoW-RGB, fMoW-Sentinel, temporal images etc. as verified in prior work).
* [2] uses visual-prompt tuning (VPT) for ViTs, but lacks a public codebase. We include multiple recent VPT baselines in Table 1 (VPT [5], GVPT [6], SA2VP [7]). ExPLoRA outperforms all by ~2%, including a pre-training baseline with VPT in Table 3.
**Q: ExPLoRA requires a non-trivial amount of additional training compared to fine-tuning a natural-image pre-trained model for an improvement in performance (Figure 7)**
We would like to refer you to our response to reviewer W3i1, [linked here](https://openreview.net/forum?id=OtxLhobhwb¬eId=AapZp7BqgM).
To summarize, we realize that our plot in figure 7 paints an incomplete picture. ExPLoRA is a pre-training method, providing an alternative to domain-specific _full pre-training_. While extended pre-training + fine-tuning requires more GPU hours than directly fine-tuning, the extended pre-training phase is amortized across multiple downstream tasks, since the same ExPLoRA model can be re-used for initialization. Further, it can be used for methods such as feature extraction, linear probing etc. that a task-specific fine-tuned model cannot do. For linear probing, ExPLoRA outperforms DinoV2/prior SoTA models by >8%. This difference is not captured via figure 7, since that only compares with fine-tuning.
Thus, the fairer comparison is with domain-specific full-pretraining. Here, ExPLoRA requires **8x-10x less compute, 16x fewer parameters** and achieves similar or higher performance. Our expanded [Table 1](https://imgur.com/a/iMjgOHv) demonstrates that ExPLoRA is vastly more efficient than other pre-training methods.
Figure 7 shows only fMoW-RGB performance. On fMoW-Sentinel (larger domain shift to multi-spectral data), full-finetuning a natural-image baseline shows a 9% performance gap with ExPLoRA (row 1, Table 4). Combined, these are significant results since ExPLoRA achieve/surpass fully pre-trained baselines using ~8-10x less compute and 10-16x fewer parameters.
---
Thank you for your feedback which has strengthened our work. If your concerns are addressed, we kindly ask that you reconsider your score.
---
References:
[1] Tent: Fully Test-time Adaptation by Entropy Minimization, _ICLR 2021_.
[2] Visual Prompt Tuning for Test-Time Domain Adaptation, _arxiv 2210.04831_.
[3] DomainAdaptor: A Novel Approach to Test-time Adaptation, _ICCV 2023_.
[4] Convolutional Visual Prompt for Robust Visual Perception, _NeurIPS 2023_.
[5] Visual prompt tuning. _ECCV 2022_.
[6] Improving visual prompt tuning for self-supervised vision transformers. _ICML 2023_.
[7] SA²VP: Spatially Aligned-and-Adapted Visual Prompt. _AAAI 2024_.
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Rebuttal Comment 1.1:
Comment: > Again, I thank the authors for their kind rebuttal, which somewhat addresses my concerns. Although I left a post-rebuttal comment in my review a few days ago, I am commenting on this based on the request from AC for further discussion on efficiency-accuracy trade-off.
In summary, **I still don't agree with the advantage of the proposed method in terms of its efficiency**.
* The authors claim that ExPLoRA should be compared with other domain-specific pre-training methods, such as ScaleMAE and SatMAE, because ExPLoRA is a kind of pre-training method.
* However, my opinion is that **non-domain-specific methods such as DinoV2 + LoRA (78.08) or DinoV2 + AdaLoRA-r8 (78.87) are already much powerful than domain-specific methods, ScaleMAE/SatMAE (77.80), so why should we compare ExPLoRA with a much inferior method, ScaleMAE?** (the value was parsed from Table 1)
* Maybe the domain-specific baselines the authors considered in this work are too weak, or it is not necessary to pre-train the model entirely on domain-specific data. The non-domain-specific method, DinoV2 + AdaLoRA-r8 (78.87), is already very strong, but the authors' proposed method requires hundreds more GPU hours to achieve a minor improvement (78.87) -> (79.28).
* This raises a question: is the domain-specific extended pertaining really necessary? For example, DinoV2 + AdaLoRA-r8 (78.87) performs better than the authors' domain-specific method `D-[L]-r64 + SA2VP` (78.51) which implies that better architecture and training technique can be much more important than domain-specific extended training.
* **Should the pre-training methods be only compared with other pre-training methods? I think this is not.** The end goal of this domain-specific training is to achieve good performance on downstream tasks from specific domains. In that sense, if the general method (non-domain-specific) already achieves strong performance on the target domains, I think we should regard that general method as a baseline. That's why I mentioned the test-time adaptation (TTA) method as well in my initial review, because TTA also has the same goal as the proposed method, i.e., improvement in performance on specific domains, while the technical approach is different.
* I don't mean that ExPLoRA has no contribution to domain-specific model developments. It seems to be an interesting approach worthy to be exploration. However, the practical usefulness of the proposed method is highly questionable given a relatively minor improvement but huge additional computations compared with finetuning-after-natural-image-pretraining baselines. That's why I think this paper's contribution is not strong enough to recommend this paper towards acceptance, and I believe this paper should be polished to improve its practical usefulness.
_I am so sorry to say this to authors too late (after AC's action), so that they can not gain any opportunity to refute this. Therefore, although I personally feel a strong weakness in the accuracy-efficiency trade-off, and disagree with the authors' statement for the fair comparison, feel free to downweight my review, AC!_
Truly sorry again.
Reviewer 83s5
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Reply to Comment 1.1.1:
Comment: Thank you for your follow-up. Although we've had very limited time for this response, we appreciate the opportunity to offer clarifications.
**Q: Why should we compare ExPLoRA with pre-training baselines? Is domain-specific pre-training really necessary?**
ExPLoRA is fundamentally a pre-training method, meant to produce models for multiple downstream tasks without requiring labeled data.
Our results and multiple prior works cited in our paper clearly demonstrate that domain-specific pre-training is increasingly necessary as the domain gap widens from natural images:
1. While DinoV2+AdaLoRA shows competitive performance only on fMoW-RGB (closer to natural images), natural image models significantly underperform
* On multi-spectral imagery (Table 4): **8-14%** performance gap compared to ExPLoRA and domain-specific models
* On temporal satellite imagery (Table 5): **6% gap** compared to ExPLoRA
* On linear probing (Table 2): ExPLoRA shows an **8% improvement**, demonstrating much higher unsupervised embedding quality critical for tasks like clustering/compression. This substantial gap highlights ExPLoRA's ability to capture meaningful domain-specific features without supervised labels.
2. Pre-training is functionally different from fine-tuning-- it doesn't require expensive human labels and produces models that can be repurposed for multiple downstream tasks (eg: supervised PEFT, feature extraction), with compute amortized across all applications. This is particularly valuable for domains such as satellite/medical imagery where labeling is more expensive and requires specialized expertise [1]. Please see [this response](https://openreview.net/forum?id=OtxLhobhwb¬eId=AapZp7BqgM) for more.
3. ExPLoRA achieves these domain-specific improvements while requiring **>16x fewer parameters and >8x less compute** than fully pre-trained baselines (see [compute augmented Tables](https://imgur.com/a/4xxC3bO)). This efficiency gain is significant for users with limited compute who still need domain-specific models for multiple downstream tasks.
**Q: DinoV2 + AdaLoRA-r8 (78.87) performs better than D-[L]-r64 + SA2VP (78.51)**
This isn't a valid comparison as it varies both initialization and PEFT method. When keeping the PEFT method constant (SA2VP), ExPLoRA clearly improves over DinoV2 by 1% (78.51% vs. 77.53%). Our best configuration, ExPLoRA+LoRA-r8, achieves 79.28% - outperforming all baselines including DinoV2+AdaLoRA and sets a **new state-of-the-art result** on the competitive fMoW-RGB benchmark.
What may appear as "minor improvements" (0.4-1%) in aggregate metrics can translate to significant real-world impacts in high-stakes domains like satellite/medical images.
**Q: Should the pre-training methods be only compared with other pre-training methods?**
No- in fact, our paper includes comprehensive comparisons with both pre-training and fine-tuning approaches. Tables 1, 4-9 all evaluate downstream task performance across various methods.
However, when assessing computational efficiency, it's appropriate to compare pre-training methods with each other because they serve the same function - producing general-purpose backbones usable for _multiple downstream tasks_ without requiring task-specific labels. This is fair as it reflects how these methods would be used in practice.
**Q: TTA also has the same goal as the proposed method, while the technical approach is different**
While both improve specific domain performance, TTA and ExPLoRA have different assumptions:
- TTA assumes shared label spaces between domains
- ExPLoRA produces unsupervised backbones without label space assumptions
These approaches are complementary, not alternatives.
**Q: The practical usefulness given relatively minor improvement but huge additional computations**
ExPLoRA's practical utility lies in replacing full domain-specific pre-training while improving performance. The computational demands are modest- ExPLoRA requires only 100 GPU hours for RGB and 300 GPU hours for multi-spectral data, which is:
- Less than the 200-600 fine-tuning GPU hours required in many cases ([see augmented Table 1](https://imgur.com/a/4xxC3bO))
- 10x less compute, 16x fewer parameters, and 8x smaller carbon footprint than full domain-specific pre-training
- A one-time cost that benefits all downstream applications
The practical benefits include:
- Using ViT-L or ViT-G models on commodity GPUs due to reduced memory/compute footprint
- Allowing researchers with limited resources to customize pre-training for powerful domain-specific models
- Feature extraction with 8% better representations for downstream applications
For applications in satellite, medical or agricultural monitoring, ExPLoRA's improvements translate to meaningful impact at a fraction of traditional costs (Impact statement).
---
We appreciate your engagement, and we hope that our response provides some clarification to your concerns.
---
[1] SatMAE, _NeurIPS 2022_. | Summary: The paper proposes ExPLoRA, a parameter-efficient way to extend pre-training of a large vision transformer from its original domain (e.g. natural images) to a new domain (e.g satellite imagery). ExPLoRA accomplishes this by unfreezing 1-2 transformer blocks for full training and applying low-rank (LoRA) updates on the rest. After this unsupervised adaptation, the model can then be fine-tuned using LoRA on labeled tasks and achieves results that match or surpass fully trained domain-specific models.
Claims And Evidence: In general the paper is sound and the claims are supported by enough evidence. However there are two claims to which I would like to draw attention to:
“As seen, un- freezing an extra block consumes almost double the number of parameters, but fails to yield the same improvement in performance ↓ 0.34%. Thus, simply increasing the number of unfrozen blocks will likely improve performance, but will not do so as effectively as ExPLoRA, and will also significantly and sharply decrease the parameter-efficiency”
In section 6.1.2, the authors provide an ablation study where they attempt to unfreeze blocks at different positions (primarily L and/or L-1). While the table supports this claim, it does not provide sufficient evidence to justify choosing only one block to unfreeze. This table is crucial, as their method depends on having at least one block unfrozen to maintain performance. Therefore, more extensive experimentation with various block positions and different numbers of unfrozen blocks would be valuable, as well as replicating these findings across additional datasets.
“Our results demonstrate an improvement of over ↑8.2% in top 1 average accuracy over prior SoTA methods”
In section 6.1.1, the authors make this claim regarding results from satellite images. This is among the paper's strongest claims (also highlighted in the abstract) and is presented in Table 2. However, the comparison appears unfair because it contrasts Dinov2 pretrained weights without domain adaptation against ExPLoRA, which includes domain adaptation. While insightful, this comparison does not clearly illustrate the main use of their method, which aims at efficient in-domain pretraining.
Additionally, I notice the absence of a Dinov2 model fully pretrained in-domain in Table 1. Including such a model would provide a more equitable comparison, as MAE baselines cannot directly be compared with Dinov2.
Methods And Evaluation Criteria: They perform extensive analysis in a specific use case which is satellite images. Besides, they report results on 3 of WiLDS datasets with additional 2 datasets in the appendix.
Theoretical Claims: There are no theoretical claims.
Experimental Designs Or Analyses: Experimental designs and analyses are overall adequate. They compare with many different PEFT methods, showing the superiority of their approach in this regard.
See section “Claims And Evidence” for missing experiments/baselines.
Supplementary Material: I reviewed section B (Additional Experimental Results) and believe it provides valuable extended insights for future users of this method.
Relation To Broader Scientific Literature: This paper builds upon MAE, DinoV2 and LoRA. They cite appropriately all the methods that they use and state clearly their contributions.
Essential References Not Discussed: None
Other Strengths And Weaknesses: Strengths:
The paper is clear, well-organized, and thorough. It effectively examines the use of LoRA for in-domain pretraining to improve results, offering a straightforward and useful method. The study includes detailed comparisons with different PEFT techniques and covers multiple varied datasets, greatly enhancing the overall analysis.
Weaknesses:
While providing useful insights, the paper's novelty is somewhat limited as it mainly expands on existing methods. Additionally, it is well-known that in-domain pretraining boosts fine-tuning performance. Hence, the paper could focus more on showing efficient methods for achieving this rather than simply restating the performance benefits (see the "Claims and Evidence" section for more details).
Other Comments Or Suggestions: None
Questions For Authors: None
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your valuable comments and for recognizing our thorough experimental validation across baselines and datasets and for providing useful insights into in-domain parameter-efficient pre-training. You may find responses to your questions below:
**Q: Further justification for which blocks to unfreeze for ExPLoRA**
We agree that block selection is an important component of our method. In section 7, we systematically analyze the properties of patch embeddings from different transformer blocks:
* Blocks that output patch embeddings with low mean/variance eigenvalues inversely correlate with higher linear probing accuracy on predicting patch position
* Linear probing accuracy for image class peaks in final layers (which also have low mean/variance eigenvalues), while patch position accuracy peaks in middle layers
* The eigenvalue patterns and classification accuracy suggest unfreezing block L or L-1 would have highest impact for extended pre-training, which is confirmed in section 6.1.2
* ExPLoRA results in lower mean/variance eigenvalues in the unfrozen block's output, and higher classification and localization accuracies across all ViT layers
* Linear probing performance in section 6.1.2 follows: block 23 > block 22 > block 9 > block 1, matching exactly the trend in the mean eigenvalue plot (figure 3)
Upon your suggestion, we've included additional baselines with blocks [L-1,L] and [1,L-1,L] unfrozen in the expanded version of table 3 [linked here](https://imgur.com/a/tWdN4xU). We find that increasing unfrozen blocks with ExPLoRA indeed improves linear probing accuracy, where our highest performing D-ExPLoRA model with blocks [1, L-1, L] unfrozen and LoRA-r64 on the rest achieves 78.04% linear probing accuracy, a 9% improvement over prior SoTA.
Note that while more unfrozen blocks improve performance, each adds to the parameter count. We aim to demonstrate strong results with a limited parameter budget. Our analysis in section 7 provides guidelines for selecting additional blocks to unfreeze when higher parameter budgets are available.
Similar trends as in figures 3-7 held across different datasets, guiding our design choices in other experiments.
**Q: Provide a DinoV2 full pre-training baseline for linear probing for fMoW-RGB**
We agree that this comparison would be useful, however, we want to note that no such baseline in prior literature exists. The SatMAE/ScaleMAE/CrossScaleMAE models were pre-trained on fMoW-RGB, with which we provide direct comparisons to demonstrate that our efficient in-domain pre-training vastly outperforms existing SoTA pre-training methods in the literature by 8% while using 8x-10x less compute.
Upon your suggestion, we have trained a full DinoV2 baseline on fMoW-RGB in the [revised Table 3 linked above](https://imgur.com/a/tWdN4xU). This required ~1200 GPU hours, more than 12x the compute required for ExPLoRA and failed to match its linear probing performance. This likely suggests that much more compute and time is required to pre-train a DinoV2 on fMoW-RGB.
**Q: The paper expands on existing methods**
With ExPLoRA, we demonstrate a highly effective alternative to expensive full pre training for new image domains. While it combines existing methods, we would like to cite peer conference [NeurIPS guidelines](https://neurips.cc/Conferences/2024/ReviewerGuidelines), which mentions that demonstrating the effectiveness of combining existing techniques can provide substantial research value.
---
Thank you again for your time in reviewing our work. We look forward to addressing any follow-up questions you may have. If your concerns are addressed, we kindly ask that you reconsider your score. | Summary: The authors aim to transfer knowledge from large pre-trained vision models to new domains efficiently, and address different downstream tasks. So, given a set of downstream tasks on a new domain, the straightforward approach is to either pre-train from scratch a large model on this new domain and then fine-tune it on the downstream tasks, or to directly fine-tune an existing large model from a different domain on the downstream tasks at hand.
Instead of these approaches, the authors propose Extended Pretraining with LoRA (ExPLoRA), which consists of the following 2 steps. First, a large vision model pre-trained on natural images, like DinoV2 or MAE, is further pre-trained on a new domain, e.g., satellite images. In this pre-training stage there is no use of labels, and the optimization objective is the same as the initial pre-training on the natural images. In this stage, the model in not fully fine-tuned, instead, 1 or 2 layers are fully unfrozen, and LoRA is used for the rest of the layers. In the second step, after the extended pre-training, the model undergoes supervised fine-tuning with a PEFT method on downstream tasks, e.g., classification of satellite images. The core idea is that extended pre-training can be considerably more efficient compared to training from scratch on a new domain, while performance is not compromised, and can even improve, especially compared to directly fine-tuning on downstream tasks.
The authors conduct multiple experiments to validate their method and explore its behavior. They use DinoV2 and MAE as pre-trained models on natural images, and they show that in most cases, ExPLoRA outperforms both models trained from scratch on new domains, as well as models directly fine-tuned on downstream tasks. Their primary experiments are on satellite images, both RGB and spectral, but they show similar results on different domains as well, e.g., WiLDS datasets. Also, they show promising results across different downstream tasks, e.g., image classification, segmentation, and object detection. In addition, they conduct ablation studies to justify their design choices and explore the features learned by ExPLoRA. Finally, additional experiments and analysis of the models behavior is provided in the supplementary material, e.g., the effect of the model size, or that of the duration of extended pre-training.
## update after rebuttal
The authors addressed the main points of my review, so I increased my score from 3 to 4.
Claims And Evidence: - Performance:
- The authors compare against the 2 main settings they aim to improve on, which is training from scratch on a new domain, and fine-tuning a pre-trained model from a different domain. I think the authors demonstrate clearly that ExPLoRA can lead to performance benefits, since it outperforms or achieves comparable performance across multiple datasets of different size and content, downstream tasks, heads (linear probe and original heads), and backbones (DinoV2 and MAE).
- Efficiency:
- It is clear that ExPLoRA uses much fewer parameters compared to training a model from scratch, since it unfreezes 1 or 2 layers, and commonly uses LoRA with up to $r=64$ for the rest of the layers. However, the required compute is not included in any of the Tables or Figures. For example, in Table 1, D-[L]-r64 with LoRA-r8 PEFT outperforms DinoV2 with LoRA-r8 by 1.2%, but at what cost in terms of compute? If I am not mistaken, in this case the ExPLoRA model and the baseline undergo the same fine-tuning on the downstream task, but the ExPLoRA model requires an additional pre-training phase, which according to Section C.1. in the Appendix, it corresponds to 200,000 additional training iterations. I understand that it may worth conducting the pre-training if performance is a priority, or if the ExPLoRA model will be used for multiple downstream tasks, so, I want to clarify that I don’t think ExPLoRA should have comparable training GPU hours with all baselines, but I think this should be clearly mentioned in the experiments, since efficiency is a primary motivation for this work.
- In addition, in Section B.2. in the Appendix, we can see that the DinoV2 baselines reach close to their peak performance after as few as approximately 30 GPU hours, while the best ExPLoRA model needs 420 GPU hours to reach its peak performance. So, I think the authors should have more experiments like this included in the main text (not just in the Appendix), and explicitly discuss compute requirements.
Methods And Evaluation Criteria: I think the authors use appropriate baselines, datasets and ablation studies. As I mentioned in the previous section, what I think is missing, is an elaborate discussion about compute.
Theoretical Claims: There aren’t any theoretical claims or proofs.
Experimental Designs Or Analyses: I think the experiments are well designed, and as I mentioned before, the authors do extensive evaluations, covering diverse scenarios. One remark I have is that in most experiments, the backbone is ViT-L, which raises questions about whether the presented results generalize to bigger scales. To their credit, the authors conduct experiments with more diverse backbones in Section B.5. in the Appendix, where they experiment with ViT-G, so, given the importance of model scale for modern applications, I would suggest to include and/or discuss such experiments in the main text.
Supplementary Material: - I think the datasets are not always adequately described, e.g., the number of images in the splits of fMoW. If not in the main text, I think the authors should include such important details about the datasets in the Appendix.
- ln 760-761, Section B.2.: “Fine-tuning DinoV2 with block 24 unfrozen and LoRA-r64 (matching ExPLoRA’s parameter budget)”. However, in Fig. 7, the FT params for DinoV2-U=[L]-r64 (orange line) is 31.1M, and for ExPLoRA models the pre-training params are 18.7M.
- ln 765: Is it 320 GPU hours or 420?
Relation To Broader Scientific Literature: The proposed method directly combines in a new way 2 fundamental ideas in the literature, unsupervised pre-training (e.g., DinoV2), and PEFT (e.g., LoRA). The main contribution is that PEFT should not be seen solely as a method to address downstream tasks when a large pre-trained model is available, but it is beneficial to first apply PEFT to extend pre-training, and then re-apply PEFT on downstream tasks.
Essential References Not Discussed: Nothing to add.
Other Strengths And Weaknesses: I would like to mention that the manuscript is very well written and easy to follow. Also, the authors motivate well the importance of satellite images, and why they focus on this image domain.
Other Comments Or Suggestions: - Eq. 6: I think notation $\Theta (r)$ is a bit confusing based on the explanation provided “where $r$ controls the fraction of trainable weights”, and the fact that $r \in [0, \infty]$. $r$ is usually used to represent the LoRA rank, which is the way it is used in Eq. 5 as well.
- ln 321, col 1: I think ExPLoRA-L-r8 is in row 11 instead of 10.
- Table 3 is discussed in Section 6.1.2., and there are multiple references to different rows, e.g., rows 11-13. It would be easier to follow such references if the rows of Table 3 were indexed.
- ln 314, col 2: I think it should be “row 3” for LoRA-tuned MAE instead of “row 4”. Similarly, in ln 315, should be “row 7” instead of “row 6”.
- In the iWildcam experiment (paragraph that starts in ln 375, col 2), the authors discuss why the linear probing performance of ExPLoRA suffers in comparison to DinoV2, emphasizing on the small domain gap. However, it is not clear to me why this is a valid hypothesis. In particular, this could explain ExPLoRA and DinoV2 having a small difference in performance, and not DinoV2 clearly outperforming ExPLoRA. I think it would be useful to clarify this argument further.
- In Fig. 3-6, the legend has names “D-ExPLoRA-blk23r64” and “M-ExPLoRA-blk23r64”, I guess “blk23” corresponds to the unfrozen block, but this notation is not used anywhere else in the paper; the same naming is used in Fig. 9 as well.
Questions For Authors: I don’t have additional questions.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for your detailed and insightful feedback. We appreciate your recognition of ExPLoRA’s novelty in combining fundamental ideas and its strong empirical performance across datasets.
**Q: Discussion of required compute of ExPLoRA vs fine-tuning baselines**
We agree that more details on compute requirements is needed, which we have added to the main text. Upon reviewing the feedback, we'd like to clarify:
* ExPLoRA is a pre-training method and is meant to provide an efficient alternative to domain-specific _full or continual pre-training_ (eg: SatMAE, ScaleMAE, GFM, etc.). These methods require at least 8x more compute than ExPLoRA pre-training and achieve lower or similar performance to ExPLoRA across different domain gaps (eg: RGB, multi-spectral, temporal data).
* Directly comparing compute requirements for fine-tuning vs extended pre-training + fine-tuning paints an incomplete picture. The ExPLoRA pre-training phase is functionally different from fine-tuning a natural-image pre-trained model. A pre-trained checkpoint serves multiple purposes- feature extraction, linear-probing, fine-tuning on various downstream tasks etc. In contrast, compute used for supervised fine-tuning yields a model usually suited for just one task (eqs 2, 3). Pre-training compute is amortized across multiple downstream tasks, and would be double counted if included in the fine-tuning budgets for each specific task.
* We realize now that Figure 7 in section B.2 is incomplete. It only compares the compute for fine-tuning a natural image model (eg: DinoV2) vs. pre-training + fine-tuning for ExPLoRA, for the fMoW-RGB task. Crucially, the pre-training + fine-tuning compute required for full domain-specific pre-training (eg: SatMAE, ScaleMAE) is missing. Further, for different domains (eg: multi-spectral satellite images), the gap between fine-tuning a natural-image model (eg: MAE) and domain-specific pre-training is much larger than for fMoW-RGB (i.e. 6%, from Table 4). Lastly, to reiterate, a directly fine-tuned DinoV2 on fMoW RGB is less flexible than an ExPLoRA pre-trained model, as the latter can be used as any _pre-trained model_- for feature extraction, probing, or further task-specific fine-tuning.
We've expanded Tables 1 and 4 with compute details [linked here](https://imgur.com/a/iMjgOHv). Note that:
* We only need to allocate 100 GPU hours to ExPLoRA pre-training to achieve the reported gains. For fairness, we use ~220 GPU hours for fine-tuning across models.
* Providing extra 100 GPU hours to fine-tuning non-ExPLoRA baselines (for an equitable total compute comparison) doesn't improve top-1 accuracy.
* VPT techniques significantly increase fine-tuning compute by extending token sequence length.
**Q: The DinoV2 baselines reach close to their peak performance in 30 GPU hours while ExPLoRA requires 420 GPU hours**
This is not a direct comparison, since Figure 7 provides different fine-tuning variants. The red curve is DinoV2 fine-tuned with LoRA-r8, which we also use for ExPLoRA models. The orange and purple curves have blocks unfrozen with LoRA-r64, representing a similar parameter budget to ExPLoRA pre-training. The orange curve reaches peak performance at ~260 GPU hours, by which point all ExPLoRA models have surpassed it.
**Q: Experimental results on larger backbone sizes beyond ViT-L**
Thank you for the suggestion. As you mention, we compare with ViT-B and ViT-G in Table 15 (appendix B.5). ViT-G experiments are more expensive (>3x parameters vs ViT-L), especially on academic compute budgets. Most prior work uses ViT-L as their backbone, so we maintain this architecture for fair comparison in our main experiments.
**Q: More detailed descriptions of datasets**
Thank you- we'll include further dataset details in the appendix. For fMoW:
* fMoW-RGB: 363k training, 53k test data points
* fMoW-Sentinel: 713k training, 85k test data points
**Q: lines 760-761, parameter budget clarification**
You're right - it should be 18.7M.
**Q: ln 765: Is it 320 GPU hours or 420?**
Within 320 total hours (pre-training + fine-tuning), ExPLoRA achieves >1% improvement over the DinoV2 baseline. The 420 hour limit was added as a buffer to demonstrate earlier convergence.
**Q: Eq.6 $\Theta(r)$ notation**
Thank you- the notation should be $\Theta$ to refer to an unconstrained parameter space (regular full-rank weights).
**Q: iWildcam linear probing result**
The unfrozen ViT block likely overfit to the training data due to the small domain gap. This effect disappears with PEFT (showing improvement over DinoV2) since all ViT attention layers' Q,V matrices are tuned with LoRA.
**Q: Row number clarifications and "blk" notation in figures 3-6**
Thank you! We've corrected these mistakes in our manuscript.
---
Thank you for your thorough feedback which has improved our paper. Please let us know if you have follow up questions. If your main concerns are resolved, we kindly request that you reconsider your score.
---
Rebuttal Comment 1.1:
Comment: I would like to thank the authors for responding to all issues I raised. I have the following comments:
- Discussion of required compute of ExPLoRA vs fine-tuning baselines
- I appreciate the detailed answer, I agree with the authors' comments, and the updated Tables are really useful. Though, I would like to ask, why only Table 1 and Table 4, and why the updated Tables are subsets of the original ones? I think compute measurements should be provided for all experiments.
- More detailed descriptions of datasets
- I think there are more datasets without details about the split sizes, e.g., WiLDS. I would suggest the authors to go through all the reported datasets and add missing details.
- In Appendix C.5. is mentioned that "Hyperparameter and training configuration details are the same as in appendix C.1", does this include number of training iterations? because there are significant differences in the dataset sizes.
- One last question, what is the architecture of the heads used with PEFT fine-tuning for downstream tasks? They were the same for the baselines? I apologize in advance if this information is already included, I realized I didn't remember since I first reviewed the paper, and I couldn't find this information by skim reading through the manuscript again.
In summary, if the authors can confirm that will add in the updated manuscript a discussion about compute which includes the points they make in "Q: Discussion of required compute of ExPLoRA vs fine-tuning baselines", and assuming that there won't be any issue with my additional questions, especially since the provided updated Tables already address my main concerns, I would be happy to increase my score.
---
Reply to Comment 1.1.1:
Comment: Thank you again for your detailed review and support of our work. For answers to your follow up questions:
**Q: Why were only Table 1 and Table 4 updated, and why are they a subset of the original?**
Yes, we agree-- we only provided subsets of Table 1 and 4 for brevity in the rebuttal. We will provide compute details for all experiments in our updated paper, such as [at this link](https://imgur.com/a/4xxC3bO), in tabular format for our main experiments, and in the appendix for other experiments if space does not permit. Thank you for letting us know that the updated tables are useful and that they resolved your main concerns.
**Q: More detailed description of datasets (eg: WiLDS)**
We will provide full split details for all datasets in the revised appendix for the camera-ready. Here are the train/val splits for all datasets for your reference:
| Dataset | #Train | #Validation |
|---------|--------|-------------|
| fMoW-RGB | 363.6k | 53.0k |
| fMoW-Sentinel | 712.9k | 84.9k |
| fMoW-Temporal | 83.4k | 14.2k |
| SpaceNet V1 | 6.0k | 1.5k |
| Resisc-45 | 18.9k | 6.3k |
| NAIP | 244.4k | 55.5k |
| EuroSAT | 16.2k | 5.4k |
| Camelyon17 | 302.4k | 33.6k |
| iWildcam | 129.8k | 7.3k |
| Globalwheat | 2.9k | 0.4k |
| VisDA2017 | 152.3k | 55.4k |
**Q: Is the number of training iterations the same across datasets?**
Thank you for catching this. You are right that some datasets have vastly different numbers of training images. For the smaller datasets, we used ExPLoRA for extended pre-training for a smaller number of iterations. We will make sure to provide these details in the modified appendix. The details are summarized here:
* 200k iterations: fMoW-RGB, Camelyon17, VisDA2017, NAIP
* 150k iterations: iWildcam
* 80k iterations: fMoW-Sentinel, fMoW-Temporal, Globalwheat
* 10k iterations: SpaceNet v1
Resic-45 and EuroSAT required no extra pre-training, since we used our ExPLoRA pre-trained models from fMoW-RGB or fMoW-Sentinel.
While fMoW-Sentinel is the largest, processing each multi-spectral input via the group-channel ViT is also more expensive than for an RGB input since the input token sequences are 2-3x longer. We found that 80k pre-training steps was sufficient for ExPLoRA’s performance gains, although more pre-training may benefit the model further.
While Globalwheat is a small dataset, each image is of a much higher resolution (1024x1024). Thus we are able to pre-train at a 224x224 resolution for 80k steps since data augmentation techniques such as random crops provide enough variety for pre-training.
**Q: What is the architecture of the heads used with PEFT fine-tuning for downstream tasks?**
The architecture used for PEFT depends on both the task and the PEFT method. We keep a given PEFT architecture the same across all experiments for a given task, unless specified otherwise such as in B.2 Figure 7. For example, for image classification in fMoW-RGB with LoRA-r8 PEFT, the “head” is a trainable linear head that is initialized from scratch. The rest of the ViT backbone is frozen. The trainable LoRA “adapters” are initialized from scratch with the specified rank (eg: 8), and applied on Q, V matrices of all attention layers. For a given PEFT configuration, the main thing that differs is the initialization of the frozen ViT backbone, which can be DinoV2 (or other natural image baselines), ExPLoRA, or fully-pretrained baselines (such as SatMAE, ScaleMAE etc.) For segmentation, we used the same PSANet head architecture used in SatMAE, and for detection, we use Detectron2 as specified in the Globalwheat experiment.
**Q: Can the authors confirm that the updated manuscript will include a discussion about compute?**
Yes, we can confirm that our updated manuscript will include this discussion and the points we made in our rebuttal response. We thank you again for your insightful feedback, and we also agree that the discussion on compute provides valuable detail to future users of our method- especially as ExPLoRA requires ~10x less compute than full pre-training baselines to achieve the same or higher performance.
---
We hope that these explanations resolve your remaining questions. We appreciate your willingness to increase your rating of our work and thank you again for your vote of confidence in our method. | null | null | null | null | null | null |
Scalable Generation of Spatial Transcriptomics from Histology Images via Whole-Slide Flow Matching | Accept (spotlight poster) | Summary: This paper proposes a method to predict gene expression from histology whole-slide images using generative flow matching. Spatial transcriptomics (ST) datasets are used to train and evaluate the model. A foundation-model encoder is used to extract visual features. Spatial attention is used to model spatial dependencies. Flow matching models the joint distribution of gene expression over the whole slide in an iterative fashion.
## update after rebuttal:
After carefully reviewing the author's rebuttal and considering other reviewer's input, i decide to keep my accept rating.
Claims And Evidence: The method claim to better consider cell-cell interaction through both spatial attention at the encoder and the flow matching iterative generative process. Although spatial attention clearly provides a way to model spatial dependencies, it is not very clear intuitively how the flow matching (FM) helps. Nevertheless, the ablation study shows that without FM, there's a small performance degradation on all benchmarks.
Methods And Evaluation Criteria: The proposed method is appropriate for the problem. In particular, it has been proven in the litterature that ST model benefits from spatial attention as the tumor generally grows out spatially. THe evaluation benchmark dataset are also appropriate for the task and have been used previously in the literature.
Theoretical Claims: No theoretical claims are made in the paper.
Experimental Designs Or Analyses: The experimental section includes 8 baselines (5 spot-base and 3 slide-based) across two benchmark ST datasets (each covering several organs). Further, two ablation studies verify the effectiveness of each module of the proposed approach, showing the improvement for each one.
Overall, this is a sound and valid experimental section.
Supplementary Material: Supplementary material is about implementation details of the 8 baselines, stats of the datasets and details of the ablation studies.
Relation To Broader Scientific Literature: The key contributions are well-related to specific litterature, in my opinion. Both key contributions (spatial attention and flow matching) are properly related to current publications and the ST litterature is also well referenced.
Essential References Not Discussed: Not that i know of.
Other Strengths And Weaknesses: strengths:
- The paper applies flow-matching methods (used in generative modeling of molecule and proteins) to gene expressions regression from image encodings. This is novel, as far as i know.
- a strong experimental analysis with extensive benchmark, ablation + complexity studies
- outperforms SOTA methods
- well written and organized. Clear math and algorithms.
- code repository is proposed
cons:
- a complex system with several modules and hyperparameters makes it challenging to evaluate
-
Other Comments Or Suggestions: no typos to report!
Questions For Authors: No questions.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We sincerely thank you for the insightful comments and will revise the manuscript accordingly. Please see our detailed responses below:
```
A complex system with several modules and hyperparameters makes it challenging to evaluate.
```
Ans: Thank you so much for the feedback. STFlow primarily consists of two core components: (1) a frame averaging (FA)-based encoder and (2) a flow matching (FM) optimization framework. We evaluate their effectiveness by (i) comparing different geometric encoders and ablating FA, and (ii) removing the iterative refinement process. Additionally, we provide results on varying the number of refinement steps and ZINB prior hyperparameters to further assess stability below. We will refine our discussion to more clearly highlight each component’s contribution.
| #steps | S=1 | S=2 | S=5 | S=10 | S=16 |
| --- | --- | --- | --- | --- | --- |
| IDC | 0.580(.005) | 0.585(.002) | 0.587(.003) | 0.585(.001) | 0.585(.001) |
| PRAD | 0.420(.003) | 0.416(.003) | 0.421(.002) | 0.414(.003) | 0.415(.004) |
| PAAD | 0.488(.001) | 0.498(.001) | 0.507(.004) | 0.499(.001) | 0.498(.001) |
| SKCM | 0.705(.002) | 0.707(.005) | 0.704(.005) | 0.703(.005) | 0.703(.005) |
| COAD | 0.315(.008) | 0.343(.004) | 0.326(.009) | 0.320(.003) | 0.321(.004) |
| READ | 0.232(.009) | 0.239(.002) | 0.240(.014) | 0.239(.003) | 0.239(.004) |
| CCRCC | 0.322(.001) | 0.340(.002) | 0.332(.003) | 0.330(.002) | 0.319(.003) |
| HCC | 0.115(.008) | 0.119(.002) | 0.124(.004) | 0.117(.003) | 0.118(.002) |
| LUNG | 0.604(.002) | 0.612(.002) | 0.610(.002) | 0.611(.002) | 0.611(.001) |
| LYMPH_IDC | 0.278(.002) | 0.310(.001) | 0.305(.001) | 0.306(.001) | 0.305(.001) |
| Average | 0.405 | 0.417 | 0.415 | 0.412 | 0.411 |
| ZINB(mean, number of failures) | (0.1,1) | (0.2,1) | (0.4,1) | (0.1,2) | (0.2,2) | (0.4,2) | (0.1,4) | (0.2,4) | (0.4,4) |
| --- | --- | --- | --- | --- | --- | --- | --- | --- | --- |
| IDC | 0.586(.001) | 0.585(.003) | 0.585(.001) | 0.584(.001) | 0.585(.002) | 0.587(.003) | 0.585(.001) | 0.583(.001) | 0.585(.001) |
| PRAD | 0.417(.002) | 0.415(.001) | 0.413(.000) | 0.415(.000) | 0.421(.002) | 0.413(.001) | 0.415(.000) | 0.415(.002) | 0.418(.001) |
| PAAD | 0.496(.002) | 0.507(.004) | 0.499(.000) | 0.499(.005) | 0.502(.004) | 0.500(.001) | 0.498(.000) | 0.499(.002) | 0.502(.006) |
| SKCM | 0.707(.007) | 0.704(.002) | 0.710(.004) | 0.704(.007) | 0.709(.003) | 0.704(.009) | 0.709(.003) | 0.703(.005) | 0.707(.008) |
| COAD | 0.339(.002) | 0.342(.003) | 0.341(.004) | 0.343(.000) | 0.338(.003) | 0.343(.004) | 0.342(.002) | 0.343(.006) | 0.340(.000) |
| READ | 0.253(.003) | 0.231(.000) | 0.243(.000) | 0.247(.004) | 0.244(.004) | 0.245(.000) | 0.236(.001) | 0.246(.000) | 0.249(.002) |
| CCRCC | 0.339(.001) | 0.337(.003) | 0.340(.004) | 0.334(.000) | 0.342(.008) | 0.329(.005) | 0.334(.000) | 0.336(.002) | 0.337(.003) |
| HCC | 0.118(.001) | 0.122(.000) | 0.123(.005) | 0.120(.003) | 0.120(.001) | 0.122(.004) | 0.126(.002) | 0.125(.003) | 0.124(.003) |
| LUNG | 0.611(.001) | 0.611(.000) | 0.611(.001) | 0.610(.000) | 0.611(.001) | 0.610(.001) | 0.608(.001) | 0.609(.000) | 0.613(.001) |
| LYMPH_IDC | 0.308(.001) | 0.310(.002) | 0.308(.001) | 0.309(.000) | 0.308(.001) | 0.304(.000) | 0.306(.001) | 0.305(.002) | 0.304(.002) | | Summary: This paper proposes a flow matching (FM) approach (called STFlow) for predicting the spatial transcriptomics (ST) from pathological Whole-Slide Images (WSIs). The core designs of STFlow contain i) learning the joint distribution $p(Y_0,\cdots,Y_N|I_0,\cdots,I_N)$ using the FM approach and ii) the E(2)-invariant spatial attention that adapts frame averaging (FA) to the attention operation for learning invariant spot-level representations. Two large-scale benchmarks are adopted to verify the effectiveness of STFlow. The experimental results show the superiority of STFlow over existing methods.
## update after rebuttal
Thanks for the author's rebuttal and the additional results. My concerns are well addressed. I am happy to raise my score from 2 to 3. The authors are encouraged to include the addition results into the revised paper and also carefully revised the paper to further improve the presentation quality.
Claims And Evidence: Most of the claims are justified by empirical experiments. However,
- the effectiveness of the author's one core design, *i.e.*, modeling the joint distribution $p(Y_0,\cdots,Y_N|I_0,\cdots,I_N)$, seems to lack convincing evidence.
- In addition, I have several concerns about the experimental design and the results, which are specified below for the authors to answer in the rebuttal.
Methods And Evaluation Criteria: **Methods**: Yes, the proposed methods make sense for the problem studied in this paper.
**Evaluation Criteria**: Some commonly-used metrics are not presented in the paper.
Theoretical Claims: N/A
Experimental Designs Or Analyses: Yes, I have carefully checked the experimental design and the results. I have several concerns about them:
- Lack of the experiments for the setting of $S$ and the visualization of the inference process of FM. These experiments could help to validate the stability of the proposed method and help readers better understand the model.
- Some results have large variance (Table 1). This calls into question the stability of the proposed method.
Supplementary Material: N/A
Relation To Broader Scientific Literature: No. The key contribution of this paper seems independent with existing works.
Essential References Not Discussed: No
Other Strengths And Weaknesses: Strengths:
- This paper propose a new generative approach to predicting ST from WSIs. It learns the joint distribution $p(Y_0,\cdots,Y_N|I_0,\cdots,I_N)$ using the FM framework. This seems novel and could be a valid contribution to the field.
- The proposed STFlow considers to learn the invariant representation for spots via E(2)-invariant spatial attention.
- Impressive results are obtained in this paper. STFlow often outperforms existing methods by large margins.
Weaknesses:
- The presentation quality is subpar. The authors fail to clarify how they tackle the issues of existing methods in Introduction. Please see *Questions For Authors* for more details
- Some important experiments are not presented in this paper. In addition, an important design in STFlow, *i.e.*, modeling the joint distribution $p(Y_0,\cdots,Y_N|I_0,\cdots,I_N)$, seems to lack justification. Please see *Questions For Authors* for more details
Other Comments Or Suggestions: Please see *Questions For Authors*
Questions For Authors: The proposed approach seems interesting and novel. Moreover, some promising results are obtained in this paper. Overall, I acknowledge this paper's technical contribution to the field and the novelty of the proposed scheme. However, I have several concerns about the presentation quality and experiments of this work. My concerns and questions are as follows:
- The Introduction analyzes the issues of existing schemes yet does not clearly explain how this work tackles these issues. Although some explanations are made in the following sections, this way could lead to inefficient reading.
- The layout of some Tabs and Figs could be improved, *e.g.*, Tab 2 on page 6.
- Could the authors provide the visualization of the inference process of FM. This experiments could help readers better understand STFlow.
- Could the authors represent the results of STFlow with different $S$. It may help to validate the stability of the proposed method.
- Some results have large variance (Table 1). This may call into question the stability of the proposed method.
- Some commonly-used metrics seem missing, *e.g.*, those metrics presented in the compared methods, TRIPLEX and HisToGene.
- How is the `w/o FM` implemented? I fail to find the details.
- The effectiveness of one core design, *i.e.*, modeling the joint distribution $p(Y_0,\cdots,Y_N|I_0,\cdots,I_N)$, seems to lack convincing evidence. How is this core design justified? Could the authors explain this?
- It would be better to provide an intuitive expatiation for how FM realizes the modeling of joint distribution. This could be more friendly to the reader unfamiliar with FM.
- In Algo.2, is $Y_0$ sampled once or multiple times when deriving the prediction of one WSI from the model?
If my concerns could be resolved, I would be happy to raise my rating.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We sincerely thank you for the insightful comments and will revise the manuscript accordingly. Due to character limits, all additional results are available in our anonymous codebase: https://anonymous.4open.science/r/Anonymous_STFlow-3616/.
```
The Introduction analyzes the issues of existing schemes yet does not clearly explain how this work tackles these issues.
```
Ans: STFlow addresses the issues as follows: (1) it reduces computational complexity via a spatial local attention mechanism, (2) it enhances spatial dependency modeling by encoding and incorporating relative orientation into attention, and (3) it captures cell-cell interactions through flow matching that effectively uses gene expression as context. We will clarify these points in the manuscript.
```
The layout of some Tabs and Figs could be improved, *e.g.*, Tab 2 on page 6.
```
Ans: Thank you for pointing this out! We will improve the layout of all tables and figures in the revised manuscript.
```
Could the authors provide the visualization of the inference process of FM. This experiments could help readers better understand STFlow.
```
Ans: We include two examples showing how STFlow refines gene expression predictions in [link](https://anonymous.4open.science/r/Anonymous_STFlow-3616/rebuttal/refinement_process.png). Step 1 shows the initial random sample Y_0, and Steps 2–5 indicate progressive denoising. The results illustrate how flow matching gradually converges to the final prediction via interpolation with a decay coefficient. The results will be included in the revised manuscript.
```
Could the authors represent the results of STFlow with different S.
```
Ans: We report STFlow’s performance across different numbers of refinement steps in [link](https://anonymous.4open.science/r/Anonymous_STFlow-3616/rebuttal/FM_sample_steps.md). The results show a clear improvement from one-step prediction (S=1) to introducing iterative refinement (S=2). In certain datasets, performance improves up to S = 5 (e.g., PAAD: 0.488 → 0.507). However, gains plateau or slightly decline beyond that. This observation aligns with prior works such as AlphaFlow and RNAFlow, which adopt S=5 as the default setting. The analysis will be included in the revised manuscript.
```
Some results have large variance (Table 1).
```
Ans: For the HEST benchmark with cross-validation, the variances are generally low, indicating stable performance. On STImage, which uses a train-val-test split, slide-based methods show higher variance than spot-based ones, likely due to variability in spatial patterns and the noise introduced by slide-level aggregation. Nevertheless, STFlow achieves lower variance than the SOTA baseline TRIPLEX in most cases.
```
Some commonly-used metrics seem missing.
```
Ans: We followed the HEST-1k benchmark setup, which uses Pearson correlation to evaluate performance. Metrics like MSE or MAE depend on absolute expression values and can be influenced by different normalization strategies, making direct comparisons less reliable. The MSE metrics on HEST are shown in [link](https://anonymous.4open.science/r/Anonymous_STFlow-3616/rebuttal/MSE.md), from which STFlow achieves the best performance.
```
How is the w/o FM implemented?
```
Ans: "STFlow w/o FM" refers to the model where the iterative refinement is removed and one-step prediction is performed, i.e., setting the number of sampling steps S = 1. We will clarify this in the revised manuscript to avoid confusion.
```
The effectiveness of one core design, *i.e.*, modeling the joint distribution p(Y0,⋯,YN|I0,⋯,IN), seems to lack convincing evidence.
```
Ans: Modeling the joint distribution captures dependencies across spatial spots, rather than predicting each independently. Our flow matching framework enables this by using whole-slide gene expressions as context during iterative refinement. Its effectiveness is shown in the “STFlow w/o FM” ablation, where removing the refinement process reduces the model to a one-step predictor. Prior gene imputation studies also support the value of leveraging spatial gene expression context.
```
It would be better to provide an intuitive explanation for how FM realizes the modeling of joint distribution.
```
Ans: Flow matching models the joint distribution by iteratively refining each spot’s gene expression using predictions from neighboring spots. This allows information to flow across spatial locations, so each prediction is influenced by its context. Through this process, the model learns how gene expressions co-vary across the tissue, effectively capturing the joint distribution.
```
In Algo.2, is Y0 sampled once or multiple times when deriving the prediction of one WSI from the model?
```
Ans: In our current implementation, Y_0 is sampled once per inference. A potential improvement is to sample multiple times and select the most confident prediction using a confidence model, which will be explored for future work.
---
Rebuttal Comment 1.1:
Comment: Thanks for the author's rebuttal and the additional results. The authors are encouraged to include the addition results into the revised paper and also carefully revised the paper to further improve the presentation quality.
---
Reply to Comment 1.1.1:
Comment: We sincerely appreciate your suggestions and will revise our paper accordingly. All results will be included in the manuscript. | Summary: The paper introduces a scalable and efficient framework for predicting spatial transcriptomics from histology images. By integrating flow matching for progressive gene refinement, E(2)-invariant spatial attention for robust spatial modeling, and whole-slide scalability, STFlow formulates gene expression prediction as a generative modeling task, effectively capturing spatial dependencies and cell-cell interactions while overcoming the limitations of existing approaches. Experimental results demonstrate that STFlow achieves state-of-the-art performance on 17 benchmark datasets (HEST-1k and STImage-1K4M), excelling in gene expression prediction and biomarker identification tasks. It outperforms pathology foundation models in spatial gene expression prediction and achieves the highest correlation scores in biomarker gene prediction (GATA3, ERBB2, UBE2C, VWF), demonstrating its effectiveness in modeling spatial dependencies and gene interactions.
Claims And Evidence: Overall, the claims in the paper are well-supported by quantitative evidence. However, to further validate the choice of ZINB, an ablation study on its hyperparameters (μ,ϕ,π) should be conducted to demonstrate their impact on prediction performance. Additionally, a hyperparameter study on the number of refinement steps in the flow matching process is needed to assess its contribution to model accuracy and convergence stability.
Methods And Evaluation Criteria: The proposed methods and evaluation criteria in the submission appear well-aligned with the problem of spatial transcriptomics prediction.
STFlow addresses the challenge of predicting spatial transcriptomics from histology images by introducing a flow matching-based generative model. STFlow explicitly models the joint distribution of gene expression across the entire slide, incorporates cell-cell interactions, and employs a local spatial attention-based slide-level encoder to reduce computational overhead. This approach overcomes the limitations of previous methods, which struggled with capturing spatial dependencies and suffered from high computational complexity.
Evaluated on two large-scale benchmark datasets, HEST-1k and STImage-1K4M, STFlow outperforms eight state-of-the-art baselines in gene expression and biomarker prediction, achieving a relative improvement compared to pathology foundation models while demonstrating superior computational efficiency.
The evaluation criteria include Pearson correlation for gene expression prediction, accuracy in predicting four key biomarkers, and computational efficiency metrics such as runtime and memory usage, ensuring a robust and comprehensive assessment.
Theoretical Claims: No
Experimental Designs Or Analyses: The study introduces STFlow, a deep learning-based approach for predicting spatial transcriptomics (ST) data from histology images. Overall, the experimental design and analysis are rigorous, and the effectiveness of the model has been validated through multiple evaluations.
Regarding the experimental design, the study compares spot-based and slide-based methods to ensure a comprehensive performance assessment. Additionally, it employs two large-scale benchmark datasets, HEST-1k and STImage-1K4M, which help reduce dataset-specific biases. To prevent data leakage, k-fold cross-validation is used, with patient-stratified splits ensuring that training and test sets do not overlap at the patient level. The study also conducts ablation experiments to assess the contributions of key components, such as the flow matching mechanism and spatial attention module, to model performance.
In terms of analysis, the study employs Pearson correlation coefficient as the primary evaluation metric to measure the relationship between predicted and actual gene expression levels. Additionally, it evaluates model performance on four critical biomarkers (GATA3, ERBB2, UBE2C, and VWF), demonstrating superior predictive accuracy over existing methods. The study also provides visualizations of gene expression predictions, showing a strong alignment between STFlow’s predictions and ground-truth expression levels, enhancing interpretability.
Supplementary Material: I reviewed the supplementary material, including implementation details, dataset statistics and additional ablation studies.
Relation To Broader Scientific Literature: First, Previous methods either predicted gene expression independently for each spot, neglecting cell-cell interactions, or relied on computationally expensive global attention mechanisms. STFlow overcomes these issues by introducing a flow matching-based generative modeling framework, which models the joint distribution of gene expression across an entire slide. This allows for iterative refinement, leading to more biologically meaningful predictions.
Second, STFlow leverages spatial attention with E(2)-invariant properties, ensuring robustness to spatial variations such as rotation and translation.
Essential References Not Discussed: No
Other Strengths And Weaknesses: This paper is clearly written and easy to read. It presents a novel approach to spatial transcriptomics prediction by introducing flow matching-based generative modeling, which effectively models joint gene expression distributions across entire slides while incorporating cell-cell interactions. STFlow demonstrates state-of-the-art performance on HEST-1k and STImage-1K4M, achieving improvement over pathology foundation models. Additionally, it excels in biomarker prediction experiments, accurately predicting key genes such as GATA3, ERBB2, UBE2C, and VWF, highlighting its potential for clinical applications.
Other Comments Or Suggestions: No
Questions For Authors: 1. The authors should perform a hyperparameter study on the number of refinement steps in the flow matching process.
2. The authors should conduct an ablation study on the hyperparameters of the ZINB prior (μ, ϕ, π) to demonstrate their impact on prediction performance.
Ethical Review Concerns: No
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thanks for your feedback on our work! We will explain your concerns point by point.
```
The authors should perform a hyperparameter study on the number of refinement steps in the flow matching process.
```
Ans: We report STFlow’s performance across different numbers of refinement steps below. The results show a clear improvement from one-step prediction (S=1) to introducing iterative refinement (S=2). In some datasets, performance continues to improve up to S = 5 (e.g., PAAD: 0.488 → 0.507). However, gains plateau or slightly decline beyond that. This trend aligns with prior works like AlphaFlow and RNAFlow, which also adopt S=5 as default. The analysis will be included in the revised manuscript.
| #steps | S=1 | S=2 | S=5 | S=10 | S=16 |
| --- | --- | --- | --- | --- | --- |
| IDC | 0.580(.005) | 0.585(.002) | 0.587(.003) | 0.585(.001) | 0.585(.001) |
| PRAD | 0.420(.003) | 0.416(.003) | 0.421(.002) | 0.414(.003) | 0.415(.004) |
| PAAD | 0.488(.001) | 0.498(.001) | 0.507(.004) | 0.499(.001) | 0.498(.001) |
| SKCM | 0.705(.002) | 0.707(.005) | 0.704(.005) | 0.703(.005) | 0.703(.005) |
| COAD | 0.315(.008) | 0.343(.004) | 0.326(.009) | 0.320(.003) | 0.321(.004) |
| READ | 0.232(.009) | 0.239(.002) | 0.240(.014) | 0.239(.003) | 0.239(.004) |
| CCRCC | 0.322(.001) | 0.340(.002) | 0.332(.003) | 0.330(.002) | 0.319(.003) |
| HCC | 0.115(.008) | 0.119(.002) | 0.124(.004) | 0.117(.003) | 0.118(.002) |
| LUNG | 0.604(.002) | 0.612(.002) | 0.610(.002) | 0.611(.002) | 0.611(.001) |
| LYMPH_IDC | 0.278(.002) | 0.310(.001) | 0.305(.001) | 0.306(.001) | 0.305(.001) |
| Average | 0.405 | 0.417 | 0.415 | 0.412 | 0.411 |
```
The authors should conduct an ablation study on the hyperparameters of the ZINB prior (μ, ϕ, π) to demonstrate their impact on prediction performance.
```
Ans: We set the zero-inflation probability $\pi=0.5$, as higher dropout rates degrade ZINB to a near-zero distribution. We conducted an ablation over the mean $\mu\in\{0.1,0.2,0.4\}$ and dispersion $\phi\in\{1,2,4\}$, with results shown below. STFlow is generally robust to these hyperparameters due to its iterative refinement, though performance can vary slightly on some datasets (e.g., 0.496–0.507 on PAAD). Exploring automated strategies for tuning prior parameters is a promising direction, as noted in our Limitation section.
| ZINB(mean, number of failures) | (0.1,1) | (0.2,1) | (0.4,1) | (0.1,2) | (0.2,2) | (0.4,2) | (0.1,4) | (0.2,4) | (0.4,4) |
| --- | --- | --- | --- | --- | --- | --- | --- | --- | --- |
| IDC | 0.586(.001) | 0.585(.003) | 0.585(.001) | 0.584(.001) | 0.585(.002) | 0.587(.003) | 0.585(.001) | 0.583(.001) | 0.585(.001) |
| PRAD | 0.417(.002) | 0.415(.001) | 0.413(.000) | 0.415(.000) | 0.421(.002) | 0.413(.001) | 0.415(.000) | 0.415(.002) | 0.418(.001) |
| PAAD | 0.496(.002) | 0.507(.004) | 0.499(.000) | 0.499(.005) | 0.502(.004) | 0.500(.001) | 0.498(.000) | 0.499(.002) | 0.502(.006) |
| SKCM | 0.707(.007) | 0.704(.002) | 0.710(.004) | 0.704(.007) | 0.709(.003) | 0.704(.009) | 0.709(.003) | 0.703(.005) | 0.707(.008) |
| COAD | 0.339(.002) | 0.342(.003) | 0.341(.004) | 0.343(.000) | 0.338(.003) | 0.343(.004) | 0.342(.002) | 0.343(.006) | 0.340(.000) |
| READ | 0.253(.003) | 0.231(.000) | 0.243(.000) | 0.247(.004) | 0.244(.004) | 0.245(.000) | 0.236(.001) | 0.246(.000) | 0.249(.002) |
| CCRCC | 0.339(.001) | 0.337(.003) | 0.340(.004) | 0.334(.000) | 0.342(.008) | 0.329(.005) | 0.334(.000) | 0.336(.002) | 0.337(.003) |
| HCC | 0.118(.001) | 0.122(.000) | 0.123(.005) | 0.120(.003) | 0.120(.001) | 0.122(.004) | 0.126(.002) | 0.125(.003) | 0.124(.003) |
| LUNG | 0.611(.001) | 0.611(.000) | 0.611(.001) | 0.610(.000) | 0.611(.001) | 0.610(.001) | 0.608(.001) | 0.609(.000) | 0.613(.001) |
| LYMPH_IDC | 0.308(.001) | 0.310(.002) | 0.308(.001) | 0.309(.000) | 0.308(.001) | 0.304(.000) | 0.306(.001) | 0.305(.002) | 0.304(.002) |
---
Rebuttal Comment 1.1:
Comment: The author has addressed my concern.
---
Reply to Comment 1.1.1:
Comment: We are glad to hear that. Thanks so much for your effort in reviewing! | Summary: The authors propose STFlow, a model for spatially resolved gene-expression prediction from WSIs.
STFlow is based on flow matching, modelling the joint distribution of the full spatial gene-expression data across each WSI, through an iterative refinement process. This enables explicit modelling of spot-to-spot interactions.
The denoiser network is a frame-averaging transformer, integrating spatial context and gene interactions within the attention mechanism.
The proposed STFlow is evaluated on both the HEST-1k and STImage-1K4M datasets. It performs well compared to recent spot-based and slide-based baseline models.
##########
##########
##########
##########
Update after the rebuttal:
All reviewers are positive overall, and the authors have provided a very solid rebuttal.
This is an interesting and very solid paper, I don't really see any reason for why it shouldn't be accepted. I have increased my score to "_4: Accept_".
Claims And Evidence: Yes.
Methods And Evaluation Criteria: Yes.
Theoretical Claims: N/A.
Experimental Designs Or Analyses: Solid experimental setup.
Supplementary Material: Quickly read the appendix.
Relation To Broader Scientific Literature: Good discussion of related work in Section 2.
Essential References Not Discussed: N/A.
Other Strengths And Weaknesses: Strengths:
- Although the paper contains quite a few typos, it's well written overall.
- The studied problem is interesting and relevant.
- The proposed STFlow model is quite interesting, I think it makes sense to jointly model the full spatial gene-expression data using flow matching.
- The experimental evaluation is solid, utilizing both the HEST-1k and STImage-1K4M datasets.
- The proposed STFlow seems to perform well compared to relevant and recent baselines (BLEEP: NeurIPS 2023, TRIPLEX: CVPR 2024). Moreover, Section 4.3 presents relevant ablation studies which indicate that the main model components positively affect the performance.
Weaknesses:
- The paper is well written overall but does contain quite a few typos etc, it would definitely benefit from some additional careful proofreading.
- I found it quite difficult to follow and understand the method description in Section 3.3. I think Section 3.1 and 3.2 are fine, but I struggled with 3.3. I think an effort should be made to work through this section again, making sure everything is described as clearly as possible.
Other Comments Or Suggestions: Questions/Suggestions:
- It would be interesting to see the computational cost for STFlow and UNI reported in Table 1. I don't really consider added computational cost a major issue, but just to see how much the transformer model and iterative refinement slows down STFlow compared to the UNI + regression layer baseline.
- Section 4.1, _"Additionally, some ST-based approaches fail to predict significantly correlated gene expression"_: Could you clarify exactly what you refer to in Table 1 here? The results for STNet and HisToGene?
- In Section 4.2, could perhaps clarify that these 3 datasets are from HEST-1k?
- It's not entirely clear to me what "STFlow w/o FM" in Table 2, Figure 4 and Table 4 means, does this correspond to setting S = 1 in Algorithm 2?
- Figure 4 is neat, it would be interesting to see more examples like these, could you perhaps add a couple to the appendix?
- It would also be interesting to see Figure 4-like visualizations of the predicted gene-expression during the iterative refinement process? I.e., what does the initial random sample $Y_0$ look like? And how does this then evolve during the S=5 refinement steps?
- It would also be interesting to see the regression accuracy as a function of the number of refinement steps S (e.g. for S = 1, 2, 4, 8, 16), does the performance increase with more and more steps, or does it quickly plateau?
- Regarding the Limitations paragraph in Section 5: I think it would be relevant to refer to the results in Table 9 in the appendix here, or at least somewhere in the main paper? Because, I think these are encouraging results? If initializing $Y_0$ with all zeros instead of sampling from the ZINB distribution, the performance drops from 0.415 to 0.407 for UNI, which is not a lot? This would still beat all baselines in Table 1? I.e., this indicates that the model is quite robust to this choice of prior?
Minor things:
- Line 86: "This enables explicit modeling cell-cell interactions" --> "This enables explicit modeling of cell-cell interactions"?
- Line 94: "WSI collections comprising total 17 benchmark datasets" --> "WSI collections comprising a total of 17 benchmark datasets"?
- Line 83: "have enabled the detecting of RNA" --> "have enabled the detection of RNA"?
- Line 96: "et al., 2024).One concurrent work" --> "et al., 2024). One concurrent work".
- Line 97: "leverages diffusion model for" --> "leverages a diffusion model for" / "leverages diffusion models for"?
- Line 111: "modeling joint distribution" --> "modeling the joint distribution"?
- Line 120: "In this work, we repurpose" --> "In this work, we reformulate"?
- Line 142: "whole-slide images (WSIs) using an FA-based Transformer", don't need to define WSIs again here.
- Line 137: "In this study, the goal of STFlow aims to predict" --> "In this study, the goal of STFlow is to predict"?
- Line 185: "However, standard regression objective cannot model cell-cell interaction as it predicts" ---> "However, the standard regression objective cannot model cell-cell interaction as it predicts"?
- Line 194: "denoised model" --> "denoiser model"?
- "Algorithm 1 STFlow: Train" --> "Algorithm 1 STFlow: Training"?
- I think all "<--" in Algorithm 1 and 2 could be replaced with just "="?
- Line 244: "an E(2)-invariant transformation for point cloud" --> "an E(2)-invariant transformation for point clouds"?
- Line 247: "minimal modification to Transformer" --> "minimal modifications to the Transformer"?
- Line 266: "guaranteed by frame averaging framework" --> "guaranteed by the frame averaging framework"?
- Section 3.4: I think it's more common to use "Eq." instead of "Equ.".
- _Spatially Resolved Gene Expression Prediction from H&E Histology Images via Bi-modal Contrastive Learning_ is a NeurIPS 2023 paper, not 2024?
- Line 363: "Table 2 achieves the highest correlation across all biomarkers" --> "In Table 2, STFlow achieves the highest correlation across all biomarkers"?
- Line 767: "Table 10 and presents", typo.
Questions For Authors: 1. Could you update Section 3.3?
2. Could you clarify what setting "STFlow w/o FM" corresponds to?
3. Could you add results for other refinement steps S (not just S = 5)?
4. Could you add some more Figure 4-like visualizations?
Justification of overall recommendation:
The studied problem is interesting and relevant, the proposed STFlow model conceptually makes sense overall, the experimental setup is solid, and STFlow seems to perform well compared to relevant baselines. While the current version requires some more proofreading and polishing, and could benefit from some additional results and visualizations (at least added to the appendix), I think that a solid rebuttal by the authors should make me want to accept this paper. I'm definitely leaning towards accept right now at least.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We greatly appreciate your valuable suggestions and will revise the manuscript accordingly. Due to character limits, all additional results are available in our anonymous codebase: https://anonymous.4open.science/r/Anonymous_STFlow-3616/.
```
I found it quite difficult to follow and understand the method description in Section 3.3
```
Ans: We apologize for the confusion. Section 3.3 introduces the formulation of frame averaging, which may be difficult to follow due to dense notation. We will simplify the notations and streamline the equations to better highlight the core idea and improve clarity for readers.
```
It would be interesting to see the computational cost for STFlow and UNI reported in Table 1.
```
Ans: We present the average inference time on the test set of each dataset across splits in [link](https://anonymous.4open.science/r/Anonymous_STFlow-3616/rebuttal/time.md). The time required for visual feature extraction is excluded, as this step can be performed during preprocessing. Notably, STFlow demonstrates high efficiency due to its use of local neighborhood information.
```
Section 4.1, *"Additionally, some ST-based approaches fail to predict significantly correlated gene expression"*: Could you clarify exactly what you refer to in Table 1 here?
```
Ans: Yes, this refers to STNet (0.286) and HisToGene (0.237), which underperform compared to the pathology foundation model UNI (0.344) on HEST-1k. This highlights the advantage of using a foundation model and the need for an effective spatial encoder—HisToGene encodes spatial context but still underperforms. We will clarify this in the revised manuscript.
```
In Section 4.2, could perhaps clarify that these 3 datasets are from HEST-1k?
```
Ans: We apologize for any confusion and will clarify it in our manuscript: “We utilize two datasets from HEST and report the average correlation for each gene across different cross-validation folds. Specifically, the IDC dataset is used for GATA3 and ERBB2, while LUNG is used for UBE2C, and SKCM for VWF.”
```
It's not entirely clear to me what "STFlow w/o FM" in Table 2, Figure 4 and Table 4 means, does this correspond to setting S = 1 in Algorithm 2?
```
Ans: "STFlow w/o FM" refers to the model where the iterative refinement is removed and one-step prediction is performed, i.e., setting the number of sampling steps S = 1. We will clarify this in the revised manuscript to avoid confusion.
```
Figure 4 is neat, it would be interesting to see more examples like these, could you perhaps add a couple to the appendix?
```
Ans: We include two biomarker examples on a sample from the IDC dataset in [link](https://anonymous.4open.science/r/Anonymous_STFlow-3616/rebuttal/biomarker_case_study.png), which will be added to our manuscript.
```
It would also be interesting to see Figure 4-like visualizations of the predicted gene-expression during the iterative refinement process?
```
Ans: We include two examples showing how STFlow refines gene expression predictions in [link](https://anonymous.4open.science/r/Anonymous_STFlow-3616/rebuttal/refinement_process.png). Step 1 shows the initial random sample Y_0, and Steps 2–5 indicate progressive denoising. The results illustrate how flow matching gradually converges to the final prediction via interpolation with a decay coefficient. The results will be included in the revised manuscript.
```
It would also be interesting to see the regression accuracy as a function of the number of refinement steps S.
```
Ans: We report STFlow’s performance across different numbers of refinement steps in [link](https://anonymous.4open.science/r/Anonymous_STFlow-3616/rebuttal/FM_sample_steps.md). The results show a clear improvement from one-step prediction (S=1) to introducing iterative refinement (S=2). In some datasets, performance improves up to S = 5 (e.g., PAAD: 0.488 → 0.507). However, gains plateau or slightly decline beyond that. This trend aligns with prior works like AlphaFlow and RNAFlow, which adopt S=5 as default. The analysis will be included in the revised manuscript.
```
Regarding the Limitations paragraph in Section 5: I think it would be relevant to refer to the results in Table 9 in the appendix here, or at least somewhere in the main paper? Because, I think these are encouraging results?
```
Ans: Yes, the model is generally robust to the choice of prior, as the iterative refinement process helps mitigate noise from the initialization. But the ZINB distribution introduces three additional hyperparameters that can impact the performance on certain datasets, such as 0.496~0.507 on PAAD as shown in [link](https://anonymous.4open.science/r/Anonymous_STFlow-3616/rebuttal/ZINB_hyperparameters.md). Automatically estimating these parameters could be a valuable future direction.
```
Minor things regarding the writing.
```
Ans: We sincerely appreciate these helpful comments and will incorporate all the suggestions in the revised manuscript.
---
Rebuttal Comment 1.1:
Comment: Thank you for the reply.
I have read the other reviews and all rebuttals.
All reviewers are positive overall, and the authors have provided a very solid rebuttal.
Minor things:
- "Groudtruth" typo in Figure 4 and the new Figure 4-like figures shown in the rebuttal.
- The examples showing the iterative refinement process (https://anonymous.4open.science/r/Anonymous_STFlow-3616/rebuttal/refinement_process.png) are really neat, would be nice to see a couple of more examples like these in the appendix.
This is an interesting and very solid paper, I don't really see any reason for why it shouldn't be accepted. I will increase my score to "4: Accept".
---
Reply to Comment 1.1.1:
Comment: We greatly appreciate your feedback! We will correct the typo (“Groudtruth”) and include more examples in our paper. All suggestions mentioned during the rebuttal will be incorporated into the revised manuscript. | null | null | null | null | null | null |
Heterogeneous Treatment Effect in Time-to-Event Outcomes: Harnessing Censored Data with Recursively Imputed Trees | Accept (poster) | Summary: The authors consider the problem of estimating an individual treatment effect from survival data, where some of the observations may be right-censored. They propose a two-stage approach, MISTR, for this problem. In the first stage, they use recursively imputed survival trees (RIST) to impute the censored survival times in the data. Using these imputed times, they can apply a known result where the the treatment effect is given as the root of the "Robinson-style partialling-out score function" in the absence of censoring. They also show how to extend their approach to the case of unobserved confounding using instrumental variables. Finally, they compare their result against the recently proposed causal survival forest (CSF) method on synthetic and real datasets, showing comparable performance in low censoring regimes and when the assumptions of CSF are met, but improved accuracy in the presence of high censoring or when some of the modeling assumptions of CSF are violated.
Claims And Evidence: The main weakness of the paper is the lack of baseline methods in the experiments. There are only two baselines, CSF (in every experiment) and IPCW-IV (in the instrumental variable settings). The authors mention two meta-learner methods which can handle right-censoring (Golmakani & Polley, 2020 and Bo et al., 2024) in the first paragraph of the Related Work section. It seems that these should be applicable to the setting of this paper, and these should therefore be included as comparison methods. If the existing literature for this problem is sparse and there are not many existing baseline methods, some naive approaches could also be included to demonstrate the value of the proposed model. Specifically, *any* method for survival analysis which estimates a conditional survival distribution can be used for this problem as follows:
- Directly estimate the survival function and include the treatment assigment as a covariate, or estimate the survival function for the treated and untreated groups separately.
- Using the estimated survival functions, estimate $\tau(x)$.
This approach ignores all of the causal inference minutiae and therefore should be expected to have worse performance. But it would still be valuable to confirm that this is actually the case, and show the value of directly accounting for the causal nature of the problem.
Similarly, one could also check naive baselines which ignore the specifics of survival analysis (i.e., the presence of censored data) and apply generic methods causal regression problems to the dataset where the censored observations are simply dropped, or where the censoring is ignored and the censored time is treated as the actual event time. Again, we would expect such approaches to have inferior performance because not accounting for censoring can lead to bias, but confirming this empirically would greatly strengthen the paper especially since the existing baselines are sparse.
Methods And Evaluation Criteria: Yes.
Theoretical Claims: Most of the theoretical claims are statements of certain estimators. It would be helpful to include a derivation or explanation for some of these in an appendix, especially the estimator for the target quantity $\tau$ in equation (2).
It also seems that equation (4) is only valid when $t > C_i$, is this true?
Experimental Designs Or Analyses: The synthetic datasets were effectively designed for simulating the different challenging aspects of the problem, e.g. high censoring, unmeasured confounding, etc.
I found the HIV clinical trial experiment to be an exceptionally convincing setup. The accuracy of causal inference methods can be difficult to evaluate on real data since the ground truth is not known. To address this problem, the authors first computed estimates for the target function using the full dataset, which contained only mild censoring. Their method and the baseline CSF obtained similar results. To show the value of their method, the authors used a held-out covariate to increase the censoring in the data, then showed that the estimate using their method remained relatively stable as the censoring increased, while the quality of the estimate of CSF degraded more significantly. I am not sure if this technique is standard as I am not an expert in causal inference, but this setup is one of the best I have seen for validation when the ground truth is unknown.
The analysis on the Illinois unemployment insurance dataset seemed incomplete. The results show that MISTR without accounting for the IV gave similar results as the baseline CSF, and that both of these deviated from MISTR-IV. However, no metrics or other analysis was provided which would indicate that the MISTR-IV results are actually *better*. Since the ground truth is not available in this setting, some qualitative analysis of the results would be helpful.
Supplementary Material: I checked Appendix Figure S11 for the Illinois unemployment insurance results.
Relation To Broader Scientific Literature: The relationship to prior work is clearly discussed. The authors focus primarily on the most relevant existing baseline, causal survival forests (CSF, Cui et al. (2023)), and emphasize that their method makes two main improvements: (1) they do not require to estimate the censoring probability, which leads to greater robustness and accuracy, and (2) their method can handle the instrumental variable (IV) setting.
Essential References Not Discussed: I am not aware of any critical references that have been missed.
Other Strengths And Weaknesses: I found the paper to be clear and well-written.
Other Comments Or Suggestions: N/A
Questions For Authors: In the last paragraph of Section 6.2, it is stated that "The maximum time for the RIST is $t_{max} = 29$, and the RMST horizon is $h=28$." The RMST is computed as $g(\widetilde{T}_i) = \min(\widetilde{T}_i, h)$. The max time for RIST and the RMST horizon are therefore very close, so if my understanding is correct, the imputed points can only impact the RMST value by a small amount (when the imputed value is between 28 and 29) and most of the imputed values will just default to the RMST horizon. In this case, it seems that the imputation procedure should have a very minimal effect. Can the authors comment on this?
---
After the rebuttal, the authors have addressed all of my questions. I have raised my score accordingly.
I also read the other reviews and rebuttals. In particular, it seems that Reviewer WUcd is concerned by the lack of a theoretical contribution, and because the proposed method seems combinatorial in nature. As this paper is focused on introducing a novel method, theoretical results are a bonus but not required, and the empirical validation of the proposed method is convincing.
Regarding the nature of the method as a combination of existing techniques, the review instructions state "For example, originality may arise from creative combinations of existing ideas." As the authors mention, it can be generally challenging to accommodate instrumental variables with nonparametric estimators. Especially given the strength of the empirical results, deriving a flexible nonparametric framework which is compatible with IVs should constitute a creative combination.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you very much for the detailed review, constractive comments, and your support for the acceptance of our paper. The following is our point-by-point response.
* The max time for RIST and the RMST horizon are very close, so it seems that the imputation procedure should have a very minimal effect.
Right censoring can occur at *any* time between 0 to $t_{max}$. As a result, the censoring rate may be high even when $h$ is very close to $t_{max}$, and therefore imputation has a substantial impact.
* The main weakness of the paper is the lack of baseline methods in the experiments.
Golmakani \& Polley, (2020) propose two algorithms for constructing super learners in survival data prediction where the individual algorithms are based on proportional hazards. Bo et al., (2024) studied two meta-learning algorithms, T-learner and X-learner, each combined with three types of machine learning methods: random survival forest, Bayesian accelerated failure time model and survival neural network. These additional baselines will be incorporated in the revised version.
The existing literature for this problem is not sparse and there are baseline methods included in Cui et al., (2023). In particular, Cui et al. showed that their method is superior to the random survival forest (Iswaran \& Kogalur, 2019), S-learner (Kunzel, 2019), enriched random survival forest (Lu et al., 2018), and the IPCW causal forest. Therefore, we focus on comparing our method with the CSF method of Cui et al. (2023). This point will be added to the revised version of the paper.
We believe that comparing to methods that ignore right censoring or causal inference principles adds little value, as their limitations are well established in the literature, even if not in our exact setting.
* It would be helpful to include a derivation or explanation for some of these in an appendix, especially the estimator for the target quantity in equation (2).
Thank you for bringing this up. The revised version will include detailed explanations, as suggested.
* It also seems that equation (4) is only valid when $t > C_i$.
Thank you for noticing this mistake, it will be corrected.
* The analysis on the Illinois unemployment insurance dataset seemed incomplete. Metrics or other analysis should be provided to indicate that the MISTR-IV results are actually better.
Thank you for this important comment. Indeed, as the reviewer points out, lacking ground truth makes any solid model evaluation and comparison challenging. Indeed, censoring and hidden confounding make the problem especially challenging in our setting. Nonetheless, following the reviewer's suggestion we have added qualitative comparisons between the top 10\% and bottom 10\% of the population expected to benefit the most and the least from the treatment, as rated by CSF, MISTR, and MISTR-IV; see Table 3 in the following link:
https://drive.google.com/file/d/1tT_ROACNebxVOC09ty2ng_q4luaBD8Ay/view?usp=sharing
. Such comparisons may reveal differences between the model results that may be explained by domain knowledge and will help to guide model selection. We see that MISTR-IV arrives quite distinct conclusions regarding the populations most and least benefitting from the treatment. We leave a full interpretation of these results to domain experts in the field.
---
Rebuttal Comment 1.1:
Comment: (I have also put this comment in my updated review but I post it here since it contains a discussion of the other reviews.)
After the rebuttal, the authors have addressed all of my questions. I have raised my score accordingly.
I also read the other reviews and rebuttals. In particular, it seems that Reviewer WUcd is concerned by the lack of a theoretical contribution, and because the proposed method seems combinatorial in nature. As this paper is focused on introducing a novel method, theoretical results are a bonus but not required, and the empirical validation of the proposed method is convincing.
Regarding the nature of the method as a combination of existing techniques, the review instructions state "For example, originality may arise from creative combinations of existing ideas." As the authors mention, it can be generally challenging to accommodate instrumental variables with nonparametric estimators. Especially given the strength of the empirical results, deriving a flexible nonparametric framework which is compatible with IVs should constitute a creative combination.
---
Reply to Comment 1.1.1:
Comment: Thank you very much, we highly appreciate your insightful and thorough review and your recommendation for the acceptance of our paper. | Summary: The authors propose a tree-based method for estimating Heterogeneous Treatment Effects (HTE) in survival analysis, and further extend it by incorporating instrumental variables to account for unobserved confounders. The authors conduct thorough and detailed experiments on both synthetic and real-world datasets to validate the effectiveness of the proposed method.
Claims And Evidence: There are several issues with the contributions claimed by the authors:
1. The authors claim that existing methods such as CSF [1] have limitations in estimating censoring rates under extreme cases. However, doubly robust methods can address this issue to some extent. Moreover, the authors' use of the conditional survival distribution proposed in RIST [2] lacks a theoretical foundation for why it would be more accurate than censoring rate estimation in extreme cases. Similar to estimating censoring rates, I think this probability would also encounter issues like extreme values, which could lead to inaccurate estimates under such issues.
2. Although the authors claim that combining IV with the proposed MISTR method can address confounding bias caused by unobserved confounders, they do not explain how IV is used to correct for bias and how it differs from previous IV methods. To me, it seems that the authors have merely applied existing IV theories and methods to MISTR without providing novel contributions.
[1] Cui, Yifan, et al. "Estimating heterogeneous treatment effects with right-censored data via causal survival forests." Journal of the Royal Statistical Society Series B: Statistical Methodology 85.2 (2023): 179-211.
[2] Zhu, Ruoqing, and Michael R. Kosorok. "Recursively imputed survival trees." Journal of the American Statistical Association 107.497 (2012): 331-340.
Methods And Evaluation Criteria: The proposed MISTR method builds upon the theory of RIST [1], which is intuitively sound but lacks formal theoretical proof. The combination of MISTR with IV is not thoroughly described, and it also lacks theoretical proof. The datasets and evaluation metrics used in the experiments are reasonable, and the experiments themselves are sufficiently detailed.
[1] Zhu, Ruoqing, and Michael R. Kosorok. "Recursively imputed survival trees." Journal of the American Statistical Association 107.497 (2012): 331-340.
Theoretical Claims: All the claims and methodologies presented in the paper lack formal theoretical proof.
Experimental Designs Or Analyses: The experimental design is reasonable and thorough, with detailed descriptions of the experimental setups.
Supplementary Material: There are no supplementary materials provided.
Relation To Broader Scientific Literature: The proposed MISTR method essentially adopts the existing characteristics of RIST for imputing censored labels [1] and uses the imputed data to estimate the HTE, lacking an original theoretical contribution. Furthermore, the subsequent combination of IV and MISTR is merely an application of existing IV theory and methods [2-7] to MISTR, without offering any novel contribution.
[1] Zhu, Ruoqing, and Michael R. Kosorok. "Recursively imputed survival trees." Journal of the American Statistical Association 107.497 (2012): 331-340.
[2] Wang, Linbo, et al. "Instrumental variable estimation of the causal hazard ratio." Biometrics 79.2 (2023): 539-550.
[3] Tchetgen, Eric J. Tchetgen, et al. "Instrumental variable estimation in a survival context." Epidemiology 26.3 (2015): 402-410.
[4] Burgess, Stephen, Dylan S. Small, and Simon G. Thompson. "A review of instrumental variable estimators for Mendelian randomization." Statistical methods in medical research 26.5 (2017): 2333-2355.
[5] Hansen, Bruce. Econometrics. Princeton University Press, 2022.
[6] Wooldridge, Jeffrey M. Introductory Econometrics: A Modern Approach 6rd ed. Cengage learning, 2016.
[7] Imbens, Guido W., and Donald B. Rubin. Causal inference in statistics, social, and biomedical sciences. Cambridge university press, 2015.
Essential References Not Discussed: The authors provide a thorough overview of the related work in survival analysis and cites most of the key studies.
Other Strengths And Weaknesses: The strengths of the paper lie in the thoroughness of the experiments. The authors conduct extensive experiments on both synthetic and real-world datasets, and provides detailed description of the experimental settings. However, several significant weaknesses are evident:
1. The paper lacks theoretical foundations, with no theoretical proofs supporting the proposed content.
2. The method proposed in the paper lacks originality. The MISTR method essentially adopts the existing characteristics of RIST for imputing censored labels and uses the imputed data to estimate the HTE, without offering an original theoretical contribution. Moreover, the combination of IV and MISTR is merely an application of existing IV theory and methods to MISTR, without presenting any novel contribution.
3. The description of how MISTR is integrated with IV is unclear.
Other Comments Or Suggestions: The following are my comments after reviewing the authors' responses in the rebuttal and discussion stages:
Some concerns have been addressed:
1. How IV and MISTR are integrated is clarified, which is missing in the original manuscript.
2. RIST's advantages over censoring rate estimation methods are clarified.
However, a major concern remains unresolved:
**The proposed method lacks a theoretical foundation.** The authors have repeatedly argued that the paper focuses more on methodological contributions rather than theoretical contributions, and therefore ”theoretical results are a bonus but not required” as Reviewer 7fsC suggested. **However, theoretical results are of course crucial and necessary for a causal inference method.** My continued emphasis on the lack of a theoretical contribution is not to suggest that the paper does not present new theory—I certainly understand that, in addition to proposing new theories, proposing correct new methods is also an important contribution. Rather, I am pointing out that the method proposed in this paper, regardless of its lack of novelty, lacks a theoretical foundation. **The authors have not provided any theoretical proof or even a discussion** (such as the theoretical discussion regarding the correctness of the RIST method in [1]) **to demonstrate the correctness of the proposed method** (i.e., the combination of the existing methods). As a result, **readers are unable to assess whether the effectiveness demonstrated in the experimental validation holds only on specific datasets, making it hard to judge when the proposed method is effective or when it may fail.** This, in turn, limits the applicability of the proposed method.
Therefore, while I fully agree that correctly combining existing methods to solve a practical problem can be considered as an important contribution. As I mentioned in my rebuttal comments, **the authors' approach of merely combining existing methods without investigating the correctness of this combination—such as whether the conditions for identifiability and consistency change after the combination—clearly represents an insufficient contribution.**
In conclusion, although I greatly appreciate the authors' writing and experiments, and I am very grateful for their responses and discussions, my recommendation still leans toward rejection.
[1] Zhu, Ruoqing, and Michael R. Kosorok. "Recursively imputed survival trees." Journal of the American Statistical Association 107.497 (2012): 331-340.
Questions For Authors: The following questions are based on my previous comments, and I encourage the authors to carefully review them.
1. Why does replacing censoring rate estimation in methods such as CSF [1] with the conditional survival distribution proposed by RIST [2] mitigate the impact of extreme cases? I believe this probability might still be susceptible to similar extreme value issues.
2. I could not find any details in the paper on how IV and MISTR are integrated. Could the authors clarify this aspect?
3. It seems that the authors simply apply the existing RIST method for imputation, then uses the imputed data to estimate HTE, followed by the application of existing IV theory to address confounding bias from unobserved variables. What is the author's original theoretical contribution?
4. In addition to the theories and methods addressing censoring within survival analysis, there are approaches that consider censoring from the perspectives of selection bias and missing data [3-7], including methods that use IV to simultaneously address confounding bias due to unobserved variables [8]. Could these methods also be applied to survival analysis problems?
Overall, I appreciate the experimental contributions of this paper; however, the theoretical contributions are quite limited, which may make it unsuitable for publication in ICML.
[1] Cui, Yifan, et al. "Estimating heterogeneous treatment effects with right-censored data via causal survival forests." Journal of the Royal Statistical Society Series B: Statistical Methodology 85.2 (2023): 179-211.
[2] Zhu, Ruoqing, and Michael R. Kosorok. "Recursively imputed survival trees." Journal of the American Statistical Association 107.497 (2012): 331-340.
[3] Heckman, James J. "Sample selection bias as a specification error." Econometrica: Journal of the econometric society (1979): 153-161.
[4] Malinsky, Daniel, Ilya Shpitser, and Eric J. Tchetgen Tchetgen. "Semiparametric inference for nonmonotone missing-not-at-random data: the no self-censoring model." Journal of the American Statistical Association 117.539 (2022): 1415-1423.
[5] Wang, Sheng, Jun Shao, and Jae Kwang Kim. "An instrumental variable approach for identification and estimation with nonignorable nonresponse." Statistica Sinica (2014): 1097-1116.
[6] Heiler, Phillip. "Heterogeneous treatment effect bounds under sample selection with an application to the effects of social media on political polarization." Journal of Econometrics 244.1 (2024): 105856.
[7] Li, Wei, Wang Miao, and Eric Tchetgen Tchetgen. "Non-parametric inference about mean functionals of non-ignorable non-response data without identifying the joint distribution." Journal of the Royal Statistical Society Series B: Statistical Methodology 85.3 (2023): 913-935.
[8] Li, B., Wu, A., Xiong, R., & Kuang, K. (2024). Two-stage shadow inclusion estimation: an IV approach for causal inference under latent confounding and collider bias. In Forty-first International Conference on Machine Learning.
Code Of Conduct: Affirmed.
Overall Recommendation: 1 | Rebuttal 1:
Rebuttal: Thank you very much for your thorough review and insightful feedback.
* Why does replacing censoring rate estimation in methods such as CSF with the conditional
survival distribution proposed by RIST mitigate the impact of extreme cases?
Thank you for raising this important issue. It is well known that inverse probability weighting estimators, while often consistent, can suffer from high variance due to instability in the weights. The CSF method combines IPCW with a doubly robust approach to avoid discarding observations with $\delta_i^h = 0$ and to mitigate bias of the censoring distribution. However, despite this robustness, the use of unstable weights can still result in substantial variance. In contrast, our proposed multiple imputation approach avoids IPW altogether. Our extensive numerical studies clearly demonstrate the superior performance of MISTR compared to CSF. We agree that this point should be better explained in the revision.
* How IV and MISTR are integrated
We agree and apologize for not clearly explaining it. Consider first the unconfounded setting and as a start assume a constant treatment effect $\tau$. Consider the partially linear model of Robinson (1988): $g(\widetilde{T}_i) = \tau W_i + f(X_i) + \zeta_i$ where $E(\zeta_i | W_i , X_i)=0$, $W_i \perp \zeta_i$, and $E(W_i|X_i ) = \Pr(W_i=1|X_i)$. Then, it is easy to verify that $g(\widetilde{T}_i) - E\{g(\widetilde{T}_i)|X_i \} = \tau \{ W_i - E(W_i|X_i) \} + \zeta_i$. In the absence of censoring, $\tau$ can be estimated by the score function provided in line 199 of the paper. Eq. (2) (of the paper) then goes beyond constant treatment effects and accommodates a heterogeneous effects function $\tau(x)$.
In the confounded setting, we relax the independence assumption between $\zeta_i$ and $W_i$, while the instrument $Z_i$ is independent of $\zeta_i$ given $X_i$, along with Assumptions B.1--B.5. Hence in the absence of censoring, Eq. (2) is replaced by
$$
S^{IV}_n(\tau(x)) =
$$
$$
\sum_{i=1}^n \alpha_i(x) \cdot \left(Z_i - \widehat{h}(X_i) \right\) \cdot \left[ g(\widetilde{T}_i) - \widehat{m}(X_i) - \tau(x) \{ \left(W_i - \widehat{e}_i(X_i) \right) \} \right] = 0
$$
where $\widehat{h}(X_i)=E(Z_i|X_i)$. We accommodate right-censoring by multiple imputation, and in Step 16 of Algorithm 1 causal forests are applied using either $S_n(\tau(x))$ or $S^{\sf IV}_n(\tau(x))$, corresponding to the MISTR and MISTR-IV estimators, respectively. We'll include a detailed explanation in the revised version.
* What is the author’s original theoretical contribution?
We view our main contribution to be the introduction of new methods. MISTR and MISTR-IV are new nonparametric estimators for HTE, designed for settings without and with unobserved confounding, respectively. Our methods build upon the foundations of RIST and Causal Forests (Athey et al., 2019), effectively merging their strengths to yield estimators with lower variance. This combination results in a notably flexible framework. As evidence of this flexibility, we show how the core approach can be easily modified to accommodate instrumental variables (resulting in MISTR-IV), extending its applicability in a way that is often challenging for other nonparametric estimators. While rigorous theoretical guarantees for our methods are currently lacking, extensive numerical studies, including using real-world datasets, demonstrate that MISTR and MISTR-IV consistently outperform state-of-the-art non-parametric alternatives, such as CSF without unobserved confounding and IPCW-IV with unobserved confounding, in terms of estimation efficiency.
* could papers [3]--[8] also be applied to survival analysis problems?
Paper [3] uses linear semiparametric or parametric regression models to relate the outcome and covariates, whereas our approach is fully nonparametric. Moreover, applying linear models to time-to-event data typically requires outcome transformation or additional constraints. Papers [4] and [5] address non-monotone missingness mechanisms, while right censoring is a special case of monotone coarsening (see Section 9.3 of ``Semiparametric Theory and Missing Data'', Tsiatis A.A., 2006)
Paper [6] focuses on HTE under sample selection without exclusion restrictions, and paper [7] deals with estimating mean functionals under non-ignorable non-response, where missingness depends on unobserved values. Paper [8] tackles both latent confounding bias—stemming from unmeasured variables influencing both treatment and outcome—and collider bias, which arises from non-random sample selection affected by both treatment and outcome. In contrast to these works, right-censored data provide partial information—the event has not occurred up to the censoring time—which must be incorporated into estimation. As such, these works are not directly applicable to our setting, though adapting them to the specific settings and constraints of survival analysis could be a valuable direction for future research.
---
Rebuttal Comment 1.1:
Comment: Thank you for your detailed response. However, some concerns remain unresolved:
The authors claim that the paper lacks a theoretical contribution but provides a methodological contribution. However, the methodological contribution, at least based on the current version of the paper and the authors' response, is also unclear. The proposed method appears to be a simple combination of two existing methods. In my view, this combination seems quite straightforward. Therefore, I kindly request that the authors provide further clarification regarding the methodological contribution, so that I can have a clear judgement for the contribution of the paper:
1. Could you elaborate on the challenges involved in combining these two methods? Are there any improvements made to these methods during the combination process?
Additionally, I have another suggestion that could potentially enhance the theoretical contribution of the paper:
2. I believe both methods have their own theoretical foundations. If combining them leads to the development of new theoretical insights, that could also be considered a valuable theoretical contribution. I hope the authors will take the time to explore this further, which would help to make the paper more comprehensive.
In conclusion, given that the paper currently lacks a theoretical contribution, and the methodological contribution remains unclear, with the only contribution being experimental, I am still inclined to a negative score.
---
Reply to Comment 1.1.1:
Comment: Thank you for your response. We would like to offer an additional perspective on our work.
Our methodological contribution lies in the development of a general framework that builds on existing methods. While the algorithm may appear straightforward, it serves as a practical and powerful tool for addressing complex challenges, as demonstrated through a comprehensive empirical study and real-world use cases. It outperforms the current state-of-the-art method of Cui et al. (which may appear more sophisticated), particularly in terms of variance. Moreover, as shown in the paper, our approach opens a new path for estimating heterogeneous treatment effects in right-censored survival data with unobserved confounders using instrumental variables - a setting where off-the-shelf non-parametric methods do not yet exist, and where the method of Cui et al. is not directly applicable.
We believe the simplicity of the solution does not diminish its practical value and contribution.
The RIST method [1], which we rely on and which was published in Journal of The American Statistical Association (JASA, a top-tier statistical journal), does not include theoretical results. While some theoretical results exist for certain types of random forests (based on U-statistics and under specific conditions), extending these results to the recursive forests we use is not trivial. Furthermore, such theoretical developments would need to be integrated with the asymptotic properties of causal forests and the methodology of multiple imputation.
This is certainly a valuable direction for future research. However, we believe the lack of formal theoretical results shouldn't detract from our work's methodological contribution. Developing such theory is challenging – indeed, even the RIST method our approach is based on lacks these guarantees. Our contribution remains significant for the task of non-parametric HTE estimation in survival data, both with and without confounding.
[1] Zhu, Ruoqing, and Michael R. Kosorok. "Recursively imputed survival trees." Journal of the American Statistical Association 107.497 (2012): 331-340. | Summary: The paper proposes MISTR—a novel non‐parametric approach for estimating heterogeneous treatment effects (HTE) in time-to-event (survival) data, where right censoring is prevalent. MISTR tackles censoring by employing multiple imputations through Recursively Imputed Survival Trees (RIST) to generate several “complete” datasets, on which causal forests are then used to estimate HTE and its variance. The method is extended to handle unobserved confounding via instrumental variables (IV), leading to the MISTR-IV variant. Extensive simulation studies and real-world analyses (e.g., HIV clinical trial data) support the authors’ claims of improved performance, especially under heavy censoring.
Claims And Evidence: Claim 1) Superior Performance Under Heavy Censoring: The authors claim that MISTR outperforms existing methods like Causal Survival Forests (CSF) and IPCW-based approaches when censoring rates are high. This claim is supported by detailed simulation studies across multiple benchmark settingsand is further validated on real-world datasets.
Claim 2) The paper asserts that MISTR-IV is the first non-parametric method that can estimate HTE in survival data in the presence of unobserved confounding using IVs. Comparative experiments (e.g., Table 3 and corresponding figures) demonstrate reduced bias in settings with confounding.
Claim 3) Avoidance of Direct Censoring Mechanism Estimation: By leveraging multiple imputation via RIST, the method bypasses the need to explicitly model the censoring distribution—a step that often introduces bias when the censoring mechanism is complex
Methods And Evaluation Criteria: Yes, simulation and real-world data from an aids clinical trial RCT is used to validate findings.
Theoretical Claims: No theoretical proofs or formal justifications are made for claims. The paper heavily relies on citations of previous methods to justify its math, but there are several instances when it would be helpful for the author to formally explain how they reached an equation or solution.
Experimental Designs Or Analyses: Experimental design is sound.
Supplementary Material: Skimmed Appendix
Relation To Broader Scientific Literature: The method builds directly on earlier work such as RIST (Zhu & Kosorok, 2012) and causal forests (Athey et al., 2019), and it compares favorably against CSF (Cui et al., 2023). The authors position their contribution clearly against the backdrop of existing literature by highlighting that previous methods often require explicit censoring probability estimation, whereas MISTR’s imputation strategy avoids this potential pitfall.
Essential References Not Discussed: NA
Other Strengths And Weaknesses: Dependence on Ignorable Censoring Assumption:
The methodology still hinges on the assumption of ignorable censoring. In many practical applications, censoring may be non-ignorable or depend on unmeasured factors. The paper does not thoroughly explore how violations of this assumption might impact the estimates, which could be a significant drawback in real-world applications.
The paper does not make strong theoretical improvements to the literature, and does not justify the theoretical claims it does make.
Other Comments Or Suggestions: It would be helpful to explain the equations presented in the main body of the paper (in addition to a formal proof in appendix)
Editing score to a 4, questions were sufficiently answered and this paper makes a meaningful contribution.
Questions For Authors: How does MISTR perform when the assumption of ignorable censoring is only approximately met? Are there diagnostic tools or adjustments you would recommend?
What methods do you suggest for assessing the strength and validity of the instrumental variables used, and how does MISTR-IV behave with weak instruments?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you very much for the careful review, thoughtful comments, and your support for the acceptance of our paper. The following is our point-by-point response.
* Explain the equations presented in the main body of the paper.
We apologize for this omission. The revised version of the paper will include additional explanations for the equations presented in the main text.
* How does MISTR perform when the assumption of ignorable censoring is only approximately met?
In survival analysis, Assumption A.4, stating that ${\widetilde{T}}_i \perp C_i \mid X_i, W_i$, is very widely used and is considered standard. In our context, see for example, Cui et al. (2023), Bo et al., (2024), Golmakani \& Polley, (2020) Iswaran \& Kogalur, (2019) and Lu et al., (2018). The reason for its ubiquity is that this assumption is essential, as for each individual only one of the two times (event or right-censoring) is observed. Consequently, their joint distribution is unidentifiable. This assumption is empirically untestable and must be accepted or rejected based on subject-matter knowledge. When there is a reason to believe this assumption may be substantially violated, for example due to the occurrence of other well-defined events, several strategies can be considered. One approach is to treat such events as competing risks and perform a competing-risks analysis. Alternatively, if one has a good knowledge of the specifics of the violation, one may employ parametric or semiparametric models that explicitly specify a joint distribution of the event and censoring times, such as copula-based models.
* What methods do you suggest for assessing the strength and validity of the instrumental variables used, and how does MISTR-IV behave with weak instruments?
Following this comment we extended our simulation study to assess the sensitivity of MISTR-IV to weak instruments by running Setting 200 (47\% censoring) and Setting 204 (88\% censoring) with IV of varying strength. We repeat the analysis of Section 6.2, modifying only the coefficient of $Z$ in the model of $W^{*}$, as reported in Table 1. The results are reported in Table 2 and Figure 1 in the following link:
https://drive.google.com/file/d/1tT_ROACNebxVOC09ty2ng_q4luaBD8Ay/view?usp=sharing .
As expected, the mean absolute error of all methods increases as the instrument weakens. Nonetheless, MISTR-IV outperforms the alternative approaches.
Validating instrumental variable strength in partially linear IV regression is a challenging topic and an active field of research (Windmeijer, (2025), Burauel (2023), Florence (2012), Hahn and Hausman (2002), Stock et al. (2002)). In linear models, IV strength is commonly evaluated using the effective first-stage F-statistic of Montiel, Olea, and Pflueger (2013). Windmeijer (2025) extends this approach to the Generalized Method of Moments (GMM) framework by proposing the Robust F-statistic. In the future we plan to investigate the best way to incorporate it in our approach.
The validity of the instrumental variable requires the standard IV assumptions: 1. Exclusion restriction: the instrument affects the outcome only through its influence on treatment assignment; 2. Independence: the instrument is independent of any unobserved confounders; 3. Relevance: the instrument is correlated with the treatment assignment. The relevance assumption can be empirically assessed by examining the correlation between the instrumental variable $Z$ and the treatment assignment $W$. In contrast, the exclusion restriction and independence assumptions cannot be tested directly and must be justified using domain knowledge.
For example, in the Illinois Unemployment Insurance Experiment, the proposal to join the experiment was randomized, supporting the independence assumption. However, validating the exclusion restriction requires establishing that the proposal itself did not influence the outcome directly regardless if the individual chooses to participate or not - a condition that is inherently unidentifiable from the observed data. Another approach gaining prominence recently is falsification tests, or negative controls (Eggers et al. 2024). Constructing such tests for censored time-to-event data is an interesting avenue for future research
* The paper does not make strong theoretical improvements to the literature.
Indeed, we view our main contribution as introducing new methods. While our design choices -- particularly addressing heavy censoring -- are strongly motivated, we do not claim a theoretical result. Instead, we demonstrate the advantages of our method through extensive experiments, including several with real-world data, and through empirical comparisons with existing approaches in realistic survival analysis settings.
---
Rebuttal Comment 1.1:
Comment: Editing score to a 4, questions were sufficiently answered and this paper makes a meaningful contribution.
---
Reply to Comment 1.1.1:
Comment: Thank you very much, we sincerely appreciate your insightful input and your recommendation for the acceptance of our work. | null | null | null | null | null | null | null | null |
Learn Singularly Perturbed Solutions via Homotopy Dynamics | Accept (poster) | Summary: This paper introduces homotopy dynamics as a strategy to solve PDEs with sharp interfaces using PINNs. The key idea is to start training with a larger interface width parameter $\epsilon$ (corresponding to a smoother solution), then gradually decrease $\epsilon$ to the desired sharp-interface regime. This approach is particularly relevant for PDEs such as the Allen-Cahn equation, where $\epsilon$ controls the interface sharpness.
Claims And Evidence: The claims are supported by the provided evidence, but the support is not particularly strong, see Experimental Designs and Analyses.
Methods And Evaluation Criteria: The proposed method and evaluation criteria are reasonable for the problem at hand. But there are alternative methods that are not explored or discussed:
- The bigger questions is, why do we use PINN for this type of problems instead of well-established numerical methods?
- Regarding the the homotopy loss $L_{H_\epsilon}$ (line 181). What happens if we don't use $L_{H_\epsilon}$? That is, we only change $\epsilon$. This would be similar to the curriculum regularization (Krishnapriyan et al. 2021).
- Since $L_{H_\epsilon}$ is supposed to mimic the forward Euler step in strategy 1, what happens if we don't use the residual loss $L_H$ and only use $L_{H_\epsilon}$?
- What is the effect of $\alpha$?
Theoretical Claims: A few clarifications would improve clarity
- Equation (13) - (18), L should be $L_H$ in equation (12)? That is, the loss under analysis is the residual loss without homotopy dynamics?
- Shouldn't $l$ depends on $\epsilon$? That is, $l = l_\epsilon$?
- In the proof Appendix A.2, line 720 and 736, What is $K_\epsilon$? Is it $K_\epsilon(\theta(0))$?
- How do we go from 736 to 740? Is it Weyl's inequality? Please clarify.
- From theorem 4.1 and the discussion afterward, if the difficulty only lies in the speed of convergence, will a larger learning rate help for original training?
- Theorem 4.3, what is $K_\epsilon$? Is it related to the $K_\epsilon$ in Theorem 4.1? If not, using a different notation might improve clarity.
- As $\epsilon\rightarrow 0$, the solution becomes more singular. Does $K_\epsilon$ remain bounded? If not, then K might not exist (line 305 column 2).
- What is $N$ in Theorem 4.3?
- Appendix A.3, it seems (45) - (48) are more like standard analysis on Euler's method? How is it related to Antonakopoulos
et al., 2022?
- Theorem 4.3 is only related to strategy 1, where Euler's method is used to evolve $\theta$, but not strategy 2. The author should explain the connection between the two strategies.
Experimental Designs Or Analyses: The experimental setup is reasonable, but the baseline comparison is relatively weak.
- Original training are known to struggle with PDEs that have highly oscillatory or near-singular solutions. Prior works have proposed strategies to address this issue:
- **Curriculum regularization**: Krishnapriyan et al. (2021) suggest first learning simpler problems before tackling harder ones, similar to the homotopy dynamics approach. They also propose learning early time steps first, which relates to the design of the homotopy in Examples 5.1 and 5.3 (where $s = 1$ corresponds to the initial condition and $s = 0$ to the full time problem).
- **Neural Tangent Kernel Perspective**: Wang et al. (2021) analyze PINN training and show that PINNs are biased toward smooth solutions, which could be relevant to Theorem 4.1. The proposed remedy involves using random Fourier features.
The homotopy dynamics approach appears to provide a more principled way to implement some of these intuitions. However, a discussion on the similarities and differences between these methods, along with a performance comparison, would strengthen the paper.
1. Krishnapriyan, A.S., Gholami, A., Zhe, S., Kirby, R.M., Mahoney, M.W., 2021. Characterizing possible failure modes in physics-informed neural networks.
2. Wang, S., Wang, H., Perdikaris, P., 2021. On the eigenvector bias of Fourier feature networks: From regression to solving multi-scale PDEs with physics-informed neural networks.
In addition, there is also a difference between the experiments and the proposed method. When describing the proposed method, only $\epsilon$ changes. However, for the experiments, another parameter $s$ is introduced, which also modify the residual loss.
Supplementary Material: The supplementary material is the same as the appendix.
Relation To Broader Scientific Literature: The proposed method improve PINN for a specific type of PDE problem.
Essential References Not Discussed: See Experimental Designs Or Analyses.
Other Strengths And Weaknesses: Strengths
- The homotopy dynamics method is a principled and effective way to address challenges in training PINNs for sharp-interface PDEs.
- The paper is well-written and easy to follow, making it accessible to readers with different levels of familiarity with PINNs and interface PDE
- Theorems provide insights into why homotopy dynamics improves training.
- The approach has the potential to benefit researchers working on PINN, particularly in problems involving sharp interface.
Weakness:
- The baseline is relatively week, see Experimental Designs Or Analyses.
- Alternative strategies are not fully explored, see Methods And Evaluation Criteria.
Other Comments Or Suggestions: - Algorithm 1, line 199, why do wee need $\Delta \epsilon_k$ in the inner loop of strategy 2
- For the numerical examples, which strategy is used?
Questions For Authors: See previous comments, Methods And Evaluation Criteria, Experiment Design and Analysis.
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: Thank you for your thoughtful review and constructive suggestions. Below, we address the concerns you raised.
- **Why do we use PINN for this type of problem instead of well-established numerical methods?**
Neural networks offer strong approximation capabilities [1] and help mitigate the curse of dimensionality [2], making them well-suited for solving PDEs. They have been widely applied in this context [3,4], particularly in operator learning, where they can significantly accelerate computation. Moreover, many AI for Science models are governed by similar equations, and neural networks enable seamless integration of experimental data into the modeling process.
- **Regarding the homotopy loss $L_{H_\varepsilon}$ (line 181):**
Without $L_{H_\varepsilon}$, simply varying $\varepsilon$ leads to instability and sensitivity to $\Delta \varepsilon$. The homotopy loss enables a stable Euler-forward-like path consistent with the homotopy dynamics. We will include supporting experiments in the revised version.
- **What happens if we use only $L_{H_\varepsilon}$ and omit the residual loss $L_H$?**
A solution satisfying $H(u, \varepsilon) = \text{Const} \neq 0$ still minimizes $L_{H_\varepsilon}$. Thus the residual loss is necessary to enforce the target PDE constraint.
- **What is the effect of $\alpha$?**
It balances the three loss terms, playing a similar role as $\lambda$.
- **Algorithm 1, line 199: Why do we need $\Delta \epsilon_k$ in Strategy 2?**
It ensures proper scaling of $L_{H_\varepsilon}$ and guides the homotopy step correctly.
- **For the numerical examples, which strategy is used?**
Strategy 1 is used for 1D Allen–Cahn and high-frequency examples. Strategy 2 is used for 2D Allen–Cahn and Burgers, where solving the linear system is more difficult.
---
**Theoretical Answer:**
- **Items 1–3:** We agree. $L$ should be $L_H$, $l$ as $l_\varepsilon$, and $K_\varepsilon$ refers to $K_\varepsilon(\theta(0))$. These will be corrected.
- **Item 4:** Based on Weyl’s inequality:
$\lambda_{\min}(A+B) \ge \lambda_{\min}(A) + \lambda_{\min}(B)$
Therefore,
$\lambda_{\min}(K_\varepsilon(\theta(t)))
\ge \lambda_{\min}(K_\varepsilon(\theta(t)) - K_\varepsilon(\theta(0))) + \lambda_{\min}(K_\varepsilon(\theta(0)))$
$\ge \lambda_{\min}(K_\varepsilon(\theta(0))) - \sigma_{\max}(K_\varepsilon(\theta(t)) - K_\varepsilon(\theta(0)))$
$\ge \lambda_{\min}(K_\varepsilon(\theta(0))) - ||K_\varepsilon(\theta(t)) - K_\varepsilon(\theta(0))||_F$
$\ge \frac{1}{2}\lambda_{\min}(K_\varepsilon(\theta(0)))$
We will add this in the revised proof.
- **Item 5:** A large learning rate won’t solve the slow convergence issue for small $\varepsilon$, and may lead to instability [3].
- **Item 6:** Thank you—we will update the notation.
- **Item 7:** For small $\varepsilon$, $K_\varepsilon$ may be large but remains finite. Using small $\Delta \varepsilon$ ensures stable error control.
- **Items 8–9:** The index should be lowercase $n$, and the correct reference is [4].
- **Item 10:** Without $L_H$ and $\lambda L_{bc}$, Strategy 2 becomes a way to solve Eq. (7). However, due to small singular values in $H_u \nabla_\theta u$, solving directly may be unstable. Thus, we adopt optimization instead. Strategy 2 shares the same dynamics as Strategy 1. Including $L_H$ ensures the solution satisfies the PDE. Even if $H(u, \varepsilon) = \text{Const} \neq 0$, it still minimizes $L_{H_\varepsilon}$, hence both terms are necessary.
---
**Comments on the Weaknesses:**
We thank the reviewer for the insightful comments. Compared with [5], our method introduces a homotopy loss that prevents convergence to bifurcation solutions. This key idea is not present in [5]. Also, the difficulty of training when $\varepsilon \to 0$ is not theoretically addressed in [6]; we believe ours is the first rigorous analysis. Strategy 2 is an alternative solver within the same framework, so our theoretical results are based on Strategy 1.
**Experimental Comparison:**
Based on Example 5.1, we added comparisons with other methods. In this example, the homotopy is defined as $H(u,s,\epsilon(s))$. Results in [Table 3 and Figures 1–3](https://drive.google.com/file/d/1fvQdXIZpm0c3fci_85Sb4CW-ZIjVHBlx/view) show that our homotopy-based method consistently achieves better accuracy.
---
**References:**
[1] [Yang et al., NeurIPS, 2023.](https://proceedings.neurips.cc/paper_files/paper/2023/hash/449a016a6ce6fba3fe50d05482abf836-Abstract-Conference.html)
[2] [E et al., Constructive Approximation, 2022.](https://arxiv.org/abs/1906.08039)
[3] [Sutskever et al., ICML, 2013.](https://proceedings.mlr.press/v28/sutskever13.html)
[4] [Atkinson et al., Wiley, 2009.](https://homepage.math.uiowa.edu/~atkinson/papers/NAODE_Book.pdf)
[5] [Krishnapriyan et al., NeurIPS, 2021.](https://arxiv.org/abs/2109.01050)
[6] [Wang et al., Comput. Methods Appl. Mech. Eng., 2021.](https://www.sciencedirect.com/science/article/pii/S0045782521002759) | Summary: In this paper, the authors present a training based method based on homotopy dynamics for handling sharp interface problems. The authors provide a proof of the convergence of the Homotopy dynamics for stable training. The experiments results demonstrate that the proposed method can help capture the sharp interfaces as well as approximating high-frequency functions.
Claims And Evidence: The authors claim that the proposed method can improve the training process for sharp interface problems, high frequency function approximation and operator learning. These claims are validated by three examples in the experiments part. The authors also provide a theoretical proof for the convergence of Homotopy Dynamics for stable training.
Methods And Evaluation Criteria: The proposed methods are evaluated on three examples: 2D Allen Cahn Equation, High Frequency Function Approximation and Burgers Equation, which looks sensible to me.
Theoretical Claims: While I have thoroughly reviewed the methodology presented in the paper, I did not perform an exhaustive line-by-line verification of all mathematical derivations and proofs.
Experimental Designs Or Analyses: The experiments demonstrate the effectiveness of the proposed method on sharp interface problem. Here the problems have more shaper interface with smaller parameter **epsilon**. The experiments show that the proposed homotopy loss keeps low while classical loss increases dramatically as the parameter value decreases.
Supplementary Material: I review the supplementary material, especially for the part Details on Experiments.
Relation To Broader Scientific Literature: The proposed method provides a training strategy for learning based method such as PINN, Operator learning to learn sharp interface problems. This paper also present some intuitions on the training difficulties caused by certain parameters in PDEs learning.
Essential References Not Discussed: n/a
Other Strengths And Weaknesses: The paper is well-written and easy to follow. The detailed background materials provided helps enhance the reader’s comprehension of the paper.
Other Comments Or Suggestions: n/a
Questions For Authors: - The examples shown in this paper are restricted in small scale 1D or 2D scenarios. Just wondering how would the method performed when applied to larger 3D cases?
- What are the training/inference time costs for the proposed method? How sensitive are the time costs to the number of trainable parameters?
- In this paper, the authors investigate the scenarios where a single parameter $\epsilon$ quantifies how singular the system is. Does the proof still holds if there are multiple parameters? How would the method extend to handle these multi parameter scenarios?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your valuable suggestions on our paper.
First, We would like to emphasize the main focus and contribution of our work. This paper addresses the core challenge of training neural networks to solve PDEs, particularly those involving sharp interfaces, where specific parameters in the PDE induce near-singularities and hinder optimization. **From a theoretical perspective, we provide a novel analysis of how such parameters affect the convergence behavior during training.** To overcome these difficulties, we propose a **homotopy dynamics-based training strategy** and rigorously establish its convergence properties. On the experimental side, we demonstrate that our method not only performs effectively on the 2D Allen–Cahn equation, but also alleviates the spectral bias commonly seen in neural network training. Furthermore, we show that this homotopy-based approach generalizes well to the operator learning setting, highlighting its versatility and broad applicability.
Below, we provide our responses to the questions and concerns you have raised.
- We appreciate the reviewer’s suggestion regarding the extension of our method to larger-scale 3D cases. While the current examples in the paper are primarily 1D or 2D, it is important to emphasize that Example 5.3 is set in the operator learning framework, which is inherently more complex and challenging than standard PDE regression tasks.
In particular, unlike most existing operator learning methods that are trained in a supervised manner (i.e., with access to input-output solution pairs), our setting adopts a fully unsupervised training strategy based on homotopy dynamics, where the model learns the solution operator solely from the PDE structure. This significantly increases the difficulty of the learning problem.
Despite this challenge, our method achieves competitive and accurate results, highlighting its potential applicability not only to standard PINNs but also to more complex, unsupervised operator learning tasks.
We thank the reviewer again for the helpful suggestion, and in the revised version of the paper, we will incorporate higher-dimensional (e.g., 3D) examples to further demonstrate the effectiveness of our approach.
- Regarding **training time**, we provide additional details here. All experiments were conducted on a single RTX 3070 Ti GPU. The corresponding computation times for training each epoch are summarized in the [Table 2](https://drive.google.com/file/d/1fvQdXIZpm0c3fci_85Sb4CW-ZIjVHBlx/view)
The detailed settings of each numerical experiment, including all parameter choices, are provided in Appendix B. We would like to emphasize that although our training time may appear relatively longer and the training procedure more involved, it enables us to achieve significantly higher accuracy. This level of precision cannot be attained by other methods, regardless of how long they are trained.
Regarding **inference time**, we take Example 5.3 as a representative case in the operator learning setting. Specifically, we compare the inference efficiency of our trained DeepONet model with that of the traditional finite difference method, by solving 1,000 instances of the PDE using both approaches. The results are summarized in the [Table 1](https://drive.google.com/file/d/1fvQdXIZpm0c3fci_85Sb4CW-ZIjVHBlx/view).
As with other neural network-based methods, increasing the number of network parameters generally leads to longer training times. Thank you for your helpful suggestion — we will include these details and clarifications in the revised version of the paper.
- The question you raised is very interesting. We believe that our proposed homotopy dynamics-based approach can be extended to cases involving multiple parameters. At present, our initial idea is that in the multi-parameter setting, the homotopy dynamics may need to update the parameters sequentially or in a coordinated manner. We consider this a promising direction and plan to explore it further as part of our future work.
Finally, we would like to thank you again for your insightful comments and questions.
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Rebuttal Comment 1.1:
Comment: Thanks for the authors' response. I will keep my score unchanged.
---
Reply to Comment 1.1.1:
Comment: Thank you again for your response and valuable suggestions. We will include a high-dimensional numerical experiment in the revised version. The results are shown below.
$$
-\Delta u = f_{\varepsilon},~~ \mathbf{x}\in \Omega, \quad
u = g,~~ \mathbf{x}\in \partial\Omega, \\
$$
where $\Omega=[-1, 1]^d$, $f_{\varepsilon}(x)=\frac{1}{\epsilon^2}\frac{1}{d}(\sin(\frac{1}{d}\sum \limits_{i=1}^{d}x_i)-2)$, which admit the exact solution $u(x)=(\frac{1}{d}\sum \limits_{i=1}^{d}x_i)^2+\sin(\frac{1}{\varepsilon}\frac{1}{d}\sum \limits_{i=1}^{d}x_i)$. We consider $d=20$ and $\varepsilon = \frac{1}{35}$. Here, we employ a neural network with 5 layers and 128 neurons per layer. The training dataset consists of 10,000 interior points and 2,000 boundary points. The model is trained for $10^6$ epochs. The results are presented below.
| Method | Original PINN | Multiscale PINN [1] ($\sigma=35$) | Homotopy |
| :----: | :-----------: | :-------------------------------: | :------: |
| L2RE | 1.00e00 | 9.98e-1 | 5.84e-3 |
The results indicate that our method performs well even for high-dimensional problems.
**Reference**
[1] [Wang et al., Comput. Methods Appl. Mech. Eng., 2021.](https://www.sciencedirect.com/science/article/pii/S0045782521002759) | Summary: The authors look at the physics-informed neural network (PINNs) setting of solving a PDE via minimizing the PDE residual. They look at cases where there are “sharp” interfaces (introducing near singularities). They propose a method based on homotopy dynamics, which involves starting with an easier to learn problem and then moving towards a harder to learn problem (where “easy” and “hard” are characterized by the parameters in the PDE). They show this on the 1D Burgers equation and 1D and 2D Allen-Cahn equations.
Claims And Evidence: The authors claim that this method makes it easier to get better error on PDE problems with near singular features. They show this on 1D Burgers, and 1D and 2D Allen-Cahn equations and that this type of training (easy to hard parameters) gets better error than directly using the PINNs approach on the “hard” problem right away.
Methods And Evaluation Criteria: The method is based on the parameters of the PDE. They start with cases when the parameter in these different PDEs is higher, and the solution is easier to compute here. Then they train the model by going from this high parameter to the low parameter (and the original target problem).
However, these PDEs are still quite easy, and the PINNs literature has come a long way since. These systems were being studied years ago, with similar errors, and the field should be moving to harder problems at this point. Additionally, there are a number of other methods for improving PINNs training and prediction (including very similar ones) that are not compared to at all. Two examples:
This method looks very similar to the curriculum regularization approach in [1], where the authors started with an easy to learn PDE problem and then slowly trained the model to solve the harder problem. The authors try to demonstrate their approach on high frequency problems, but many approaches to address high frequency function approximation already exist, a simple one is to add Fourier features [2]. Additionally, if looking at the operator learning setting, how would it look to use something like Fourier Neural Operator [3] instead? These papers are many years old at this point, and the field has progressed a lot since: new approaches should be looking at much harder problems, comparing appropriately to prior approaches, and going beyond methods that have already been proposed.
The authors also mention resampling: there are also adaptive weighting methods that sample places where the PDE residual is high [4]. However, it seems like this approach is also not that computationally cheap since it requires training the network for longer by starting with the easier-to-learn parameter and then going to the harder one.
[1] Krishnapriyan et al. Characterizing possible failure modes of physics-informed neural networks. NeurIPS (2021)
[2] Wang, Wang, Perdikaris. On the eigenvector bias of Fourier feature networks. CMAME (2021)
[3] Li et al. Fourier Neural Operator. ICLR (2021)
[4] C. Wu, M. Zhu, Q. Tan, Y. Martha, L. Lu. A comprehensive study of non-adaptive and residual-based adaptive sampling for physics-informed neural networks. CMAME (2023).
Theoretical Claims: The authors present a theoretical analysis around the effectiveness of training PINNs via this homotopy dynamics approach. There are various places where a lot more steps would be helpful. There are also a lot of assumptions that are being made in these claims, such as only analyzing 2 layer neural networks, and looking at the width of the NN with ReLU activation functions. Does analysis based on ReLU activation functions actually apply here given that the neural network needs to be continuously differentiable to get derivatives and train with the PDE residual?
Also, how do you make the assumption in Eqn 31 in appendix?
Experimental Designs Or Analyses: The authors set up the three different PDE problems. They train a PINN with and without using the homotopy dynamics approach (directly solving the problem vs going from easy to hard parameters). See the above comment that there are now many methods to train PINNs better, many of which have addressed similar problems that the authors are looking at. At this point, it is needed to show proof-of-concept on much more difficult problems, such as those that many current PINNs methods struggle with.
Supplementary Material: I looked over the supplementary material, which is primarily proof-based.
Relation To Broader Scientific Literature: There is a lot of work on PINNs and better training methods for PINNs, as well as a wide range of work on using ML to solve PDEs. This work needs to be better contextualized against this broad landscape, and a lot of the progress that has been made in the field.
Essential References Not Discussed: Work that proposes a similar idea, as well as other works that attempt to deal with the same problems (such as Fourier features for high-frequency learning), are discussed above. There are many off-shoots and follow-ups of these works that are also relevant.
Other Strengths And Weaknesses: See above for comments. The primary comments are that this work proposes something very similar to past work in the PINNs literature, doesn’t compare or contextualize against a vast literature of PINNs work that has been done to address many of the problems described here, and the experiment problems shown are relatively easy (compared to how far the field has come since).
Other Comments Or Suggestions: See above for comments.
Questions For Authors: - How does this compare to adding Fourier features? How about the many other approaches that have been done for PINNs, such as the very similar curriculum regularization or adaptive sampling / adaptive weighting of the loss function?
- What is the computational cost of this method?
- These systems have been well-studied and are easy. Can these methods show proof-of-concept on much harder systems?
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: Thank you for your careful reading and valuable suggestions.
First, we would like to emphasize the main motivation and contribution of our work. **From a theoretical perspective, we analyze how such parameters affect training convergence speed**. To overcome these difficulties, we propose a **homotopy dynamics-based training strategy** with rigorous convergence analysis.
Below, we address the questions and concerns you have raised.
- **Comparision to Related Work**
We would like to emphasize that, to the best of our knowledge, **our work is the first to provide a theoretical justification that in sharp interface problems**, the parameter $\epsilon$ directly determines training difficulty—the smaller the $\epsilon$, the harder the optimization (see **Theorem 4.1**).
While our approach shares a high-level idea with curriculum-based methods (progressing from easy to hard tasks), it differs significantly in design. Unlike [1], which lacks a systematic mechanism, our homotopy dynamics defines a continuous path in the PDE parameter space with convergence guarantees. Moreover, we provide a dynamical update rule and a theoretically grounded strategy for choosing the homotopy step size $\Delta\epsilon$ (see **Theorem 4.3**), which is not addressed in [1].
Regarding Fourier feature methods [2], their success depends on prior knowledge and sensitive tuning of the feature scale $\sigma$. Our focus is on sharp interface problems, which differ from general multiscale settings. Example 5.2 shows that our method can generalize beyond sharp interfaces, demonstrating its versatility.
As for resampling-based methods [3,4], they often require large sample sizes and careful tuning, making them computationally expensive. In contrast, our approach achieves competitive accuracy with fewer collocation points and lower computational cost.
We further highlight these strengths in Example 5.1 (2D Allen–Cahn, $\epsilon = 0.05$). Unlike [1], which needs 50 time steps ($\Delta t = 0.1$), our homotopy strategy reaches the steady state in only 10 steps ($\Delta s = 0.1$) and uses just 2,500 collocation points. This demonstrates both the efficiency and effectiveness of our method.
Finally, we have added additional experimental comparisons, which further support the advantages of homotopy-based training and [Results](https://drive.google.com/file/d/1fvQdXIZpm0c3fci_85Sb4CW-ZIjVHBlx/view) show that our homotopy-based method consistently achieves better accuracy.
- **Theoretical Clarifications**
We appreciate the reviewer’s comments regarding theoretical assumptions and will incorporate further details in the revised version.
1. **Network Depth and Generality**: While we present the theory using two-layer networks for simplicity, our framework can be readily extended to deep architectures, building on standard results such as those in [2]. Our theoretical analysis focuses on how a small $\varepsilon$ induces optimization difficulties, regardless of the network depth, and the results remain valid. We use shallow networks solely to simplify the notation and enhance readability, thereby helping readers grasp our key points.
2. **Activation Functions**: Although we use ReLU in our theoretical analysis, the results hold for other smooth activations such as $\tanh$ and $\text{ReLU}^k$ (except for Lemma A.1, which has a known analog in [2]). In the revision, we will clarify that our results are **not restricted to ReLU**, and we will present a more general analysis accordingly.
3. **Clarification of Eq. (31)**: We note that Eq. (31) is **not an assumption**, but rather defines the **continuous kernel limit** as $m \to \infty$ (based on Law of Large Numbers). We will provide further explanation in the appendix to clarify this point.
- **Other Questions**
- Based on Example 5.1, we added comparisons with other methods. Results in [Table 3 and Figures 1–3](https://drive.google.com/file/d/1fvQdXIZpm0c3fci_85Sb4CW-ZIjVHBlx/view) show that our homotopy-based method consistently achieves better accuracy.
- The training time and inference time for the numerical experiments can be found in [Table 1 and 2](https://drive.google.com/file/d/1fvQdXIZpm0c3fci_85Sb4CW-ZIjVHBlx/view).
- Our setting includes not only single PDEs, but also unsupervised operator learning, which is harder than the commonly studied supervised setup. Prior works [3,4] have explored this, but our method achieves higher accuracy. We believe our homotopy strategy can be extended to even more complex systems in future work.
**References**
[1] [Krishnapriyan et al., NeurIPS, 2021.](https://arxiv.org/abs/2109.01050)
[2] [Wang et al., Comput. Methods Appl. Mech. Eng., 2021.](https://www.sciencedirect.com/science/article/pii/S0045782521002759) \
[3] [Zhang et al., J. Comput. Phys., 2024.](https://doi.org/10.1016/j.jcp.2023.112638) \
[4] [Li et al., Comput. Methods Appl. Mech. Eng., 2023.](https://doi.org/10.1016/j.jcp.2025.113843)
---
Rebuttal Comment 1.1:
Comment: Thank you for the response. I maintain concerns that the examples looked at here are too toy, as they have been well-studied for years now. Additionally, it would be useful to see more discussion on how the baseline comparisons were set up, and/or any code to compare these. For the Fourier features point, there is an experiment that explicitly relies on trying to capture high-frequency features, so Fourier features and other multi-scale approaches are a natural comparison.
For the training time per epoch, the useful thing would be a total comparison of time trained, etc. against the speed of a numerical solver given the same accuracy. I think these examples are toy enough that a numerical solver will be faster.
---
Reply to Comment 1.1.1:
Comment: Thank you again for your response and valuable suggestions. In response to your concern, we would like to make the following clarifications.
- **Comparison with tradition numerical method**
We conducted a detailed comparison between the finite difference method (FDM) and the DeepONet trained with our homotopy strategy by solving 1,000 instances of the Burgers' equation with varying initial conditions. We compared inference time, computational time, and relative $L^2$ error. As shown below, while FDM generally yields high accuracy, its computational cost rises sharply as $\varepsilon$ decreases due to CFL stability constraints. Moreover, its accuracy also degrades for small $\varepsilon$, likely due to resolution limitations.
| | | **Finite Difference Method** (FDM) | | | | **DeepONet (trained by Homotopy)** | | |
| :-----------: | :--------------: | ---------------------------------- | :---------: | ---------------------- | :--------: | :--------------------------------: | :---------: | ----------------- |
| $\varepsilon$ | $\Delta t$ | L2RE | MSE distance($x_s$) | Computational Time (s) | Loss $L_H$ | LE2RE | MSE distance ($x_s$) | Inference Time(s) |
| 0.5 | $5\times10^{-5}$ | 1.63e-12 | 7.35e-13 | 239.98 | 7.55e-7 | 1.50e-3 | 1.75e-8 | 0.2 |
| 0.1 | $1\times10^{-5}$ | 5.83e-4 | 1.57e-5 | 1239.77 | 3.40e-7 | 7.00e-4 | 9.14e-8 | 0.2 |
| 0.05 | $5\times10^{-6}$ | 1.01e-2 | 4.20e-3 | 2416.23 | 7.77e-7 | 2.52e-2 | 1.2e-3 | 0.2 |
- **High dimension case**
We will include a high-dimensional numerical experiment in the revised version. The results are shown below.
$$
-\Delta u = f_{\varepsilon},~~ \mathbf{x}\in \Omega \quad
u = g,~~ \mathbf{x}\in \partial\Omega,
$$
where $\Omega=[-1, 1]^d$, $f_{\varepsilon}(x)=\frac{1}{\epsilon^2}\frac{1}{d}(\sin(\frac{1}{d}\sum \limits_{i=1}^{d}x_i)-2)$, which admit the exact solution $u(x)=(\frac{1}{d}\sum \limits_{i=1}^{d}x_i)^2+\sin(\frac{1}{\varepsilon}\frac{1}{d}\sum \limits_{i=1}^{d}x_i)$. We consider $d=20$ and $\varepsilon = \frac{1}{35}$. Here, we employ a neural network with 5 layers and 128 neurons per layer. The training dataset consists of 10,000 interior points and 2,000 boundary points. The model is trained for $10^6$ epochs. The results are presented below.
| Method | Original PINN | Multiscale PINN [1] ($\sigma=35$) | Homotopy |
| :----: | :-----------: | :-------------------------------: | :------: |
| L2RE | 1.00e00 | 9.98e-1 | 5.84e-3 |
The results indicate that our method performs well even for high-dimensional problems. For this high-dimensional problem, traditional numerical methods face significant challenges, making neural network-based approaches naturally advantageous. In our comparison, we observe that even the Fourier feature-based multiscale PINN [1] struggles to handle high-dimensional, high-frequency problems effectively. In contrast, our proposed homotopy-based training method achieves notably higher accuracy.
- **Comparison with Multiscale PINN [1]**
Thank you for the suggestion. We compared with the Multiscale PINN in Example 5.2, which approximates a one-dimensional high-frequency function. Using the same network architecture, it achieves an MSE of $9.89 \times 10^{-8}$ at $\sigma = 30$, outperforming our method. This is likely due to its built-in basis functions $\sin(\sigma \pi x)$, which align well with targets like $\sin(50 \pi x)$. However, as shown in the high-dimensional Poisson example, its performance degrades significantly in more complex, high-dimensional settings.
- **Setting for baseline model**
Due to space constraints, we omitted detailed baseline settings in the response. For clarity, the baseline models share the same network architecture, sample points, and training epochs as our homotopy-based method. Code and further implementation details will be included in the revised paper.
We have also provided supplementary information regarding the training time of our proposed method, as shown in the table below.
| Example | 1D AC Equation | Example 5.1 | Example 5.2 | Example 5.3 |
| :--------------------------: | :------------: | ----------- | :---------: | ----------- |
| Training time for each epoch | 0.05s | 0.09s | 0.01s | 0.4s |
| Total epoch (step) | 1.0e3 | 4.0e6 | 4.0e6 | 2.0e6 |
[1] Wang et al., Comput. Methods Appl. Mech. Eng., 2021. | Summary: This paper proposes Homotopy Dynamics to train neural network for solving sharp interface problems. For sharp interface problems, the parameter $\epsilon$ in the PDE affects the singularity of the solution. As $\epsilon \to 0$, the PDE becomes increasingly singular and thus the solution is difficult to compute. The authors first train the
neural network on PDEs with a large $\epsilon$, and then adjust the neural network according to the evolution of the homotopy dynamics until $\epsilon$ decreases towards the target value. To validate the performance of the proposed methods, Numerical experiments on Allen-Cahn equation, high frequency function approximation, and Burgers equation are performed to validate the performance of the proposed method.
Claims And Evidence: Most of the claims made in the submission are supported by clear and convincing evidence.
Question:
- In Theorem 4.1 the upper bound of $\lambda_{\min}(K_{\epsilon})$ is given. In line 301, 'Consequently, the training speed can reach $\exp(−Cn^3t$) based on Eq. (19), which is fast and implies that training is
easy.' This statement cannot be derived from Theorem 4.1 unless the bound is tight. More explanation is needed.
Methods And Evaluation Criteria: The numerical experiments make sense for validating the performance of the proposed method.
Theoretical Claims: I did not carefully check the correctness of proofs for theoretical claims in Appendix A.
Experimental Designs Or Analyses: The experimental design appears sound and aligns well with the theoretical framework.
Supplementary Material: I did not carefully review the supplementary material.
Relation To Broader Scientific Literature: The paper overcomes the optimization challenges lies in the training of neural network for solving PDEs; as introduced in Section 1. However, the motvation of using neural network to solve these PDEs are not adequately discussed. To my knowledge, the numerical solution of the example problems are well-studied using method other than neural network, to name just a few literature: some references in the paper including [Kreiss & Kreiss, 1986], [Hao & Yang, 2019] and
Kim, Yongho, Gilnam Ryu, and Yongho Choi. "Fast and accurate numerical solution of Allen–Cahn equation." Mathematical Problems in Engineering 2021, no. 1 (2021): 5263989.
Shen, Jie, and Xiaofeng Yang. "Numerical approximations of allen-cahn and cahn-hilliard equations." Discrete Contin. Dyn. Syst 28, no. 4 (2010): 1669-1691.
Jiwari, Ram. "A hybrid numerical scheme for the numerical solution of the Burgers’ equation." Computer Physics Communications 188 (2015): 59-67.
Essential References Not Discussed: The paper adequately discusses the key related works necessary for understanding the context and its contributions.
Other Strengths And Weaknesses: Strengths:
- The proposed method improve the accuracy of the solution compared with other neural network-based methods.
Weaknesses:
- The motivation of using neural network to solve this problem is not convincing enough.
- In line 40. 'Leveraging neural network architectures to solve PDEs,... particularly in handling complex domains and incorporating empirical data'. Both these aspects were not emphasized throughout the paper.
Other Comments Or Suggestions: Some typos:
- In line 94 right column, 'represent represent'
- In line 182 left column, the indices of $u$ are not consistent.
Questions For Authors: - As the neural network is designed and trained for a specific PDE, I think comparison with traditional methods should be included. For example, the computation cost (training time for using neural network versus the computation time using numerical solvers to solve the nonlinear equation); the accuracy of the solution, etc... to highlight the advantage of the proposed method.
- In example 5.3, why not directly train and solve for the steady state solution since it is independent of the initial condition.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your careful reading and valuable suggestions. Our work addresses the core challenge of training neural networks to solve PDEs with sharp interfaces, where small parameters introduce near-singularities that hinder optimization. **From a theoretical perspective, we analyze how such parameters affect training convergence.** To overcome these difficulties, we propose a **homotopy dynamics-based training strategy** with rigorous convergence analysis. Experimentally, we show the method performs effectively on the 2D Allen–Cahn equation, mitigates spectral bias, and generalizes well to the operator learning setting.
In response to the concerns you raised, we provide the following answers:
- **Motivation for using neural networks.** Neural networks are widely used as PDE solvers due to their strong approximation power[1] and ability to mitigate the curse of dimensionality [2]. They also benefit from automatic differentiation for efficient derivative computation. However, training neural networks for complex PDEs remains difficult. Our work targets these optimization challenges with a homotopy-based solution.
For time-dependent PDEs like Allen–Cahn, computing the steady-state solution ($T \to \infty$) with traditional solvers requires very small $\Delta t$ as $\epsilon \to 0$, making them expensive. Neural networks, once trained, allow efficient inference—especially on GPUs. In Example 5.3, we add a comparison between our homotopy-trained DeepONet and classical finite difference methods across 1,000 equations (see [Table 1](https://drive.google.com/file/d/1fvQdXIZpm0c3fci_85Sb4CW-ZIjVHBlx/view?usp=sharing)), demonstrating significant computational speedups.
Neural network methods for these PDEs have gained attention recently[3,4,5]. Many physical models (e.g., phase-field dynamics) are governed by Allen–Cahn-type equations. Neural networks provide a path to integrate real experimental data into more accurate physical models.
- **Clarification on Theorem 4.1.** In Theorem 4.1, we present two inequalities. The first inequality (Eq. (19)) characterizes the worst-case scenario, attaining equality when all components vanish except the one associated with the smallest eigenvalue. In practice, however, the decay of the other components is typically faster, rendering Eq. (19) nearly tight. An eigenvalue decomposition reveals that components along other eigen-directions diminish more rapidly, so that the smallest-eigenvalue component dominates after a short transient period.
For the second inequality (Eq.(20)), the Lidskii–Mirsky–Wielandt theorem provides the following full inequality:
$$
\lambda_{\text{min}}(D_\varepsilon^{T} D_\varepsilon)\lambda_{\text{min}}(S^{T} S) \le \lambda_{\text{min}}(K_\varepsilon) \le
\lambda_{\text{max}}(D_\varepsilon^{T} D_\varepsilon)\lambda_{\text{min}}(S^{T} S)
$$
Thus, when $\varepsilon$ is large, the training speed ranges from $\exp(-Ct/n)$ to $\exp(-Ctn^3)$. For small $\varepsilon$, it consistently decays as $\exp(-Ct/n)$. The upper bound of the above inequality is attained in specific cases where a nonzero vector $x$ exists such that it is the eigenvector of the largest eigenvalue of $D_\varepsilon^\top D_\varepsilon$, and $D_\varepsilon x$ is the eigenvector of the smallest eigenvalue of $S^\top S$. This occurs under certain $S$ and $D_\varepsilon$ structures, depending on the PDE and sampling distribution. Hence, when $\varepsilon$ is large, training can be relatively easy in some cases; however, when $\varepsilon$ is small, training becomes universally difficult.
- **Clarification on Example 5.3.** The objective in this operator learning task is to map the initial condition to its corresponding steady-state solution. In Example 5.3, we select a setup where the steady state is identical across initial conditions. This simplifies verification of whether the operator correctly maps diverse inputs to the same target. However, our homotopy-based training is not restricted to such cases and can be applied to settings where steady states differ. This example serves as a proof-of-concept showing the method's effectiveness even in an unsupervised operator learning setting, contrasting with the typical supervised approaches.
Finally, we thank the reviewer for the constructive feedback and helpful suggestions, which have greatly improved the clarity and completeness of our paper.
**Reference:**
- [1][Yang et al., NeurIPS, 2023.](https://arxiv.org/abs/2305.08466)
- [2][E et al., Constructive Approximation, 2022.](https://arxiv.org/abs/1906.08039)
- [3][Wight et al., Commun. Comput. Phys., 2021.](https://arxiv.org/abs/2007.04542)
- [4][Zhang et al., J. Comput. Phys., 2024.](https://doi.org/10.1016/j.jcp.2023.112638)
- [5][Li et al., Comput. Methods Appl. Mech. Eng., 2023.](https://doi.org/10.1016/j.jcp.2025.113843)
---
Rebuttal Comment 1.1:
Comment: Thank you for addressing my questions and concerns. I have increased my score accordingly.
------------------- Below are updated before April 7 --------------------------------
Thank you for the response. I have some follow-up questions and comments:
1. In Table 1, what is the accuracy of the numerical solvers? I am asking because usually the numerical methods solves to a relative high accuracy. Probably it is not fair (and not necessary) to compare inference time against solver time.
2. In table 2, training time for each epoch is listed, how many epochs in total for training towards target epsilon for each example?
3. As the advantage of neural network approach is to overcome the curse of dimensionality, it would be helpful to see some examples (high dimension and large scale) that classical methods cannot handle.
---
Reply to Comment 1.1.1:
Comment: - We appreciate the reviewer’s concern regarding the fairness of comparing inference time with numerical solver time. To clarify, our intention in Table 1 is not to suggest that DeepONet can fully replace classical numerical solvers in all scenarios, but rather to demonstrate the potential efficiency gains in the **operator learning** setting when solving a large number of PDE instances.
In our revised Table 1 as shown below, we include both the inference time and corresponding accuracy metrics for the DeepONet model and the traditional finite difference method (FDM). As shown, although FDM typically achieves high accuracy, its computational cost increases significantly as $\varepsilon$ decreases, due to the stability constraints imposed by the CFL condition. At the same time, we observe that the accuracy of FDM also deteriorates under small $\varepsilon$, possibly due to resolution limitations.
In contrast, the DeepONet trained via our proposed homotopy dynamics strategy offers **substantially faster inference** across all tested settings, with **only moderate degradation in accuracy**. This efficiency–accuracy trade-off highlights the advantage of using DeepONet in contexts where many-query evaluations are required, such as uncertainty quantification or real-time control.
| | | **Finite Difference Method** (FDM) | | | | **DeepONet (trained by Homotopy)** | | |
| :-----------: | :--------------: | ---------------------------------- | :---------: | ---------------------- | :--------: | :--------------------------------: | :---------: | ----------------- |
| $\varepsilon$ | $\Delta t$ | L2RE | MSE distance($x_s$) | Computational Time (s) | Loss $L_H$ | LE2RE | MSE distance ($x_s$) | Inference Time(s) |
| 0.5 | $5\times10^{-5}$ | 1.63e-12 | 7.35e-13 | 239.98 | 7.55e-7 | 1.50e-3 | 1.75e-8 | 0.2 |
| 0.1 | $1\times10^{-5}$ | 5.83e-4 | 1.57e-5 | 1239.77 | 3.40e-7 | 7.00e-4 | 9.14e-8 | 0.2 |
| 0.05 | $5\times10^{-6}$ | 1.01e-2 | 4.20e-3 | 2416.23 | 7.77e-7 | 2.52e-2 | 1.2e-3 | 0.2 |
- Thank you for the suggestion. We have also included the total number of training epochs required. All training in our experiments is performed using full-batch training.
| Example | 1D AC Equation | Example 5.1 | Example 5.2 | Example 5.3 |
| :--------------------------: | :------------: | ----------- | :---------: | ----------- |
| Training time for each epoch | 0.05s | 0.09s | 0.01s | 0.4s |
| Total epoch (step) | 1.0e3 | 4.0e6 | 4.0e6 | 2.0e6 |
- Thank you very much for your valuable suggestion. Indeed, we have conducted a high-dimensional numerical experiment, as shown below.
$$
-\Delta u = f_{\varepsilon},~~ \mathbf{x}\in \Omega,\\
\quad u = g,~~ \mathbf{x}\in \partial\Omega, \\
$$
where $\Omega=[-1, 1]^d$, $f_{\varepsilon}(x)=\frac{1}{d}(\sin(\frac{1}{\epsilon^2}\frac{1}{d}\sum \limits_{i=1}^{d}x_i)-2)$, which admit the exact solution $u(x)=(\frac{1}{d}\sum \limits_{i=1}^{d}x_i)^2+\sin(\frac{1}{\varepsilon}\frac{1}{d}\sum \limits_{i=1}^{d}x_i)$. We consider $d=20$ and $\varepsilon = \frac{1}{35}$. Here, we employ a neural network with 5 layers and 128 neurons per layer. The training dataset consists of 10,000 interior points and 2,000 boundary points. The model is trained for $10^6$ epochs. The results are presented below.
| Method | Original PINN | Multiscale PINN [1] ($\sigma=35$) | Homotopy |
| :----: | :-----------: | :-------------------------------: | :------: |
| L2RE | 1.00e00 | 9.98e-1 | 5.84e-3 |
The results indicate that our method performs well even for high-dimensional problems.
**Reference**
[1] [Wang et al., Comput. Methods Appl. Mech. Eng., 2021.](https://www.sciencedirect.com/science/article/pii/S0045782521002759) | null | null | null | null | null | null |
A Theory for Conditional Generative Modeling on Multiple Data Sources | Accept (poster) | Summary: This work analyzes the effect of training with multiple data sources on conditional generative models. The authors establish a bound on the total variation distance between true and model distributions in terms of the bracketing number.
## update after rebuttal
The other reviews and the rebuttal have increased my confidence in my initial estimate of the quality of this paper, so I have increased my score by 1 accordingly.
Claims And Evidence: The experimental data aligns well with the theoretical bounds for the Gaussian case. For ARMs and EBMs, the connection to the experiment with diffusion models should be more clearly delineated.
Methods And Evaluation Criteria: Yes, the combination of a simple setup with Gaussians and an empirical evaluation based on diffusion models for image data fits well.
Theoretical Claims: I skimmed the appendix but did not check the correctness of the proofs in detail.
Experimental Designs Or Analyses: There is no explicit experimental design. The standard deviations on the results seem reasonably small based on the smoothness of the curves but it would be great to report an error estimate for the FID scores.
Supplementary Material: I had a brief look at the code but did not check it in detail.
Relation To Broader Scientific Literature: \-
Essential References Not Discussed: \-
Other Strengths And Weaknesses: I don't see any specific weaknesses but I am not knowledgeable enough about this field to judge the importance of these results to the wider community. My impression is that this paper examines a practically relevant setting theoretically in a sound way and and validates the main results empirically.
Other Comments Or Suggestions: - I believe in line 61 there should be parentheses around $K - 1$.
Questions For Authors: 1. How exactly does the diffusion model experiment relate to your bounds for ARMs and EBMs?
2. What are the obstacles for applying these bounds to practical generative models?
3. Is there a direct connection between the FID and your theoretical guarantees?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: # Experimental suggestion: Error estimate for FID scores
We thank the reviewer for the valuable suggestion regarding error estimation.
We would like to clarify that the real-world experiments in Section 5.2 were run only once due to the long training time. Based on these trained models, we additionally performed multiple samplings using five different random seeds to estimate the randomness in calculating FID scores following the reviewer's suggestion. The mean values and standard deviations of FID scores over multiple samplings are reported in the table below (corresponding to Table 1 of our submission).
| $N$ | $\mathrm{Sim}$ | $K$ | Avg. FID (Single) | Std Dev (Single) | Avg. FID (Multi) | Std Dev (Multi) |
| --- | --- | --- | --- | --- | ---| ---|
| 500 | 1 | 3 | 30.03 | 0.0086 | 29.94 | 0.0057 |
| | | 10 | 30.18 | 0.0018 | 29.28 | 0.0336 |
| | 2 | 3 | 32.69 | 0.0160 | 30.69 | 0.0158 |
| | | 10 | 30.54 | 0.0056 | 28.75 | 0.0035 |
| 1000 | 1 | 3 | 28.01| 0.0034 | 26.41| 0.0064 |
| | | 10 | 27.49 | 0.0028 | 25.84 | 0.0250 |
| | 2 | 3 | 30.58 | 0.0047 | 29.35 | 0.0051 |
| | | 10 | 29.01 | 0.0013 | 27.81 | 0.0084 |
We will include these results in the revised version.
# Typo: Missing parentheses
Thank you for pointing this out. We will correct this in the revised version.
# Q1: Experiments on diffusion models and the theory for ARMs & EBMs
We thank the reviewer for the insightful question.
EBMs, as mentioned in lines 51-55 in our submission, are a general and flexible class of generative models closely connected to diffusion models. To be specific, first, the training and sampling methods in [1,2] are directly inspired by EBMs. The distinction is that EBMs parameterize the energy function, while diffusion models parameterize the score function, which is the energy function's gradient. Second, [3] shows that under a specific energy function formulation (Equation (5) in their paper), EBMs are equivalent to constrained diffusion models. Their experimental results (Table 1, Rows A and B in their paper) indicate that the constraint has a minor impact on generative performance. Thus, our diffusion model experiments provide insight into EBMs' behavior in real-world settings to some extent.
Additionally, we have added supplementary simulations for ARMs according to the formulation in Section 4.2. The empirical TV errors exhibit similar trends as theoretical bounds in Theorem 4.3 regarding several key factors—the number of sources $K$, sample size $n$, and data length $D$. Due to space constraints in the rebuttal, please refer to our response to Reviewer 7LUU (Q1) for detailed experimental settings and results.
We will add the above discussions for EBMs, and simulation results along with implementation details for ARMs in the revised version of our paper.
# Q2: Obstacles for practical application
As discussed in Section 7 in the submission (lines 422-432, right column), our theoretical formulation of multi-source training through conditional generative modeling abstracts real-world scenarios to some extent. In practice, conditions may not be explicitly given (e.g., in language models) or may involve multiple source labels (e.g., large-scale image generation).
Our analysis provides a first step toward understanding multi-source training under a simplified yet reasonable setting. Extending it to more complex, fine-grained multi-source interaction scenarios is a valuable direction for future work. Possible approaches might include: characterizing distribution similarity without explicit conditions [1,2] or investigating the multiple-label case by compositional generative modeling [3, 4].
[1] Ben-David, S., & Borbely, R. S. (2008). A notion of task relatedness yielding provable multiple-task learning guarantees.
[2] Jose, S. T., & Simeone, O. (2021). An information-theoretic analysis of the impact of task similarity on meta-learning.
[3] Okawa, M., Lubana, E. S., Dick, R., & Tanaka, H. (2023). Compositional abilities emerge multiplicatively: Exploring diffusion models on a synthetic task.
[4] Lake, B. M., & Baroni, M. (2023). Human-like systematic generalization through a meta-learning neural network.
# Q3: Connection between FID and theoretical guarantees
Our theory provides guarantees for the average TV distance (lines 142-155, left column), which quantifies distribution estimation quality but is incomputable without access to the true conditional distributions.
Therefore, in real-world experiments (Section 5.2), we use FID as a practical alternative. FID measures the similarity between generated and real data distributions by comparing their feature representations in a pretrained neural network. It is widely used to evaluate image generation quality and serves as the best available metric for our setting.
We will add the above discussion to clarify the choice of FID in the revised version. | Summary: This paper takes the first step toward a rigorous analysis of multi-source training in conditional generative modeling, where each condition represents a distinct data source. Specifically, the article establishes a general distribution estimation error bound in average total variation distance for conditional maximum likelihood estimation based on the bracketing number.
Result shows that when source distributions share certain similarities and the model is expressive enough, multi-source training guarantees a sharper bound than single-source training.
They further instantiate the general theory on conditional Gaussian estimation and deep generative models including autoregressive and flexible energy-based models, by characterizing their bracketing numbers. Simulations and real-world experiments validate this theory.
Claims And Evidence: Yes.
Methods And Evaluation Criteria: It makes much sense to the problem at hand.
Theoretical Claims: Yes, I have checked them.
Experimental Designs Or Analyses: Yes, I have checked them.
Supplementary Material: I have reviewed all the supplementary material.
Relation To Broader Scientific Literature: The author has listed these findings in the related work and preliminary section.
Essential References Not Discussed: No.
Other Strengths And Weaknesses: ## Strength
This article is well organized and well written, using mathematical notations clearly and making it easy to understand. The new theory establishes a theoretical bridge between the general error bound of single-source training and multi-source training in conditional generative modelling. This will guide the researchers in choosing the data sources and models empirically and theoretically.
## Weakness
This article has a small issue. Providing intuitive explanations for some theoretical concepts would be beneficial. Additionally, the assumptions in this work deviate slightly from real environments.
Other Comments Or Suggestions: No.
Questions For Authors: 1. Can you provide an intuitive explanation of the ε-upper bracketing number? An example would be helpful.
2. I initially felt some counter intuitiveness about the error bound of a single source. I believe one model training with one dataset has no relation to the whole number of datasets K, but I realize that this work computes the accumulated error of all models, so the error bound will be related to K. I don't know if I understand you correctly. I would like to discuss this with the author.
3. In real-world training, the model with large parameters for multi-source training does not always achieve better results than small expert models with single-source training. For example, when K=10 for Model=10, counting all errors of these 10 models corresponding to one dataset will be higher than a model for all these 10 datasets. However, the error of each model corresponding to one dataset will not always be higher than the model with 10 datasets. What is your opinion of this example, and does this example match your theory?
4. I would like to know if the N and K in Table 1 are set to larger values, such as N=1500 or 2000 and K =15 or 20, the results will have a similar tendency to those in Table 1.
5. The theoretical analysis for the error bound is based on EBM and ARM; however, the article does not provide numerical results for these models but with diffusion models. I think the author should provide some experiment results on ARM or EBM, which would be better.
6. Is the model for multi-source training the same as the single-source training in theoretical analysis and empirical training?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: # Q1: Intuitive explanation for upper bracketing number
The $\epsilon$-upper bracketing number is a notion to quantify the complexity of an infinite set of functions. The key idea is to construct a finite collection of "brackets" that enclose every function in the set within a small margin.
To illustrate this, consider a simple example. Suppose we have the infinite function set $\mathcal{F} = \lbrace f(x) = c:x\in [0,1];c \in [0,1] \rbrace,$ which consists of all constant functions taking values in the interval $[0, 1]$. We can construct an $\epsilon$-upper bracket for $\mathcal{F}$ by defining a finite set $\mathcal{B} = \lbrace b(x)=k\epsilon : k=0,1,\dots,\lceil 1/\epsilon \rceil \rbrace,$ which contains $\lceil 1/\epsilon \rceil+1$ functions. Then, for any function $f \in \mathcal{F}$, there exists a bracket function $b \in \mathcal{B}$ such that:
(1) For all $x \in [0,1]$, the bracket function is always an upper bound: $b(x) \ge f(x)$.
(2) The total "gap" between $b$ and $f$, measured by the integral $\int_0^1 b(x) - f(x) dx$, is at most $\epsilon$. Therefore, the $\epsilon$-upper bracketing number of $\mathcal{F}$ is at most $\lceil 1/\epsilon \rceil+1$.
In our paper, we extend this idea to conditional probability spaces. There, each condition defines its own function set, and we construct corresponding upper brackets that ensure every conditional distribution is approximated with a small error uniformly across conditions.
We will include additional intuitive explanations and diagrams to make this idea more accessible in the revised version.
# Q2: Definition of the estimation error
Your interpretation is essentially correct. In our paper, we define the error in terms of the average TV distance (see Equation 4 on line 147, left column). This metric evaluates the accuracy of conditional distribution estimates across all $K$ sources by averaging the error over each source. Therefore, even for single-source training, the error bound is related to $K$ because it aggregates the errors from the $K$ separate models.
# Q3: Guarantee on one specific source
You have correctly captured the main idea. Our theory demonstrates that, in terms of the average distribution error, multi-source training has a better guarantee than single-source training. However, this does not necessarily imply that for every individual source, the corresponding multi-source model will yield lower error than a dedicated single-source model. Thus, your example is consistent with our theoretical findings.
# Q4: Real-world experiments with larger $N$ and $K$
We would like to clarify that the selection of sample sizes and the number of classes in the experiments in Section 5.2 was influenced by several inherent characteristics of ILSVRC2012 dataset:
- Sample Sizes: The maximum number of images per class in ILSVRC2012 is 1300, so we selected sample sizes of 1000 and 500 images per class, which are common choices.
- Number of Sources: Given that distribution similarity levels were manually defined, it was difficult to establish a large number of structured subdivisions. To be specific, to ensure reasonable similarity levels for the controlled experiment, we designed two-level tree structure for the dataset, as shown in Figure 3 on Page 35 of our submission. Overall, we divided the whole ILSVRC2012 into 10 high-level categories (mammal, amphibian, bird, fish, reptile, vehicle, furniture, musical instrument, geological formation, and utensil). Each category was further subdivided into 10 subsets (e.g., for mammals, we have Italian greyhound, Border terrier, standard schnauzer, etc.). Defining such semantically meaningful and mutually exclusive divisions is not trivial. As a result, the number of classes within each similarity level in our experiments is limited to 10.
Additionally, for the 10-dimensional Gaussian example in Section 5.1, we used a maximum sample size of $N = 5000$ and $K = 15$ (see Figure 1(a) and (b)), which we believe are sufficiently large to verify the theoretical predictions in that case.
We will add the above explanations for the experimental settings in our revised version.
# Q5: Experiments for ARMs or EBMs
Following the reviewer's suggestion, we have added supplementary simulations for ARMs and further illustrations for EBMs. Generally speaking, for ARMs, the empirical TV errors exhibit similar trends as theoretical bounds in Section 4.2 regarding several key factors—the number of sources $K$, sample size $n$, and data length $D$. For EBMs, we clarify their connection with the diffusion model experiments. Due to space constraints in the rebuttal, please refer to our response to Reviewer 7LUU (Q1) for details.
# Q6: Consistency of models used for multi/single
Yes, for both theoretical analysis and empirical experiments, the models used for multi-source and single-source training are exactly the same across all settings, such as model architecture, number of parameters, initialization, and optimizers.
---
Rebuttal Comment 1.1:
Comment: Thanks for the clarification. I have read the author's rebuttal for all reviewers, and it has solved my concerns. So, my evaluation remains unchanged.
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Reply to Comment 1.1.1:
Comment: We thank Reviewer MrF2 for acknowledging our contributions and constructive feedback. | Summary: This paper investigates conditional generative models with multiple data sources. It establishes a general upper bound on the MLE error. The theoretical result is then specialized to conditional Gaussian distributions, autoregressive models, and energy-based models. Finally, the theoretical findings are validated through both simulation studies and real-world experiments.
Claims And Evidence: I think the advantage of multi-source training is not very convincing, and the characterization is somewhat confusing.
Intuitively, multi-source training should only be beneficial when there are similarities among different classes. For example, in the Gaussian distribution setting in Section 4.1, when $d_1 = d$, i.e., there are no shared features across all sources, single-source training should perform just as well as multi-source training. Therefore, a reasonable characterization of the advantage should involve conditions on the ground truth data distribution. However, in Section 4.3, the advantage of multi-source learning is quantified by $S$ and $d_e$, both of which are parameters of the distribution family rather than direct information about the underlying data distribution.
Methods And Evaluation Criteria: Yes
Theoretical Claims: No
Experimental Designs Or Analyses: The experimental designs are reasonable.
Supplementary Material: No.
Relation To Broader Scientific Literature: This paper provides theoretical guarantees for conditional generative models, with results applicable to both large language models and diffusion models.
Essential References Not Discussed: No.
Other Strengths And Weaknesses: This paper is overall well-written and presents a solid theoretical framework for multi-source learning.
Other Comments Or Suggestions: None.
Questions For Authors: None.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: # Q1: Characterization of multi-source advantage
We thank the reviewer for the insightful comment.
We would like to clarify that the advantage of multi-source training is indeed measured by the model parameter sharing, while the degree of the model parameter sharing reflects the source distribution similarity under our theoretical formulation (lines 94-108, right column).
We understand the reviewer’s concern. In the Gaussian model (Section 4.1), $\beta_{sim} = \frac{d - d_1}{d}$ measures the proportion of shared mean vector dimensions, which seems to correspond to the property of the ground truth distribution. While for EBMs (Section 4.3), $\beta_{sim} = \frac{S}{S+d_e}$ is based on model parameters, which does not explicitly represent the data distribution itself.
Despite this difference, in both cases, $\beta_{sim}$ is fundamentally defined by the extent of parameter sharing across sources. The distinction arises from the modeling paradigm: the Gaussian case assumes a parametric form for distributions, where model parameters (e.g., mean vectors) explicitly encode data properties, whereas EBMs use neural networks as a function approximator to fit probability densities without a predefined distributional form, making no explicit connection between parameters and data.
We will add detailed clarification on the relationship between parameter sharing, distribution similarity, and the advantages of multi-source training in the revised version.
---
Rebuttal Comment 1.1:
Comment: Thanks for the clarification. My evaluation remains unchanged.
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Reply to Comment 1.1.1:
Comment: We thank Reviewer QALB for acknowledging our contributions and constructive feedback. | Summary: This paper provides a theoretical framework proving that training conditional generative models on multiple data sources outperforms single-source training when sources share similarities. The authors instantiate their theory across Gaussian distributions, autoregressive models, and energy-based models, demonstrating that both the number of sources and their similarity improves multi-source training benefits. Simulations and experiments with diffusion models validate the theoretical findings, explaining why large generative models trained on diverse but related data often perform better than specialized models.
Claims And Evidence: The paper's claims are supported by theoretical proofs and empirical evidence that appear convincing.
Methods And Evaluation Criteria: Yes.
This paper uses bracketing numbers as a theoretical tool to measure distribution space complexity, which is well-suited for analyzing generative model estimation errors.
And three representative model types (Gaussian, autoregressive, energy-based) are selected that cover key generative modeling approaches.
The evaluation framework connects TV error to FID, and systematically varies K and βsim identified in the theory, making the approach well-aligned with the problem being studied.
Theoretical Claims: I'm not an expert in theoretical deep learning, but I feel the structure of the proof is sound and clear. Although I haven't checked the details of the proof, it seems solid to me.
Experimental Designs Or Analyses: I noticed that Figure 1 shows a very close alignment between theoretical and empirical results. This perfect alignment is somewhat suspicious. From my understanding, the theoretical bounds are derived using worst-case analysis and typically contain constants that are not optimized, making perfect alignment with empirical results unusual. In most papers comparing theory and practice, you'd expect to see similar trends but with some gap between theoretical bounds and empirical measurements. Can the authors explain more about that?
The theoretical results cover three model types (Gaussian, ARM, EBM), but real-world experiments focus only on diffusion models, with no validation for autoregressive models. This should be a more important experiment.
The theory addresses large-scale generative modeling, but experiments use relatively small datasets (500-1000 images per class) and only up to 10 classes, raising questions about how well the findings generalize to truly large-scale settings.
Supplementary Material: N/A
Relation To Broader Scientific Literature: N/A
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: I really like the topic of this paper and believe this is very important to the field.
Even though the theoretical proof seems solid, the experiment part is weak. The whole section focuses on simple cases, and hard to evaluate the generality of the theory. There are more factors that are not involved, such as ARM.
Other Comments Or Suggestions: See the sections above.
Questions For Authors: See the sections above.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: # Q1: Close alignment in Figure 1
We appreciate the reviewer’s careful examination of Figure 1.
As detailed in lines 339-340 of our submission (the caption of Figure 1), the empirical and theoretical values are plotted on **separate vertical axes**: empirical values correspond to the left axis, while theoretical values correspond to the right axis. This visualization normalizes differences in constants between empirical results and theoretical bounds, emphasizing the comparison of trends rather than absolute values.
We will highlight the dual-axis annotation in Figure 1 in the revised version to avoid any potential confusion.
# Q2: Experiments for ARMs
We thank the reviewer for the valuable comment.
Following the reviewer's suggestion, we have conducted supplementary simulations for ARMs according to the formulation in Section 4.2. Experimental settings and results are presented below. Generally speaking, the empirical TV errors exhibit similar trends as theoretical bounds in Theorem 4.3 regarding several key factors—the number of sources $K$, sample size $n$, and data length $D$.
In all experiments, we define a ground-truth sequential discrete distribution, enabling exact computation of the practical TV error. We fix the vocabulary size $M=2$, neural network configurations with $d_e=W=64$, $L=5$, $B=1$. Then we vary $K$ in $[1, 3, 5, 7, 10]$, $n$ in $[1000, 3000, 5000, 10000, 30000]$, and $D$ in $[10, 12, 14, 16, 18]$ to examine alignment of practical TV error with theoretical bounds. For each setting, the batch size and learning rate are selected from $\lbrace 100, 300, 500 \rbrace$ and $\lbrace 10^{-5}, 10^{-4}, 10^{-3} \rbrace$ for the minimum likelihood. Empirical TV errors are presented in the following tables:
| $K \uparrow$ | 1 | 3 | 5 | 7 | 10 |
| --- | --- | --- | --- | --- | --- |
| single | 0.0763 | 0.1212 | 0.1519 | 0.1787 | 0.2127 |
| multi | 0.0763 | 0.1145 | 0.1318 | 0.1364 | 0.1369 |
| $n \downarrow$ | 1000 | 3000 | 5000 | 10000 | 30000 |
| --- | --- | --- | --- | --- | --- |
| single | 0.5680 | 0.3516 | 0.2882 | 0.2036 | 0.1212 |
| multi | 0.5491 | 0.3467 | 0.2747 | 0.1922 | 0.1145 |
| $D \uparrow$ | 10 | 12 | 14 | 16 | 18 |
| --- | --- | --- | --- | --- | --- |
| single | 0.2036 | 0.3785 | 0.5932 | 0.7242 | 0.7505 |
| multi | 0.1922 | 0.3530 | 0.5068 | 0.5747 | 0.6289 |
The results show consistent trends between practical TV error and theoretical bounds with respect to $n$, $K$, and $D$, i.e., the TV error decreases as $n$ and increases with $K$ and $D$, and multi-source training generally outperforms single-source training.
We will add the simulation results and implementation details for ARMs in the revised version.
# Q3: Real-world experiments are on small datasets
We would like to clarify that the selection of sample sizes and the number of classes in the experiments in Section 5.2 was influenced by several inherent characteristics of ILSVRC2012 dataset:
- Sample Sizes: The maximum number of images per class in ILSVRC2012 is 1300, so we selected sample sizes of 1000 and 500 images per class, which are common choices.
- Number of Sources: Given that distribution similarity levels were manually defined, it was difficult to establish a large number of structured subdivisions. To be specific, to ensure reasonable similarity levels for the controlled experiment, we designed two-level tree structure for the dataset, as shown in Figure 3 on Page 35 of our submission. Overall, we divided the whole ILSVRC2012 into 10 high-level categories (mammal, amphibian, bird, fish, reptile, vehicle, furniture, musical instrument, geological formation, and utensil). Each category was further subdivided into 10 subsets (e.g., for mammals, we have Italian greyhound, Border terrier, standard schnauzer, etc.). Defining such semantically meaningful and mutually exclusive divisions is not trivial. As a result, the number of classes within each similarity level in our experiments is limited to 10.
While our experiments are not on large-scale datasets, there are existing studies that provide valuable empirical observations for large-scale multi-source training as mentioned in our Introduction section (lines 8-13, right column), including: cross-lingual model transfer for similar languages [Pires et al., 2019], pretraining with additionla high-quality images to improve overall aesthetics in image generation [Chen et al., 2024], and knowledge augmentation on subsets of data to enhance model performance on other subsets [Allen-Zhu & Li, 2024a]. They have offered relevant findings that inform our work.
We will provide a more detailed explanation of our experimental settings in the revised version.
To summarize, we sincerely thank the reviewer for the constructive comments regarding our experiments, which we believe can improve the quality of this paper. | Summary: The paper establishes a distribution estimation error bound in average total variation distance for conditional maximum likelihood estimation. The main result is based on the bracketing number; it shows that when source distributions share certain similarities and the model is expressive enough, multi-source training guarantees a sharper bound than single-source training.
Claims And Evidence: The paper focuses mostly on the theoretical part of the claims, which is backed by detailed proofs. Simulations and real-world experiments on diffusion models partly validate the results.
Methods And Evaluation Criteria: The evaluation criteria seems reasonable.
Theoretical Claims: I am not very familiar with this particular problem. Due to time limit, I did not carefully check the proofs.
Experimental Designs Or Analyses: I am not entirely sure if I missed something. But it seems that the paper characterizes the bracketing numbers for conditional Gaussian
estimation, autoregressive models and energy-based models, but the real-world experiments focus largely on a particular diffusion model, i.e., EDM2. There seems to be a discrepancy between the proposed theory and its numerical validation.
Supplementary Material: Yes, I focused specfically on the codebase provided in the supplementary material.
Relation To Broader Scientific Literature: The paper establishes a new framework for the analysis of multi-source training in conditional generative modeling, where each condition represents a distinct data source. This could be potentially helpful for general multimodal data learning.
Essential References Not Discussed: None.
Other Strengths And Weaknesses: Please see the ``Experimental Designs Or Analyses`` section.
Other Comments Or Suggestions: I would like to see more experimental results regarding autoregressive models or EBMs to validate the theoretical results.
Questions For Authors: Sorry if I missed this part, but can the authors advise on how to quantify the source similarity $\beta_{\rm sim}$ for general datasets?
Ethical Review Concerns: None
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: # Q1: Experiments for ARMs or EBMs
We thank the reviewer for the valuable comment.
Following the reviewer's suggestion, we have conducted supplementary simulations for ARMs according to the formulation in Section 4.2. Experimental settings and results are presented below. Generally speaking, the empirical TV errors exhibit similar trends as theoretical bounds in Theorem 4.3 regarding several key factors—the number of sources $K$, sample size $n$, and data length $D$.
In all experiments, we define a ground-truth sequential discrete distribution, enabling exact computation of the practical TV error. We fix the vocabulary size $M=2$, neural network configurations with $d_e=W=64$, $L=5$, $B=1$. Then we vary $K$ in $[1, 3, 5, 7, 10]$, $n$ in $[1000, 3000, 5000, 10000, 30000]$, and $D$ in $[10, 12, 14, 16, 18]$ to examine alignment of practical TV error with theoretical bounds. For each setting, the batch size and learning rate are selected from $\lbrace 100, 300, 500 \rbrace$ and $\lbrace 10^{-5}, 10^{-4}, 10^{-3} \rbrace$ for the minimum likelihood. Empirical TV errors are presented in the following tables:
| $K \uparrow$ | 1 | 3 | 5 | 7 | 10 |
| --- | --- | --- | --- | --- | --- |
| single | 0.0763 | 0.1212 | 0.1519 | 0.1787 | 0.2127 |
| multi | 0.0763 | 0.1145 | 0.1318 | 0.1364 | 0.1369 |
| $n \downarrow$ | 1000 | 3000 | 5000 | 10000 | 30000 |
| --- | --- | --- | --- | --- | --- |
| single | 0.5680 | 0.3516 | 0.2882 | 0.2036 | 0.1212 |
| multi | 0.5491 | 0.3467 | 0.2747 | 0.1922 | 0.1145 |
| $D \uparrow$ | 10 | 12 | 14 | 16 | 18 |
| --- | --- | --- | --- | --- | --- |
| single | 0.2036 | 0.3785 | 0.5932 | 0.7242 | 0.7505 |
| multi | 0.1922 | 0.3530 | 0.5068 | 0.5747 | 0.6289 |
The results show consistent trends between empirical and theoretical values with respect to $n$, $K$, and $D$, i.e., the TV error decreases as $n$ and increases with $K$ and $D$, and multi-source training generally outperforms single-source training.
Additionally, we would like to clarify the connection between our diffusion model experiments and the theoretical analysis of EBMs. As mentioned in lines 51-55 in our submission, EBMs are a general and flexible class of generative models closely connected to diffusion models. To be specific, first, the training and sampling methods in [1,2] are directly inspired by EBMs. The distinction is that EBMs parameterize the energy function, while diffusion models parameterize its gradient (the score function). Second, [3] shows that under a specific energy function formulation (Equation (5) in their paper), EBMs are equivalent to constrained diffusion models. Their experimental results (Table 1, Rows A and B) indicate that the constraint has minor impact on generative performance. Thus, our diffusion model experiments provide insight into EBMs' behavior in real-world settings to some extent.
We will provide the implementation details and simulation results for ARMs in the revised version of our paper, along with the above discussions for EBMs.
[1] Song, Y., & Ermon, S. (2019). Generative modeling by estimating gradients of the data distribution.
[2] Song, Y., Sohl-Dickstein, J., Kingma, D. P., Kumar, A., Ermon, S., & Poole, B. (2020). Score-based generative modeling through stochastic differential equations.
[3] Salimans, T., & Ho, J. (2021). Should EBMs model the energy or the score?
# Q2: Quantifying similarity for general datasets
We thank the reviewer for raising this insightful question.
In our paper, $\beta_{sim}$ is defined by induction based on our three specific model instantiations in Section 4. It is not an inherent, directly measurable property of the source distributions themselves, meaning it cannot be directly computed given general datasets.
A fundamental question underlying the reviewer's inquiry might be: *How can we quantify dataset similarity in practice with theoretical guarantees?* We acknowledge that there is no single method currently that provides a solution to this problem, and we are still exploring ways towards this goal.
Possible approaches might include: (1) From a practical perspective, a small proxy model can be used to estimate source distributions' interaction [4]. (2) From a theoretical perspective, several existing notions in multi-task learning and meta-learning could be adapted for this purpose, such as transformation equivalence [5], parameter distance [6], and distribution divergence [7].
[4] Xie, S. M., Pham, H., Dong, X., et al (2023). Doremi: Optimizing data mixtures speeds up language model pretraining.
[5] Ben-David, S., & Borbely, R. S. (2008). A notion of task relatedness yielding provable multiple-task learning guarantees.
[6] Balcan, M. F., Khodak, M., & Talwalkar, A. (2019). Provable guarantees for gradient-based meta-learning.
[7] Jose, S. T., & Simeone, O. (2021). An information-theoretic analysis of the impact of task similarity on meta-learning. | null | null | null | null |
Revisiting Continuity of Image Tokens for Cross-domain Few-shot Learning | Accept (spotlight poster) | Summary: This paper investigates the role of image token continuity in Vision Transformers (ViTs) for Cross-Domain Few-Shot Learning (CDFSL). The authors observe that disrupting token continuity (e.g., shuffling patches or perturbing frequency components) significantly degrades source-domain performance but only marginally affects target domains. They hypothesize that continuity aids ViTs in learning large spatial patterns, which are less transferable across domains, while smaller patterns within patches are more domain-invariant. Based on this insight, they propose a method combining spatial and frequency-domain disruptions to encourage reliance on smaller patterns, achieving state-of-the-art performance on CDFSL benchmarks.
Claims And Evidence: Yes, the authors have conducted several experiments to show the importance of image token continuity for CSFSL. However, more theoretical proof would be better for understanding the claim.
Methods And Evaluation Criteria: To some extent the proposed method is reasonable. Given the validated claim about image token continuity, the authors propose a method that breaks the continuity during training. As mentioned in L192-L195, such a method can keep local patterns undisrupted. However, it is not clear why the following frequency-domain disruption as in Sec.3.2 can hold such a property.
Theoretical Claims: No theoretical claims in this paper.
Experimental Designs Or Analyses: The authors have conducted comprehensive experiments to show the effectiveness of the proposed method. The ablation study can also validate the effectiveness of each design.
Supplementary Material: The supp. mainly contains implementation details for the experiments, e.g. datasets and metrics. The content can help readers better understanding the whole paper.
Relation To Broader Scientific Literature: The insight on the relationship between token continuity and pattern size can help future researches on the design of more powerful ViT backbones. The authors adopt amplitude shuffling but innovate by balancing disruptions across patch clusters. This addresses a limitation of naive frequency augmentation and improves transferability, bridging frequency-domain insights with CDFSL, and potentially other cross-domain tasks.
Essential References Not Discussed: NA
Other Strengths And Weaknesses: Strengths:
1. The method is clearly explained.
2. This paper brings novel insight about the ViT architecture.
Weaknesses:
1. It would be better if the continuity problem can be analyzed theoretically.
2. I wonder if breaking continuity could harm the source domain performance severely.
3. The authors can include experiments with more backbones.
4. Despite the impact statement, I still have concerns about the role of CDFSL given so many large models with great generalization ability.
5. Computation cost can be included in the paper.
Other Comments Or Suggestions: Please refer to weaknesses.
Questions For Authors: Please refer to weaknesses.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your thoughtful feedback and constructive suggestions. Below are our responses to your concerns:
## **1. More Proofs for Continuity**
Our method is consistent with the proofs of the previous works [1-3] in that the small patterns are easier to transfer than larger ones. But we differ in that (1) our method discusses the transferability of small patterns for ViT while [1-3] are originally designed for CNNs; (2) we provide a simple way to enhance the learning of small patterns by perturbing patches with no additional branches or losses.
[1] Cross-domain few-shot learning with task-specific adapters
[2] Task-aware adaptive learning for cross-domain few-shot learning
[3] Discriminative Sample-Guided and Parameter-Efficient Feature Space Adaptation for Cross-Domain Few-Shot Learning
## **2. Frequency Disruption Breaks the Continuity**
Qualitatively, images from an anonymous GitHub link ([https://anonymous.4open.science/r/More-visualization/visualizations.png]) illustrate how our method breaks large-scale spatial patterns while preserving fine-grained, domain-agnostic features (e.g., textures, edges), which aligns with our motivation.
Quantitatively, experiments in Fig. 2 and Fig. 4 validate the feasibility of our methods.
## **3. Source domain performance trade-off**
As suggested, we have provided the performance on the source domain (miniImageNet) for reference.
| Model | Source Domain | Target Domain |
| -------- | ------------- | ------------- |
| Baseline | 97.78 | 63.91 |
| **Ours** | 96.33 | 66.76 |
While there is a slight performance trade-off on the source domain, this aligns with our hypothesis: disrupting token continuity prioritizes learning smaller, transferable patterns over domain-specific holistic features. Crucially, the significant gains on **target domains** (e.g., +6.5% on ISIC) demonstrate the effectiveness of our approach for cross-domain adaptation.
## **4. Experiments with other pretraining and backbones**
(1) Other pretraining
We have conducted experiments with CLIP pretraining. Results confirm our method’s generalizability.
| Backbone | CropDisease | EuroSAT | ISIC | ChestX | **Average** |
| :------- | :---------- | :--------- | :--------- | :--------- | :---------- |
| Baseline | 93.02% | 74.37% | 40.92% | 23.99% | 58.08% |
| **Ours** | **94.03%** | **80.90%** | **43.31%** | **24.45%** | **60.67%** |
(2) Other backbone
While our method is designed for ViTs, we test an **MLP-Mixer backbone** (patch-based architecture):
| Backbone | CropDisease | EuroSAT | ISIC | ChestX | **Average** |
| :------- | :---------- | :--------- | ---------- | ---------- | :---------- |
| Baseline | 85.12% | 78.34% | 36.45% | 22.31% | 55.56% |
| **Ours** | **87.45%** | **80.21%** | **40.12%** | **25.67%** | **58.36%** |
This demonstrates applicability to **other patch-based architectures**.
## **5. Role of CDFSL vs. large pretrained models**
While large vision-language models (VLMs) have demonstrated remarkable generalization capabilities, their effectiveness heavily relies on the assumption that downstream tasks share *similar data domains* with their pre-training corpora (e.g., natural images and generic text). However, in **vertically specialized scenarios** (e.g., medical imaging, remote sensing), where **domain gaps are extreme** and task-specific patterns diverge significantly from generic priors, **directly fine-tuning VLMs often yields suboptimal performance** [4], even worse than training domain-specific models (e.g., UNet) from scratch [5]. Pre-trained models like DINO struggle with medical X-rays (22% accuracy on ChestX) due to fundamentally different texture and structural semantics compared to natural images. However, training large vision-language models from scratch is impractical due to limited data in target domains. This highlights the necessity of CDFSL-specific designs to address domain shifts that challenge even powerful pre-trained models.
[4] Hallusionbench: an advanced diagnostic suite for entangled language hallucination and visual illusion in large vision-language models
[5] Lightweight Frequency Masker for Cross-Domain Few-Shot Semantic Segmentation
## **6. Computation cost**
Our method introduces **no additional trainable parameters**.
During training, the computational overhead (baseline: 126.42s vs. ours: 140.48s per epoch) stems from the clustering-based frequency disruption during training, which is acceptable compared with the gains in cross-domain performance. Moreover, some engineering tricks, such as bipartite matching, can accelerate the clustering process, which we leave for future works.
During inference, since our method introduces no additional parameters, inference time matches the baseline exactly with no computational overhead. | Summary: This paper investigates the role of image tokens' continuity in Vision Transformers for Cross-Domain Few-Shot Learning. The authors identify an interesting phenomenon: disrupting the continuity of image tokens significantly affects performance in source domains but has only a marginal impact on target domains with large domain gaps. Based on this observation, the authors propose a simple yet effective method to disrupt image token continuity in spatial and frequency domains, encouraging the model to focus on smaller, more transferable patterns. The approach achieves state-of-the-art results on four CDFSL benchmark datasets. The paper also includes detailed analyses and ablation studies to support its claims.
Claims And Evidence: The claim that disrupting the continuity of image tokens reduces domain gaps and improves transferability is supported by experiments on four benchmarks.
Methods And Evaluation Criteria: 1. The proposed methods are reasonable and align well with the CDFSL task.
2. The rationale for the warm-up phase and clustering in the frequency domain is intuitively explained, but the clustering threshold could use more justification.
Theoretical Claims: The paper does not make strong theoretical claims or provide formal proofs. The focus is largely on empirical observations and practical methods.
Experimental Designs Or Analyses: 1. The experimental design is sound and well-structured, with comprehensive ablation studies and comparisons to state-of-the-art methods.
2. The choice of specific hyperparameters (e.g., clustering threshold, amplitude sampling standard deviation) could be better justified.
Supplementary Material: The appendix sufficiently describes the datasets, implementation details, and additional experimental results.
Relation To Broader Scientific Literature: The paper builds on recent work in CDFSL and ViT architectures. It extends the understanding of positional embeddings and token continuity in ViT.
Essential References Not Discussed: No essential references are missing.
Other Strengths And Weaknesses: Strengths:
1. The identified phenomenon about token continuity is novel and provides new insights into ViT's behavior under domain shifts.
2. The visualizations and domain similarity analysis enrich the paper's interpretability.
Weakness:
1. The paper lacks a more detailed comparison of the proposed balanced disruption against other diversity-promoting methods.
2. Some design decisions, such as the choice of clustering threshold, require stronger justification.
Other Comments Or Suggestions: Include a discussion on the potential limitations of the method, such as its applicability to non-ViT models.
Questions For Authors: How sensitive is the model's performance to the choice of the clustering threshold in the balanced frequency-domain disruption?
Can the proposed method be generalized to CNN-based models? If not, what are the limitations?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your thorough review and constructive feedback. Below are our detailed responses to your concerns:
## **1. Justification of Clustering Hyperparameters**
The clustering threshold in Eq. 16 controls the **granularity of patch grouping** in the frequency domain. Higher threshold values (e.g., >40%) enforce stricter similarity criteria, resulting in smaller clusters (more fragmented groups). At the extreme (threshold → 100%), each patch forms its own cluster, which degenerates to non-cluster random sampling. Since some image regions occupy larger areas (e.g., background), this will lead patches in the dominant areas to change frequency with other patches in the same area, i.e., their frequencies are not changed, maintaining the original continuity. In contrast, lower thresholds (e.g., <40%) allow looser grouping, creating larger clusters. As shown in **Fig. 6b**, the optimal threshold (**30%**) achieves a critical balance.
The amplitude sampling standard deviation (ϵ) in Eq. 21 **governs the diversity of style proportions assigned to patch clusters** during frequency-domain disruption. Specifically, **smaller ϵ** results in near-uniform style proportions across clusters. This over-regularizes the disruption, limiting diversity and failing to suppress large patterns effectively. As shown in **Fig. 7**, **Larger ϵ** introduces high variability in style mixing ratios, creating *heterogeneous disruptions* that break global continuity.
## **2. Comparison with Diversity-Promoting Methods**
We add comparisons to state-of-the-art diversity-enhancing techniques:
| Method | CropDisease | EuroSAT | ISIC | ChestX | **Average** |
| :----------- | :---------- | :--------- | :--------- | :--------- | :---------- |
| Random-Drop | 91.23% | 84.42% | 43.89% | 24.06% | 60.90% |
| Wave-SAN | 94.84% | 88.79% | 48.71% | 26.98% | 64.82% |
| **Ours** | **96.02%** | **90.42%** | **52.36%** | **28.23%** | **66.76%** |
Our method outperforms both approaches because:
Random-Drop indiscriminately discards patches, losing critical local patterns. Wave-SAN focuses on global frequency bands, overlooking localized high-frequency components critical for fine-grained transfer.
## **3. Limitations and Non-ViT Applicability**
Our method is **inherently ViT-dependent** due to:
- Reliance on **patch-based tokenization** for spatial and frequency disruptions.
- **Self-attention mechanisms** that propagate disrupted token relationships.
Experiments with CNNs (DINO-ResNet50) show limited gains (**+0.7% average** vs. **+2.8% for ViT**), as CNNs’ overlapped sliding-window convolutions and local inductive biases hinder explicit token continuity control. Notably, we also apply our methods to **MLP-Mixers** (see answer 5), and we observe **2.8%** improvements in target-domain accuracy, which verifies our adaptability to token-based structures.
## **4. Sensitivity to Clustering Threshold**
As shown in Fig. 6b, performance remains stable for thresholds between 10%-35%, with optimal results at 30%. This "sweet spot" balances local pattern retention and global disruption, indicating our method is not sensitive to the specific choice of clustering threshold.
## **5. Generalization to Other Structures**
While our method is designed for ViTs, we test an **MLP-Mixer backbone** (patch-based architecture):
| Backbone | CropDisease | EuroSAT | ISIC | ChestX | **Average** |
| :------- | :---------- | :--------- | ---------- | ---------- | :---------- |
| Baseline | 85.12% | 78.34% | 36.45% | 22.31% | 55.56% |
| **Ours** | **87.45%** | **80.21%** | **40.12%** | **25.67%** | **58.36%** |
This demonstrates applicability to **other patch-based architectures**. However, traditional CNNs (**+0.7% average**) remain incompatible due to their lack of explicit tokenization and overlapped sliding-window convolutions.
------
We thank you for highlighting these critical points. Revised sections in the manuscript (marked in blue) address all concerns. Your feedback has significantly strengthened our work! | Summary: This article explores the impact of image token continuity on model performance in the context of cross-domain few-shot learning (CDFSL). The study demonstrates that disrupting image token continuity can reduce the gap between the source and target domains to some extent, thereby improving the model's generalization ability on the target domain. The authors propose a novel method that disrupts image token continuity in both the spatial and frequency domains, encouraging the model to better learn small-scale spatial patterns rather than relying on large-scale ones. The source-domain training includes two core steps, namely Warm-Up Spatial-Domain Disruption and Balanced Frequency-Domain Disruption. Experimental results show that the proposed method significantly improves model performance on four benchmark datasets, validating the effectiveness of the proposed method.
## Update After Rebuttal
I have checked the authors' rebuttal, and found most of my concerns have been solved, so I choose to maintain my score of Weak accept.
Claims And Evidence: In the submitted paper, the authors present several important claims primarily centered on the impact of image token continuity on cross-domain few-shot learning (CDFSL). These claims are supported by experiments and theoretical analysis in the text, and overall, they can be considered to have clear and convincing evidence.
I have just one small suggestion: The authors state that disrupting image token continuity significantly affects model performance in the source domain but has a relatively minor impact on the target domain. This phenomenon is one of the core findings of the paper. So could the authors provide the obtained classification values in Figure 1 (e.g., above the bar), which will allow the readers to more intuitively compare the results achieved in source and target domain?
Methods And Evaluation Criteria: The proposed methods and the used evaluation criteria are reasonable. The proposed method (disrupting token continuity) is remarkably simple, not requiring complex architectural designs, yet it effectively enhances the model's generalization ability in the target domain. In addition, I personally like the **balance operation** in the frequency-domain disruption step, whose motivation is clearly stated.
Theoretical Claims: There is no proof and theoretical claim included in the paper.
Experimental Designs Or Analyses: After checking the experimental part, I believe the experimental designs are soundness, and the results are able to indicate the effectiveness of the proposed method in improving model's generalization ability for solving cross-domain few-shot learning process.
However, I have the following concerns:
1. The authors only present the results on the target-domain (out-of-domain results), but in my own opinion, cross-domain learning should not significantly degrade the source-domain (in-domain) performance. So could the authors provide the classification accuracy on the pre-trained miniImageNet dataset?
2. Many recent cross-domain few-shot learning methods [1],[2],[3] have evaluated their performance on a larger and more complex dataset, namely Meta-dataset [4]. So could the authors provide more results on this dataset to show the generalization ability of their method on more diverse target domains?
3. Besides the classification accuracy, the model effeciency is also an important metric. Considering the proposed method involves a clustering process and a balanced sampling in the source-domain training phase, which may introduce additional computational overhead. So could the authors provide some discussions on the model effeciency?
4. The details of the clustering process is missing, the authors only state that "we set a similarity threshold of 0.3 for clustering image patches, where patches exceeding this threshold are fused into a single cluster." Which clustering algorithm is used？Could the authors provide the detailed steps of their clustering process or make appropriate citations of related works？
[1] Li W H, Liu X, Bilen H. Cross-domain few-shot learning with task-specific adapters[C]//Proceedings of the IEEE/CVF conference on computer vision and pattern recognition. 2022: 7161-7170.
[2] Guo Y, Du R, Dong Y, et al. Task-aware adaptive learning for cross-domain few-shot learning[C]//Proceedings of the IEEE/CVF International Conference on Computer Vision. 2023: 1590-1599.
[3] Perera R, Halgamuge S. Discriminative Sample-Guided and Parameter-Efficient Feature Space Adaptation for Cross-Domain Few-Shot Learning[C]//Proceedings of the IEEE/CVF Conference on Computer Vision and Pattern Recognition. 2024: 23794-23804.
[4] Triantafillou E, Zhu T, Dumoulin V, et al. Meta-dataset: A dataset of datasets for learning to learn from few examples[J]. arXiv preprint arXiv:1903.03096, 2019.
Supplementary Material: I have carefully checked all the parts of the supplementary material.
Relation To Broader Scientific Literature: One of the key findings of this paper is "disrupting image token continuity encourages the model to better learn small-scale spatial patterns rather than relying on large-scale ones, which can reduce the gap between the source and target domains". The similar concept is related to many previous works [1],[2],[3] in designing local descriptors for improving the model's generalization ability. So I believe this finding is validated by existing studies and is technically reasonable.
[1] Li W, Wang L, Xu J, et al. Revisiting local descriptor based image-to-class measure for few-shot learning[C]//Proceedings of the IEEE/CVF conference on computer vision and pattern recognition. 2019: 7260-7268.
[2] Wertheimer D, Tang L, Hariharan B. Few-shot classification with feature map reconstruction networks[C]//Proceedings of the IEEE/CVF conference on computer vision and pattern recognition. 2021: 8012-8021.
[3] Rong Y, Lu X, Sun Z, et al. Espt: A self-supervised episodic spatial pretext task for improving few-shot learning[C]//Proceedings of the AAAI Conference on Artificial Intelligence. 2023, 37(8): 9596-9605.
Essential References Not Discussed: The statement in the paper "larger patterns are always harder to transfer than smaller ones" is a similar concept to the pervious findings that "The low-level local visual features can be more easily transferred to the target domain than those high-level semantic features", so I believe some related works [1], [2], [3] should be appropriately cited and discussed.
[1] Li W, Wang L, Xu J, et al. Revisiting local descriptor based image-to-class measure for few-shot learning[C]//Proceedings of the IEEE/CVF conference on computer vision and pattern recognition. 2019: 7260-7268.
[2] Wertheimer D, Tang L, Hariharan B. Few-shot classification with feature map reconstruction networks[C]//Proceedings of the IEEE/CVF conference on computer vision and pattern recognition. 2021: 8012-8021.
[3] Rong Y, Lu X, Sun Z, et al. Espt: A self-supervised episodic spatial pretext task for improving few-shot learning[C]//Proceedings of the AAAI Conference on Artificial Intelligence. 2023, 37(8): 9596-9605.
Other Strengths And Weaknesses: Strengths:
1. This paper is well written and easy to follow, the experiments and ablation studies are sufficient to demonstrate the effectiveness of the proposed method.
2. The motivation of designing the model is clearly stated, and some empirical analysis are preformed to well-support their motivation.
Weaknesses:
Please refer to the questions in "Methods And Evaluation Criteria" and "Experimental Designs Or Analyses"
Other Comments Or Suggestions: The texts in some figures (e.g., Figure 5) are too small to read.
Questions For Authors: In my own opinion, disrupting the image token continuity can reduce the gap between the source and target domains is a nature observation, since such operation will destory the semantic information in the training data. In an extreme case, we can shullfe every pixel in input image, resulting in nearly random noise, leading to quite similar domain distributions of source and target, but losing almost all the useful information for model training. So solely measuring the CKA similarity between the two domains may not correctly reflect the domain generalization ability (for classification tasks). Could the authors provide more discussions on this? And also explain how to achieve a balance between the information loss and the domain generalization?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your thorough review and constructive feedback. Below are our detailed responses to your concerns:
## **1. Classification Values in Figure 1**
The numerical values in Fig.1 are summarized below:
| Disruption Method | Source Acc. | Target Acc. |
| :---------------------- | :---------- | :---------- |
| Original | 97.78 | 63.91 |
| Remove Pos. | 90.03 | 61.95 |
| Shuffle Patches | 87.25 | 62.25 |
| Shuffle Patch Amplitude | 68.13 | 59.80 |
| Shuffle Patch Phase | 67.41 | 59.78 |
## **2. Source-Domain Performance**
Ours achieves 66.76% on target (+2.85%), with 96.33% vs Baseline’s 97.78% on source.
## **3. Meta-Dataset Results**
Due to time and resource constraints, we first pretrain on our datasets (miniImagenet), and then we evaluate on parts of the Meta-Dataset under 5-way 5-shot settings:
| Dataset | Baseline | Ours (Δ) |
| :------------ | :------- | :---------------- |
| Birds | 94.23 | **96.51 (+2.28)** |
| FGVC-Aircraft | 70.37 | **70.43 (+0.06)** |
| Fungi | 61.03 | **62.98 (+1.95)** |
| VGG Flower | 89.64 | **89.72 (+0.08)** |
| Traffic Sign | 60.46 | **61.93 (+1.47)** |
| Ave. | 75.15 | **76.31(+1.16)** |
## **4. Computation cost**
Our method introduces **no additional trainable parameters**.
During training, the computational overhead (baseline: 126.42s vs. ours: 140.48s per epoch) stems from the clustering-based frequency disruption during training, which is acceptable compared with the gains in cross-domain performance. Moreover, some engineering trick, such as bipartite matching, can accelerate the clustering process, which we leave for future works.
During inference, since our method introduces no additional parameters, inference time matches the baseline exactly with no computational overhead.
## **5. Justification of Clustering**
### Algorithm Overview
### Step 1: Patchify & Standardize
**Image Segmentation**
Split an input image into non-overlapping patches:
$$
\mathbf{P} \in \mathbb{R}^{N \times p^2 \times C}
$$
**Normalization**
Standardize each patch to zero mean and unit variance:
$$
\mathbf{P}_i = \frac{\mathbf{P}_i - \mu_i}{\sigma_i + \epsilon},
$$
### Step 2: Similarity Computation
**Cosine Similarity Matrix**: Calculate cosine similarity between all neighbouring patch pairs:
$$
\mathbf{S}_{i,j} = \frac{\mathbf{P}_i \cdot \mathbf{P}_j}{\|\mathbf{P}_i\| \cdot \|\mathbf{P}_j\|}
$$
**Threshold Clustering**: Group patches into clusters beyond the threshold
$$
\text{Cluster}(i,j) = \begin{cases}
1 & \text{if } \mathbf{S}_{i,j} > \tau \newline 0 & \text{otherwise}
\end{cases}
$$
### Step 3: Cluster Merging
For each image:
- Initialize each image as a singleton cluster.
- Merge neighbouring patches i and j if beyond threshold
- Repeat until no merges occur.
## **6. References and Other Revisions**
Our method is consistent with [1-3] in that we hold the small patterns are easier to transfer than larger ones, but we differ in that (1) our method discusses the transferability of small patterns for ViT while [1-3] are originally designed for CNNs; (2) we provide a simple way to enhance the learning of small patterns by perturbing patches with no additional branches or losses.
We promise we will add discussions to the [1], [2], [3] and increase font sizes for Fig.5 Readability.
## **7. Balance Between Information Loss and Generalization**
To complement the CKA metric, we also use the MMD distance to measure the domain distance, with larger value indicating larger distance.
| Disruption Granularity | Source Acc. | Target Acc. | CKA | MMD |
| :--------------------- | :---------- | :---------- | :--- | :--- |
| 224×224 (pixel-level) | 21.3 | 20.5 | 0.03 | 0.61 |
| 112×112 | 23.68 | 22.95 | 0.03 | 0.57 |
| 56×56 | 36.33 | 31.09 | 0.04 | 0.56 |
| 28×28 | 59.45 | 56.97 | 0.05 | 0.54 |
| 16×16 | 64.82 | 61.05 | 0.22 | 0.43 |
| 14×14 | 87.25 | 62.25 | 0.22 | 0.41 |
| 8×8 | 94.39 | 62.26 | 0.15 | 0.47 |
| 7×7 | 94.93 | 62.26 | 0.14 | 0.47 |
| 4×4 | 96.49 | 62.26 | 0.12 | 0.49 |
| 2×2 | 97.38 | 62.99 | 0.08 | 0.50 |
| No disruption | 97.78 | 63.91 | 0.07 | 0.50 |
Moderate disruptions achieve optimal **MMD-CKA-accuracy balance**. Extreme disruptions harm both domains (low accuracy, high MMD, low CKA). This analysis confirms our method preserves **transferable semantics** while suppressing domain-specific structures, implying the default patch size is enough to achieve the balance. | Summary: This paper provides a novel perspective to improve the performance cross-domain few-shot learning (CDFSL). The key insight is that disrupting the continuity of image tokens in ViT will force the model to learn smaller patterns which are more easily transferred under extreme domain gaps. The observation is interesting and they design several experiments to prove the hypothesis. Based on this motivation, a new model is proposed for CDFSL by disrupting the continuity of image tokens with 2 stages, including a warm-up spatial-domain disruption and a balanced frequency-domain disruption. Experiments show good improvements over previous works.
Claims And Evidence: The idea is well-motivated and sufficient experiments have been designed to support the hypothesis.
Methods And Evaluation Criteria: The methods is cleverly designed, and model evaluation is standard for CDFSL
Theoretical Claims: N/A
Experimental Designs Or Analyses: (1) Well, the experiments show good improvement over the few-shot target domain. The author should also provide the performance on source domain for future reference. This is because the performance gains on the target domain come at the expense of performance on the source domain, as pointed by the author in the manuscript.
(2) Can the authors provide more visualization of disrupted images to better understand the impact of the various disruption methods, like Shuffle Patch Amplitude.
Supplementary Material: Yes, the supplementary material is well-organized and provides detailed comparisons with previous works.
Relation To Broader Scientific Literature: This work provides a new perspective to tackle cross-domain few-shot learning tasks (CDFSL), and investigates the influence of continuity of image tokens in ViT on cross-domain performance. This will potentially inspire more follow-ups works in this domain
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: N/A
Other Comments Or Suggestions: ================================
after reading the rebuttal, my concerns have been mostly addressed. I will keep my original score of recommending acceptance.
Questions For Authors: N/A
Ethical Review Concerns: N/A
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for your constructive feedback and valuable suggestions. Below are our responses to your comments:
## **1. Source domain performance**
As suggested, we have provided the performance on the source domain (miniImageNet) for reference.
| Model | Source Domain | Target Domain |
| -------- | ------------- | ------------- |
| Baseline | 97.78 | 63.91 |
| **Ours** | 96.33 | 66.76 |
Although there is a slight performance trade-off on the source domain, this aligns with our hypothesis: disrupting token continuity prioritizes learning smaller, transferable patterns over domain-specific holistic features. Crucially, the significant gains on **target domains** (e.g., +6.5% on ISIC) demonstrate the effectiveness of our approach for cross-domain adaptation.
## **2. Visualization of disrupted images**
An anonymous GitHub link ([https://anonymous.4open.science/r/More-visualization/visualizations.png]) with 16 visualized examples of disrupted images in three types is provided. These visualizations illustrate how our method breaks large-scale spatial patterns while preserving fine-grained, domain-agnostic features (e.g., textures, edges), which aligns with our motivation.
We appreciate your insightful feedback and hope these revisions address your concerns. Thank you again for your time and effort in reviewing our work! | null | null | null | null | null | null |
Towards Understanding Gradient Dynamics of the Sliced-Wasserstein Distance via Critical Point Analysis | Accept (poster) | Summary: The paper studies the existence and stability of critical points for semi-discrete sliced Wasserstein loss functions. In particular, they prove that there exist critical points which do not coincide with the global minimum, but also that any of those critical points is unstable under small perturbations. The authors include some numerical experiments for validating the theoretical results.
## After rebuttal
The authors addressed my comments and questions adequately. I keep my rating at "accept".
Claims And Evidence: The results are clear and underpinned by formal proofs.
In particular, the authors provide in Section 5 explicit examples of (Lagrangian) critical points located on lower-dimensional subspaces.
As an elementary tool, they characterize critical points of the semi-discrete sliced Wasserstein distance by the barycentric projection and prove that limits of discrete measures which are Lagrangian critical points are again Lagrangian critical point.
While I believe that the claims are interesting and the proofs are correct (even though I hadn't the opportunity to check them in detail), some limitations of the analysis could be emphasized more clearly in the introduction (please correct me if I got one of those limitations wrong):
- the examples and instability results from Section 5 are only in 2D
- the instability result only considers critical points of this specific form
Methods And Evaluation Criteria: The proof techniques are feasible.
Theoretical Claims: Due to the high review load, I was not able to check the proofs in detail. Based on my intuition, the claims of the statements are realistic.
Experimental Designs Or Analyses: Not applicable (the major claims are purely theoretical).
Supplementary Material: I did not look at the supplementary material.
Relation To Broader Scientific Literature: The geometry and properties of sliced Wasserstein losses was studied in several papers recently. As far as I know, the results on the non-existence of stable critical points are new and I consider them as a significant contribution.
Essential References Not Discussed: Generally, the literature part is comprehensive and well-organized. Some additional papers should/could be discussed:
Li and Moosmueller consider in the paper "Measure transfer via stochastic slicing and matching" a stochastic gradient descent on the sliced Wasserstein distance in the continuous case (where both measures have densities). It is stochastic in the sense that in each iteration one random direction is chosen. The authors show global convergence of this scheme, which also implies that there don't exist stable critical points.
There is a paper, that proposes a numerical scheme (Altekrueger et al. "Neural Wasserstein Gradient Flows for Discrepancies with Riesz Kernels" ICML 2023) to escape critical points introduced by searching for Lagrangian instead of Wasserstein critical points (i.e. in the regular tangent space instead of the geometric one see the field "strenghts and weaknesses" below).
Other Strengths And Weaknesses: The existence and characterization of critical points of the sliced Wasserstein distance is a problem which is of very high interest for the optimal transport community. Given that the paper makes significant progress in this direction, I definitely vote for acceptance. However, I have a couple of comments (not ordered by importance):
- From my perspective, and also in the view of machine learning applications, the most fundamental limitation of the paper is the absolute continuity assumption for the target measure. In particular, for most machine learning applications, the target measure is given by a dataset and therefore discrete. From a computational viewpoint it is usually impossible to compute the Laguerre tesselations which are required to compute the gradient in the semi-discrete case. Given the difficult nature of the problem, I would not expect the authors to consider a more general case as they have done. But I would expect them to discuss this limitation.
- Similarly as in the previous content, I would ask the authors to clarify in the abstract, that they study mostly the semi-discrete case of the SW objective.
- The authors extensively work with the different notions of critical points (Lagrangian and Wasserstein). These notions are directly related to the notions of geometric and regular tangent spaces of the Wasserstein space, which are contained in the book of Ambrosio, Gigli, Savare and were studied in more detail in the PhD thesis of Gigli. In these notations, Wasserstein critical points coincide with critical points with respect to the geometric tangent space and Lagrangian critical points coincide with critical points in the regular tangent space. For absolutely continuous measures both tangent spaces coincide. For the final version I would highly recommend the authors to work out this relations in a clean way.
- In particular, I would guess that the claim of Prop 4.3 is somehow related to the statement, that the barycentric projection is always contained in the regular tangent space (see the PhD thesis of Gigli Thm 4.15).
Reference for the PhD thesis of Gigli:
"On the geometry of the space of probability measures endowed with the quadratic optimal transport distance"
Other Comments Or Suggestions: see other fields
Questions For Authors: - Is it clear that the Wasserstein gradient flow starting at a discrete measure with a absolutely continuous target measure remains discrete? If not, can we relate the discrete setting to the continuous one? Maybe in the sense of mean-field limits?
- Maybe some "outlook-question": Is it sufficient to choose a random direction in a gradient descent scheme of the loss to escape the critical points (like in the paper of Li, Moosmueller mentioned above)?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for your positive feedback and relevant questions.
- Concerning the limitations of the analysis in Section 5 : it is indeed true that most of the examples we discuss are in 2D, with the exception of our Proposition 5.1(b) which gives some examples of critical points in arbitrary dimension $d > 1$. We will make the introduction clearer about the limitations of this section.
- Regarding the limitations of our assumption of absolute continuity of the target measure $\rho$, we refer to the discussion in our answer to reviewer BmZL. We will make sure to discuss this more extensively in a revised version of our article. In particular, note that one of the advantages of the Sliced-Wasserstein distance is precisely that the Laguerre tesselations are easy to compute in 1D. Indeed, if we assume that $\rho$ is discretized using $M$ points on the real line, then the Laguerre cells are computed by sorting the $M$ points, and the $i$-th Laguerre cell consists of the $i$-th chunk of $\frac{M}{N}$ points in the sorted list.
- Thank you for bringing these additional references to our attention. In particular, the paper by Li and Moosmueller appears to be extremely relevant to our analysis as their assumption (A3) essentially means that the target $\mu$ is the only barycentric Lagrangian critical point in the compact set $K_{\sigma_0,\mu}$ in which the iterates of their scheme remain. This indeed ties our theoretical analysis of Lagrangian critical points to considerations of convergence of practical schemes optimizing $SW$ objectives. On the other hand, as we understand it, the paper by Altekrüger at al considers perturbations by velocity plans, which is a larger class of perturbations than in our Lagrangian framework (as a velocity plan allows to split atoms, while a perturbation by a vector field $\xi \in L^2(\mu,\mathbb{R}^d)$ cannot)
- We agree that it would be fruitful to establish clear links between the different notions of critical points and the different types of tangent spaces investigated by Gigli et al. We will include a discussion on this in a revised version of the article, maybe in an appendix, since for the sake of clarity we have avoided to make use of the theory of gradient flows developed by Ambrosio, Gigli, Savaré in the main body of the article.
- Whether the Wasserstein gradient flow starting at a discrete measure with an absolutely continuous target measure remains discrete is an excellent question. For $W_2$ objectives, it is known that the gradient flow diffuses (this is necessary as the flow converges to $\rho$ exponentially in the $W_2$ metric, see for instance Proposition 3.1 in [1]. For the $SW$ objective, although we have not formally shown that the flow of the $SW$ "diffuses" discrete measures, we expect it to do so. This is in fact why we chose to work with the "Lagrangian" framework and Lagrangian critical points. Indeed, what we study is the behavior of the system $dX_t^i/dt = - \nabla F(X_t^i)$ where $F$ is defined in Section 3, which corresponds to the continuous time limit of the gradient descent algorithm implemented in practice. Therefore, considering perturbations by vector fields $\xi$, which can't "split" atoms, allows for a theory better suited to analyze how algorithms relying on particle dynamics work.
[1] Huang, Y. J., & Malik, Z. (2024). Generative Modeling by Minimizing the Wasserstein-2 Loss. arXiv preprint arXiv:2406.13619.
- We have not investigated specifically what happens when the gradient descent is performed using a very small number of directions, such as $L = 1$. However, in our numerical experiments, we did observe that it is extremely easy to escape critical points such as those described in Proposition 5.1 or Proposition 5.2, as long as some stochasticity is introduced in the choice of directions.
---
Rebuttal Comment 1.1:
Comment: Many thanks for your replies. As written in the original review, I vote for acceptance. One remark:
> In particular, note that one of the advantages of the Sliced-Wasserstein distance is precisely that the Laguerre tesselations are easy to compute in 1D. Indeed, if we assume that $\rho$ is discretized using $M$ points on the real line, then the Laguerre cells are computed by sorting the $M$ points, and the $i$-th Laguerre cell consists of the $i$-th chunk of $\frac{M}{N}$ points in the sorted list.
I would not consider your argument "we can compute the Laguerre tesselations b discretizing $\rho$" as valid here. There are some claims of the paper (such as Prop. 3.3) which are false without the assumption that the target measure has a bounded density (at least from my intuition, correct me if I am wrong). In particular, if I understand it correctly, the proposition says that the gradient descent "remains valid" (in the sense that it does not hit the diagonal) over the iterates. From my viewpoint it remains a bitter taste if such a result is shown for the absolute continuous case, but later on used in a discretized setting. And without discretizing $\rho$, the computation involves the integration of the density over the orthogonal complement, which is most likely intractable. However, for this paper I would consider it as ok to keep it as a loose end...
---
Reply to Comment 1.1.1:
Comment: Thank you for your reply. Regarding Proposition 3.3, the main advantage of assuming that the $\rho_\theta$ are densities bounded by some constant $\beta > 0$, is that we can control how close the critical points and the iterates of the gradient descent can be to the diagonal by a constant of the form $\frac{C(d)}{\beta N}$ with explicit dependence on $\beta, N$. Note, however, that the fact that the iterates do not hit the diagonal as long as the step size is small enough (the second bullet point of the Proposition) does not actually require this boundedness assumption to hold. In particular, it holds for a discretized $\rho$ (the gradient descent for such a $\rho$ being well-defined thanks to the extension of Proposition 3.1 discussed in our reply to reviewer BmZL).
Since we carried out our analysis in the semi-discrete setting, the additional assumption on $\rho$ didn't seem to be too costly an assumption so we wrote the entire Proposition under it, although we see now that in the light of the possible extensions of our other results to larger classes of $\rho$, our Proposition 3.3 now appears somewhat limited. We will thus also clarify these points in a revised version of our article. | Summary: This paper proposes a systematic study of the Sliced-Wasserstein functional in an optimization context where the target measure is continuous and the measure to optimize is discrete. The authors use the notion of ‘Lagrangian critical point’ of a functional defined over probability measures, since it aligns well with a particle based discretization of the objective functional. The authors then show a number of properties of this functional related to its well-behavedness when a gradient descent is used to optimize it. They also provide a characterization of the critical points of the objective (namely good behavior when the number of points in the optimized measure grows), and show that unstable critical points may exist both theoretically and experimentally. They finally show experimentally the convergence behavior of gradient descent on this functional.
## Update after rebuttal
Thanks to the authors for the answers to some of my questions. I would have appreciated discussion about the other few points raised in the rest of my review. Nevertheless, my opinion on the paper is largely positive and I maintain my score to 4.
Claims And Evidence: The paper is mostly theoretical. In terms of technical contributions, the authors characterize the points of non-differentiability of the objective, compute the gradient explicitly for Lp-norm ground costs on the subset where the functional is actually differentiable. They also show that a standard gradient descent typically remain away from the problematic points. They proceed to characterize critical points and show practical examples of unstable critical points in relatively simple settings. The experiments support the theoretical analysis of the critical points and are consistent with the expected behavior of gradient descent from the theoretical analysis.
Methods And Evaluation Criteria: This point does not really apply since the paper is mostly theoretical and the experiments are mostly confirming qualitatively some of the theoretical developments.
Theoretical Claims: I did not check thoroughly the proofs or the supplementary material. I find that a few claims in the introduction about the analysis of W_2^21 as the objective are a bit too depth in the cited works and would benefit a bit more exposure and recontextualization (I couldn’t find some of them in the related references), maybe as an additional appendix to avoid that the reader has to check many references to find the relevant theorems , or rederive things on their own.
Experimental Designs Or Analyses: I did check the soudness of the experiments, and have no particular complaints about them. It would have been interesting, experimentally at least, to give an idea about the behavior of other algorithms that are more likely to be used in practice, e.g. SGD or ADAM.
Supplementary Material: I briefly reviewed the contents of the supplementary but dit not go in depth.
Relation To Broader Scientific Literature: The paper raises interesting points about the optimization of optimal transport distances to a reference measure. A choice that is deliberate is that the authors choose to consider cases where the target measure is absolutely continuous but the measure to optimise is discrete, and discrete in the sense that it corresponds to a Lagrangian view on the measure, i.e. a collection of particles. This brings the paper close to the setting of semi-discrete optimal transport. This choice is different from what has already been treated in the literature, which adressed the cases where both the target and the variable admit densities, or are both discrete. The case chosen by the authors is indeed of practical interest, but corresponds to one possibility among several to optimize the SW distance. The choice of an absolutely continuous target is not suited to generative modeling (where the target is only known by discrete samples) but is suited for variational inference, which is of broad interest. The choice of a Lagrangian discretization of the measure is also of interest, but other choices such as parameterizing the density of the objective via a generative model could also have been discussed (which is something that is actually done in practice). More generally, this positioning within the existing literature could have been made more explicit. However, the findings in the considered case are interesting and insightful.
Essential References Not Discussed: I am not aware of such missing references for this paper.
Other Strengths And Weaknesses: Though one could find that the setting of the paper could be restrictive, the approach is original and the results interesting. Namely it shows the theoretical difficulties of the optimization of SW distance, and offers a few guarantees the GD is likely to be relatively well behaved and to avoid non differentiabilities, while converging in practice to a stable critical point. The theoretical results generally provide new insight on important questions about the optimization dynamics of SW.
However, I found the rest of the introcution to be particularly well written and provides a good introduction to optimization over measures in ML.
Other Comments Or Suggestions: It is a bit awkward to have the introductory material about OT and SW distances presented after an introduction that is clearly not understandable if one is not already familiar with that material. I suggest moving the last part of the introdution which already gets quite technical and discusses results that are not broadly known about critical points and the behavior of W2 in a specific section after the introduction. Maybe details could be provided in an additional appendix (citing relevant theorems in the literature for instance) to make the introductory material more self contained.
Questions For Authors: 1) Which parts of the theoretical analyses also hold in more general settings in terms of discretization choices for the measure to be optimized, or with other types of target measures (atomless, discrete, mixed…) ? This would make the contributions more impactful and more broadly applicable in practical scenarios.
2) Is there any hope in a second order analysis of the critical points, or somehow accessing the quality of the (stable) critical points towards which GD would converge ? An experiment showing possible bad behavior in practice would be interesting.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for your relevant remarks and questions.
- Regarding the possible generalizations of our results to other types of optimized or target measures (notably discrete ones), we refer to our answer to reviewer BmZL which addresses these points extensively. Note in particular that even though we assumed throughout the article that the target measure $\rho$ is a density, this is mostly because we started our investigation from the study of the semi-discrete setting, and most of our results can actually be proven when $\rho$ is simply assumed to be without atoms. This covers many types of measures often encountered in machine learning, such as measures supported on lower dimensional manifolds of $\mathbb{R}^d$.
- We did make some attempts at a second order analysis of the $SW$ distance, but it turned out to be a significantly difficult problem. Most of what we know concerns cases such as the ones in Proposition 5.2, where we have explicit expressions of the quantile functions and we can compute explicit Taylor expansions of the $SW$. Even the discrete case is difficult : while formally differentiating under the integral sign does indeed give the expression of $\nabla F$ (Proposition 3.1), we cannot obtain the Hessian of $F$ by this method, as formally differentiating again $\nabla F$ under the integral sign gives $\frac{1}{Nd} I_d$, which cannot be the actual Hessian of $F$ as $F$ is not convex (it is semiconcave by Proposition A.2). Furthermore, attempts to numerically approximate the Hessian were inconclusive, as the computed Hessian would converge to $\frac{1}{Nd} I_d$ when we increased precision or added more directions (which is to be expected from the analysis of Appendix B, which shows that the approximation of $SW$ using a fixed number $L$ of directions $\theta_1,\ldots,\theta_L$ has Hessian $\frac{1}{NL} \sum_l \theta_l \theta_l^T$ everywhere where it is defined, and this converges to $\frac{1}{Nd} I_d$ when $L \to \infty$ and the $\theta_l$ are choosed randomly). | Summary: The paper under consideration presents theoretical results regarding (Section 3) properties of discrete gradient descent w.r.t. SW functional (with absolute continuous target measure) and (Section 4) properties of (lagrangian) critical points of SW functional; (Section 5) provides some examples of lower-then-data dimension critical points different from the target functional and states that they (seems to be) unstable. The paper has an experimental section which illustrates some of the theoretical findings.
### Update after the rebuttal
I thank the authors for their response. I think, my current score is solid
Claims And Evidence: Ok.
But I have a question: (lines 369-371): “We can find $\xi$ such that …”. I do not understand how to find such $\xi$? May you give some examples of such $\xi$?
Methods And Evaluation Criteria: N/A: The paper is theoretical
Theoretical Claims: I checked only the general flow of the statements of the theorems/propositions in the main text. I didn’t check the proofs.
Experimental Designs Or Analyses: N/A: The paper is theoretical
Supplementary Material: Supplementary materials primarily contain proofs. Didn’t checked by me.
Relation To Broader Scientific Literature: Some related but not cited papers devoted to modelling Wasserstein gradient flows w.r.t KL-divergence:
[1] Large-scale Wasserstein Gradient Flows, NeurIPS’21
[2] Optimizing Functionals on the Space of Probabilities with Input Convex Neural Networks, TMLR
[3] Proximal Optimal Transport Modeling of Population Dynamics, AISTATS’22
Also, not that directly related, but also a good reference. This work study gradient flows in Sliced-Wasserstein space:
[1] Efficient Gradient Flows in Sliced-Wasserstein Space, TMLR
Essential References Not Discussed: Everything seems to be ok.
Other Strengths And Weaknesses: On the one hand (without delving into proofs), I find the manuscript more-or-less understandable and easy-to-read. It is definitely a strength for such a theoretical work with a lot of statements.
On the other hand, the main weakness of this paper is that it is almost fully theoretical. There is an experimental section, but it just presents some illustrations of some theoretical claims.
So, my opinion is as follows: as the theoretical work, the paper is good, but it has rather limited practicality. Maybe Proposition 3.2. is interesting to some extent.
Other Comments Or Suggestions: No
Questions For Authors: 1. Line 154, second line: “descent lemma” for this objective. What is “descent lemma”?
2. Minor, lines 367 an 371 - conflict of notations, $a$ used for different properties.
3. What does it mean: “alternating vector field $\xi$”? - lines 369-370 (second column)
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your positive remarks and comments. Regarding the questions you raised :
- We meant by "descent lemma" a result that guarantees that, provided some conditions on the initial point and the step size are satisfied, one step of the gradient descent will decrease the loss. In particular, it gives the maximal step-size for which descent is maximal and still guaranteed - this size is related to the inverse of the smoothness constant of the functional. Above this limit, descent is not guaranteed for an explicit time-discretization, as corroborated by our experiments (Figure 2) where step-size below $2Nd$ yields descent while step-size above $2Nd$ diverges. Hence, while this is a theoretical result, it gives practical hints for optimization of the $SW$ distance in practice since below $2Nd$ (which is a known quantity) the descent is guaranteed. The term "descent lemma" is a standard term in optimization, cf for instance [1]. We will revise the article to clarify this point.
[1] Bauschke, H. H., Bolte, J., & Teboulle, M. (2017). A descent lemma beyond Lipschitz gradient continuity: first-order methods revisited and applications. Mathematics of Operations Research.
- Regarding the meaning of "a suitable alternating vector field $\xi$" at lines 369-371 (second column), we meant was that (using the notations of Proposition 5.2) by approximating the perturbation $\mu^t$ by $(Id+t\xi)\mu$ where $\xi$ rapidly alternates between $\vec{n}$ and $-\vec{n}$ on the segment $S$, we may hope that $SW^2_2((Id+t\xi)\mu,\rho)$ will also have a maximum at $t = 0$. For example, for $S = [-1,1] \times \{0\}$, we may consider $\xi$ such that $\xi(x,0) = \vec{e_2}$ for $x \in [i/n,(i+1)/n)$ with $i$ even, and $\xi(x,0) = -\vec{e_2}$ for $x \in [i/n, (i+1)/n)$ with $i$ odd, with $n$ large. In the experiments shown in Figure 1, we use such alternating perturbations. We will make our formulation clearer in a revised version of the article.
We thank you for the additional references, which we will accordingly cite in a revised version of our article. | Summary: This paper investigates the properties of gradient flows for the Sliced-Wasserstein (SW) distance when used as an objective functional. It rigorously develops different notions of critical points—Eulerian, Wasserstein, and Lagrangian (including a barycentric variant)—and studies the convergence and stability properties of discrete gradient descent schemes that approximate the continuous Wasserstein gradient flow. The theoretical contributions include proving that, under suitable assumptions, the discrete (particle-based) critical points converge to a continuous critical point and that “bad” critical points (e.g., those supported on lower-dimensional structures) are unstable. Numerical experiments are provided to validate the theoretical findings and illustrate the behavior of gradient descent dynamics with various step sizes.
Claims And Evidence: The paper’s claims are well supported by a combination of rigorous theoretical analysis and simple synthetic numerical experiments. The main claims -- such as the equivalence of discrete and continuous notions of criticality (Proposition 4.3 and Theorem 4.4) and the instability of lower-dimensional critical points (Proposition 5.2) -- are backed by detailed proofs in the supplementary material and supported by illustrative experiments. However, some claims rely on technical assumptions (e.g., compact support, absence of atoms) that may limit generality, and additional discussion on these assumptions would be beneficial.
Methods And Evaluation Criteria: The methodology is sound: the paper formulates the SW objective within the Wasserstein space $P_2(\mathbb R^d)$ and develops discrete gradient descent dynamics on an empirical measure. This approach is appropriate for bridging continuous optimal transport theory with practical particle methods. Empirical evaluation is conducted through of numerical experiments that give the readers a better sense of validation of the theoretical analysis.
Theoretical Claims: I carefully checked several key proofs (notably those for Proposition 3.1, Proposition 4.3, and Theorem 4.4). The derivations appear to be mathematically rigorous, and the use of techniques from optimal transport theory (e.g., Wasserstein geometry, barycentric projections) is correct.
Experimental Designs Or Analyses: The experiments are designed to illustrate both the convergence behavior of gradient descent (with respect to various step sizes) and the instability of undesired critical points. The numerical analyses (e.g., the plots in Figures 1 and 2) support the theoretical insights. One concern is the limited range of experiments only on synthetic data, but given the theoretical nature of this paper, this is not a major issue.
Supplementary Material: I reviewed part of the supplementary material that includes detailed proofs of the main theoretical results.
Relation To Broader Scientific Literature: The paper is well situated within the literature on optimal transport, Wasserstein gradient flows, and generative modeling using SW distances. It builds on foundational works in the field (e.g., by Ambrosio et al., Villani, and Bonnotte) and connects with recent studies on particle methods and generative models (e.g., Merigot et al., 2021; Liutkus et al., 2019).
Essential References Not Discussed: n/a
Other Strengths And Weaknesses: The paper provides a deep and rigorous theoretical analysis of the SW gradient flow, filling a gap in the literature regarding the convergence properties and stability of critical points.
Other Comments Or Suggestions: n/a
Questions For Authors: - How do the results extend (or fail to extend) if the target measure $\rho$ or the approximating measures $\mu$ are not atomless? Could you comment on potential generalizations or necessary modifications of your framework in such cases?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for your positive remarks and relevant questions. Even though we restricted our theoretical analysis of the $SW$ distance to absolutely continuous target measures (and in Section 3 to discrete approximating candidates), this was mostly for the sake of simplicity, and it is indeed possible to extend many of our results to larger classes of measures, often (but not always) without requiring significant adaptation of the proofs. For example :
- Direct extensions :
- In section 4, the notion of barycentric Lagrangian critical point for $SW^2_2(\cdot,\rho)$ can be defined for arbitrary measures $\mu, \rho \in P_2(R^d)$, as the 1D optimal transport plans $\gamma_\theta$ are always uniquely defined.
- If we replace the assumption that $\rho$ is absolutely continuous by the assumption that it has no atoms, then Propositions 3.1, 3.2, 4.3, 4.6, Theorem 4.4 and Corollary 4.7 remain true.
- Minor extensions :
- When $\rho$ is an uniform point cloud $\rho = \frac 1N \sum_{i=1}^N \delta_{Y_i}$ (with the same $N$ as in $\mu$), it should be possible to prove analogues of Propositions 3.1 and 3.2, replacing the barycenters $b_{\theta,i}$ by the reordered projections of the points $Y_i$ in the statements of the propositions (in fact, Theorem 1 in Bonneel et al. 2015 is the analogue of our Proposition 3.1 with $p=2$).
- Proposition 3.3 remains true under the weaker assumption (A1) on $\rho$ that there exists $\beta > 0$ and $\Theta \subset \mathbb{S}^{d-1}$ with $\mathcal{H}^{d-1}(\Theta) > 0$ such that $\rho_\theta$ is a density bounded from above by $\beta$ for every $\theta \in \Theta$
- The proof of Proposition 5.2 should be adaptable to the case where we only assume of $\rho$ that it has no atoms, and $\exists b > 0$ and a neighborhood $U \subset \mathbb{S}^1$ of $\vec{n}$ such that $\forall \theta \in U$, $\rho_\theta$ is a density bounded from above by $b$ - let's call this assumption (A2).
- Significant extensions :
- The proofs of Propositions 3.1 and 3.2 should be adaptable to arbitrary $\rho$. The main difficulty would be that the Power cells $V_{\theta,i}$ are not well-defined. We would instead have to work with a decomposition $\rho_\theta = \sum_i \rho_{\theta,i}$ where $\rho_{\theta,i}$ is coupled to $\langle X_{\sigma_\theta(i)}, \theta \rangle$ by the optimal 1D transport plan (when $\rho_\theta$ has no atoms, we have $\rho_{\theta,i} = \rho_{\theta|V_{\theta,i}}$)
- Theorem 4.4 also holds under the assumption that $\rho$ has no atoms and that the set of atoms of $\mu$ is closed, but proving this requires more sophisticated methods. The sketch of the proof is roughly the following : the beginning of the proof is the same as in the article. We cannot use Proposition 4.6(c) as $\mu$ may have atoms, but we can prove that Equation (152) still holds is $\xi$ is assumed to cancel at the atoms of $\mu$, and this allows to prove $v_\mu = 0$ $\mu$-ae on the complementary of the set of atoms of $\mu$. Then, by considering perturbations of each individual atom of $\mu$, we show that $v_\mu$ also cancels at the atoms. Since this assumption on $\mu$ seems unnatural and its proof is more complex, we chose to state the theorem in the article under the stronger but more natural assumption that $\mu$ is without atoms.
Moreover, regarding the limitations of our analysis :
- While our original assumption of absolute continuity of $\rho$ does limit the applicability of our results, the extensions we discussed to weaker assumptions on $\rho$ such as atomlessness, (A1) or (A2), allow us to cover a much wider range of target measures, including many types of singular measures which arise in machine learning, such as densities supported on a lower dimensional manifold (for example, $\rho = \frac 12 \mathcal{H}^1_{[-1,1]\times\{0\}} \in \mathcal{P}_2(\mathbb{R}^2)$ has no atoms, and satisfies (A1) and (A2) for $\vec{n} = \vec{e}_2$)
- The assumption of compact support of $\mu, \rho$, which we some of our results require, seem harder to relax. Indeed, it is needed in Proposition 4.6(c) to obtain regularity properties of the Kantorovich potentials, which we use to prove the differentiability, while the proof of Theorem 4.4 makes use of the fact that in a compact space, $SW_2$ and $W_2$ are equivalent distances metrizing the topology of weak convergence.
- Finally, the fact that our numerical experiments, in which the target measures were discretized, exhibit the behaviors of convergence and instability that our theoretical analysis highlighted, suggests that our results should still be relevant in the cases where the target measure $\rho$ is approximated by a discrete measure.
We will add in a revised version of our article a discussion of the generalizability of our results and of their limitations. | null | null | null | null | null | null |
An Efficient Private GPT Never Autoregressively Decodes | Accept (poster) | Summary: The authors mainly aim to improve the efficiency of private inference for autoregressive language models. First, they observe that the decoding time is relatively insensitive to the input length. Next, they adapt speculative decoding to the private inference setting. The authors employ a small public model as a drafter and a larger private model as a verifier. A key technical challenge lies in the verifier's rejection rule, which typically requires computationally expensive reciprocal operations. To address this, the authors propose a novel protocol that allows rejection of draft tokens. Experimental results demonstrate improvements in decoding speed, achieving 2.1× to 6.0× efficiency gains.
## update after rebuttal
I appreciate the authors for commenting on the remaining concern. Using a smaller public model may be partly due to resource constraints, but the main reason is the copyright for larger models. If a public model could match the performance of a private one, there would be no need to use private models. Therefore, in realistic scenarios, public models are inherently expected to underperform compared to private models. As a result, for complex tasks like reasoning, the accuracy gap is likely to remain significant. While the proposed method may offer some speedup in such tasks, the overall impact would likely be limited. For this reason, I believe the broad effect of the work is not substantial enough and will maintain my score as weak accept.
Claims And Evidence: * They claim that the decoding time is relatively insensitive to the input length based on Figure 1 and Figure 2. However, for softmax, their computation cost increases drastically as the input length increases in Figure 1. Thus, if the input length is over 64 or 128, the input length might be one of the major bottlenecks. The comparison when input length is 64 would make the claim stronger.
* The efficiency of the proposed protocol for rejection rule is shown in Table 2.
Methods And Evaluation Criteria: * Efficiency evaluation is well presented in Figure 5.
* The paper does not report model performance (e.g., accuracy or perplexity), focusing solely on speed improvements. While speculative decoding with hard matching theoretically preserves model outputs, the use of soft matching may introduce performance degradation. An empirical analysis of how soft matching impacts accuracy or output quality would be valuable for practitioners, especially to understand the trade-off between efficiency and performance.
Theoretical Claims: There are no theoretical claims.
Experimental Designs Or Analyses: See Evaluation Criteria.
Supplementary Material: There are no supplementary materials.
Relation To Broader Scientific Literature: * If performance is preserved, the paper would be significant, as it demonstrates substantial speedups by leveraging public drafter models for private inference.
Essential References Not Discussed: None
Other Strengths And Weaknesses: * In practical deployments, the drafter is constrained to be a small LLM. However, small models typically lack the capacity to generalize across diverse tasks and require task-specific alignment. Obtaining aligned drafters for every possible task is impractical, and without proper alignment, the effectiveness of speculative decoding diminishes. This limitation is evident in Table 1, where the rejection rate increases substantially when the drafter is not aligned with the target task.
Other Comments Or Suggestions: None.
Questions For Authors: See the above sections.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for the positive feedback and appreciation of our work. We appreciate your insights and would like to provide more clarification.
# Question 1: Figure 1&2 claim that the decoding time is relatively insensitive to the input length. However, for softmax, the cost increases drastically as the input length increases. Thus, if the input length is over 64 or 128, its time might be one of the major bottlenecks.
We appreciate the reviewer's rigorous feedback and will enhance our demonstration to clarify this claim. In standard decoding, the input length is fixed at one. Our method's selection of the input (or draft) length should keep the latency insensitivity. Experiments show that using too many draft tokens (e.g., 64 or 128) indeed increases latency, so we avoid such large numbers. Instead, we focus on a reasonable range, like 1 to 16 draft tokens in Figure 1, or 4, 8, and 16 in Figure 5.
# Question 2: If performance (perplexity) is preserved, the paper would be significant, as it demonstrates substantial speedups by leveraging public drafter models for private inference.
We would like to clarify that soft matching through speculative sampling theoretically preserves the accuracy performance (e.g. perplexity) of the private model [1], as we mentioned in Line 239. It guarantees that tokens sampled from the distributions $p(x)$ and $q(x)$ using speculative sampling are distributed identically to those sampled from $p(x)$ alone. This implies that the probability of sampling any token $\hat{x}$ from both $p(x)$ and $q(x)$ is precisely $p(\hat{x})$. As a result, the expected perplexity of the sampled tokens with respect to some oracle baseline remains unchanged, thereby maintaining the performance concerned by the reviewer.
We provide a brief proof of why the tokens sampled by two types of sampling algorithm follow an identical distribution; further details can be found in Appendix A of [1]. The probability of sampling a token $\hat{x}$ using speculative sampling is:
$$
P\\{x = \hat{x}\\} = P\\{x = \hat{x} | acc\\} \cdot P\\{acc\\} + P\\{x = \hat{x} | rej\\} \cdot P\\{rej\\}
$$
- When the proposed token is accepted: The public model proposes $\hat{x}$ with probability $P\\{x = \hat{x} | acc\\} = q(\hat{x})$. The acceptance probability for $\hat{x}$ is $P\\{acc\\} = \min\left(1, \frac{p(\hat{x})}{q(\hat{x})}\right)$.
- When the proposed token is rejected: The public model may propose any token, which is then rejected. The rejection probability is $P\\{rej\\} = \sum_{x'} q(x') \cdot \left(1 - \min\left(1, \frac{p(x')}{q(x')}\right)\right) = 1 - \sum_{x'} \min(q(x'), p(x'))$. The token is re-sampled from the adjusted distribution with $P\\{x = \hat{x} | rej\\} = norm(\max(0, p(\hat{x}) - q(\hat{x})))$.
Substituting these into the equation, we obtain:
$$
P\\{x = \hat{x}\\} = q(\hat{x}) \cdot \min\left(1, \frac{p(\hat{x})}{q(\hat{x})}\right) + \left(1 - \sum_{x'} \min(q(x'), p(x'))\right) \cdot norm(\max(0, p(\hat{x}) - q(\hat{x}))) = p(\hat{x})
$$
This confirms that the speculative sampling process preserves the original distribution $p(x)$, as desired. If you have any further questions, please feel free to let us know.
[1] Fast inference from transformers via speculative decoding. ICML 2023
# Question 3: The paper does not report model performance (e.g., perplexity). An empirical analysis of how soft matching degrades output quality would be valuable for practitioners.
As discussed in Question 2, there is no inherent trade-off between efficiency and accuracy performance when adopting the soft maching. The soft matching theoretically maintains the accuracy performance, i.e. same expected perplexity towards some oracle output. This theoretical guarantee is a key strength of our method, allowing speed improvements without concerning the output quality.
# Question 4: In practice, drafter models are limited to small LLMs, which often lack generalization across tasks and need task-specific alignment. Aligning drafters for every task is impractical, and without proper alignment, the efficiency declines.
In our experiments, even using non-aligned small models, we achieve an average acceptance rate of 40% for the different-series model and an average of 65% for the same-series model, which already presents approximately 1.6X and 3X average speedup.
The alignment further increases the benefits to 2X and 5X average speedup. Notably, the alignment is much easier and more practical than traditional fine-tuning tasks that prioritize accuracy as the primary objective. As illustrated in Figure 4, the alignment requires only a small public GPT, a minimal aligning dataset, and can be efficiently tuned on a small GPU.
Furthermore, the effectiveness of our approach is expected to increase as client-side computational capabilities continue to advance. Such advancements enable the leveraging of larger and more powerful public models, thereby enhancing the acceptance ratio as Table 1 indicates.
---
Rebuttal Comment 1.1:
Comment: I appreciate the detailed response. Most of my concerns have been addressed. However, given the inherent limitations of small LLMs, the potential gains in broader applications such as reasoning remain limited. As a result, I am maintaining my score as a weak accept.
---
Reply to Comment 1.1.1:
Comment: We are glad that previous response addressed most of your concerns. Regarding your remaining question about limited capabilities of small public models, besides the evidence in prievious response, we offer a further detailed explanation about the choice of public models. In fact, in the secure inference scenario considered in this paper, clients can freely choose larger public models, which is precisely where the potential of our method lies.
This flexibility in choosing public models arises from the inherent orders-of-magnitude latency gap between plaintext and secure inference [1,2], as we also explained in Line 220. For models of the same size and running in the same environment, secure inference is typically hundreds of times slower than plaintext inference. As a result, in our POST approach, compared to the major bottleneck of secure verification, the time spent on public decoding is a negligible part, as the following Table shows.
**Table 1: The latencies for the public model autoregressively generate 8 tokens, and the latencies for the private model verify 8 tokens in one forward pass. All latencies use the same CPU environments. We use seconds to measure the latency.**
||Public decoding|Secure verification (3000Mbps, 1ms)|Secure verification (1000Mbps, 10ms)|
|-|-|-|-|
|GPT-2|0.14|27.6|67.2|
|Vicuna-7B|3.36|320|480|
|FLAN-T5-XL|1.82|132|238|
|T5-efficient-XL|1.94|148|243|
According to the above results, even if clients select a public model of the same size as the private model, the time spent on public decoding remains negligible in the end-to-end delay, while a higher acceptance ratio (speedup) is expected to be achieved. Therefore, the flexibility to choose larger models shows promising acceleration potential of our method.
Additionally, a potentially overlooked aspect is that clients capable of performing secure inference typically have the resources to utilize larger LMs than those minimal LMs in our paper. As a price of the privacy protection, secure inference [3,4,5] requires clients to possess some computational and communication capabilities (which aligns with the trend of increasingly powerful client devices, such as those equipped with GPUs). Such demand is due to the widely used secure inference protocols that often require clients to perform computations and communications comparable to those of the server. For example, the computational and communication between two parties are nearly symmetric in MPC protocols, and clients perform heavy encryption and decryption in HE multiplication.
[1] SecretFlow-SPU: A performant and User-Friendly framework for Privacy-Preserving machine learning, ATC 2023
[2] https://github.com/mpc-msri/EzPC, 2024
[3] Bumblebee: Secure two-party inference framework for large transformers, NDSS 2025
[4] Nimbus: Secure and efficient two-party inference for transformers, Neurips 2024
[5] Bolt: Privacy-preserving, accurate and efficient inference for transformers, S&P 2024 | Summary: The paper proposes an efficient method for secure inference in generative pre-trained transformer (GPT) models by replacing the traditional autoregressive secure decoding process with a Public decOding and Secure verificaTion (POST) approach. The POST method leverages publicly available GPT models to generate multiple candidate tokens in plaintext, which are then verified securely against a private model. The authors optimize this process through speculative sampling and knowledge distillation, significantly improving token acceptance rates. Their approach achieves between 2.1× and 6.0× speedups compared to traditional secure decoding, without compromising privacy or output quality.
Claims And Evidence: The authors provide convincing evidence supporting their claims of increased inference efficiency and maintained privacy through extensive experimental validation. The speedup claims (2.1× to 6.0×) are backed by thorough performance measurements under different model pairings (Vicuna-7B/LLaMA, FLAN-T5-XL/T5-efficient, FLAN-T5-XL/FLAN-T5-small&base) and network scenarios (LAN/WAN).
Methods And Evaluation Criteria: The proposed methods and evaluation criteria are appropriate and justified. The authors select a range of representative models (small and large GPT variants) and tasks (text-to-SQL, mathematical reasoning, code generation, finance QA) to demonstrate the broad applicability and effectiveness of their method. The benchmark datasets are standard and widely used, making the evaluation meaningful.
Theoretical Claims: The theoretical claims (such as those related to speculative sampling) have been reviewed. The provided protocol for speculative sampling is logically sound, clearly described, and addresses critical performance bottlenecks inherent in secure computation.
Experimental Designs Or Analyses: The experimental designs are sound and rigorous. The authors provide detailed latency analyses, clearly attributing observed performance improvements to their methodological innovations. The breakdown of latency components (communication, computation, transmission) further reinforces the validity of their findings.
Supplementary Material: I have not checked it.
Relation To Broader Scientific Literature: It clearly outlines differences from related approaches, such as BumbleBee, Nimbus, and other cryptographic optimizations, emphasizing the novelty of leveraging public GPT models for secure verification.
Essential References Not Discussed: The references discussed appear comprehensive.
Other Strengths And Weaknesses: Strengths:
- Clearly articulated motivation and innovative use of public models for secure verification.
- Strong experimental validation demonstrating significant practical improvements.
- Practical protocol optimization for cryptographic operations enhancing real-world applicability.
Weaknesses:
- The approach relies on the acceptance ratio achieved by the public model; if the alignment is suboptimal, the speedup may diminish.
- The complexity of the secure verification protocol may present implementation challenges in real-world deployments.
- Additional exploration of scalability with larger vocabulary sizes or more diverse model architectures would be beneficial.
Other Comments Or Suggestions: NA
Questions For Authors: NA
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for the reviewer's appreciation of our efforts and valuable feedback on our paper. We address the main concerns as follows.
# Question 1: The approach relies on the acceptance ratio achieved by the public model; if the alignment is suboptimal, the speedup may diminish.
Our experiments demonstrate a consistent acceptance ratio and speedup across three pairs of models and four tasks. Even under suboptimal conditions, such as utilizing a small, irrelevant public model, the alignment achieves acceptance ratios of 50%–70% (corresponding to a speedup of approximately 2X–3.3X). When employing a small model from the same series, the acceptance ratios improve to 75%–82% (corresponding to a speedup of around 4X–5.5X).
Furthermore, as discussed in Line 293 and Line 370, the acceptance ratio has greater potential than what the experimental results suggest. For instance, our experiments only adopt the 68M or 160M GPT models as the public model. As client-side computational capabilities continue to advance, it is anticipated that the acceptance ratio will increase through the utilization of larger and more powerful public models. Additionally, our experiments only use a very small alignment dataset and do not involve extensive hyper-parameter searching. A more thorough alignment process is expected to yield higher acceptance ratios, particularly if the server provides a more appropriately aligned public model, benefiting from its insights into the training datasets and access to enhanced computational resources.
# Question 2: The complexity of the secure verification protocol may present implementation challenges in real-world deployments.
The proposed approach reduces the execution time of secure inference by a factor of 2X to 6X, while preserving the same levels of security and accuracy. Although this introduces some additional implementation complexity, we are willing to mitigate this challenge by open-sourcing our implementation.
# Question 3: Additional exploration of scalability with larger vocabulary sizes or more diverse model architectures would be beneficial.
Thank you for your advice on the scalability analysis. Currently, our experiment includes three pairs of model architectures and four tasks. We focus on these aspects as they are most relevant to the proposed approach. Regarding vocabulary size, we utilize a vocabulary consisting of approximately 30,000 tokens, which provides comprehensive token coverage and is commonly adopted by popular LLMs. The existing experiments are sufficiently convincing to demonstrate the effectiveness of our method, but we are willing to include additional experiments to further justify the scalability concerning vocabulary size and model architectures in our next version. | Summary: This paper focus on secure inference on GPT, and presents POST, which contains (1) a private sampling protocol optimized for cryptographic primitives and (2) model alignment using knowledge distillation to speedup the secure inference. Experiments demonstrate speedup compared to standard decoding across three pairs of public-private models and different network conditions.
Claims And Evidence: 1. In section 4.2, the author claims that the division is refactored into multiplication (line 267). It is unclear why this can be done. The proof in Appendix D lacks showing the range of p(x)/q(x).
2. In this paper, the author introduces the alignment of public model and private model. If the alignment dataset closely resembles the private dataset (line 303-304), how to evaluate the potential privacy leakage? No evidence is provided towards this.
Methods And Evaluation Criteria: The proposed methods and evaluation make sense.
Theoretical Claims: In Appendix D, the authors try to prove the division can be refactored as multiplication. However, it is not stated what is the range of p(x)/q(x). Therefore, I am not sure whether the claim is correctly proved.
Experimental Designs Or Analyses: 1. This paper lacks experimental comparison with prior works [1-2] on secure GPT inference. Despite that the author claims the proposed work is orthogonal to prior works, it is worth to show at least one combination to verify this claim.
[1] Hou, X., Liu, J., Li, J., Li, Y., Lu, W.-j., Hong, C., and Ren, K. Ciphergpt: Secure two-party gpt inference. Cryptology ePrint Archive, 2023.
[2] Gupta, K., Jawalkar, N., Mukherjee, A., Chandran, N., Gupta, D., Panwar, A., and Sharma, R. Sigma: secure gpt inference with function secret sharing. Cryptology ePrint Archive, 2023.
Supplementary Material: I read all supplementary material.
Relation To Broader Scientific Literature: The proposed POST is in parallel with prior methods [1-3] in the field of secure inference of GPT, which is a strength of this paper. This paper also discussed recent secure inference on GPT in Appendix B.
[1] Hao, M., Li, H., Chen, H., Xing, P., Xu, G., and Zhang, T. Iron: Private inference on transformers. Advances in Neural Information Processing Systems, 35:15718–15731, 2022.
[2] Zeng, W., Li, M., Xiong, W., Tong, T., Lu, W.-j., Tan, J., Wang, R., and Huang, R. Mpcvit: Searching for accurate and efficient mpc-friendly vision transformer with heterogeneous attention. In Proceedings of the IEEE/CVF International Conference on Computer Vision, pp. 5052–5063, 2023.
[3] Lu, W.-j., Huang, Z., Gu, Z., Li, J., Liu, J., Ren, K., Hong, C., Wei, T., and Chen, W. Bumblebee: Secure two-party inference framework for large transformers. Cryptology ePrint Archive, 2023.
Essential References Not Discussed: No.
Other Strengths And Weaknesses: Strength: The motivation section is well-written and intriguing. Showing latency breakdown in terms of one-way delay, transmission and computation is critical to the community.
Other Comments Or Suggestions: A minor comment about clarity: Figure 3 is not clear enough for illustrating the proposed methods of this work. There is no information about where the secure inference happens, no input to the private model and public model, not showing 'draft tokens', 'bonus token'. I suggest the authors to enrich Figure 3 and present more details. As the authors claim the proposed POST is an orthogonal approach to prior works (in line 33), it is important to make the framework clearly visualized. Current Figure 3 does not help understand the paper.
Questions For Authors: In this paper, the author introduces the alignment of public model and private model. If the alignment dataset closely resembles the private dataset (line 303-304), how to show/evaluate/quantify whether there is privacy leakage?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your thorough examination and thoughtful feedback on our paper. We address the main concerns as follows.
# Question 1: In Appendix D, the authors try to prove the division can be refactored as multiplication. However, it is not stated what is the range of p(x)/q(x). Therefore, I am not sure whether the claim is correctly proved.
We provide an explanation here and will include more detailed explanations for the derivation in Appendix D to ensure it is easy to follow.
Equation (6) derives the equivalent condition for determining whether a token should be rejected. We assume the reviewer’s concerns is about the elimination of the $min()$ function in the third line $r \geq \min \left(1, \frac{p(\hat{x})}{q(\hat{x})}\right)$. The equivalence of the conditions in line 3 and line 4 is established through two cases based on the range of $\frac{p(\hat{x})}{q(\hat{x})}$.
- $\frac{p(\hat{x})}{q(\hat{x})} \in [0,1]$: The $min()$ function can be directly removed, as stated in Equation (6).
- $\frac{p(\hat{x})}{q(\hat{x})} \in (1,\infty)$: The third line simplifies to $r>1$. Since $r$ is drawn from a uniform distribution over the interval $[0,1]$, the conditions in both line 3 and line 4 are never satisfied. Consequently, the equivalence remains valid.
If you have any further questions, please feel free to let us know.
# Question 2: If the alignment dataset closely resembles the private dataset (line 303-304), how to evaluate the potential privacy leakage?
Line 303 discusses the case in which the server provides the aligned public model. We assume the concern is about the open-source aligned public model incurring potential privacy leakage of the alignment dataset. This issue is independent of this work and widely exists. For instance, the base model used for alignment, open-source smaller versions of private models, can similarly expose privacy risks related to the pre-training dataset (private dataset). Such kind of issue can be resolved using the well-established framework known as differential privacy [1]. Differential privacy preserves the utility of the training data while anonymizing it with metrics that quantify the upper bound of privacy leakage. In our alignment scenario, if the alignment data resembles the private dataset (for instance, including private information), the direct use of the original dataset for training is avoided. Instead, a sanitized aligning dataset is generated [2,3], or differential privacy is applied during the gradient descent process [4].
Moreover, the potential for privacy leakage in our alignment is more manageable compared to the potential leakage of pre-training datasets from open-source small models. This is because the alignment's objective is to let the public model mimic the output distribution of easily predicted tokens. This makes the requirements on the alignment dataset much smaller than traditional training: a very small number of data is sufficient (Figure 4), and alignment on simple tokens rarely involves sensitive information.
To avoid any privacy leakage, a cautious server can choose to use relevant publicly available datasets or not provide the alignment. This may result in slightly slower performance, but thanks to our speculative sampling protocol, even non-aligned public models still achieve a 1.5X to 5X speedup.
[1] The Algorithmic Foundations of Differential Privacy, Foundations and Trends in Theoretical Computer Science 2014
[2] Dp-opt: Make large language model your privacy-preserving prompt engineer, ICLR 2024
[3] Privacy-Preserving In-Context Learning with Differentially Private Few-Shot Generation, ICLR 2024
[4] Deep learning with differential privacy, CCS 2016
# Question 3: Lack experimental comparison with prior works (such as CipherGPT and SIGMA) on secure GPT inference. Despite that the author claims the proposed work is orthogonal to prior works, it is worth to show at least one combination to verify this claim.
Sorry for any confusion regarding our experimental setup. In fact, the speedup in Figure 5 is the comparison with the latest work, both with and without the integration of our method. The baselines are the SOTA 2PC secure inference works for Transformer, as detailed in Line 366, including the linear layer protocol from Nimbus [1] and the non-linear layer protocol from BumbleBee [2]. We will further clarify this in the paper.
[1] Bumblebee: Secure two-party inference framework for large transformers, NDSS 2025
[2] Nimbus: Secure and efficient two-party inference for transformers, Neurips 2024
# Question 4: Improve Figure 3 for better clarity.
Thank you for the valuable suggestion. We will enhance Figure 3 to improve its clarity. For example, we will highlight the workflow of the secure inference process, emphasizing the distinctions between our approach and prior works. We will also illustrate the appearance of the "draft token" and "bonus token" throughout the process to provide a clearer understanding. | Summary: To accelerate privacy-preserving inference, the authors propose a Public Decoding and Secure verificaTion (POST) approach that utilizes public GPT models, based on the observation that securely decoding one token vs. multiple tokens takes a similar latency.
Since the efficiency of secure decoding depends on the acceptance rate of tokens proposed by the public model, they purpose two optimizations 1) a private sampling protocol specific to crypto primitives 2) model alignment using knowledge distillation. The optimized approach remains the same privacy level and generation quality while improving up to 6x speed up across different public-private model pairs.
Claims And Evidence: page 2 col 1 line 90-92: “This approach broadly applies across different cryptographic protocols and GPT models, where we observe similar insensitivity.“
In the paper, the authors clarify how the approach is applied to versatile GPT models, but it’s not clear to me how it can be applied to different cryptographic protocols. Specifically, in the abstract, the authors mention that the speculative sampling protocol is specific to crypto primitives.
Methods And Evaluation Criteria: I really enjoy reading the motivation section. The two observations clearly motivate the later-on approaches to optimize the decoding phase in the generation process.
Theoretical Claims: * There is the proof for the correctness of the sampling protocol (in the appendix although) and also security analysis for privately reject draft tokens and knowledge distillation.
* page 6 col 1 line 292: it appears that the complexity remains substantial since 2^l represents the size of the field. Could the author clarify why this level of complexity is considered acceptable?
Experimental Designs Or Analyses: * The experimental design effectively addresses my initial questions from the 'methods' section, specifically regarding the runtime of the knowledge distillation process and the accuracy improvement post-alignment.
* Could the author elaborate on the choice of the three pairs of public and private models? I understand the inclusion of pairs from different series (the first two pairs) and a pair from the same series (the third pair). However, what is the underlying rationale for selecting two pairs from different series?
* What dataset was used for the knowledge distillation? I am curious whether the acceptance rate was influenced by any similarities between the dataset used for alignment and the dataset used for evaluation.
* Despite the use of different methodologies, I would appreciate a performance comparison with related work.
Supplementary Material: N/A
Relation To Broader Scientific Literature: While other works mainly optimize the protocols or modify the model architectures, this work is complementary to those works and can be integrated for further performance.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: Strengths: The experiment is well-designed and effectively demonstrates the enhancements achieved through the proposed methodologies.
Weaknesses: The contribution of this work may be considered incremental since it primarily utilizes standard techniques such as knowledge distillation and batching multiple tokens.
Other Comments Or Suggestions: Typos or Comments:
page 1 col 2 line 9: missing space after the parenthesis “Pang et al., 2024)lever-“
Questions For Authors: N/A
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We are grateful for the reviewer's appreciation of our efforts. Below, we respond to your constructive comments in detail.
# Question 1: Could the author clarify the ambiguity in Line 90 in Introduction and the Line 27 in abstract?
Thank you for pointing out the potential ambiguity. We clarify it here and will revise the text to avoid any further confusion. Line 90 describes the whole POST approach, and line 27 refers to only the proposed sampling protocol.
- In lines 90-92: We claim POST is compatible with mainstream 2PC protocols for Transformer models (e.g., BOLT [4], BumbleBee [2], Nimbus [3]) because the key observation: the latency insensitivity to input length holds across these protocols, for which we provide more experiments in Appendix F.
- In line 27: We refer to the efforts of designing speculative sampling protocols in Section 4.2 to eliminate operations that are inefficient for cryptographic primitives.
# Question 2: Line 292: Could the author clarify why the $2^l$ complexity is considered acceptable?
The $O(2^l)$ term in the comparison protocol's overhead represents a special case with maximal communication size but minimal communication rounds [1]. Since we focus on optimizing the number of comparison calls rather than the protocol itself, we use this special case as a simplification for easier understanding, and the footnote on page five writes the general form $O(q \cdot 2^m)$ of communication complexity, where $q*m=l$. Here, $O(2^l)$ corresponds to use $q=1$. Larger $q$ reduces communication size but increases rounds. Existing works [2,3] typically choose $q=8$ to balance this trade-off, which we also adopt in experiments. In this way, bit width only partly contributes to exponential complexity.
# Question 3: What is the underlying rationale for selecting two pairs from different series?
We design two kinds of experiments to show the effectiveness in different cases.
- Same-series models: This is the favorable setting in practice, as private models often have open-source smaller versions, which can achieve speedups of 4.2X–6.0X.
- Different-series models: This is to highlight robustness and general applicability. Even in less favorable conditions, we still have speedups of 2.1X–4X.
# Question 4: What dataset was used for the knowledge distillation? Whether the acceptance rate is influenced by any similarities between the alignment dataset and evaluation dataset.
In this work, the alignment dataset is randomly sampled from the downstream training dataset. As explained in Sec. 4.3, the rationale for using similar datset is the case when client uses relevant public datasets or generates sanitized datasets from his queries (e.g., via differentially private generation [5,6] that preserves utility while removing sensitive information).
Our experiments show that alignment dataset similarity to the downstream task impacts the acceptance rate. For instance, testing Vicuna-7B and LLaMA-160M with an irrelevant alignment dataset, Alpaca [7], to the evaluated tasks.
||Not-aligned|Irrelevant-aligned|Relevant-aligned|
|-|-|-|-|
|SP|0.302|0.372|0.592|
|GS|0.536|0.602|0.691|
|CP|0.405|0.463|0.665|
|FN|0.576|0.595|0.650|
Directly using a non-aligned public models yields a 1.4X–2.3X speedup, while non-relevant dataset slightly improves it to 1.6X–2.5X. The best results (2.5X–2.9X speedup) occur when using a similar alignment dataset. Thus, we recommend selecting an similar alignment dataset for higher acceptance rates.
# Question 5: Despite the use of different methodologies, I would appreciate a performance comparison with related work.
Sorry for any confusion regarding our experimental setup. In fact, the speedup in Figure 5 is the comparison with the latest work, both with and without the integration of our method. The baselines are the SOTA 2PC secure inference works for Transformer, as detailed in Line 366, including the linear layer protocol from Nimbus [1] and the non-linear layer protocol from BumbleBee [2]. We will further clarify this in the paper.
# Question 6: The contribution of this work may be considered incremental since it primarily utilizes standard techniques such as knowledge distillation and batching multiple tokens.
Our key contributions include being the first to introduce observations on public models and latency insensitivity to input length. The novel paradigm (public decoding and secure verification) is not merely a standard batching technique but a strategically designed approach based on these insights. Additionally, we optimize this paradigm not only through knowledge distillation but also with a specialized sampling protocol.
# Reference
[1] Cryptflow2, CCS 2020
[2] Bumblebee, NDSS 2025
[3] Nimbus, Neurips 2024
[4] Bolt, S&P 2024
[5] Dp-opt: Make large language model your privacy-preserving prompt engineer, ICLR 2024
[6] Privacy-Preserving In-Context Learning with Differentially Private Few-Shot Generation, ICLR 2024
[7] https://github.com/tatsu-lab/stanford_alpaca | null | null | null | null | null | null |
Locality-Sensitive Hashing for Efficient Hard Negative Sampling in Contrastive Learning | Reject | Summary: This paper addresses the computational challenge of efficiently finding high-quality hard negative (HN) examples in large, high-dimensional datasets for contrastive learning. The authors propose a novel GPU-friendly Locality-Sensitive Hashing (LSH) technique which projects the input vectors to binary buckets, then apply xor + popcount to find neighbors with the smallest hamming distances. The approach is evaluated on several textual and visual datasets, demonstrating superior computational efficiency compared to other HN mining strategies without significant performance degradation. The key contribution is a lightweight framework for HN sampling that leverages a global view of the dataset while maintaining low computational costs during training.
Claims And Evidence: Below are the two major claims from the paper:
1. Built a lightweight and efficient framework for HN sampling using LSH, offering a global view of the dataset with low computational costs. Authors provided end-to-end runtime in Figure 1. However, a LSH vs kNN or other approximated nearest neighbor search benchmark is missing.
2. Demonstrated mining pre-epoch hard negatives using the LSH method above improves the model performance significantly. Authors evaluated the idea on six datasets across two modalities.
Methods And Evaluation Criteria: This paper introduces a method employing Locality-Sensitive Hashing (LSH) as an Approximate Nearest Neighbor (ANN) technique to mitigate the computational overhead associated with pre-epoch Hard Negative (HN) sampling. The proposed LSH method projects input vectors using random orthogonal bases and subsequently quantizes them into binary representations, encoding the position of each datapoint relative to hyperplanes. This binarization process substantially decreases storage requirements and facilitates rapid similarity searches via Hamming distance, which leverages efficient bitwise operations (XOR and popcount). During training, anchors are iteratively sampled, along with their corresponding positive and negative sample batches. Positive samples are drawn closer to the anchor, while negative samples are pushed away, thereby promoting accelerated convergence. Among the samples, those exhibiting the closest distance yet classified as negative to the anchor are deemed "hard negatives" and are critical for training efficacy. The authors propose the utilization of their LSH technique to expedite the identification of these hard negatives, employing a GPU-optimized LSH implementation that utilizes binary operations of XOR and popcount.
The methodology was evaluated across six datasets and benchmarked against random sampling, batch hard sampling, pre-epoch full sampling, and pre-epoch incremental sampling. Results demonstrate a significant reduction in runtime compared to the brute-force pre-epoch approach, while achieving a level of quality comparable to pre-epoch full sampling.
Theoretical Claims: The theoretical claims of hard negative mining follows previous work in hard negative minings.
The random projection followed by hyperplane splitting also follows previous work. However, it may be better to provide some proofs and insight of how the projected hamming distance relate to the original k nearest neighbors.
Experimental Designs Or Analyses: This work compared against random sampling, batch hard sampling, pre-epoch full sampling, and pre-epoch incremental sampling. Demonstrating competitive results to full sampling, but with better runtime. Authors also alter different numbers of bits and observe the mean positional distance of the HSH estimate.
However, it would be great if the authors can also provide a recall-qps trade-off plot like many other ANN research does. https://ann-benchmarks.com/index.html.
The other thing that is missing is the original embedding size used for nearest neighbor search. The most accurate LSH setting provided in this paper used 1024 bits, which may not be that small when compared to the original embedding size.
Supplementary Material: Authors provides additional similarity details of the LSH when increasing the number of bits. The visualization is quite useful for users to pick their preferred number of bits.
Relation To Broader Scientific Literature: -
Essential References Not Discussed: The xor-popcount computation can be written in regular CUDA programs, but on the Nvidia Ampere architecture there's a specialized tensor core instruction (XorPopc) that can compute much faster than regular CUDA programs (https://github.com/NVIDIA/cutlass/blob/main/include/cutlass/arch/mma_sm80.h#L1441C3-L1441C12).
Other Strengths And Weaknesses: -
Other Comments Or Suggestions: -
Questions For Authors: 1. Can author provide the recall-qps trade-off chart like https://ann-benchmarks.com/index.html?
2. Can author provide some theoretical analysis of how the hamming distance relates to the ground truth nearest neighbors?
3. What is the size of the original embedding? Can authors plot the compression ratio of LSH vs its recall in a chart as well?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: 1. Thank you for your suggestion. We agree that including a recall-QPS trade-off chart for our LSH approaches would provide additional clarity. We will replace Figure 1 with this graph. While Figure 1 was originally intended to illustrate processing time from a dataset size perspective by comparing our LSH method to cosine similarity over full embedding sizes, we believe the proposed chart provides a clearer and more direct view of the speed-performance tradeoff of our approach.
2. Yes, we have given a more detailed insight to this topic in answer 3 for reviewer udPs.
3. The original embedding depends on the data modality. For our image retrieval task we utilized a ConvNeXt-Base thus resulting in an embedding size of 1024 of float32 values. For the textual modality we utilized a Distill-RoBERTa-base with a embedding size of 768 of float32 values, we add this in 4.2. Implementation Details. While we describe the compression ratio briefly in Line 205-210 we agree with the reviewer that this should be better visualized to further strengthen our proposition, we can add a plot for this in our supplementary.
We also thank the reviewer for making us aware that cuda supports xor-popcount as a native implementation. This enables an even faster calculation of our methodology for the search directly on the GPU, which further accelerates our methodology! | Summary: This paper explores hard negative (HN) sampling in contrastive learning and proposes a Locality-Sensitive Hashing (LSH)-based Approximate Nearest Neighbor (ANN) approach to improve computational efficiency while maintaining competitive performance. The proposed method enables fast and efficient pre-epoch HN selection, making it scalable to large datasets. The paper includes experiments on multiple textual and visual datasets to evaluate its effectiveness. While the research topic is relevant and well-motivated, several methodological and presentation issues need to be addressed to strengthen the validity and clarity of the work.
## update after rebuttal
Claims And Evidence: Yes
Methods And Evaluation Criteria: Yes
Theoretical Claims: Yes
Experimental Designs Or Analyses: Yes
Supplementary Material: Yes. A.1. Similarity Distribution Analysis. A.2. VIGOR Analysis. A.4. Training Process. A.5. Architecture Details.
Relation To Broader Scientific Literature: Yes
Essential References Not Discussed: no
Other Strengths And Weaknesses: Strengths:
1. The paper addresses an important challenge in contrastive learning—efficient hard negative (HN) sampling. By leveraging Locality-Sensitive Hashing (LSH) as an Approximate Nearest Neighbor (ANN) approach, the study provides a scalable solution that is particularly relevant for large-scale datasets.
2. The proposed method significantly reduces the computational cost of HN selection, making it more practical for real-world applications where dataset size is a bottleneck.
3. The paper evaluates the method on **both textual and visual datasets, which strengthens its applicability across different modalities.
Weaknesses:
1. The paper lacks a strong mathematical foundation for key claims, such as the correlation between cosine similarity and Hamming distance. Providing a formal derivation or empirical validation would enhance the rigor of the study.
2. Some parts of the paper, particularly mathematical formulations and explanations of feature transformations, are unclear and require better notation, proper equation numbering, and detailed symbol definitions.
3. While LSH is known for its efficiency, the paper does not adequately compare it with alternative dimensionality reduction techniques (e.g., PCA, learned embeddings) or discuss how much information is lost in the process.
Other Comments Or Suggestions: No
Questions For Authors: 1. The current structure of the paper contains redundancies and sections that could be streamlined to enhance readability.
1) Such as "we propose a lightweight Approximated Nearest Neighbor (ANN) approach that leverages Locality-Sensitive Hashing (LSH)" and "Our work first explores HN sampling methods and introduces LSH as an ANN approach" are repetitive.
2) Preliminary section (3.1) contains excessive common knowledge. Large portions of this section summarize well-known aspects of contrastive learning and hard negative mining, making it longer than necessary.
2. Justification of Hash Encoding Needs Clarification. The paper proposes LSH-based binary encoding to reduce computational cost, but it does not clearly explain its advantages over other dimensionality reduction techniques.
1) What makes LSH particularly suitable for this problem compared to traditional PCA-based or learned feature compression methods?
2) Does the hashing step introduce any loss of information? If so, how does it affect the quality of hard negative mining?
3. The Purpose and Impact of Data Transformations (Lines 197-208) Need More Explanation. The paper describes a series of transformations applied to the original feature representations but does not provide a clear justification for them. Why are these specific transformations applied? Is there empirical evidence that these steps improve the quality of HN sampling?
4. Several equations in the paper lack clarity, proper notation, and explanations of symbols, making them difficult to follow.
1) Equations should be numbered and properly punctuated. Example: Lines 206 and 214 introduce equations without explaining all variables used (e.g., what does "i" represent?).
2) The paper discusses random rotation matrices (R) and binary hashing functions (hi) but does not clearly define their mathematical properties. Are R and hi learnable or fixed?
5. The paper claims that angle-based similarity (cosine similarity) and binary Hamming distance are positively correlated, but it does not provide a theoretical proof or strong empirical validation for this assumption. What is the precise mathematical relationship between cosine similarity and Hamming distance?
6. Is the Feature Mapping Learnable? The transformation of original feature vectors into binary hash codes raises concerns about potential information loss. Are the transformation matrices (R) and hashing functions (hi) optimized during training, or are they static? If they are static, how do we ensure that important information is retained?
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: We thank the reviewer for the comments and will address them accordingly:
1. Thank you for the suggestion, we will address this and structure the paper more clearly by, for example, removing redundancies and improve citation clarity as suggested by udPs.
2. See 1.
3. See 1.
4. LSH has the advantage of not being data dependent. We think that data dependent feature compression methods such as PCA would fail in this task. First, they often assume some underlying data structure. PCA for example needs the data to be distributed in some linear subspace. As the whole purpose is to find a suited embedding space it seems counterintuitive to us to add arbitrary constraints to this embedding. Second, data dependent compression methods by definition depend on the current embedding. That means as the embedding space changes over time, the compression model must be refitted. Recalculating the SVD for PCA after every update is computationally expensive. LSH on the other hand is a very lightweight and efficient method for the sole purpose of finding an ANN.
5. See 4.
6. Yes, the hashing step introduces a loss of information due to both dimensionality reduction and binarization of the feature vectors. We empirically analyze how this affects the quality of hard negative sampling in Figures 3 and 4. In particular, we observe that as the number of bits decreases, the overlap with cosine similarity-based hard negative sampling decreases and the average positional distance to retrieved negatives increases. Furthermore, our quantitative results (Tables 1 and 2) confirm that lower bit counts correspond to performance degradation when using LSH-derived negatives compared to cosine similarity-based hard negative sampling.
7. Thank you for pointing out that there is still some clarity missing. We follow the classical procedure of LSH with random projections for ANN as in Wang et al. 2015 (Learning to Hash for Indexing Big Data - A Survey) which we will better explain in Section 3.2.
8. We will improve the structure and clarity in the math notations in the corresponding Section 3.
9. Thank you for pointing this out. We will double check our equations and add additional explanations as suggested. In this particular case “i” refers to the index of vector z. We wanted to describe that every dimension of the projection z of and embedding y is converted into a bit depending on its sign.
10. We state that we use a random rotation matrix that features orthonormal vectors sampled from a gaussian distribution and is fixed throughout the training. The gaussian sampling is taken from Wang et al. 2015 (Learning to Hash for Indexing Big Data - A Survey) and orthonormalization is empirically justified by our experiments. Thus, the matrix R is not learnable. $h_i$ should denote the binarization of the affine linear transformation of the ith row of the random rotation matrix and is thus not learnable too.
11. According to Wang et al. 2015 (Learning to Hash for Indexing Big Data - A Survey) the collision probability of two vectors, c and y in the ith bucket $(i.e. P(h_i(c)=h_i(y)))$ is equal to $1 - \frac{\theta_{cy}}{\pi}$, $\theta_{cy}$ denoting the angle between c and y. As the hamming distance is just the sum of dependent Bernoulli trials, each of them with a success rate of $1-P(h_i(c)=h_i(y))=1 - \frac{\theta_{cy}}{\pi}$ it equals to the said Binomial distribution. We explained this in more detail in answer 3 for reviewer udPs.
12. We only learn the embedding. The procedure to identify hard negatives is static throughout the whole training process as mentioned in Section 4. It is solely based on the random initialization of the projection matrix. Information loss is not that relevant as the only necessary condition is that points with high cosine similarity result in a low hamming distance between them. Preserving additional structure or information is not necessary, as our experiments show, and we will add a statement of that effect in 3.2 explaining our approach. | Summary: This paper introduces a Locality-Sensitive Hashing-based method for efficient Hard Negative sampling in contrastive learning. This method converts feature embeddings into binary representations, which enables fast approximate nearest neighbor searches.
Claims And Evidence: Most of the claims are supported by experiment results. However, this paper lacks formal theoretical guarantees on the quality of LSH-based hard negation and does not analyze the impact of different hash function choices.
Methods And Evaluation Criteria: The proposed method and evaluation criteria make sense.
Theoretical Claims: In this paper, the authors didn't introduce formal proofs for theoretical claims. Specifically, they didn't provide formal bounds for the probability that an LSH-sampled neighbor is a true hard negative and they didn't explore the impact of different hash functions on retrieval quality.
Experimental Designs Or Analyses: I suggest that the authors could add some experiments to analyze the effect of dataset size on LSH performance.
Supplementary Material: There is no supplementary material.
Relation To Broader Scientific Literature: This work is based on contrastive learning and approximate nearest neighbor search literature.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: Strengths:
1. This paper is well-structured and well-written.
2. The experiments are comprehensive and include various datasets.
Weaknesses:
1. The authors could consider providing formal error bounds for LSH-based sampling. It would be helpful to analyze how approximation errors affect model performance. Comparing LSH errors with other approximate nearest neighbor methods could also strengthen the evaluation.
2. There is no formal theoretical analysis for LSH-based hard negative sampling. I think adding a mathematical guarantee or error analysis would make the paper more rigorous.
Other Comments Or Suggestions: Please refer to above all parts.
Questions For Authors: 1. I'm wondering if LSH could adjust bit sizes dynamically during training based on model convergence to optimize both efficiency and accuracy. Have you explored any adaptive strategies for selecting the optimal bit size at different training stages?
2. Would LSH performance degrade in highly structured feature spaces where feature relationships follow a specific hierarchy? If so, what measures can be taken to mitigate potential issues and ensure robust performance across different data distributions?
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: We thank the reviewer for the comments and will address them accordingly:
1. Yes we agree with Reviewer XybM, that investigating dynamic bit sizes can be interesting. Therefore we already explored this idea on both the VIGOR dataset and MS MARCO. We started with 8 bits and gradually increased to 16, 32, 64, up to 1024 bits over the training epochs. However, this adaptive strategy resulted in slightly worse performance than using a fixed 128-bit setting throughout training. This effect appears to be due to the interaction with the cosine decay learning rate schedule. As training progresses, higher bit resolutions allow for finer-grained hard negative mining, which increases the difficulty of the retrieved samples. At the same time, the decreasing learning rate limits the model's ability to adapt to these harder samples, resulting in smaller weight updates. In principle, this problem could be mitigated by combining bit increase with a dynamic learning rate schedule (like multi-cycle or restart-based), but how to determine the increase of the needed learning rate is an open question. We agree that this is a promising direction for future work and can include the experiments we already did in the supplementary material.
2. Performance degradation of LSH in highly structured feature spaces is unlikely. In fact, structured data should typically exhibit high cosine similarity between embeddings belonging to the same hierarchical cluster. Given $$ \operatorname{Pr}\left[h_i\left(c\right)=h_i\left(y\right)\right]=1-\frac{\theta_{c y}}{\pi}=1-\frac{1}{\pi} \cos ^{-1} \frac{c^{\top} y}{\left\|c\right\|\left\|y\right\|} $$ , data points that are hierarchically or structurally related will naturally have a high probability of sharing identical or closely matching hash vectors. This property ensures the robustness of LSH when dealing with structured or hierarchical data distributions. Moreover, the slight randomness inherent in LSH can actually enhance contrastive learning by occasionally sampling negatives from nearby but different clusters, thus improving batch diversity and generalization.
We have provided an empirical insight into the relationship between the quality of LSH samples and model performance in figure 5. From a theoretical viewpoint Har-Peled et al. 2012 (Approximate Nearest Neighbor: Towards Removing the Curse of Dimensionality) work on a slightly different problem and Wang et al. 2015 (Learning to Hash for Indexing Big Data - A Survey) which we base our LSH paradigm on does not provide any deeper theoretical insides. Therefore we could not fall back on their work. The conclusion we draw regarding the implications on the hamming distance will be reworked to provide a clearer and better structural insight. We explain this in more detail in answer 3 for reviewer udPs. | Summary: The paper addresses the efficient sampling of hard negatives in contrastive learning by introducing an approximate nearest neighbor method based on Locality Sensitive Hashing (LSH). This method quantizes real-valued feature vectors into binary representations for approximate nearest neighbor search, thereby reducing both search time and space costs. The method is demonstrated to outperform other hard negative mining strategies in terms of computational efficiency on multiple text and visual datasets, with no significant degradation in performance.
Claims And Evidence: 1. The paper conducts experiments across multiple datasets, comparing the search times of the LSH method with other methods (such as random sampling, BatchHard sampling, Pre-Epoch Full sampling, and Pre-Epoch Incremental sampling). The results show that the LSH method significantly reduces search time under different bit-width settings.
2. The paper evaluates performance on multiple datasets using metrics such as Recall@1, Recall@5, and MRR@10. The results indicate that the LSH method maintains computational efficiency while achieving performance comparable to or better than the best methods.
3. The paper performs experiments on multiple text and visual datasets, including MS MARCO, CVUSA, CVACT, VIGOR, SOP, and InShop. The results demonstrate that the LSH method performs well on both modalities.
Methods And Evaluation Criteria: The paper proposes an efficient sampling method based on LSH, which significantly reduces computational and storage overhead by quantizing high-dimensional feature vectors into binary representations. The paper uses standard retrieval metrics such as Recall@1, Recall@5, and MRR@10 to evaluate the model's performance. These metrics are widely used in information retrieval and contrastive learning tasks and effectively measure the model's performance in retrieval tasks. Therefore, the method and evaluation criteria proposed in the paper are suitable for the current problem and application, especially in large-scale datasets and high-dimensional feature spaces, where the LSH method demonstrates significant advantages.
Theoretical Claims: 1. The paper introduces LSH by mapping high-dimensional vectors to low-dimensional binary spaces, thereby reducing computational complexity while maintaining similarity. It also includes random rotation matrices and centralization, ensuring that the hash function can evenly distribute data points, thereby increasing the probability of hash collisions. This is theoretically sound.
2. The paper proposes the application of LSH to hard negative sampling in contrastive learning. Through LSH, it is possible to efficiently find negative samples similar to the anchor, thereby improving learning performance. Experimental results on different datasets support the effectiveness of LSH in contrastive learning. It has been proven that the LSH method maintains computational efficiency without significantly reducing performance.
Experimental Designs Or Analyses: 1. Figures 4 and 5 demonstrate that LSH can effectively approximate true nearest neighbors by overlapping rate and average position distance. Figure 7 further shows that the similarity distribution of LSH retrieved samples outperforms random sampling.
2. Tables 1 and 2 present the Recall and MRR@10 metrics of the LSH method on multiple datasets, which are close to or better than the Pre-Epoch Full. However, the storage savings are only mentioned through theoretical analysis, and no actual memory usage experimental data is provided.
3. The paper conducts experiments on both image (e.g., CVUSA, SOP) and text datasets (e.g., MS Marco), but the performance on the text modality is relatively weaker. The paper does not deeply analyze how the inherent differences between text and image features affect the performance of LSH.
Supplementary Material: 1. The paper analyzes the similarity distribution between approximate nearest neighbors (ANN) sampled via the LSH method and the actual nearest neighbors (NN) retrieved by cosine similarity, indicating that the LSH method can better capture the similarity in the original embedding space.
2. The paper provides a detailed description of data augmentation techniques, batch construction strategies, number of training epochs, and image size adjustments in image experiments.
3. The paper conducts an analysis of overlap and mean positional distance on a subset of the VIGOR dataset, demonstrating that the LSH method has an advantage in selecting more effective hard negative samples.
Relation To Broader Scientific Literature: 1. The paper utilizes Locality-Sensitive Hashing (LSH) for efficient hard negative sampling, building on the widespread application of LSH in reducing computational complexity in large-scale datasets. The authors extend this approach to contrastive learning, demonstrating its effectiveness in handling high-dimensional embeddings.
2. The paper addresses the challenge of efficiently sampling hard negative examples in contrastive learning. Previous research has shown that hard negative samples significantly enhance the performance of contrastive learning. The proposed method not only maintains the quality of hard negative samples but also reduces the computational overhead associated with traditional methods.
3. The paper includes a theoretical analysis of the LSH method, providing insights into its behavior and effectiveness. This complements prior theoretical work on LSH and its applications in various fields.
Essential References Not Discussed: 1. The paper proposes an efficient hard negative sampling method based on LSH, but does not cite some early works that applied LSH in contrastive learning.
2. The paper conducts a theoretical analysis of the LSH method, but does not reference some important literature on the theoretical foundations of LSH.
Other Strengths And Weaknesses: 1. The paper proposes an efficient hard negative sampling method based on LSH, which is a significant addition to existing contrastive learning methods. This approach significantly reduces computational complexity by quantizing high-dimensional feature vectors into binary representations while maintaining the quality of hard negative samples.
2. Hard negative samples play a crucial role in contrastive learning, significantly enhancing model performance. The method not only improves sampling efficiency but also reduces computational resource consumption, which is significant for processing large-scale datasets.
3. LSH has been extensively studied in approximate nearest neighbor search, and the method in this paper primarily applies it to hard negative sampling in contrastive learning, lacking deeper innovation.
4. The paper has inconsistent citation formats and the structure is not clear enough.
Other Comments Or Suggestions: 1. It is recommended to supplement more literature in the related work section, especially the important progress in the fields of contrastive learning and LSH in recent years. This will help readers better understand the background and contributions of the paper.
2. It is recommended to unify the citation format of references to enhance the professionalism and readability of the paper.
3. It is suggested to further deepen the theoretical analysis of the LSH method, which will help strengthen the theoretical foundation of the paper.
Questions For Authors: 1.The paper mentioned applying LSH to hard negative sampling in contrastive learning. However, LSH has already been extensively studied for approximate nearest neighbor search. Could you further elaborate on the innovative aspects of your method compared to existing work?
2.The paper notes that nearest neighbor retrieval for textual data is more challenging than for image data, likely due to the semantic complexity and polysemy of text. Have you considered designing specialized LSH strategies for different modalities?
3.Despite the efficiency of LSH in approximating nearest neighbors, the paper mentions the lack of theoretical guarantees for the quality of hard negative sampling. Have you considered providing a more rigorous theoretical analysis for the LSH sampling method?
4. Why not using other more recent data-independent hashing methods to help the hard negative sampling problem?
Code Of Conduct: Affirmed.
Overall Recommendation: 1 | Rebuttal 1:
Rebuttal: We thank the reviewer for their comments, and begin by addressing them below:
1. We agree with the reviewer that LSH has been extensively studied in the context of approximate nearest neighbor search. However, its application in contrastive learning, especially for hard negative sampling during training, remains underexplored. Moreover, in the few cases where it has been used, its application is often limited to specific modalities.
For example, Gillick et al. (Learning Dense Representations for Entity Retrieval 2020) employed quantization-based fast inner product search (Quantization based Fast Inner Product Search Guo et al., 2015) for entity retrieval. While effective, this method relies on data-dependent codebook training, introducing additional complexity and limiting generalizability.
In contrast, our approach uses data-independent LSH to efficiently sample hard negatives in a way that is broadly applicable across tasks and modalities. Unlike data-dependent methods, our projection does not require continuous retraining, which is a common limitation as embeddings evolve during training. We will make this distinction more explicit in the Research Gap and Introduction. As noted in our response to reviewer SDTH, we have also quantified the benefits of our method in terms of computational savings per epoch, demonstrating its practical scalability in large-scale settings.
2. Thanks for the suggestion. Modality-specific LSH methods such as bag-of-words approaches (BM25) for hard negative search have been explored (Karpukhin et al. 2020, Dense Passage Retrieval for Open-Domain Question Answering). However, they can also be prone to false negatives, and perform worse than embedding-based approaches (Xiong et al. 2021, Approximate Nearest Neighbor Negative Contrastive Learning for Dense Text Retrieval). In contrast, our approach is modality-agnostic as we operate directly on embeddings and generalize across text, image, and multimodal data. This allows for a unified and scalable retrieval framework without relying on modality-specific heuristics.
3. We based our LSH sampling approach mostly on Wang et al. 2015 (Learning to Hash for Indexing Big Data - A Survey) who refer to the well known fact that the collision probability of two points is equal to their similarity but to our understanding do not offer deeper insights regarding the similarity between the point with the nearest computed hamming distance and the anchor/query. Other LSH related work such as Har-Peled et al. 2012 (Approximate Nearest Neighbor: Towards
Removing the Curse of Dimensionality) states that for a defined radius, and a nearest neighbor existing in that radius of a query point, we find an approximate neighbor in some $cr$ neighborhood of the query point. We on the other side always return the neighbor with the smallest projected hamming distance to the query/anchor point which is different.
Therefore we can not build upon their work and offer the following insight instead. As the hamming distance is the sum of d independent Bernoulli trials it corresponds to a binomial distribution with success rate equal to their cosine distance. For large bit sizes this is approximating a normal distribution with mean equal to bit size times cosine distance. When a point x is closer to the anchor than a point y this should ideally reflect in a smaller hamming distance, i.e. $\mathrm{HammDist}(c, y) - \mathrm{HammDist}(c, x) > 0$. Let $Z=\mathrm{HammDist}(c, y) - \mathrm{HammDist}(c, x)$. As the difference of two normal distributions $Z$ is again a normal distribution with mean $\mu_Z=n (\mathrm{sim}(c,y)- \mathrm{sim}(c,x))$ and variance $\sigma_{Z}^2 = n \left( (1 - \mathrm{sim}(c,x)) \mathrm{sim}(c,x) + (1 - \mathrm{sim}(c,y)) \mathrm{sim}(c,y) \right)$. Therefore $$P(Z<=0)=P\left(\frac{Z-n (\mathrm{sim}(c,y) - \mathrm{sim}(c,x)) )}{ \sqrt{(n ((1- \mathrm{sim}(c,x)) \mathrm{sim}(c,x) + (1- \mathrm{sim}(c,y)) \mathrm{sim}(c,y))}}\right).$$ with increasing bit size the probability of $\mathrm{HammDist}(c,y) < \mathrm{HammDist}(c,x)$ decreases. We already outlined this in L194-202 but we will strengthen this section with the above comprehensive insight. Thank you for the suggestion!
4. Thanks for the suggestion. We use a random hyperplane-based LSH, chosen for its simplicity, strong performance on high-dimensional embeddings, and efficient GPU implementation.
While more advanced variants such as cross-polytope LSH offer improved theoretical recall, they involve more complex encoding and decoding schemes that are less suitable for large-scale, batched GPU workflows. Similarly, multi-probe techniques are complementary to our approach and could be integrated to further improve recall, but we found our current setup sufficient for effective hard negative mining. We will add this in our Discussion to address this more clearly.
We also thank the reviewer for pointing out the citation unification, we will enhance this further!
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Rebuttal Comment 1.1:
Comment: The authors addressed the core issues raised in the review by clarifying the versatility of their data-agnostic LSH method and strengthening the theoretical link between Hamming distance and cosine similarity through probabilistic modeling. However, critical gaps remain unresolved. Their application of LSH still falls under existing technical adaptations, lacking substantial justification for its inherent innovation. Additionally, while the binomial approximation of Hamming distance is theoretically reasonable, it overlooks practical impacts of high-dimensional sparsity (e.g., long-tail effects) on distribution. Although the method claims "modality-agnostic" applicability, its generality is weakened by the absence of validation on more complex multimodal tasks. Consequently, I keep my original score. | Summary: This paper proposes to use locality-sensitive hashing to extract nearest neighbors as hard negatives when performing contrastive learning to train sentence embedding. The authors perform experiments to verify that the proposed method can achieve almost the same embedding quality and that the search time runs an order faster than the most accurate baseline.
Update after rebuttal:
The authors' response addressed my concern regarding the motivation of the new method. My score remains unchanged.
Claims And Evidence: yes
Methods And Evaluation Criteria: yes
Theoretical Claims: n/a
Experimental Designs Or Analyses: yes
Supplementary Material: no
Relation To Broader Scientific Literature: n/a
Essential References Not Discussed: yes
Other Strengths And Weaknesses: Strength:
1. The proposed method is clean and effective.
2. The authors use math formulas and visualization to explain how LSH is used in a clear way
3. Comprehensive experiments were done on the relationship between the number of bits used in LSH and the hard negative quality. And how hard negative quality affects final sentence embedding quality.
Weakness:
1. Perhaps the authors can try stronger datasets where the gaps between different methods are more obvious.
Other Comments Or Suggestions: n/a
Questions For Authors: 1. I am curious how much is the hard negative search time compared to the training time. If most of the time is spent on training the models on the samples within epochs, then optimizing the search time seems to be not well motivated.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank the reviewer for his insightful comments. To address the concern about our motivation, we measured the training times per epoch (averaged over 3 epochs) using a DGX-2 on different datasets and compared these to the pre-epoch HN search times shown in Figure 1 and the search time with 128 bit:
| Dataset | Dataset size - train | Training time per epoch without search time (s) | Search time per epoch LSH 128 bit (s) | Search time per epoch Pre-Epoch HN (s) | Search time proportion per epoch when using Pre-Epoch HN |
|---------------|--------------|---------------------------------------------|----------------------------------------|------------------------------------------|----------------------------------|
| CVUSA/CVACT | 35,532 | 181.91 | 0.35 | 25.10 | 12.12% |
| VIGOR | 40,007 | 395.20 | 0.437 | 41.10 | 9.42% |
| SOP | 59,551 | 137.24 | 0.717 | 69.04 | 33.46% |
| InShop | 25,882 | 65.57 | 0.21 | 13.33 | 16.89% |
| MS Marco | 532,736 | 566.92 | 33.57 | 7553.27 | 93.01% |
We agree this provides important details to our motivation, and we will include this table in the supplementary materials. We thank the reviewer for encouraging us to clarify this aspect further.
We appreciate the reviewer's comment regarding the choice of dataset. As stated in our research gap (Section 2.3), our goal is to evaluate whether a binarized, low-dimensional representation can match the performance of full-scale embeddings in the context of hard negative sampling for contrastive learning. The results in Tables 1 and 2 indicate that the performance gap remains small, which is consistent with our research goal. If there were a significant performance drop when comparing pre-epoch incremental sampling to our LSH-based sampling, it would suggest that LSH is ineffective for efficient hard negative selection. However, the minimal performance differences observed support our hypothesis and demonstrate that LSH provides a practical balance between computational efficiency and representational effectiveness. | null | null | null | null |
Modification-Considering Value Learning for Reward Hacking Mitigation in RL | Reject | Summary: The paper proposes a novel value learning RL algorithm intended to reduce the probability of having agents developing reward hacking (i.e., unsafe and unintended behavior due to non-optimal definition of the reward function). The paper proposes two variations of their algorithm, which in high-level basically uses a environment model to reason over whether if a sample should be added to the experience replay buffer before doing so. Some experimental results are presented in relatively simple environments comparing the approach to alternative similar training regimes.
Claims And Evidence: The main claim of the paper is that the contributed algorithm addresses a specific type of reward hacking, therefore by using it we would be avoiding some instances of reward hacking.
The evidence provided is mainly empirical in modified gridworld domains, plus a MuJoCo domain where if the agent executes a certain sequence of actions it receives an extra "unintended" reward. A comparison showing the performance of the proposed method x the "base version" of the algorithm is shown, where the metric is mainly the accumulated reward achieved by the algorithms.
Methods And Evaluation Criteria: I am not very convinced the empirical evaluation shown here is really appropriate for several reasons:
1) First, I am not even sure if the gridworld domains actually represent a realistic situation related to reward hacking. I would expect that reward hacking wouldn't be identified by the user at all (otherwise they would have corrected the reward function). If I understand correctly the gridworlds intended to show a scenario in which a human would be :"watching" the policy learned and identifying where reward hacking happened, which while a strong assumption, is sorta ok, but would require some thought on how often and how the human would be required to be watching the policies, and exactly which form this feedback should take.
2) THe Mujoco environment is closer to what I would expect as a good reward hacking environment, where a "hidden" sequence of actions would enable a very high reward. However I am not sure how avoiding the reward hacking was incrporated in the metrics shown in the experimental evaluation. Because the reward hacking sequence was removed from the sum of rewards in the graph is it expected that pursuing this sequnece of actions would necessarily result in a lower sum of rewards? That's not really a great way of evaluating it because it gets mixed together with approaches that just can't learn the task. It would be better to report in a table or graph the amount of times the reward hacking sequence was triggered.
For the method, I couldn't really get why the proposal would avoid reward hacking. What the proposal is doing is basically having a counterfactual for adding a training sample or not, which I could not understand what is the relation whatsoever with the reward hacking (in the POV of the agent it would just be a higher reward, how would it know that it would result in a "worse policy"?). So to me the method sounds a bit disconnected from the objective.
Theoretical Claims: Paper is empirical
Experimental Designs Or Analyses: Apart from what was mentioned in Methods And Evaluation Criteria, the method did not show any comparison against another method developed explicitly for avoiding reward hacking. This might indicate that the assumptions followed by the method are too restrictive and the authors could not adapt any other method to compare against fairly.
Supplementary Material: No.
Relation To Broader Scientific Literature: Authors provided a good review of related paper, but did not add them to the experimental evaluation.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: I would say that the paper is really unclear on the assumptions followed, some of which are quite restricting.
The reader has to read in details the method to only understand several pages into the paper that the method requires as an INPUT an already trained "safe" policy as a starting point. Therefore, the method could be seem as a way of improving an already-decent policy, not really an algorithm to be training from scratch. Moreover, the methods consists of performing a very high number of rollouts and optimization steps in the environment model just to decide which samples to use for training of the "final policy". The authors are not clear at all on that the users of their method should be prepared to invest an obscene amount of extra compute to use the method (except from a very quick comment in the appendix). Overall I would say the method description should start with.a clear list of assumptions and requirements for using the method.
Another critical matter is that after reading the whole paper I still don't understand WHY the proposed method should address reward hacking. I cannot get what is the reasoning behind checking if a sample will improve the policy before using it for training as a way of avoiding reward hacking, since the agent won't be able to tell apart a very high reward from a great policy and the high reward from hacking. I am probably missing something.
Other Comments Or Suggestions: Reorganize paper so that in the beginning of the respective section it's very clear:
- What is the reasoning behind using this method for reward hacking
- What are the assumptions/costs expected when using the approach, and in which situation it would make sense to use it
- Exactly how the gridworlds are simulation a realistic reward hacking situation?
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Post-rebuttal
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Perhaps "safe" wasn't the best word to describe it but I did mean that the agent needs to have access to a reward hacking-proof utility function to begin with, which sounds to me very unrealistic in most of the cases. The only situation I can think of that this could be useful is if you trained your agent in an controlled environment and you want to make sure that the samples your agent gather during deployment are not poisoned.
Overall the reasons for my scoring remain.
Questions For Authors: - What is the reasoning behind checking if a sample will improve the policy before using it for training as a way of avoiding reward hacking?
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: Thank you for your detailed review and insightful questions. We appreciate the chance to clarify MCVL's mechanism, assumptions, and evaluation. We will revise the paper to make these points clearer.
> For the method, I couldn't really get why the proposal would avoid reward hacking. [...] how would it know that it would result in a "worse policy"? [...] I cannot get what is the reasoning behind checking if a sample will improve the policy [...]
The core idea is that the agent has a utility function $U$ which can judge how good the trajectory is according to *prior experience*. When the agent encounters a new transition, it uses this utility function to check if learning from this transition will result in a behavior *aligned with prior experiences*. It checks that the new policy would not contradict all previous experiences without reward hacking. It doesn’t mean that the policy is “improved” in the standard RL sense.
When MCVL forecasts that learning from a transition will make the agent execute behaviors that it does not prefer now, it rejects the update. We describe this in L.157(left)-L.131(right) in the Method. We will clarify the description and add another one in Introduction.
> The reader has to read in details the method to only understand [...] that the method requires as an INPUT an already trained "safe" policy [...], the users of their method should be prepared to invest an obscene amount of extra compute...
We apologize for the lack of clarity and will make assumptions and costs more prominent.
* **Input:** MCVL requires an initial **utility function**, not a safe *policy*. This function captures initial preferences and can be learned from non-hacking data (e.g., Safe env, or random rollouts as in Reacher experiment). The utility function needs to prefer trajectories from current policy over reward hacking policy by the time reward hacking sequence is triggered. If reward hacking is hard to discover, the utility function has time to learn from transitions before it happens, without relying on the initial one. This is mentioned in the Abstract/Introduction, but we will make it more prominent. The RL *policy* can train from scratch.
* **Cost:** MCVL adds computational overhead. We discuss this and potential ways to mitigate it in the first paragraph of the Limitations section. With one of the proposed solutions, using a threshold, we observe a moderate ~1.8x slowdown vs. TD3 in Reacher environment. The goal of the paper was to show that reward hacking can be mitigated by avoiding inconsistent utility updates; we are leaving further optimizations to the future work. We will add more information on this topic in the paper.
> I am not even sure if the gridworld domains actually represent a realistic situation [...]. I would expect that reward hacking wouldn't be identified by the user at all. [...] how the gridworlds are simulation a realistic reward hacking situation?
To study reward hacking and measure its mitigation, we need environments where we can detect and measure it. Our experiments show that in several environments used by prior work to illustrate the problem of reward hacking, it can be avoided by preventing inconsistent utility updates. We expect this principle to generalize to situations where reward hacking is hard to detect by the user. Our experiments do not assume humans watching the policy learned and identifying reward hacking.
> THe Mujoco environment [...] how avoiding the reward hacking was incrporated in the metrics [...] report [...] the amount of times the reward hacking sequence was triggered.
* **Metric:** *Performance* tracks the *intended* task reward (reaching the target), *excluding* the hacking reward. When the baseline hacks, it neglects the target, causing *performance* to drop. MCVL improves *performance* throughout the training, showing it learns the intended task successfully. This distinguishes it from simply failing to learn. We will highlight this in the paper.
* **Hacking Frequency:** Figure 3e (bottom) implicitly shows this. Returns above 0 for the baseline require hacking. MC-TD3's returns show it rarely triggers the sequence (legitimate triggers are possible when the intended goal is nearby). We will add text clarifying this.
> the method did not show any comparison against another method developed explicitly for avoiding reward hacking.
Direct comparisons are hard due to differing assumptions. MCVL's requirement (initial utility function) is often *less* restrictive than requirements of other work. The only prior work applicable to deep RL is ORPO [1] and it requires a safe policy. Our response to Reviewer dDMw includes **new experiments showing an ORPO-like approach would struggle** in our setting.
We hope this clarifies MCVL's rationale and addresses your concerns.
[1] Cassidy Laidlaw, Shivam Singhal, Anca Dragan - Correlated Proxies: A New Definition and Improved Mitigation for Reward Hacking, In ICLR 2025 | Summary: Traditional Reinforcement Learning (RL) agents often demonstrate reward hacking, which is defined as the ability to maximize rewards without providing the desired outcomes. The paper studies reward hacking in RL by using General Utility in order to learn and update utility functions at the trajectory level. Inconsistencies between the current and updated utility functions are minimized using Modification-Considering Value Learning (MCVL). MCVL starts with an initial utility function and refines it by comparing the expected utility values of the current and updated functions. The modify command is embedded in the new action space and used alongside actions in the trajectories. MCVL is combined with DDQN (for discrete tasks) and TD3 (for continuous tasks). The proposed method demonstrates improved intended behaviors by virtue of the performance metric across safe and full environment configurations as well as different training scenarios.
Claims And Evidence: Please refer to strengths and weaknesses.
Methods And Evaluation Criteria: Please refer to strengths and weaknesses.
Theoretical Claims: Please refer to strengths and weaknesses.
Experimental Designs Or Analyses: Please refer to strengths and weaknesses.
Supplementary Material: Yes, the appendix.
Relation To Broader Scientific Literature: Please refer to strengths and weaknesses.
Essential References Not Discussed: Please refer to strengths and weaknesses.
Other Strengths And Weaknesses: ### Strengths
* The paper is well written and easy to follow.
* Experiments and environments considered in the work are well thought out.
### Weaknesses
* **Learned Modifications**: I am struggling to understand the learning and modification scheme used for modifying the utility function. _modify_ is a part of the action space but not entirely learned either using a loss function or trainable parameters. The modification is derived based on the discrepancy in expected values between utility functions of the policies. But wouldn't the new updated policy with fresh T trajectory samples always be better? Intuitively, the updated policy has more information about the environment and agent performance and thus, it must yield a more value function. In the current setup, I am not sure if comparing policy discrepancies is a systematic way of modifying utility as the agent does not learn or is made aware of these modifications in any form.
* **Performance Metric**: Authors compare the robustness of MCVL to reward hacking using episodic returns and the performance metric. However, I am unable to understand the performance metric. What does performance signify here? How is it quantified? How is the performance metric defined (intuitively and mathematically) for a given environment? For instance, episode return is the average sum of discounted rewards at each step. Furthermore, authors mention that performance indicates the intended behavior of the agent on an environment. How does one know this intended behavior beforehand? In its current form, the metrics and experimental evaluation shed little light on how MCVL addresses reward hacking.
* **Ablation Study**: While the paper evaluates MCVL on continuous and discrete tasks on different agents, it does not evaluate the efficacy of the proposed method in mitigating reward hacking. For instance, authors only compare return and performance metrics which tell us little about whether the agent has learned meaningful behaviors as a result of the proposed techniques. Instead, authors could study and compare how their proposed additions benefit the agent. Authors could compare ablations between trajectory-level and per-step-level learning of the policy. Similarly, what if instead of selectively using _modify_ we conduct random modifications of the utility function? Currently, the paper only compares the performance of MCVL on two baseline RL algorithms and does not shed light on the contribution of the proposed techniques.
* **Contribution and Novelty**: I am struggling to understand the novel contribution of the work and its utility for the RL community. How does the algorithm benefit RL algorithms since the only proposal that has been made is to selectively _modify_ the utility function? While the paper also shifts from a state-level policy learning setting to trajectory-level learning, recent RL algorithms of today (Decision Transformer [1], Diffusion RL [2]) operate on trajectory-level samples.
[1]. Chen et al, Decision Transformer: Reinforcement Learning via Sequence Modeling, NeurIPS 2021.
[2]. Janner et al, Planning with Diffusion for Flexible Behavior Synthesis, ICML 2022.
Other Comments Or Suggestions: NA
Questions For Authors: Please refer to strengths and weaknesses.
Ethical Review Concerns: NA
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: Thank you for your review and valuable suggestions. We address your points below and will incorporate the responses into the paper.
> Learned Modifications: [...] But wouldn't the new updated policy with fresh T trajectory samples always be better? [...] comparing policy discrepancies is [not] a systematic way of modifying utility...
Your intuition holds for standard RL agents optimizing a fixed target ($U_{RL}$). However, MCVL agents optimize their *current* utility ($U_{VL_t}$) and consider the consequences of *changing* that utility. As explained in the Method section (Lines 157 left-132 right), an update might contain new information that leads to future behavior deemed undesirable by the agent's *current* values ($U_{VL_t}$).
MCVL evaluates if incorporating new data (leading to $U_{VL_{t+1}}$) would result in behavior with lower expected utility according to the *current* $U_{VL_t}$. If so, the update is rejected. We are preventing the agent from learning to prefer trajectories (like reward-hacking trajectories) that its current self evaluates negatively. It's akin to considering long-term consequences before changing one's preferences based on short-term gains.
> Performance Metric: [...] What does performance signify here? How is it quantified? [...] How does one know this intended behavior beforehand?
The performance metric, standard in prior work such as AI Safety Gridworlds [1] (as mentioned in L. 192), is the discounted sum of *true rewards* reflecting the *intended* task goal. This contrasts with the *observed reward*, which might be flawed and exploitable (leading to hacking).
The intended behavior (and thus true reward) is defined by the environment designer [1]; we use the standard definitions for these benchmark tasks. We describe the performance metric of each environment in Sec 4.1. Crucially, MCVL **does not require** the true reward/performance metric for training – it's used purely for *evaluation* to demonstrate that MCVL successfully avoids reward hacking (i.e., maintains high performance on the intended task even when the observed reward is misleading). Declining performance alongside increasing observed returns signals hacking; our results show MCVL prevents this decline.
> Ablation Study: paper [...] does not evaluate the efficacy of the proposed method in mitigating reward hacking. [...] compare ablations between trajectory-level and per-step-level learning [...], what if instead of selectively using modify we conduct random modifications [...]?
Our experiments directly evaluate efficacy by tracking both observed returns and the true performance metric. As noted above, the divergence (or lack thereof) between these *is* the measure of reward hacking [2].
Regarding specific ablations:
* **Trajectory vs. Step-level:** MCVL uses standard step-level RL (DDQN/TD3 policies map states to actions) but incorporates trajectory-level *context* when deciding whether to perform the utility update (*modify*) for a given transition. This decision is the only difference to the baselines we compare to.
* **Random *modify*:** Randomly discarding transitions wouldn't remove all transitions with misleading rewards. MCVL's selective rejection is specifically designed to prevent updates predicted to lower current utility. A more relevant baseline, rejecting updates based on reward prediction error, is included in Figure 4a and performs worse.
* **Other Baselines:** Please also see our response to Reviewer dDMw, where new experiments show that, unlike MCVL, occupancy measure regularization methods, such as ORPO, would struggle to learn the optimal policy while avoiding reward hacking. Section 4.4 and Appendix C also contain further ablations.
> Contribution and Novelty: [...] struggling to understand the novel contribution [...] How does the algorithm benefit RL algorithms, [...] recent RL algorithms [...] operate on trajectory-level samples.
MCVL's core contribution is a novel mechanism to **mitigate reward hacking within existing RL frameworks** by ensuring utility function updates are consistent with the agent's current values.
Its benefit is enhancing the *safety and reliability* of RL agents by preventing them from learning unintended, potentially harmful behaviors when reward functions are imperfect. This is a critical AI Safety problem.
While Decision Transformer and Diffusion RL use trajectories for *sequence modeling* or *planning*, MCVL uses trajectory information to *validate potential updates* during standard RL training. It modifies existing algorithms (DDQN, TD3) to make them safer, rather than being a new trajectory-based learning paradigm itself. After training, the policy remains a standard state-to-action map.
Thank you again for your review and please let us know if you have any further questions or suggestions.
[1] Leike, J., et al. AI safety gridworlds. 2017.
[2] Skalse, J., et al. Defining and characterizing reward gaming. NeurIPS, 2022.
---
Rebuttal Comment 1.1:
Comment: I thank the authors for their response. After going through the authors' rebuttal and response to other reviewers, my concerns regarding the learned modifications and ablations remain.
**Learned Modifications:** The modififcation _modify_ is not learned which raises the question on the efficacy of the scheme. It is not completely known what the new update presents to the agent and how it benefits learning. On the other hand, an update made using the new policy with fresh samples is always better. This is by definition of the policy improvement principle.
**Ablation Study:** Authors added the new ORPO baseline which partly addresses the concern. However, the efficacy of the components utilized in the MCVL framework still remain unadressed. The paper would largely benefit from a toy experiment or two comparing the role of various components in making MCVL effective, for example- a comparison between different modify schemes. This remains as my main reservation for the acceptance of the paper.
Given that my concerns remain and my belief that the modification scheme must possess a learned component for it to be truly effective for reward hacking (and beneficial to the machine learning community), I would like to keep my current score. I thank the authors for their efforts.
---
Reply to Comment 1.1.1:
Comment: We thank the reviewer for their thoughtful rebuttal comment. We appreciate the opportunity to address the remaining concerns:
**Learned Modifications:**
> *modify* is not learned which raises the question on the efficacy of the scheme [...] an update made using the new policy with fresh samples is always better. This is by definition of the policy improvement principle.
We understand the reviewer's perspective on learned components and the policy improvement principle. However, our goal is distinct from standard policy optimization, and our design choices reflect this:
* Our scheme for deciding *when* to modify the utility function is **principled** and, we argue, **optimal** within the specific context of modification-considering agents as defined in our work. These agents aim to maximize their *current* utility function, $U_{VL_t}$. Therefore, they should only accept a modification (leading to $U_{VL_{t+1}}$) if doing so does not decrease the predicted utility of the *resulting future policy*, evaluated according to their *current* objective ($U_{VL_t}$).
* Our method implements exactly this check. Specifically, we compare two values evaluated under the current utility function $U_{VL_t}$: (1) the predicted utility of the future policy resulting from continuing to optimize $U_{VL_t}$, and (2) the predicted utility of the future policy resulting from optimizing the *potential next* utility function $U_{VL_{t+1}}$. Modification proceeds only if the second value is not lower than the first.
* While the final comparison is a deterministic step, it relies critically on **learned components**: the prediction of future policies and the utility function itself are learned.
* We believe that while predicting *modify* directly might offer computational advantages, the core effectiveness in preventing reward hacking stems from the principled check based on the agent's current utility. We consider optimizing computational efficiency a direction for future work.
* The policy improvement principle guarantees optimality concerning the maximization of cumulative returns under the *observed reward function*. However, reward hacking occurs precisely because maximizing the observed reward function can lead to undesirable outcomes not captured by it. Our method deliberately deviates from standard policy improvement when necessary to *prevent reward hacking*, which is a different objective than simply maximizing observed rewards.
**Ablation Studies:**
> The paper would largely benefit from a toy experiment or two comparing the role of various components [...] a comparison between different modify schemes. This remains as my main reservation...
We believe our existing experiments already provide substantial ablation evidence for the key components of MCVL. We will ensure these are emphasized more clearly in the paper.
Specifically, we performed the following ablations:
* **Alternative Modification Rule:** We compared our modification check to an alternative rule based on reward prediction error. This experiment showed that simply discarding modifications based on reward prediction error does not lead to learning optimal non-hacking policy (Figure 4a, "Discard by reward"). This directly addresses the efficacy of our specific modification check compared to a plausible alternative.
* **Ablation of Future Policy Forecasting:** We tested a variant that compared policies before and after each gradient step (instead of forecasting further into the future), which failed to prevent reward hacking (Figure 4a, "Each Step").
* **Ablation of Inconsistent Transition Handling:** We compared our mechanism (removing inconsistent transitions) to an alternative (assigning a large negative penalty reward). The penalty method proved ineffective (Figure 4a, "Punishment"), validating our specific design choice for handling utility inconsistencies.
* **Impact of Utility Function Training:** We studied how varying the amount of initial utility function training affects performance, including an ablation where the initial utility function was random (no training), demonstrating the need for some initial training (Figure 4b, 0 steps).
* **Impact of Inconsistency Check Training:** We investigated the effect of the number of training steps ($l$) for the inconsistency check, including an ablation with no training ($l=0$), showing its necessity (Figure 5a, $l=0$).
We hope this clarifies the reasoning behind our design choices and highlights the existing ablation studies. We will revise the paper to make the justification for our modification scheme and the results of these ablations more prominent.
We thank the reviewer again for their constructive feedback. | Summary: This paper studies how to mitigate reward hacking by considering the change of trajectory utilities. The agent is initially trained in a Safe environment in which exploiting the reward leads to the intended behavior, and then continued in a Full environment with different dynamics/rewards. The paper claims that there will be a drop in terms of the previous utility function if the agent hacks the new environment, and proposes MCVL to detect such a signal and reject the utility update if the reward hacking happens. Experiments are conducted in several grid-world environments and a continuous-control environment. The proposed MCVL can successfully avoid reward hacking, while the conventional RL baseline exploits the misleading rewards.
## Post rebuttal update
The added experiment with ORPO reveals some interesting conclusions about how regularizing occupancy measurement could fail in scenarios where the oracle policy deviates a lot from an initial safe (reference) policy. However, this experiment cannot change the fact that the proposed method makes too strong assumptions about the knowledge of a safe initial utility function.
Claims And Evidence: 1. The paper claims that MCVL iteratively refines the initial coarse utility function, but it seems that the experiment results cannot reflect how the utility function is updated.
2. This work is claimed as the first to demonstrate successful learning of non-reward hacking behaviors in the benchmark environments. I think the authors should compare with other methods to mitigate reward hacking (such as those mentioned in the Introduction and Related works) to better support this claim. Currently, the main results only compare MCVL with ordinary RL, and the results seem unsuprising.
Methods And Evaluation Criteria: The proposed method generally makes sense if an initial aligned utility function is available. This work assumes access to a safe environment and a safe reward function. By optimizing the reward function in the safe environment, the optimal behavior is always the intended behavior. I think the assumption in this setting is strong, since designing reward functions that lead to the exact intended behavior itself is challenging.
Theoretical Claims: Not applicable.
Experimental Designs Or Analyses: 1. In the experimented environments, the intended behavior is always the optimal solution under the reward design in the Safe version, therefore, alternative behaviors that deviate from the intended behavior would lower the initial utility. I am not sure if assuming the knowledge of a Safe version is reasonable for practical applications. I think it would be better to explain how the setting with Safe and Full versions relates to real-world scenarios.
2. MCVL is mainly compared against standard DDQN and TD3 algorithms, and the results show that MCVL successfully avoids reward hacking. This positive result is appreciated, but adding more baseline methods that use different ways to mitigate reward hacking would strengthen the result.
Supplementary Material: I did not review the supplementary material.
Relation To Broader Scientific Literature: This paper is mostly related to AI safety.
Essential References Not Discussed: I cannot point out essential references not discussed as I am not familiar with the topic of AI safety.
Other Strengths And Weaknesses: None.
Other Comments Or Suggestions: None.
Questions For Authors: Please check the previous sections.
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: Thank you for your thorough review and valuable suggestions. We would like to clarify several points and will incorporate these clarifications in the paper.
> The paper claims that MCVL iteratively refines the initial coarse utility function, but it seems that the experiment results cannot reflect how the utility function is updated.
Refining the utility function means the agent continuously updates it using transitions not judged as reward hacking. Our results demonstrate MCVL robustly detects hacking while successfully learning improved non-hacking policies across diverse environments. We welcome specific suggestions for additional experiments or metrics if needed.
> I think the authors should compare with other methods to mitigate reward hacking [...] Currently, the main results only compare MCVL with ordinary RL, and the results seem unsurprising.
The only prior work that is applicable to regular RL environments is ORPO [1]. Direct comparison with it is challenging due to different requirements (it requires known safe policy, uses policy gradient methods, works only with stochastic policies, and requires tricky discriminator tuning).
To make a fair comparison, we evaluated if an ORPO-like objective *could* succeed in our setting. We trained Q-functions for Initial (Safe env), Hacking (Full env, observed reward), and Oracle (Full env, true reward) settings using DDQN. We then checked if any regularization weight $\lambda > 0$ exists s.t. the ORPO objective $F(\pi, \pi_{ref}) = J(\pi, \tilde{R}) - \lambda \cdot D(\mu_{\pi}||\mu_{\pi_{ref}})$ satisfies *both* $F(\pi_{Oracle}, \pi_{Initial}) > F(\pi_{Initial}, \pi_{Initial})$ *and* $F(\pi_{Oracle}, \pi_{Initial}) > F(\pi_{Hacking}, \pi_{Initial})$. Note that just avoiding reward hacking would be trivial assuming a known safe policy. We tested two ways of obtaining stochastic policies required for ORPO: softmax of Q-values and $\epsilon$-greedy ($\epsilon=0.05$), with $\chi^2$ and KL divergences. Occupancy measures were computed with a 1000 policy rollouts.
The table presents percentage of runs such $\lambda$ exists (10 seeds):
|Policy|Divergence|Box Moving|Absent Supervisor|Tomato Watering|Rocks and Diamonds|
|:-|:-|:-|:-|:-|:-|
|Soft-Q|$\chi^2$|0%|0%|0%|0%|
|Soft-Q|KL|0%|0%|0%|0%|
|$\epsilon$-greedy|$\chi^2$|70%|40%|30%|0%|
|$\epsilon$-greedy|KL|40%|50%|0%|0%|
Our results show that frequently no such $\lambda$ exists, indicating ORPO's occupancy measure regularization would likely fail to learn optimal policy without reward hacking for any choice of hyperparameters. Occupancy regularization may struggle when:
1. Oracle policy differs significantly from Initial one (comparable to difference between Hacking and Initial). The experiments in [1] use a modified Tomato Watering environment where the bucket was moved further away. It increases the difference of occupancy between Hacking policy and safe policy.
or
2. High hacking rewards require large $\lambda$, but large $\lambda$ prevents Oracle policy learning (e.g., in Rocks and Diamonds).
In contrast, MCVL consistently achieves the Oracle policy performance in all these environments.
We will add full details of the experiment and additional metrics to the paper.
> The proposed method generally makes sense if an initial aligned utility function is available. This work assumes access to a safe environment and a safe reward function. [...] I think the assumption in this setting is strong [...]
*Crucially, our core requirement is an initial, reasonably aligned utility function, not necessarily a fully specified Safe environment or reward function.* A Safe *environment* can be used to learn the initial utility function, but it can also be learned from other sources like non-hacking random rollouts (as in our Reacher experiment). We use Safe environments in our gridworld experiments because triggering reward hacking in the original environments is too easy. A Safe *reward function* is **not** required for training MCVL; we use it purely for evaluation.
> I am not sure if assuming the knowledge of a Safe version is reasonable for practical applications. [...] explain how the setting [...] relates to real-world scenarios.
As discussed (Lines 203-219), the Safe/Full setup models real-world scenarios like transferring from simulation to real-world and restricted lab environment to not restricted. We also mention that Safe is not required if reward hacking is hard to discover. We will clarify this paragraph and add additional examples including
* Training on simpler tasks with simpler reward design.
* Monitoring agent and removing trajectories with reward hacking.
* Using human demonstrations for initialization.
Thank you again for your valuable feedback. Please let us know if our responses address your concerns and if you have further suggestions.
[1] Cassidy Laidlaw, Shivam Singhal, Anca Dragan - Correlated Proxies: A New Definition and Improved Mitigation for Reward Hacking, ICLR 2025 | Summary: This paper addresses the problem of reward hacking by framing it within the General Utility Reinforcement Learning (GU-RL) framework. The authors introduce trajectory value functions and a mechanism for explicit utility inconsistency detection. Their proposed utility update technique can be integrated into standard value-based methods such as DDQN and TD3, leading to the implementations MC-DDQN and MC-TD3. These methods are demonstrated to be effective in preventing reward hacking in environments from the AI Safety Gridworlds as well as in MuJoCo tasks.
Claims And Evidence: Yes.
Methods And Evaluation Criteria: Yes.
Theoretical Claims: Yes.
Experimental Designs Or Analyses: Yes.
Supplementary Material: Each part, and especially implementation details.
Relation To Broader Scientific Literature: The key contributions of the paper connect closely to several strands of prior research in reinforcement learning and AI safety, especially, General Utility Reinforcement Learning and Reward Hacking and Specification Gaming.
Essential References Not Discussed: No.
Other Strengths And Weaknesses: I find the problem addressed in this paper very interesting, and the proposed approach is reasonable. However, the method currently has some limitations—for instance, it assumes access to rollouts from the true environment transition model, which significantly restricts its applicability. This means that the method can typically only be applied when an explicit transition model is available or when the simulator has been modified accordingly. The paper does acknowledge these limitations.
Other Comments Or Suggestions: 1. The experiments in this paper are primarily conducted under the assumption of access to rollouts from the true environment transition model. Although the authors mention that considering approximate transition models is a future direction, I am curious: How robust is MCVL to inaccuracies in the learned transition model? For example, if the learned model deviates slightly from the true environment dynamics, can the forecasting mechanism still reliably detect utility inconsistencies?
2. Is the choice of rollout length (h) for policy forecasting critical? Could the authors elaborate on how sensitive the performance is to different values of h? Is there a principled method to set this parameter, or does it require extensive tuning for each environment?
3. The paper demonstrates the effectiveness of MC-DDQN in four discrete action-space environments, and MC-TD3 on the MuJoCo Reacher task (continuous action space). Given that Reacher is a relatively basic task and the experimental data between these two settings are imbalanced, would it be possible to test one or two additional MuJoCo tasks to further showcase the performance of MC-TD3?
Questions For Authors: See Suggestions.
-----
**Updated Review:** Thank you for the clarification. I acknowledge the novelty of the proposed idea. However, I regret that the current evaluation is limited to custom-designed environments, and no additional experiments were provided to test generalizability and the sensitivity of h. This constraint notably limits the applicability of the method to broader benchmarks. I suggest clearly stating this as a limitation in the final version.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you very much for your thorough review and valuable suggestions. We are happy to answer your questions and will incorporate all answers in the final manuscript.
> How robust is MCVL to inaccuracies in the learned transition model? For example, if the learned model deviates slightly from the true environment dynamics, can the forecasting mechanism still reliably detect utility inconsistencies?
Our method is robust to noisy transition models. We only use the transition model to compare trajectories produced by two policies. The only requirement for our method to work correctly is that rollouts where the policy executes reward hacking behavior have lower utility than the rollouts of the policy that does not hack rewards. To verify this empirically we are now running an additional experiment. There we add noise sampled from $\mathcal{N}(0,1)$ to each *one-hot* encoded observation produced by the transition model to simulate a situation where the transition model is inaccurate. We ran this experiment in the Box Moving environment and our method still obtains optimal true reward while avoiding reward hacking. We will include this experiment in the paper.
> Is the choice of rollout length (h) for policy forecasting critical? Could the authors elaborate on how sensitive the performance is to different values of h? Is there a principled method to set this parameter, or does it require extensive tuning for each environment?
We provide descriptions of all hyperparameters and discuss how they can be chosen in Appendix G. Here is what we write about rollout length (h):
“This parameter controls the length of the trajectories used to compare two predicted policies. The trajectory length must be adequate to reveal behavioral differences between the policies. In this paper, we used a fixed, sufficiently large number. In episodic tasks, a safe choice is the maximum episode length; in continuing tasks, a truncation horizon typically used in training may be suitable. Computational costs can be reduced by choosing a smaller value based on domain knowledge.“
The performance of the algorithm is not sensitive to $h$, as long as reward hacking occurs within $h$ steps. Extensive tuning is not required as this parameter can be set to maximum episode length.
> Would it be possible to test one or two additional MuJoCo tasks to further showcase the performance of MC-TD3?
Unfortunately, existing MuJoCo tasks are not directly applicable because of our evaluation protocol. It requires each environment to have different observed and true rewards to measure episode returns and performance metric respectfully. To make the experiment meaningful, both rewards need to be carefully curated, plausible and explainable. Unfortunately, designing new environments is not simple and beyond the scope of this work. We establish new state-of-the-art performance on existing environments and we agree that designing more complex environments for evaluation of reward hacking is an important direction of future work. Please note that our method is applicable to standard RL environments, and special environments are merely required to evaluate the performance of any algorithm that mitigates reward hacking.
Thank you again for your valuable feedback! Please let us know if you find our responses satisfactory and if you have any further suggestions. | null | null | null | null | null | null |
The Harder Path: Last Iterate Convergence for Uncoupled Learning in Zero-Sum Games with Bandit Feedback | Accept (poster) | Summary: This paper improves the lower bound for learning matrix games with bandit feedback and last-iterate convergence in the uncoupled setting from $O(T^{-1/2})$ to $O(T^{-1/4})$. The authors then propose a black-box reduction from an algorithm with the so-called “output convergence” to the last-iterate convergence, though still requiring the computation of average policies. The authors then try to fix this drawback by proposing the regularized mirror descent algorithm and a variant of it by using the doubling trick.
Claims And Evidence: I think some claims in this work might not be technically rigorous. Please see the weakness part below for details.
Methods And Evaluation Criteria: Yes.
Theoretical Claims: I did not check the correctness of the proof details.
Experimental Designs Or Analyses: Not applicable.
Supplementary Material: I did not check the appendix.
Relation To Broader Scientific Literature: The theoretical findings are new. But I am still concerned about its technical values. Please see the weakness part below for details.
Essential References Not Discussed: No.
Other Strengths And Weaknesses: **Weakness**
1. **Theoretical Results**: In the abstract, the authors claim that they propose two algorithms to achieve the optimal rate of $O(T^{-1/4})$. However, I think this is a bit misleading and even a bit overclaimed.
* In Algorithm 1, if I understand correctly, the key insight is that an algorithm with “output convergence” can be translated into an algorithm with last-iterate convergence. Nevertheless, I think there is no fundamental difference between the definitions of “output convergence” and the average-iterate convergence. If an algorithm has the average-iterate convergence, then the output sequence $(\hat{\mu}^t, \hat{\nu}^t)$ can be chosen as $(\hat{\mu}^t, \hat{\nu}^t)=(\sum_{1\le i\le t} \mu_i, \sum_{1\le i\le t} \nu_i,)$, which is guaranteed to converge. This leads to at least two downsides of Algorithm 1 in this work: the two players are not fully uncoupled and it is still required to compute the average policy profile, which are also noted by the authors at the end of Section 6.
* To tackle the above issues, the authors propose Algorithm 2, which is indeed fully uncoupled and does not require computing the average policy profile. However, its convergence guarantee is not anytime. To further fix this issue, the authors consider equipping their Algorithm 2 with the common doubling trick, at the cost of making the algorithm coupled again.
Therefore, I have to say I do not think that the authors really establish an algorithm that has anytime last-iterate convergence and operates in a truly uncoupled manner, like the algorithm in [1]. Besides, [1] establish a high-probability convergence guarantee while the definition of the $\ell^p$ convergence in this work only permits the convergence in expectation.
2. **Presentation**: Some parts of this work seem to lack sufficient explanations. Lemma 6.1 is a key lemma in this work and I would suggest the authors give more discussions and the proof sketch (if possible) in the paper. Besides, on the RHS of Line 302-329, the authors just introduce the design of the “regularized mirror descent” but without giving any discussions or explanations about this. Why can this kind of design enable a convergence rate of $O(1/t)$ for the Bregman divergence? Further, what is the intuition behind the LHS of Line 336 and 338? Since $\mu^0$ is a uniform distribution, I think the operation on Line 336 is equivalent to the following FTRL-style update?
$$
\mu^t\in \arg\min_{\mu} –(1-\tau\eta^t)\langle \nabla \psi(\mu^{\tau,t}), \mu \rangle+ \psi(\mu)
$$
[1] Cai et al. Uncoupled and Convergent Learning in Two-Player Zero-Sum Markov Games with Bandit Feedback. NeurIPS, 2023.
Other Comments Or Suggestions: Please see the weakness part above.
Questions For Authors: Please see the weakness part above.
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: We thank reviewer TkNJ for taking the time to review our article and for the clarity suggestion. We address the concerns below.
>Nevertheless, I think there is no fundamental difference between the definitions of “output convergence” and the average-iterate convergence.
We preferred to state the results and Lemma 6.1 under the assumption that $\mathcal{A}$ has a convergence of its output, whether it comes from averaging (as in the EXP3-IX algorithm that we use) or other means. We preferred to state it this way, as the output could also come from a reweighted average for example, or by sampling uniformly at random a policy among the ones played.
>Therefore, I have to say I do not think that the authors really establish an algorithm that has anytime last-iterate convergence and operates in a truly uncoupled manner, like the algorithm in [1].
While the anytime algorithms require a common seed and are not uncoupled in the same sense as in [1], they match the definition of uncoupledness that is required for the lower bound stated in Theorem 5.1 to hold. This lower bound relies on the absence of communication \textit{between} the iterations and does not exclude an agreement before the start of the iterations. One of the main points of the two anytime algorithms was especially to characterize the minimax rate.
Furthermore, we would argue that the main weakness of Algorithm 2, the lack of anytime guarantees, is not problematic in practice. One of the main applications of last-iterate is to avoid the averaging of complex representation as explained in line 32-right, and the anytime convergence is not important for this matter.
>Lemma 6.1 is a key lemma in this work and I would suggest the authors give more discussions and the proof sketch (if possible) in the paper.
The paragraphs above Lemma 6.1 provide the key point behind the lemma and can be seen as a proof sketch, we will add more quantitative arguments and re-organize the section to make it more apparent.
>Besides, on the RHS of Line 302-329, the authors just introduce the design of the “regularized mirror descent” but without giving any discussions or explanations about this. Why can this kind of design enable a convergence rate of $\mathcal{O}(1/T)$ for the Bregman divergence?
We could add that the “regularized mirror descent” algorithm can roughly be seen as applying a regular mirror descent with the regularized operator $F_\tau$, hence the name, the two-steps update making the computation and the proof easier. This regularization makes the operator strongly monotone. Similarly to how strong convexity accelerates the convergence to the minimum, strong monotonicity makes the mirror descent convergent at a rate $\mathcal{O}(1/T)$. We propose to add a proof sketch of Lemma 7.1 to explain how we obtain this result.
>Further, what is the intuition behind the LHS of Line 336 and 338? Since
$\mu^0$ is a uniform distribution, I think the operation on Line 336 is equivalent to the following FTRL-style update?
Indeed, the two updates are equivalent. However, the intuition between Line 336
$$\mu^{t} \gets argmin_{\mu_\in\Delta_A} (1-\tau\eta^t)KL(\mu,\mu^{\tau,t}) + \tau\eta^t KL(\mu,\mu^0)$$
is to regularize the iterates toward the uniform, to "stabilize" the algorithm and allow the convergence. This specific regularization is not normally present in FTRL and only appears in the above equation because of the $(1-\eta^t\tau)$ factor.
---
Rebuttal Comment 1.1:
Comment: I appreciate the detailed responses of the authors. Nevertheless, some of my key concerns remain unsolved:
**Algorithm 1: “Output Convergence” and Average-iterate Convergence.**
I agree that the definition of the “output convergence” considered in this work does not restrict on how the output convergent policy is generated (either by a reweighted average or "sampling uniformly at random a policy among the ones played"). Nevertheless, note that the original motivation of establishing algorithms with last-iterate convergence guarantees in the common literate is exactly to avoid *computing average policy* or *sampling a policy from the policy set* generated in the running of the players' algorithm, as this might induce additional (or even prohibitively large) computation or storage overhead. Therefore, I do not think there are fundamental differences between the definitions of “output convergence” and the average-iterate convergence, and my concern remains unsolved.
**Algorithm 2 and 3.**
* **Lacking anytime guarantees**: I also agree that lacking anytime guarantees - the downside of Algorithm 2 in this work - might not be a serious problem when implementing the algorithms in practice. Nonetheless, from the theoretical point of view, the improvement on the convergence rate of Algorithm 2 comes from more like at the cost of sacrificing some advantages of the algorithm in [1], which thus makes Algorithm 2 less appealing and somewhat limits the technical values of the algorithmic design and the results in this work.
* **Not truly uncoupled**: Similarly, I do concur that requiring a common seed between the two players (the downside of Algorithm 3 in this work) might also not be a critical problem that hinders the implementation of the algorithms in practice. However, again, this makes the improvement on the convergence rate of Algorithm 3 come from more like at the cost of sacrificing some good features of the algorithm in [1], and limits the technical values of the algorithmic design and the results to some extent.
* **Convergence in expectation**: Besides, I do not seem to find the responses by the authors to my concern that the algorithms in this work only have expected convergence, while the algorithm in [1] has a high probability convergence guarantee.
Overall, I would definitely support the acceptance of this work, if there were no works such as [1]. However, currently, given the algorithm in [1], the aforementioned downsides of the algorithms in this work really prevent me from supporting the acceptance of this work, though the rates indeed have been improved in some sense.
---
Reply to Comment 1.1.1:
Comment: We again thank reviewer TkNJ for the response.
>Algorithm 1: "Output convergence" vs. "Average-iterate convergence":
It seems from your response that we agree on this matter. The output convergence assumption used in Algorithm 1 follows, in the case of EXP3-IX as in many other cases, from the average-iterate convergence of $\mathcal{A}$; the term "output convergence" is not used to hide this fact, but only to be slightly more general. This makes Algorithm 1 only relevant for matching the lower bound, and is the issue stated on Lines 295-300 (right):
"One of the main points of the last-iterate convergence is to avoid the computation of the average necessary in the regret-based algorithm. Not only is this computation still required here (the output of EXP3-IX is an average), but also needs to be done at almost every iteration."
>Algorithm 2 and 3:
We understand your concerns about the lack of anytime guarantees of Algorithm 2 and the common seed of Algorithm 3 as we state in the papers, as we do not strictly improve the results of [1]. Nonetheless, these algorithms are the only ones to match up to logarithmic factors the $\mathcal{O}(t^{-1/4})$ lower bound and characterize the optimal rate, which alone makes the results interesting in our opinion.
>Convergence in expectation
We apologize for not responding to this part, as we saw it as a statement of a weakness mentioned for example in Table 1 of the paper, which we therefore agree with. Note that, as pointed out by Reviewer eajt, [1] provides in Appendix C a rate of $\mathcal{O}(t^{-1/6})$ in expectation, which we will add to this table. | Summary: This paper studies the last-iterate convergence rates of uncoupled learning dynamics in two-player zero-sum games with bandit feedback. One of the main contributions of the paper are lower bounds for uncoupled learning dynamics: (1) $\Omega(t^{-1/(2+p)})$ lower bound for any-time $\ell_p$ last-iterate convergence rates when $p \in (0,2]$; and (2) $\Omega(t^{-1/4})$ lower bound for $p \ge 2$. Then the authors propose two algorithms for the problem. The first one is a general framework that could transform the guarantee of output sequence to last-iterate convergence by simultaneously exploring or exploiting. By appling EXP3-IX, this framework gives $\tilde{O}(t^{-1/(2+p})$ last-iterate convergence rates. The drawback of this approach is (1) it is not fully uncoupled as it requires shared randomness; (2) it still requires iterate-averaging in execution. The second algorithm uses regularization and achieves $O(t^{-1/4})$ $\ell_2$ last-iterate convergence. However, the convergence is not any-time as the time horizon is required to choose the step size. A doubling trick fixes this issue but introduces synchronization again just like the first algorithm.
Claims And Evidence: Yes. The claims are supported by proofs.
Methods And Evaluation Criteria: N/A
Theoretical Claims: I checked the proofs for the lower bounds and the other proofs also look fine to me.
Experimental Designs Or Analyses: N/A
Supplementary Material: N/A
Relation To Broader Scientific Literature: This paper studies the last-iterate convergence rates of uncoupled learning dynamics in two-player zero-sum games with bandit feedback. The paper's results contribute to the broad line of research in learning in games, which has recently been applied in machine learning. More specifically, uncoupled learning dynamics in games have been studied recently: [1] gives the first algorithm with $O(t^{1/8})$ high-probability last-iterate convergence and $O(t^{-1/6})$ expected last-iterate convergence; [2] generalizes this result to monotone games. The current paper provides the first lower bounds for the problem. The paper also offers new algorithms with improved convergence rates. Although strictly speaking, they are not fully uncoupled,
[1] Cai, Yang, Haipeng Luo, Chen-Yu Wei, and Weiqiang Zheng. "Uncoupled and convergent learning in two-player zero-sum markov games with bandit feedback." NeurIPS 2023
[2] Dong, Jing, Baoxiang Wang, and Yaoliang Yu. "Uncoupled and Convergent Learning in Monotone Games under Bandit Feedback." arxiv preprint, 2024
Essential References Not Discussed: I think related works have been substantially discussed. The only comment I have is regarding the results in [1]. For uncoupled learning in zero-sum games, there are two results in [1] for last-iterate convergence rates measured by the duality gap: (1) $O(t^{-1/8})$ high-probability bound and (2) $O(t^{-1/6})$ bound in expectation. This paper discusses the first one but not the second one. Since the current paper focuses on last-iterate convergence in expectation, comparing the second bound in [1] would make the discussion more complete.
Other Strengths And Weaknesses: This is a good paper. The presentation is clear and easy to follow, and the authors thoroughly explain the high-level ideas.
This paper provides the first lower bounds for uncoupled learning under bandit feedback and separate bandit feedback with full gradient feedback. These results are very interesting.
The algorithms proposed in the paper are also interesting. In particular, I appreciate that the authors distinguish "any-time" last-iterate convergence from convergence when the time horizon $T$ is known. Clearly, the former is stronger and the "real" guarantee one seeks for last-iterate convergence. The authors do a good job of clearly stating the weaknesses of both of their algorithms, which I appreciate. As the authors admit, both algorithms fail to achieve the any-time last-iterate convergence in a fully uncoupled way, yet they could yield $O(t^{-1/4})$ convergence if we allow some shared randomness.
Other Comments Or Suggestions: Some equations may be explained in more detail. See my question.
Questions For Authors: 1. Could you explain how to derive line 682 from line 679-680? Maybe it is trivial, but I think some explanation would be helpful for the readers.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We thank Reviewer eajt for the review and for pointing out a result that we missed in one of our references.
>I think related works have been substantially discussed. The only comment I have is regarding the results in [1]. For uncoupled learning in zero-sum games, there are two results in [1] for last-iterate convergence rates measured by the duality gap: (1) $\mathcal{O}(T^{-1/8})$ high-probability bound and (2) $\mathcal{O}(T^{-1/6})$ bound in expectation. This paper discusses the first one but not the second one. Since the current paper focuses on last-iterate convergence in expectation, comparing the second bound in [1] would make the discussion more complete.
Indeed, this $\mathcal{O}(t^{-1/6})$ result in expectation is an unhighlighted result of [1] that we missed and that should appear in Table 1. Their result is stated for the $\ell^1$ norm in Theorem 4 of Appendix $C$, but a slight change to the proof seems to make it hold for the $\ell^2$ norm.
>Could you explain how to derive line 682 from line 679-680? Maybe it is trivial, but I think some explanation would be helpful for the readers.
The link between the two lines is relatively direct computation-wise, but it is far from obvious and deserves more explanation. The internal randomness $\omega$ of the two players is independent of the game by construction, which implies that $\mathcal{D}(P_0^{\omega},P_{\theta^T}^{\omega})$ is $0$. The same can be said of $a^t|z^{t-1}$ for any $t$: the policy $\mu^t$ of the min-player is predictable with respect to $(\sigma(z^t))$, and the action $a^t$ is sampled from $\mu^t$ independently from the past. This implies that $\mathcal{D}((P_0^{a^t|z^{t-1}},P_{\theta^T}^{a^t|z^{t-1}})$ is also $0$ for all $t$.
Finally, the terms of the sum come from developing the observation of the min-player given the predictable policy $(1/2+\delta^t,1/2-\delta^t)$ of the opponent, as explained in line 189-right of the main paper.
These explanations will be added to the proof. | Summary: The paper aims to improve the upper and lower bounds in Last Iterate Convergence for Uncoupled Learning in Zero-Sum Games with Bandit Feedback
Claims And Evidence: The evidence is fairly clear, but I will provide a detailed explanation of my questions in the following sections.
Methods And Evaluation Criteria: N/A
Theoretical Claims: As I mention later in my review, I would like to congratulate the authors on their honest and transparent presentation of results. With that in mind, I have a few questions to ensure we are on the same page:
1. Why are we attempting to minimize communication if we allow the loss function to be designed with a common regularization term (with a shared regularizer weight)? Could these two characteristics be relaxed simultaneously?
2. While I conducted a careful proof-reading, I did not have time to fully grasp the necessity of the shared random variable seed in communication. Why can’t the incoming p^i play the role of u? I am trying to understand why we cannot instead leverage arbitrary information from strategies in the sequence.
3. In lines 236–243, there is a reference to an information-theoretic old-fashioned result. Could you elaborate on this? Specifically, why does allowing observation enable us to estimate each matrix entry? I assume the matrix size is at least O(t^{-1/2})—could you provide a more detailed explanation? I found this particularly interesting.
4. One aspect that initially confused me was the lower bound. In the proof in the Appendix, you exclusively examine three different games, rather than a random matrix with Bernoulli entries. What exactly is meant by “Bernoulli” in the main text? Was this an earlier idea, or am I missing something in the problem formulation?
Experimental Designs Or Analyses: It is an excellent paper that does not require experiments.
However, what I would like to see clarified is whether the paper models the behavior of a game-learning process between two independent agents or if it simply describes a collaborative uncoupled dynamics algorithm that will be employed in one server.
Supplementary Material: Yes, I have read the supplementary material in full detail.
Relation To Broader Scientific Literature: The paper achieves better learning rates than those found in the literature.
Without having reviewed the results of Cai and Dong on zero-sum Markov games, could you explain how their baseline translates to the stage-game setting? The reason I ask is that Markovian noise introduces additional stochasticity, and I would like to determine whether this improved learning rate can be obtained “for free” in this setting. Finally, I would also like to know whether the authors believe a similar result could be achieved using standard gradient descent or optimistic gradient descent under bandit feedback, rather than requiring full feedback.
Essential References Not Discussed: I would like to request a comment and a more detailed explanation regarding lines 195–207.
Specifically:
1. Is there any existing literature on the concept of passing bits to others through artificial choices? If so, I would appreciate references or further discussion on this point.
2. I would also like to better understand an aspect related to the notion of uncoupled dynamics. Based on the authors’ description, it is unclear whether the step size is a common constant step size, a varying common step size, or if different step sizes have been collaboratively chosen to shape the dynamics—or if they truly remain “uncoupled.”
3. Why exactly do we want an uncoupled algorithm rather than the even more general notion of independent play? Does this choice primarily aid parallelization, or does it serve as a better model of real-world scenarios?
Other Strengths And Weaknesses: For me, the most interesting aspects of this paper are:
(a) The honesty in the statements. I truly commend one or more of the authors for their transparency in presenting the results.
(b) The structured distinction between different iterate types. While it may not necessarily be the most accurate modeling approach, I appreciate the authors’ effort to clearly differentiate between last-iterate, average-iterate, output-iterate, and how these relate to asymptotic vs. general results.
As a faculty member, if all the papers I reviewed were of this level of quality, I would genuinely enjoy reviewing even more.
Other Comments Or Suggestions: Clarification Requests & Suggested Revisions
Page 19, Line 1038
• Why is there a norm applied to the KL-divergence? Could you clarify the reasoning behind this?
Page 18
• In the secondary order bound, please clarify whether the negative third-order term pertains specifically to exponential gradient descent (for the case of the entropy regularizer).
• Initially, I attempted to prove this for any regularizer, but I do not believe it holds for \ell_2 regularization. Am I mistaken?
• Are there other regularizers (e.g., Tsallis) that satisfy the property \nabla h^3 < 0?
• If the claim is indeed correct for all regularizers, please explain why.
Page 17
• I would appreciate a more detailed explanation of why the property \equiv holds in this context.
• Personally, I prefer to express mirror descent using the constrained optimality condition inequality. While this does not change the correctness of the algorithm, I would appreciate it if you could state a lemma indicating whether this applies only to entropy regularization or to all regularizers.
Page 16
• This part was quite confusing to me. In Page 16, it is evident that the authors follow a constant-sum formulation rather than zero-sum. While this does not impact the dynamics, I would like to understand:
• (a) Why was this choice made?
• (b) Why does F_\tau have 1-L for the y-player, whereas the F operator has -L? These two seem inconsistent—could you clarify?
Page 15
• In the last three inequalities, I believe that we should have B_t \log B in the pre-last summand (first line).
• I would recommend multiplying all summands by 2, and for the first one, multiplying by \sqrt{t} (I believe this might be a typo).
Proofreading Issues & Formatting Corrections
• Line 797: Missing closing parenthesis.
• Line 650: Should be |\delta^t/3| instead of the current notation.
• Line 640: There are two colons instead of one.
Page 13
• The paper uses the additive KL divergence property. Could you please rewrite this section?
• The issue is that \mathbb{E}_0 does not refer to P_0, but rather to P_0^{z^T}.
• As a result, when summing over the history, there are redundant elements.
• I am not suggesting that it is incorrect, but I would appreciate a detailed response in your replies to verify that there are no proofreading issues here.
Line 689
• Please include one explanatory sentence for the reader, clarifying which terms are zero and why in this line.
⸻
Final Notes
I appreciate the effort that has gone into this paper. The above points focus on improving clarity, correctness, and presentation to ensure that all arguments are fully transparent and well-supported.
Would you be able to address these concerns in your response?
Questions For Authors: Questions and Clarifications for Discussion
I would greatly appreciate it if you could provide responses to the questions I have posed in the previous sections.
One of the most critical aspects of the paper is the discussion surrounding learning-output-last-iterate iteration. Having served on multiple review committees, I have often encountered disputes between different models and interpretations of these notions.
Let’s see if I have understood correctly:
• A sequence is called learning if its past completely determines its predictability.
• Consider Rock-Paper-Scissors as an example. We say that a sequence is learning if its behavior depends on observations from previous rounds.
• If the distribution is stationary, then it is also a learning sequence, correct?
• In other words, any sequence that can be computed based on past information qualifies as a
learning sequence.
Thus, the natural question arises:
##What constitutes a non-learning sequence?##
Let’s now examine a classic question that often arises in the algorithms community:
• Suppose I compute a last-iterate sequence of extra-gradient updates inside a subroutine.
• However, in the main function, I output the time-averaged sequence as my “actual”
sequence.
If I understood correctly, the paper attempts to reconcile this distinction using the output and last-iterate sequence framework.
• That is, \hat{\mu}_t represents the averaged sequence, while \mu_t represents the last-iterate sequence.
• Is this the correct intuition?
Defining the $played$ Distribution in a Bandit Setting (lines 192)
What exactly determines the distribution being $played$?
• In a bandit setting, how do we rigorously define this distribution?
• Unlike in a centralized version of bandit game, we do not submit our mixed strategy to an authority that then returns a bandit feedback element, right .
• Instead, in a bandit setting, we simply announce pure strategies.
Could you clarify these details? I appreciate the effort you have made to formalize these distinctions—even if we later find issues with the model during the rebuttal discussion, your approach to structuring these ideas is commendable.
⸻
Final Request: Intuition Behind the Doubling Modified Trick
While I was able to follow and learn a lot from this paper, I found the method for the doubling modified trick highly unintuitive.
Could you provide a more detailed intuition behind:
1. How this method was chosen (designed)?
2. Why it works?
This was the part of the analysis that had the least intuition regarding the computations, and I would greatly appreciate further clarification.
P.S. A satisfactory response to the questions I’ve raised—especially regarding the distinctions from prior work, the modeling clarity around bandit feedback and iterate definitions, and the theoretical subtleties—could lead me to raise my score to “Strong Accept”.
P.S.2 I may have asked this already, but I was genuinely surprised that the authors do not require any form of \epsilon-greedy exploration.
One possible explanation is the clever anchoring step involving the term
$(\tau\cdot \eta_t) D_{\mathrm{KL}}(m, m_0)$,
but I’d really like to understand how the analysis successfully avoids the need for exploration noise.
• Is this avoidance enabled by the negative third derivative of the regularizer (e.g., $\nabla^3 h < 0$)?
• Or is there another mechanism or structural property of the setup that removes the need for explicit exploration? When is the assumption of the extrapolation necessary and when not?
A short clarification on this point would be greatly appreciated, as it’s quite non-standard and technically impressive—if valid.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We would like to express our sincere gratitude to Reviewer U4sa for their very comprehensive and constructive feedback. We appreciate the encouragement, particularly the acknowledgement of our "honest and transparent presentation of results".
We prepared a response for all of the questions, but we were greatly limited by the 5000 characters limit. We will only be able to submit (once) the response to the rest of the questions (especially some of the longest replies) after the reviewer's response.
>Q1
For our analysis to hold, the regularization term currently needs to be the same for both players for Algorithm 2. As it is a hyper-parameter, we consider this requirement to be substantially weaker than actual communication.
>Q2
The reason we use this shared seed that allows the sampling of a shared Bernoulli with parameter $p^i$ at each iteration, and not a Bernoulli directly is to make sure the two players have exactly the same sample $B^i$. The two players indeed need to explore and exploit simultaneously, as the exploitation (i.e. playing the output of $\mathcal{A}$) of one would otherwise bias the exploration of the other: the guarantees of $\mathcal{A}$ only holds if both players play the algorithm over the relevant iterations.
>Q3
If at each iteration $i$, the actions $a^i$ and $b^i$ are observed by the two players, then, for any entry $(a,b)$ of the matrix, the expected value of this entry can be estimated by averaging all of the observations for which $(a^i,b^i)=(a,b)$. Assuming that each action profile is played on average $\Omega(t)$ times over $t$ iterations as $t$ scales to $+\infty$, then each entry of the matrix can be estimated with a precision of $\tilde{\mathcal{O}}(t^{-1/2})$ using Hoeffding inequality. Suppose each player computes its minimax strategy associated with the resulting estimated matrix (which can be done "offline", without observations) and plays it at each iteration. It can then be shown that the exploitability gap scales with the precision of $\tilde{\mathcal{O}}(t^{-1/2})$.
>Q4
As explained in line 620, the proof also uses random matrices with Bernoulli entries, the entries of the matrix $M^\epsilon$ being the parameter of these Bernoulli. The confusion might come from lines 647-669, where we do the computation directly using this matrix, as the exploitability gap is defined for the expected loss matrix. We will add a sentence to clarify.
> Markov games question
We are not sure we fully understand the question. We assume that "learning rate" refers to our guarantees. While their second algorithm reduced to a single stage seems to be similar to their first algorithm on matrix games, the opposite transformation (transforming an algorithm that works on matrices into an algorithm that works on Markov games) is not trivial. In particular, their approach relies on estimating the value associated with each state.
>gradient descent question
Any mirror descent algorithm (including gradient descent) would not converge in general. In particular, if a fully mixed equilibrium exists, then the divergence between this equilibrium and the iterates is non-decreasing on expectation at each iteration.
We think optimistic gradient descent would not work, but we think optimistic multiplicative weights update (which relies on the Shannon entropy instead) could if we use two different rates for the intermediate iterates and the actual iterates. We are not sure whether the optimal rate of $\mathcal{O}(t^{-1/4})$ is attainable with this method and if an additional problem-dependent constant would be necessary.
>page 19
Typo
>page 18
Indeed, this property does not hold for any regularizer, although it works for the most common ones, such as Shannon, Tsallis or the log-barrier (we only get $\nabla h^3 \leq 0$ for the $\ell_2$ regularizer).
>page 17
It follows the fact that the gradient of the minimizer of a convex function belongs to the opposite of the (here constant) normal cone associated with this point and the constraints.
>page 16
(a) This choice was made as Lemma C.1 relies on the estimated loss being non-negative.
(b) typo
>page 13
Each term $t$ is the expectation of the same KL divergence with $\theta^{t-1}$ taken under $P_0^{z^{t-1}}$. As $z^{t-1}$ is the only random variable in each term of the sum, this is the same as taking the expectation under $P_0$ directly.
>line 689
See reviewer 3.
> Questions for authors
While a learning sequence is predictable using the internal randomess and the past actions and reward, a non-learning sequence could be based on the unknown entries of the matrix $L$, for example, which would go against the lower bound.
The next intuition is correct
In this setting, it is easier to consider that we announce our mixed strategy to an authority, which then returns both the sampled action and the associated reward. Otherwise, the convergence would indeed fail with the pure strategies.
---
Rebuttal Comment 1.1:
Comment: I may have asked this already, but I was genuinely surprised that the authors do not require any form of \epsilon-greedy exploration. One possible explanation is the clever anchoring step involving the term $(\tau\cdot \eta_t) D_{\mathrm{KL}}(m, m_0)$, but I’d really like to understand how the analysis successfully avoids the need for exploration noise.
I would appreciate a more mathematically precise clarification regarding the avoidance of greedy exploration
---
Reply to Comment 1.1.1:
Comment: There is again a hard limit of one response with 5000 characters. We include below the responses that were missing from the rebuttal, as it was not possible to give a complete answer to all of the questions within this limit. Despite this issue, we thank once more Reviewer U4sa for asking many relevant questions.
>Greedy exploration
The algorithm relies on an estimate of the loss, based on importance sampling. As this estimator is unbiased, it only appears through the "variance" term $\mathcal{D}(w^t,\tilde{w}^{\tau,t+1})$ that appears in the analysis (Lemma 7.1), which can be shown to be in expectation at most
$$(\eta^t)^2\sum_{i=1}^{A+B} (w^t_i\nabla^2 h(\overline{w}^t_i))^{-1}$$
using Taylor, for some $\overline{w}^t_i$ between $w_i$ and the unprojected $\tilde{w}^{t,\tau}_i$. With a gradient descent (relying on the $\ell^2$ regularization), $\nabla^2 h$ is constant equal to $1$, and this term is not bounded as $w_i^t$ approaches zero. Some $\epsilon$-greedy exploration would limit this term to $(A+B)(\eta^t)^2/\epsilon$, but degrade the last-iterate guarantees.
Instead, we rely on a regularization that is more suited to the problem. The Shannon entropy satisfies both $\nabla^2 h(w_i^t)=1/w_i^t$ and, as you mentioned, $\nabla^3 h\leq 0$, which guarantees using the non-positivity of the estimate of the opposite of the loss and the definition of $\tilde{w}_i^{t,\tau}$ that $\nabla^2 h(\overline{w}_i^t)\geq 1/w_i^t$. The $w$ dependence in the upper bound of the divergence then disappears. Note that this works for any regularizer that satisfies $\nabla^2 h(w_i)=\Omega(1/w_i)$ and $\nabla^3 \leq 0$, this also includes Tsallis entropy and the log-barrier.
>Doubling trick
The main idea behind this method is that, in contrast to the regret setting, using a doubling trick with a hard reset is not possible because of the last iterate constraints. For this reason, instead of suddenly switching to the new instance with a reduced regularization, the algorithm keeps the previous last iterate and plays a mix between the former and the new instance. It is then able to progress with the smaller regularization while still playing a good policy on average, thanks to this former best iterate being played with an initial way higher probability. As the new instance progresses, we are able to decrease this probability and thus focus on the new (asymptotically better) instance.
>Passing bits
We are not aware of references on this point in this precise context. In a multiplayer multi-armed bandit problem in which collision occurs if two players choose the same arm, [1] proposes a protocol of communication between the agents relying on these collisions.
One method could be the following, for player 1 to pass a bit of information to player 2:
-A parameter L is fixed to be the same for both players.
-To pass a $1$, player 1 plays the first action $L$ times, then the second $L$ times, and so on. To pass a $0$, he plays only the first action $A\times L$.
-The second player plays its action uniformly and keeps track of the losses of each batch of $L$ iterations separately. If for a given action, the distribution of losses is statistically different between two batches, the output is 1, otherwise, it is 0.
>Step size
For simplicity of the analysis and of the presentation, a common step size has been chosen, but this is not mandatory: the two players can take different step sizes, and the algorithm will enjoy the same guarantees up to some constant factor. The only requirement for the rate to remain the same is that the step size is higher than $1/(t\tau)$ asymptotically for any player, as otherwise, the regularization is too strong and prevents any substantial learning.
>Uncoupled algorithm
One of the main reasons behind the study of uncoupled algorithms is that it indeed better models the way a practical algorithm would learn an actual game. We think that learning how to play the game using the feedback of a profile of actions, rather than with each action independently, is fundamentally slower as the size/complexity of the game increases, as it amounts to learning a matrix (of size $A\times B$) rather than learning two vectors (of size $A+B$).
[1] Etienne Boursier, Vianney Perchet, SIC-MMAB: Synchronisation Involves Communication in Multiplayer Multi-Armed Bandits, NeurIPS 2019 | Summary: This paper studies a zero-sum matrix game in which two players repeatedly select stochastic policies, sample actions, and receive stochastic losses—without access to the underlying payoff matrix—that depend on their joint actions. The authors aim to develop an uncoupled algorithm that independently controls each player without explicitly observing the other player’s actions, while ensuring last-iterate convergence of the players' policies to a Nash equilibrium.
The paper establishes a convergence rate lower bound of $\Omega(T^{-1/4})$ for this problem. To address the challenge, the authors propose two algorithms (Algorithm 2 and Algorithm 3). They show that Algorithm 2 achieves an $\ell^2$ convergence rate of $O(T^{-1/4})$, while Algorithm 3 achieves an $\ell^2$ convergence rate of $\tilde{O}(T^{-1/4})$.
Claims And Evidence: It is concerning that the abstract claims both proposed algorithms achieve the optimal convergence rate. Could the authors kindly clarify whether the algorithms match the lower bound up to constant factors, only in terms of the order of $T$, or if the rates differ by logarithmic factors (e.g., $\log(T)$)?
Methods And Evaluation Criteria: The evaluation criteria (convergence rates) make sense.
Theoretical Claims: The consistent use of Big-$O$ notation to express lower bounds throughout the paper is somewhat confusing, as Big-$\Omega$ notation is typically used for lower bounds. For instance, this appears in Section 1 when referencing the lower bound from [Cai et al., 2023], as well as in Table 1 and Section 2. Could the authors kindly clarify whether this usage is intentional?
Experimental Designs Or Analyses: This paper does not provide any numerical study.
Supplementary Material: I am aware of the proofs in the appendices.
Relation To Broader Scientific Literature: This paper contributes to the broader online learning research community by providing a tighter (compared to prior works, e.g., [Cai et al., 2023]) convergence lower bound for a specific setting of zero-sum matrix game.
Essential References Not Discussed: Could the authors kindly provide appropriate citations for the transformation procedure described in Section 6?
Other Strengths And Weaknesses: Strengths:
- The paper addresses a complex setting of zero-sum games by incorporating bandit feedback, uncoupled learning, and last-iterate convergence.
- It provides a convergence rate lower bound for the considered problem, contributing to the theoretical understanding of this setting.
Weakness:
- The presentation of the theoretical results is unclear.
- This paper does not include any numerical validation to support the effectiveness of the proposed algorithms.
Other Comments Or Suggestions: The notation $\ell^p$ ($\ell^t$) appears to be used with different meanings in various parts of the paper, which may lead to confusion. It would be helpful if the authors could clarify or standardize the notation to improve readability.
Questions For Authors: - Could the authors confirm whether, to the best of their knowledge, the convergence rate upper and lower bounds presented in this work are the tightest currently known?
- If so, could the authors kindly elaborate on the analytical tools or techniques they employed to derive a tighter lower bound on the convergence rate compared to prior works?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank Reviewer bHVB for taking the time to review our submission and especially for pointing out the issues in the notations. We address the concerns below.
>It is concerning that the abstract claims both proposed algorithms achieve the optimal convergence rate. Could the authors kindly clarify whether the algorithms match the lower bound up to constant factors, only in terms of the order of $T$ or if the rates differ by logarithmic factors (e.g., $\log (T)$)?
The rate is indeed only matched up to logarithmic factors, and we do not try to hide it in the paper. In the abstract, this comes from an oversight due to the change of the $\tilde{\mathcal{O}}$ notation to $\mathcal{O}$ as the lower bound does not include any log factor. We will change the abstract to address this confusion.
>The consistent use of Big-$\mathcal{O}$ notation to express lower bounds throughout the paper is somewhat confusing, as Big-$\Omega$ notation is typically used for lower bounds. For instance, this appears in Section 1 when referencing the lower bound from [Cai et al., 2023], as well as in Table 1 and Section 2. Could the authors kindly clarify whether this usage is intentional?
This is an oversight, and we will change the relevant Big-$\mathcal{O}$ notations into Big-$\Omega$ (including in the abstract).
>Could the authors kindly provide appropriate citations for the transformation procedure described in Section 6?
While the idea behind the transformation procedure is natural, we are not aware of an article using this trick to transform an average profile convergence into a last-iterate convergence. If you have any precise references in mind that we did not stumble upon, please do not hesitate to give them so that we can add them to the paper
>The notation $\ell^p$ ($\ell^t$) appears to be used with different meanings in various parts of the paper, which may lead to confusion. It would be helpful if the authors could clarify or standardize the notation to improve readability.
Indeed, we use the notation $\ell^p$ for the convergence of the sequence and $\ell^t$ for the loss, and we assumed changing one of the two would bring more confusion. As the two refer to two completely different objects, we considered this overlap of notation acceptable. However, we propose to instead talk of the convergence of the sequence of the random variables $EG(\mu^t,\nu^t)$ in the $L^p$ space toward $0$, which we also believe to be better in addition of avoiding this overlap.
>Could the authors confirm whether, to the best of their knowledge, the convergence rate upper and lower bounds presented in this work are the tightest currently known?
The rates presented in Table 1 are the tightest currently known for high probability convergence. There also exists a $\mathcal{O}(t^{-1/6})$ rate for the $\ell^2$ convergence that was pointed to us that we will add to the table (and which we directly improve).
>If so, could the authors kindly elaborate on the analytical tools or techniques they employed to derive a tighter lower bound on the convergence rate compared to prior works?
The idea of the tighter lower bound is the focus of section 5 and is based on improving the classical lower bound on best arm identification (see e.g. [1]) for our context. This lower bound is based, from the point of view of one player, on the difficulty between distinguishing a sequence of $T$ Bernoulli $\mathcal{B}(1/2)$ and a sequence of $T$ Bernoulli $\mathcal{B}(1/2-\varepsilon)$, which is required to guarantee $\epsilon$-optimality. We show that $\epsilon$-optimality in the context of last-iterate convergence for games can require distinguishing between a sequence of $T$ Bernoulli $\mathcal{B}(1/2)$ and a sequence of $T$ Bernoulli $\mathcal{B}(1/2-\varepsilon_t)$ for $t$ varying between $1$ and $T$, with $\varepsilon_t=\mathcal{O} (EG(\mu^t,\nu^t))$. This implies a trade-off at each iteration between getting more information on the $\varepsilon$-optimal strategy and playing near-optimal profiles $(\mu^t,\nu^t)$, which explains the worse rate.
[1] Jean-Yves Audibert, Sébastien Bubeck. Best Arm Identification in Multi-Armed Bandits, COLT 2010
---
Rebuttal Comment 1.1:
Comment: I really appreciate the authors' clarification in response to my questions. I encourage them to proceed with implementing the changes discussed in the rebuttal. Given the commitment to these changes, I am raising my overall recommendation score.
---
Reply to Comment 1.1.1:
Comment: We thank Reviewer bHVB again for taking the time to read our response and for improving his recommendation score. | null | null | null | null | null | null |
Linear Bandits with Partially Observable Features | Accept (poster) | Summary: The paper proposes a method to solve the linear bandit problem with only a subset of features per arm visible to the learner without assuming any structural property beforehand. The authors do this by transforming each context vector onto an augmented space with dimension $K$ and learn the respective augmented feature vector to minimize the regret. They apply a doubly robust algorithm (robust wrt. estimated model and rewards). The authors provide a sublinear regret upper bound, a lower bound and proof the consistency of their estimator. Experiments showcase the effectiveness of their algorithm to other baselines.
Claims And Evidence: I did not check all of the proofs but from what I saw they look mostly clear and convincing I list some concerns in the weakness/questions section.
Methods And Evaluation Criteria: Comparing regret bounds for different compositions of number of arms and dimension make sense in this setting.
Theoretical Claims: I only skimmed through the proofs, with more focus on theorem 3.
Experimental Designs Or Analyses: I read through the experimental section and the scenarios explained for each plot. I have no issues there, though I did not check any code.
Supplementary Material: See above.
Relation To Broader Scientific Literature: The key contribution is a new model for the partially observable features setting without any additional assumptions on the structure of the problem through feature augmentation and the respective regret bound.
Essential References Not Discussed: Not to my knowledge.
Other Strengths And Weaknesses: Strength: I like the idea of using augmentation to mitigate the missing information and exploiting the observable features. The fact that no further assumptions are made makes the model quite powerful.
Weakness: I find the paper in section 3.2 hard to follow. For example it is not quite clear to me wether a compatibility condition is used or not for the oracle inequality. Also the exploration aspect of the algorithm is not quite clear to me, what is the benefit to random exploration for instance? Also I don't see how the basis vectors $b_i$ for the augmented context vectors are determined, I assume they have to minimize $d_h$?
Other Comments Or Suggestions: I think there is a small error in the regret definition in equation (2). Shouldn't it be just $\theta^\star$ and $z_{a^\star}$ instead of $z_\star$?
At the end of page 6 you wrote "To the best of our knowledge,Theorem 3 is the first regret bound sublinear in T for the latent features without any structural assumption." Technically this is not correct since the regular UCB algorithm for stochastic bandits would also achieve a sublinear bound.
In lines 228 to 231 you wrote that for the compatibility condition to hold the minimum eigenvalue has to positive, which does not have to be true in general. In some instances the compatibility condition is a more relaxed condition than having a positive minimum eigenvalue.
Questions For Authors: Do you actually use a compatibility condition or do you rely on a full rank gram matrix?
If you use a full rank gram matrix in the augmented space, how does you exploration strategy ensure full rank?
How do you select the set of orthogonal basis vectors $b_i$ ?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We are thankful for your careful review and for acknowledging the impact of our contributions. We will address the following questions one by one, and we believe that the answers will collectively provide a comprehensive response.
* **On Use of Compatibility Condition**
* It is well known that the full rank matrix implies the compatibility condition. Without loss of generality, we assume that the observed features are full rank (lines 187-188, left column) and the augmented vectors are orthogonal each other and to the observed feature space. Please refer to Lemma 4 for the detailed proof starting from line 1486 in the last page of appendix. Because the Gram matrix of the augmented features has positive minimum eigenvalue, it satisfies the compatibility condition for the convergence of the lasso estimator.
* **Ensurability of Full Rank Gram Matrix under Our Exploration Strategies**
* Our exploration method ensures full rank in two ways: (i) by randomly sampling a $K$ augmented feature vector for predetermined number of round $\mathcal{E}\_t$, and (ii) by performing resampling and coupling based on the multinomial distribution defined in (9). These two strategies explore over all $K$ arms efficiently. Additionally, as we have indicated in the footnote 3 in the manuscript (lines 217-219, left column), even though the observed feature Gram matrix is not full rank, we can apply singular value decomposition on the observed features to reduce the feature dimension to $\bar{d} \le K$ with $R(X)=\bar{d}$.
* **Selection of Orthonormal Basis**
* Theoretically, our regret bound holds for any choice of basis in $R(X)^\perp$. In practice, we perform singular value decomposition (SVD) of the observed feature matrix $X = \sum\_{i=1}^{r}\sigma\_i u\_i v\_i^\top$ and select the right singular vectors corresponding to zero singular values, i.e., ${v\_i\in\mathbb{R}^K:\sigma\_i=0}$, as $b\_1,\ldots,b\_{K-d}$ in our experiments. Then $b\_1,\ldots,b\_{K-d}$ form an orthonormal basis that is orthogonal to the row space of $X$.
* **Other Corrections**
* Regret definition in Eq. (2)
* Thank you for pointing this out. We will revise the notation in the revision.
* At the end of page 6 you wrote "To the best of our knowledge,Theorem 3 is the first regret bound sublinear in $T$ for the latent features without any structural assumption." Technically this is not correct since the regular UCB algorithm for stochastic bandits would also achieve a sublinear bound.
* We appreciate your clarification. We intended to state that our result is the first of its kind in linear parametric bandit problems. If by "regular UCB algorithms" you are referring to the algorithms for non-feature-based multi-armed bandit (MAB) settings, we agree that the original sentence may be misleading. We will revise it for clarity as follows: "To the best of our knowledge, Theorem 3 presents the first regret bound faster $\tilde{O}(\sqrt{KT})$, particularly for algorithms that account for unobserved features, without relying on any structural assumptions."
* In lines 228 to 231 you wrote that for the compatibility condition to hold the minimum eigenvalue has to positive, which does not have to be true in general. In some instances the compatibility condition is a more relaxed condition than having a positive minimum eigenvalue.
* Thank you for pointing this out. We agree with your observation and will revise the sentence, for accuracy, as follows: "For the estimator in Eq. (8) to correctly identify the zero entries in $\mu\_{\star}$, the compatibility condition must hold (van de Geer \& Bühlmann, 2009). While the compatibility condition does not necessarily require a positive minimum eigenvalue in general, in our setting, in our setting, the Gram matrix $\lambda\_{\min}\left(t^{-1}\sum\_{s=1}^{t}\tilde{x}\_{a\_s}\tilde{x}\_{a\_s}^\top\right)$ has a positive minimum eigenvalue. Thus, the compatibility condition is implied without any additional assumption."
In this work, we study linear bandits with partially observable features, where rewards depend on both observed and unobserved features, a common situation in real-world applications. Our problem setting is more general than prior works, and it remains underexplored. We directly tackle challenges arising from unobserved features. Specifically, we propose a novel algorithm equipped with a new estimation technique, and a novel analytical framework distinct from existing approaches. Our method achieves regret not only sublinear but also converges faster than those reported in previous studies, which also shows superior empirical performance in numerical experiments. We believe these contributions are significant.
Reference: van de Geer, S. A. and Bühlmann, P. (2009), On the conditions used to prove oracle results for the lasso. | Summary: ### Problem Setting
The paper studies the **linear bandit problem with partially observable features**, where rewards depend on a full set of features, but the learner only observes a subset of them. This setting models real-world scenarios (e.g., recommendation systems) where unobserved latent features (e.g., user preferences) influence outcomes. Existing linear bandit algorithms fail here because they either assume full feature observability or impose restrictive structural assumptions (e.g., linear mappings) between observed and latent features. The paper relaxes these assumptions, allowing latent features to have arbitrary relationships with observed ones, and formalizes the problem through geometric relationships between the subspaces spanned by observed and latent features.
---
### Main Algorithmic Ideas
The proposed **RoLF (Robust to Latent Features)** algorithm addresses partial observability via two key innovations:
1. **Feature Space Decomposition**: RoLF explicitly decomposes the reward into components spanned by observed features and their orthogonal complement, enabling estimation of both observable and latent effects without prior knowledge of latent dimensions.
2. **Doubly Robust Estimation**: A novel estimator combines ridge regression on observed features with importance weighting to correct for bias from unobserved factors, ensuring robustness to arbitrary latent feature interference.
Critically, RoLF requires no prior knowledge of latent feature properties (dimensions, alignment with observed features) and dynamically adapts to the geometric relationship between feature subspaces.
---
### Main Results
1. **Regret Bounds**:
- If observed features span the latent space ($ \text{span(observed)} \supseteq \text{span(latent)} $), RoLF achieves $ \widetilde{O}(\sqrt{dT}) $ regret, matching the optimal rate for standard linear bandits.
- If latent features dominate ($ \text{span(observed)} \subseteq \text{span(latent)} $), regret scales as $ \widetilde{O}(\sqrt{KT}) $, aligning with multi-armed bandit limits.
- In the general case, regret is $ \widetilde{O}(\sqrt{(d + d_h)T}) $, where $d_h$ is the effective latent dimension orthogonal to observed features.
2. **Empirical Validation**: Experiments confirm RoLF outperforms baseline algorithms when latent features are present.
Claims And Evidence: All claims in the paper are supported by theoretical proofs.
Methods And Evaluation Criteria: The method design is sensible and supported by experiments. The evaluation tests the algorithm's handling of unknown features by varying latent feature dimensions and their impact, which appears reasonable.
Theoretical Claims: The theory appears to be sound, but I have not had the time to thoroughly check the proofs.
Experimental Designs Or Analyses: I’m a bit confused about the experimental results. In each graph, the cumulative regret of the proposed RoLF-Lasso algorithm suddenly flattens at a certain point and stays flat afterward. This doesn’t align with my understanding of how regret typically grows in bandit experiments. I think the authors might need to explain why the regret suddenly becomes flat.
Supplementary Material: I have not closely reviewed the supplementary material.
Relation To Broader Scientific Literature: This paper is the first to study partially observable features in linear bandits. It shows that when too few features are observable, the linear bandit will recover to multi-armed bandits (MAB), linking the two frameworks and identifying the point where linear modeling and additional context advantages weaker.
Essential References Not Discussed: To my knowledge, I haven’t found any references that were left undiscussed.
Other Strengths And Weaknesses: I believe the strength of this work lies in introducing a meaningful new topic within the linear bandit setting and providing what appears to be a solid theoretical analysis. However, the weakness lies in the presentation of the paper, as many parts lack clear explanations. Below are my specific comments and questions for further clarification.
Other Comments Or Suggestions: The paper can be further improved in terms of writing and presentation. For instance, there are excessive blank lines between lines 326-329, and page 8 is not fully utilized. While these issues are not strictly necessary, the paper does not convincingly demonstrate that the content can be fully explained without filling these spaces.
Specifically, several key concepts and definitions are left unexplained:
1.the content of Table 1 is not well-explained, and the accompanying text does not align with the table.
2.In line 147, the regret formula includes $ z_* $ and $ z_t $, neither of which is defined. Based on the notation in the regret formula, these appear to be $ d $-dimensional vectors rather than full feature vectors, but this is not clearly explained.
Therefore, I believe the work could be further improved in terms of clarity and writing.
Questions For Authors: I have some question about the result of regret bound. Regarding the results in Table 1, I understand the first scenario: it suggests that even though there are some unknown parts of the features, these features are either unimportant or can be linearly expressed by the known features, thus reducing the problem to standard linear bandits. The second scenario indicates that the unknown features are so numerous that even with some side information, it’s insufficient, causing the problem to degenerate into a multi-armed bandit setting, where the features essentially useless. Both scenarios make sense to me.
However, I find the third result less clear. Based on my understanding, the bound includes $ d $ as the dimension of known features and $ d_h $ as the dimension of unknown features. Intuitively, as the proportion of unknown features increases relative to known features, the problem should become more challenging. That is, if $ d + d_h $ remains constant, increasing $ d_h $ should make the problem harder. Yet, according to the bound, as long as $ d + d_h $ remains unchanged, the final performance is the same. This seems confused to me, and I believe the authors may need to discuss this problem.
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: We appreciate your feedback on page usage. We will make full use of the page limit and avoid leaving unused space in the revision.
* **On Explanation and Mislocation of Table 1**
* We appreciate you for giving us an opportunity to clarify Table 1. We will relocate the table to a more suitable position (e.g., below Section 3, line 159, right column) and add clarifying explanation.
* Table 1 summarizes how the regret bound of our algorithm varies with the relationship between the row space of observed features (span(observed), i.e., $ R(X)$) and that of unobserved features (span(latent), i.e., $ R(U)$).
* Specifically, if span(latent) is fully included in span(observed), the quantity $d\_h$ becomes 0 since the unobserved reward component can be expressed by the observed features. For the opposite case, $d\_h=K-d$. A detailed discussion can be found from line 206 (left column) to line 177 (right column).
* We also provide the experimental results for Case 1 and 2 in Table 1: (i) $R(U)\subseteq R(X)$ and (ii) $R(U)\supseteq R(X)$, respectively. For (i), we sample $X\in\mathbb{R}^{d\times K}$ from $N(0\_d,I\_d)$ and a coefficient matrix $C\in\mathbb{R}^{d\_u\times d}$ from $\text{Unif}(-1/\pi,1/\pi)$, and compute $U$ as $CX$, where $d\_u=d\_z-d$ (line 91, right column). In case (ii), we sample $U\sim N(0\_{d\_u},I\_{d\_u})$, then construct $X$ via multiplication with a coefficient matrix, as in (i). The full feature matrix $ Z$ is formed by concatenating $ X$ and $ U$.
* The experiments are conducted with the following setups: (i) $d\_z=30,d=15$, and $K$, the number of arms, varies by 20, 30, and 40; (ii) $d\_z=40,d=10$, with $K=10,30,50$; (iii) $d\_z=20,d=10$, with $K = 15, 25, 35$. Results are available at: https://tinyurl.com/RoLFFigs1
* **On Notation of $z\_{\star}$ and $z\_t$**
* We appreciate the opportunity to clarify the definition of the given notation. In Eq. (2), $z\_\star$ denotes the *true* feature vector associated with the optimal action $a\_\star$, as defined in lines 139–140 on the left column, and $z\_t$ denotes the *true* feature vector corresponding to the action selected in round $t$, i.e., $a\_t$. As defined in Eq. (1) (line), both vectors consist of a combination of observed and unobserved components. We will include this clarification in the revision.
* **Clarification of Theoretical Results**
* We appreciate the opportunity to clarify the results regarding $d\_h$.
* Before providing clarification, we would like to emphasize that the first scenario in Table 1 does not imply that the unobserved features are unimportant; rather, as you have correctly pointed out, it indicates that they can be linearly expressed by the observed features.
* The formal definition of $d\_h$ is provided in (6) (line 216, the left column). To clarify, $d_h$ is not the \emph{dimension of unknown features}; $d\_h$ is the number of required basis vectors to express the unknown portion of reward, $(I\_K-P\_X)U^\top \theta\_{\star}^{(u)}$.
* Even if the dimension of the unobservable features, $d\_u$, increases, the problem does not become more difficult -- as long as the unobserved component of the reward can still be expressed using only $d\_h$ basis vectors. However, if the increment of the unobservable feature increases $d\_h$, then the problem becomes harder as it requires additional parameter to express the unknown portion of reward. Thus, $d\_h$ characterizes the intrinsic difficulty of the problem, which supports our $O(\sqrt{(d + d\_h)T})$ regret bound. We will include the details in the manuscript.
* **Clarification of Experimental Results on Curve Flattening**
* We appreciate your careful observation. While the cumulative regret curve of our algorithm may appear to flatten suddenly, it is not completely flat -- this impression comes from the steep growth of the regret curves of baseline algorithms. In fact, it continues to grow slowly over time. The apparent flattening is due to the forced exploration phase (lines 5-6 in Algorithm 1), which ensures sufficient coverage of the action space early on. After this phase, resampling and coupling strategies both enhance the efficiency of the doubly robust (DR) estimation, resulting in slower regret growth. A shorter exploration phase would yield a more gradual and adaptive flattening.
We would like to emphasize the significance of the problem: linear bandits with partially observable features, where rewards depend on both observable and unobservable features -- common in practice, yet underexplored. Our work addresses core challenges with a new algorithm for partial observability, equipped with a novel estimation strategy. Our method achieves sublinear regret bounds with faster convergence rate than prior work, and shows superior empirical performance. We believe these contributions are substantial and hope they are recognized.
---
Rebuttal Comment 1.1:
Comment: Thank you for your effort on the rebuttal. While the concern regarding Table 1 has been addressed, I still have a few remaining concerns.
- You emphasize the significance of the problem by stating that “it is common in practice yet underexplored”. However, you don’t provide a convincing example to support this claim. Even the example at the beginning of the paper—about product recommendation—is rather vague. In the linear bandit setting you consider, it’s unclear how the roles of users and items are defined. Based on the standard interpretation in linear bandits, the context typically corresponds to the items (which the recommender system can observe and choose), while the user is modeled as the unknown parameter. So it’s confusing that in your setup, the user is treated as the observed context and the item as the unknown parameter. I’m not claiming my understanding is definitely correct, but the fact that such confusion arises suggests that your explanation of the problem setting is unclear. This does not appear to be a well-established problem in the bandit community (at least for now), and for that reason, I find your attempt to emphasize the significance of the problem unconvincing, as it seems to imply that this is already a widely recognized issue in the community — which, to my knowledge, is not the case.
- Regarding the experiment, I’m not convinced by your explanation. You explaned that the figure are influenced by the impression of linear regret in the overall plot, but based on the scale of the y-axis, the regret of your two methods shows very little change within the 1200 rounds. Even without the impression of linear regret, the variation is still minimal. This unusually small increase in regret over time seems quite odd. This pattern is not observed in prior works mentioned in this paper, such as Park & Faradonbeh (2022), Kim et al. (2023a), and Park & Faradonbeh (2024).
**[New]** Thank you for your further reply. I believe the problem is meaningful, and your code appears to be correct. However, my remaining concern is the abnormal phenomenon, which I believe should be clearly explained in the revision.
It’s unclear whether this is caused by a plotting artifact, an issue with the experimental setup (e.g., the task might be too easy, allowing the algorithm to immediately find the optimal arm after the exploration phase), or some underlying assumption. The initial explanation related to “impression” doesn’t seem very convincing to me. If possible, could the authors provide a version of the plot with the linear regret removed — showing only the currently flat-looking part? This might help clarify the explanation without the impression issue and allow for a clearer observation of the regret growth in this region.
Since the discussion deadline is approaching, the authors may consider directly updating the new plot in the anonymous link.
---
Reply to Comment 1.1.1:
Comment: # Significance of the problem
We would like to offer a more concrete case to better illustrate the significance of **linear bandit with partially observable features**. Consider in **online advertising** (without personalization, i.e., serving to general users):
Each ad (arm) $a \in [K]$ is associated with a true but **partially observable feature vector** $\mathbf{z}_a$:
$$
\mathbf{z}_a =[\mathbf{x}_a, \mathbf{u}_a]^\top= \begin{bmatrix}
\color{blue}{x_a^{(1)}},
\color{blue}{x_a^{(2)}},
\color{blue}{x_a^{(3)}},
\color{red}{u_a^{(1)}},
\vdots ,
\color{red}{u_a^{(d_u)}}
\end{bmatrix}^\top,
$$
where $\mathbf{x}_a$ is observable and $\mathbf{u}_a$ is latent.
For example:
- $ \color{blue}{x_a^{(1)}} $: ad category (e.g., travel, fashion, tech)
- $\color{blue}{x_a^{(2)}}$: ad format (e.g., banner, video, carousel)
- $ \color{blue}{x_a^{(3)}} $: time of display
These are **observable** to the platform. (Note that some of these observable features may be categorical, which can be turned into dummy variables.) However, **latent factors** such as emotional appeal, creative design quality, or brand familiarity also influence the click-through rates but are **not directly quantifiable or observed** ($ \color{red}{u_a^{(j)}} $'s). The **reward (click/no click)** depends on the **entire $\mathbf{z}_a$**, but the learner (advertiser/platform) **only sees $\mathbf{x}_a$**—leading to a **realistic partial observability challenge**. This example illustrates why we believe our model is practically meaningful.
Similar situations arise in many other domains:
- **Clinical trials**, where treatments (arms) have observable features (e.g., dosage, chemical formulation) and unobserved ones (e.g., manufacturing variability, side effect risks) that influence outcomes.
- **Online retail**, where products have not only observed metadata (e.g., price, brand, category), but also latent factors (e.g., freshness, trendiness) can impact purchase rates.
In all of these cases, outcomes depend on both **observed** and **unobserved features**, and our model provides a principled and practical framework for learning in such settings—with strong theoretical guarantees.
We invite the reviewer to the following reflection:
**Question:** Which is more realistic? (i) *All* features influencing the reward are *always* observed, or (ii) *Some* relevant features might be *unobservable* in practice?
We believe many practitioners would agree that (ii) better reflects real-world conditions.
Moreover—and just as importantly—in practice, **one typically does not know** if all relevant features are observed or some influential factors are unobserved. Our work directly addresses this aspect, offering a solution that requires no prior knowledge of the unobserved feature space.
---
We also respectfully disagree with the claim that our setting is not well-established within the bandit research community. There is a growing body of works on **bandits with partially observable features**, including. Tennenholtz et al. (2021), Kim et al. (2023), and Park & Faradonbeh (2022; 2024). Our work generlizes this line of research, by **removing the structural assumptions on the latent features** commonly imposed in prior studies.
Putting these together, we strongly believe that our setting is both theoretically well-motivated and practically relevant. More importantly, we propose a provably efficient algorithm that also shows superior performance in experiments.
---
# Experiments
We take such concerns very seriously. **Our code was already submitted for full transparency**, and we have **re-validated the implementation** following your comment. We found no issues at all. It is 100% correct. **For even more transparency, we provide the notebook file that reproduces our results**:
Link: [Jupyter notebook with results](https://tinyurl.com/rolf-code-jupyter).
So there should NOT be any more concerns.
Regarding the prior works mentioned, we respectfully note that those studies assume **stochastic features** that are resampled at each round. In contrast, our setting considers fixed feature vectors as clearly stated in the paper—making the settings quite different.
Finally, we believe the seemingly flatter regret curve arises naturally from **basis-augmented features**, which reduce information loss; **doubly robust estimation**, which improves statistical efficiency; and **forced exploration**, known to yield fast convergence after initial rounds (e.g, Goldenshluger & Zeevi, 2013; Hao et al., 2020; Chakraborty et al., 2023).
**We kindly and respectfully ask the reviewer to re-evaluate our important work.**
---
**Additional references**
* Goldenshluger & Zeevi (2013), "A linear response bandit problem."
* Tennenholtz et al. (2021), "Bandits with partially observable confounded data."
* Hao et al. (2020), "High-dimensional sparse linear bandits."
* Chakraborty et al. (2023), "Thompson sampling for high-dimensional sparse linear contextual bandits." | Summary: This paper studies linear bandits with partially observable features. The authors suggest an epsilon greedy type algorithm based on a doubly robust estimator. A regret bound of the algorithm is provided with supporting numerical experiments.
Claims And Evidence: The authors claim that the basis of orthogonal space to feature space can be used for the estimation of rewards to fill the absence of information due to partial observability. The reviewer believes that this is convincing.
Methods And Evaluation Criteria: The regret is a widely used evaluation criterion. It makes sense.
Theoretical Claims: I have not checked all proofs. But, the claims make sense and fit my intuition.
Experimental Designs Or Analyses: The experiment should be more neutral to other benchmark methods. The space of (significant) unobserved vectors should be a small subset of R(X)^t for fair comparisons. If no unobserved vectors are associated with rewards, regret could be worse than other methods due to overfitting, even though the lasso/ridge estimator provides some shrinkage. This part is not fully described, so hard to figure it out.
Supplementary Material: I have not.
Relation To Broader Scientific Literature: As this work addresses linear bandits (not contextual bandits), for literature review, could you please compare it with others about linear bandits, not with ones about contextual bandits? If no literature about linear bandits is available, the authors should clarify it.
Essential References Not Discussed: The following work is similar to this work.
Tennenholtz, Guy, et al. "Bandits with partially observable confounded data." Uncertainty in Artificial Intelligence. PMLR, 2021.
Other Strengths And Weaknesses: This work's idea and method are great. Also, the quality of English is good.
Weakness:
Methods are not fully described.
In (8), what is p and \delta? How do we determine it?
Could you please more specifically describe the details about the method, such as the reference of the provided exploration method and the constants C_e log(2Kt^2/\delta)?
Other Comments Or Suggestions: NA
Questions For Authors: Could you provide more details about the experiment setups, especially the space R(X) and R(U)? Also, could you please provide the regression equations of rewards?
How (10) is unbiased even though lasso/ridge is used?
Ethical Review Concerns: NA
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We are grateful for your valuable feedback and acknowledgment of our contributions. We are happy to address each of your comments.
* **On Descriptions of Notation and Methods**
- Thank you for the opportunity to clarify this point. Definitions of $p$ and $\delta$ are given after Eq. (9) (lines 263-270, left column) and Algorithm 1 (lines 276-277, right column), respectively. We will add explanations immediately after Eq. (8) in the revision. As described in Algorithm 1, both quantities are hyperparameters: (i) $p$ is the coupling probability used to define the multinomial distribution for pseudo-action sampling; (ii) $\delta$ is the algorithm's confidence parameter.
- Our exploration method uses *coupling* of an action $a\_t$ from $\epsilon\_t$-greedy policy with a counterfactual action $\tilde{a}\_t$, drawn from the multinomial distribution in Eq. (9). While Xu \& Zeevi (2020) also use counterfactual actions for exploration, our method differs in two points: (i) they sample counterfactuals from the previous policy, whereas ours conditions on $a\_t$; (ii) we explicitly resample $\tilde{a}\_t$ for coupling. A minimum of $C\_e\log (2Kt^2/\delta)$ exploration rounds ensures the imputation estimator $\check{\mu}^L$ is accurate enough for use in the main estimator $\widehat{\mu}^L$. Fewer rounds may cause error accumulation in $\widehat{\mu}^L$.
* **On Experimental Setups and Comparison with Baselines**
- Our experimental setting is the *"otherwise"* case in Table 1, where neither $R(X)$ nor $R(U)$ fully contains the other.
- We also examine cases (i) $R(U)\subseteq R(X)$ and (ii) $ R(U) \supseteq R(X) $. For (i), we sample $X\in\mathbb{R}^{d\times K}$ from $N(0\_d,I\_d)$ and a coefficient matrix $C\in\mathbb{R}^{d\_u\times d}$ from $\text{Unif}(-1/\pi,1/\pi)$, and computed $U$ as $CX$, where $d\_u=d\_z-d$ (see line 91, right column). In case (ii), we first sample $U\sim N(0\_{d\_u},I\_{d\_u})$, then construct $X$ analogously as in case (i). $ Z $ is formed by concatenating $ X $ and $ U $.
- Additional experiments are conducted for both cases, with the following setups: (i) $d\_z=30,d=15$, and $K$, the number of arms, varies by 20, 30, and 40; (ii) $d\_z=40,d=10$, with $K = 10, 30, 50$; (iii) $d\_z=20,d=10$, with $K=15,25,35$. Results are available at: https://tinyurl.com/RoLFFigs1
- For the case with no unobserved features, results are already included in the manuscript (lines 416–426, left column; Fig. 4), where $d\_z = d$, thus removing latent potions from rewards. As shown in the figure, our algorithm still outperforms the baselines with no overfitting observed.
* **On Regression Equations**
- As noted in the manuscript(line 123, left column), the true mean reward is $ x\_a^\top \theta^{(o)}\_\star+u\_a^\top\theta^{(u)}\_\star$, where $x\_a$ is observed and $u\_a$ is latent. Baseline methods (e.g., OFUL, LinTS, DRLasso) only use $x\_a$, modeling the regression as $f\_{base}(x\_a) = x\_a^\top \theta^{(o)}\_\star$. However, ours augments $x\_a$ with $b\_1,\ldots,b\_{K−d}$ to model as $f_{ours}(x\_a, b\_1,\ldots,b\_{K-d})=[x\_a\;e\_a^\top b\_1\cdots e\_a^\top b\_{K-d}] \mu\_\star,$ which recovers the true mean reward as argued in Eq. (4) (lines 194–200, left column) and Eq. (7) (lines 184–187, right column).
* **On Unbiasedness of Estimators**
- The pseudo-reward (Eq. (10) in lines 237-240, right column) is unbiased as it involves no regularization. In contrast, the main estimator is biased due to the inclusion of lasso/ridge regularization.
* **Comprehensive Literature Review**
* **Comparisons with Linear Bandits**: Due to space limitations, we deferred the comparison with linear bandits to appendix, but we are more than happy to move it to the main text in the revision. Regarding linear bandits with fixed features, we have also discussed comparisons with linear bandits under model misspecification (lines 96-108, right column) as well as in Appendix A.
* **Tennenholtz, Guy, et al. (2021)**: We appreciate your pointer to this related work. Upon inspection, while their setting appears similar to ours -- the true features and rewards contain both observed and unobserved components -- their work differs from ours in two points. First, they assume access to offline partially observed dataset to reduce the dimensionality of the problem, whereas partial observability arises naturally in ours, with no offline access. Second, they leverage the correlation between observed and unobserved features, which requires estimation; ours is agnostic to such correlation. Moreover, we exploit the observed features via feature augmentation and doubly robust estimation, resulting in faster regret convergence than their UCB-based approach. We will include this comparison in the revision.
Reference: Xu, Y. and Zeevi (2020), A. Upper counterfactual confidence bounds: a new optimism principle for contextual bandits. | null | null | null | null | null | null | null | null |
From Local Details to Global Context: Advancing Vision-Language Models with Attention-Based Selection | Accept (poster) | Summary: The paper introduces **Attention-Based Selection (ABS)**, a method to enhance vision-language models (VLMs) like CLIP by addressing limitations of random cropping, which often introduces background noise and compromises global semantic understanding. ABS leverages **DINO's attention maps** to guide cropping in **Raw Image Space** and **Feature Space**. Additionally, a **soft matching** technique filters irrelevant text descriptions for each crop, improving alignment between visual and textual modalities.
The main results indicate that ABS achieves **state-of-the-art performance** on 10 datasets across two benchmarks (zero-shot classification and out-of-distribution generalization), outperforming methods like WCA and CuPL. Besides, it matches or surpasses fine-tuning approaches (e.g., CoOp, TPT) without requiring additional training data in the out-of-distribution generalization benchmark. Ablation studies also validate the necessity of each component, with ABS improving accuracy by up to **2.98%** over baselines.
The main findings are that introducing DINO feature maps to select key regions for cropping is effective, and cropping both the original images and the intermediate feature maps is crucial.
Claims And Evidence: Yes, the claims made in the submission are supported by clear and convincing evidence.
Methods And Evaluation Criteria: Yes.
Theoretical Claims: No, because this paper doesn't has proofs for theoretical claims.
Experimental Designs Or Analyses: Yes, I have reviewed all the experiments mentioned in the Section 4. I have identified the following issues:
1. The experimental details in Table 3 are not described clearly enough. For example, it is not clear how many shots are specifically used, or whether the whole data from ImageNet are used for fine-tuning. Besides, fine-tuning the model with the data from ImageNet itself may actually reduce the generalization ability of the model on other distributions of ImageNet, because the fine-tuning process may causes the model to overfit the distribution of the original ImageNet. Therefore, the baselines that this method needs to compare with should be models fine-tuned using the few-shot datasets from target datasets like ImageNet-V2 and ImageNet-R.
Supplementary Material: Yes, I review all the supplementary material.
Relation To Broader Scientific Literature: The method proposed in this paper can help VLMs improve their performance in tasks such as image recognition.
Essential References Not Discussed: No.
Other Strengths And Weaknesses: **Strengths:**
1. The method proposed in this paper is simple, effective, and intuitive.
2. The paper is clearly written and quite readable.
**Weaknesses:**
I have two main concerns regarding the ABS method proposed in this paper:
1. The ABS method strongly depends on the quality and accuracy of the Attention Map generated by DINO. Therefore, when the attention map of DINO is of poor quality (for example, it focuses on the background or misidentifies objects), this method may have a negative impact on the object classification accuracy of the model.
2. There is a significant increase in inference time overhead. For single - image classification, this method changes the number of images for feature extraction from 1 to 2N, thus significantly reducing the corresponding inference speed. This situation is also shown in Table 8. Although Table 8 indicates that the performance is greatly improved compared to the original CLIP, I think ABS should not only compare it with the original CLIP but also with methods like CuPL. Since these methods also only need to infer one image, the performance improvement compared to them may not be significant enough to ignore the growing reasoning overhead.
Other Comments Or Suggestions: NA.
Questions For Authors: 1. What is the dimension of $F_{mid}$ in Equation 7? The specific process of Feature Map interpolation could be described in more detail.
2. How can we maximize the avoidance of the negative impact of inaccurate attention maps of DINO on the method?
3. Soft Matching essentially weights the image-text similarities of different images and texts. The goal of this weighting is to increase the relative ratio of the image-text similarities between similar and dissimilar image-text pairs. Have the authors tried other weighting methods, such as the approach similar to cross-modal late interaction in FILIP [1]? It would be better if there were some exploratory experiments in this regard.
[1] Yao, Lewei, et al. "FILIP: Fine-grained Interactive Language-Image Pre-Training." International Conference on Learning Representations.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: **Q1**: Experimental details in Table 3.
**A1:** Thanks. The results of baselines in Table 3 follow WCA protocol: Tuning-based methods are 16-shot source-trained and target-evaluated for OOD generalization. Notably, our method requires no fine-tuning, operating in a zero-shot manner on both source and target datasets and even surpasses fine-tuned methods.
Regarding your concern, we include in the table below the results of Coop fine-tuned directly on target data. Since our method functions as a plug-and-play module without requiring fine-tuning, integrating it with Coop further enhances performance.
||ImageNet-S|ImageNetv2
|-|-|-
|Coop ft. on tar.|49.79|70.59
|Coop ft. on tar. + ABS|**51.47**|**72.63**
**Q2:** About negative impact of DINO.
**A2:** Thanks.
1. DINO establishes a new contrastive learning framework that learns superior visual representations. Its exceptional attention maps, which have gained prominence for reliably pinpointing primary objects across diverse datasets, provide the foundation for our feature selection mechanism. And also a lot of works [2][3] using DINO for assistance. This reliability in object localization motivates our strategic adoption of DINO's attention maps to guide our selection process.
2. We observe that DINO's attention maps consistently localize semantically relevant object regions in multiple datasets. While occasional inaccuracies may occur, our adaptive crop_ratio enhances diversity in the cropped regions to mitigate such cases. Furthermore, our soft matching strategy effectively downweights irrelevant image crops, thereby reducing potential negative impacts from DINO's misalignments.
3. We observe that different attention heads in DINO may focus on distinct regions. In our paper, we simply average all attention heads. To further mitigate potential negative effects from DINO, we use attention maps from heads with higher variance, ensuring the selection maintain strong focus on salient objects. The following table shows the results demonstrate nearly identical performance to our original method. This suggests that ABS already achieves low error rates in attention map selection, making further error reduction less noticeable.
Regarding more explicit filtering of negative attention maps, we will conduct further research.
||ImageNet|ImageNet-A
|-|-|-
|Ours w. diverse head|71.96|61.86
|Ours w. mean head|71.92|61.80
ref:
[2] Zero-guidance segmentation using zero segment labels. CVPR 2023.
[3] Proxyclip: Proxy attention improves clip for open-vocabulary segmentation. ECCV 2024.
**Q3:** About inference time overhead.
**A3:** Thanks. When processing and encoding images, we do need to augment a single image into 2N crops. However, our hyperparameter sensitivity experiments reveal that the results are not sensitive to the num_crop. Therefore, we can reduce the value of N to lower time costs, while achieving average improvements of approximately **2%** on Zero-shot classification and **5%** on OOD datasets compared to CuPL, both of which represent significant gains. Additionally, we can follow the approach of WCA by pre-storing image features prior to inference. This ensures that the final similarity computation stage incurs comparable time costs to CuPL, while delivering substantially enhanced performance.
||encoding time|zero-shot avg. acc.|OOD avg. acc.
|-|-|-|-
|CuPL|0.0008|39.83|61.93
|ABS (N=10)|0.0105|41.65|65.59
**Q4:** About dimension in Equation 7.
**A4:** Thanks. The specific process of interpolation please refer to **our answer A2 to Reviewer dz4u** and the pseudo-code is as follows:
```
# s_p: sampled patches from DINO attention
raw_crops = []
fea_crops = []
mid_fea = CLIP(x, layer=l-1)
for p in s_p:
c_size = random(α, β)
c_img = crop_img(x, p.center, c_size)
raw_fea = CLIP(c_img)
raw_crops.append(raw_fea)
c_fea = crop_fea(mid_fea, p.center, c_size)
r_fea = interpolate(c_fea, original_size)
f_fea = CLIP.final_layer(r_fea)
fea_crops.append(f_fea)
com_fea = concatenate(raw_crops + fea_crops)
```
**Q5:** About negative impact of DINO.
**A5:** Thanks. Please refer to **A2**.
**Q6:** Comparison with other weighted methods.
**A6:** Thanks. FILIP [1] proposes a token-level matching approach for VLM pretraining. However, since its pretrained model is not publicly available, we cannot directly apply its token-level matching to VLMs that were not pretrained with this method. As an alternative, we experiment with the weight-based matching approach proposed in WCA and common entropy weighted methods and compared them with our soft matching. The results demonstrate the superior performance of our soft matching, indicating its enhanced capability to select more semantically aligned image-text pairs for effective matching.
||ImageNet|DTD|ImageNetV2
|-|-|-|-
|Ours w/ WCA weighted|71.22|53.36|65.23
|Ours w/ entropy weighted|70.76|53.12|64.94
|Ours|**71.92**|**54.26**|**66.19** | Summary: Recent studies have explored the use of multiple image crops obtained through random cropping, utilizing text descriptions generated by LLMs to assess the similarity between image and text embeddings for zero-shot classification tasks. This paper builds on that concept by addressing the noise caused by random cropping operations. It does this by selectively sampling crops and feature subsets that focus on the salient regions identified by the attention map from DINO. Experimental evaluations across several benchmarks show performance improvement.
Claims And Evidence: The claim regarding uncertainty from random cropping in Figure 1 is not sufficiently valid. The only sample sizes provided are 30×30 and 90×90, which fall outside the interval (0.4, 0.9) used in this paper. At higher resolutions, the uncertainty introduced by the cropping operation may significantly decrease. Therefore, a more comprehensive empirical evaluation is necessary to clarify this claim.
Methods And Evaluation Criteria: - The operation described in lines 208-211, which involves "reintroducing the interpolated cropped feature maps into the model," raises some concerns. Do the authors concatenate the original [CLS] token with the interpolated feature map as the input for the final attention residual block? If so, how can the [CLS] token effectively capture the local semantics associated with the cropped region? A more detailed clarification or analysis would be appreciated.
Theoretical Claims: There is no theoretical analysis provided.
Experimental Designs Or Analyses: - The experiment results only demonstrate compatibility with CLIP. Since the feature selection strategy ( $F_{fs}$ ) may not be model-agnostic, I'm curious whether the proposed pipeline can integrate with other VLMs. A related study, specifically WCA, has shown results using ALIGN, AltCLIP, and GroupViT (please refer to Table 10 of [1]). Conducting a similar experiment could provide valuable insights.
- The results shown in Table 4 of the ablation study indicate that the factors ( $F_{rs}$ ) and ($ F_{fs} $) contribute to performance degradation on some benchmarks. It appears that the main improvement in performance is primarily attributable to the soft-matching strategy, while the impacts of ($ F_{rs} $) and ($ F_{fs} $) remain unclear.
[1] Visual-Text Cross Alignment: Refining the Similarity Score in Vision-Language Models. ICML 2024.
Supplementary Material: I have reviewed the appendix provided.
Relation To Broader Scientific Literature: - The proposed framework is mainly based on WCA [1], with its own contributions of handling the cropping uncertainty.
- Utilizing network feedback mechanisms such as attention to guide the cropping process [2] and zero-shot inference [3,4] is a well-explored technique. The attention-based strategy presented in this paper resembles those earlier studies.
[1] Visual-Text Cross Alignment: Refining the Similarity Score in Vision-Language Models. ICML 2024.
[2] Crafting better contrastive views for siamese representation learning. CVPR 2022.
[3] Proxyclip: Proxy attention improves clip for open-vocabulary segmentation. ECCV 2024.
[4] Zero-guidance segmentation using zero segment labels. CVPR 2023.
Essential References Not Discussed: - The clarity regarding this paper's position in recent attention-guided studies is still ambiguous (Sec.2.3).
Other Strengths And Weaknesses: ### Pros:
- The paper is well organized.
- The motivation is clear, and the method is simple and intuitive.
Other Comments Or Suggestions: n/a
Questions For Authors: n/a
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: **Q1:** Claims And Evidence.
**A1:** Thanks. The purpose of employing cropping is to enable the model to focus on local features of objects, thereby achieving better alignment with certain LLM descriptions. However, random crop exhibits two inherent limitations: When using smaller crop sizes, it introduces randomness and compromises global semantic coherence; while with larger crop sizes, although uncertainty diminishes (as you mentioned), this comes at the cost of sacrificing the ability to concentrate on local features, instead providing more global information similar to using full images.
Our method addresses this by enabling the model to eliminate randomness while preserving global semantics when focusing on local and pivotal features. Through ablations in the table below, we observe that our approach does not exhibit monotonically increasing accuracy with larger crop sizes. Conversely, it achieves superior results with smaller crop sizes, whereas WCA demonstrates an incremental pattern with increasing crop sizes. This contrast underscores the significance of our method's dual capability in eliminating randomness and maintaining global semantic integrity during local feature focusing, ultimately enhancing the model's optimal performance.
|crop_ratio|0.3-0.9|0.4-0.9|0.5-0.9|0.6-0.9|0.7-0.9|0.8-0.9
|-|-|-|-|-|-|-
|WCA|70.80|70.89|70.95|70.99|71.03|**71.03**
|ABS|71.75|71.87|71.92|**71.99**|71.88|71.84
**Q2:** Clarification of feature crop operation.
**A2:** Thanks. In our method, feature selection is performed before the forward of the final transformer layer. Given input features with dimensions [bs, 197, 768], we first separate the [CLS] token ([bs, 1, 768]) from the remaining tokens ([bs, 196, 768]). The remaining tokens are reshaped into 2D size [bs, 14, 14, 768]. Based on DINO’s attention map, we then select N crops from this feature map. Each crops is interpolated to the original feature map size, and concatenated with the [CLS] token, reconstructing the feature into [bs, N, 197, 768]. This modified feature is fed into the final transformer layer. During this layer's forward, the [CLS] token interacts with the crops to capture diverse local features enriched with global semantic information. We will supplement this detail in subsequent versions of our paper.
**Q3:** Integrating with other VLMs.
**A3:** Thanks. As shown in the table below, we apply our method to a broader range of VLMs (e.g. ALIGN, AltCLIP and GroupViT) in ImageNet and achieved superior performance compared to other approaches.
|VLM|Waffle|CuPL|WCA|ABS
|-|-|-|-|-
|ALIGN|65.22|66.24|66.77|**67.85**
|AltCLIP|74.29|75.74|76.20|**76.85**
|GroupViT|42.42|44.53|45.27|**46.96**
**Q4:** The impact of different components of our method.
**A4:** Thanks. Please refer to **our answer A1 to Reviewer C2Mc.**
**Q5:** Contribution of the work.
**A5:** Thanks. Please refer to **our answer A1 to Reviewer bJ6A.**
**Q6:** About other attention-based strategy methods.
**A6:** Thanks. [2] employs heatmaps to localize target regions. However, it relies on dynamically updating bounding boxes during training, which is incompatible with our zero-shot scenario. Furthermore, while [2] can successfully locate target regions, it fails to address the preservation of global information after cropping, which may lead to inter-class confusion in the model.
[3] combines features from VFMs with CLIP through Proxy Attention, which enhances the prominence of primary objects. [4] proposes to balance global and local contexts within CLIP's attention layers by analyzing attention values to estimate region-wise saliency. However, these methods fail to focus the model on local object features and lack the capability to focus on localized features of individual objects. In contrast, our approach not only highlights local object characteristics but also preserves crucial semantic information, offering a more comprehensive solution.
We implement the core modules of [3] and [4] within our framework and conduct experiment on the ImageNet dataset. As shown in the table below, our method demonstrates superior performance, validating the advantage of our approach in simultaneously focusing on local features while preserving global semantic information. A comprehensive comparison with methods [2]-[4] will be presented in the subsequent version of our paper.
||ImageNet
|-|-
|Proxyclip [3]|70.36
|zero-seg [4]|68.37
|Ours|**71.92**
**Q7:** The clarity regarding this paper's position.
**A7:** Thanks. The key insight of ABS compared to previous attention-based methods lies in two aspects: not only do we leverage attention-guided cropping in the raw space to focus on local regions while eliminating randomness, but more importantly (and to the best of our knowledge) we are the first to implement attention-guided feature space selection to complement global semantics. This dual-space cropping enables the crops to better align with LLM descriptions. | Summary: The paper proposes an Attention-Based Selection (ABS) method to improve zero-shot classification and out-of-distribution generalization capabilities of vision-language models (VLMs). ABS leverages DINO’s attention maps to guide the cropping of images, thus preventing random crops from focusing on irrelevant background areas. The method also introduces feature-level cropping to supplement global semantic context. Finally, a soft matching mechanism filters large language model (LLM)-generated text descriptions to improve visual-textual alignment. The authors report state-of-the-art results on multiple benchmarks, demonstrating the effectiveness of ABS.
Claims And Evidence: The claims made by the authors are supported by the experimental results, and the motivation behind the proposed approach is sound.
Methods And Evaluation Criteria: The proposed method, including the use of DINO's attention maps for guiding cropping, feature-level cropping, and soft matching of textual descriptions, is conceptually clear, well-motivated. The evaluation on standard benchmarks aligned with current practices in the vision-language modeling literature.
Theoretical Claims: The paper does not explicitly present theoretical proofs or formal theoretical claims.
Experimental Designs Or Analyses: The comparisons across multiple widely recognized datasets and three different CLIP backbones (ViT-B/32, ViT-B/16, ViT-L/14) clearly support the viewpoint.
Supplementary Material: The supplementary material includes additional visualizations and ablation experiments.
Relation To Broader Scientific Literature: The paper is effectively situated within the broader literature of vision-language modeling, specifically highlighting recent advances such as WCA, CuPL, and methods employing attention-based augmentation.
Essential References Not Discussed: The paper provides a comprehensive summary of recent relevant literature.
Other Strengths And Weaknesses: **Strengths**
1. The paper is clearly written and provides strong motivation for its proposed method.
2. Extensive experiments validate the effectiveness of the proposed method, and fair comparisons were conducted.
3. The visualizations clearly reflect the authors' intentions.
**Weaknesses**
1. Although the method is effective, its contribution to the field is relatively minor, merely proposing a small modification to an existing problem.
2. Table 6 (Lines 425-539) is not properly cited; instead, numerical results are presented directly in the text.
Other Comments Or Suggestions: 1. In Equation (1) and (10), it is recommended to use an upright font for "cos" to maintain consistency throughout the paper.
2. There are inconsistencies in the capitalization of certain headings.
Questions For Authors: 1. How were the hyperparameters set, and why were they unified across all datasets?
2. How sensitive is the method to the precision of soft matching? Would the performance drop significantly if the matching precision is imperfect or noisy (e.g., descriptions slightly mismatching the cropped areas)?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: **Q1:** About contribution.
**A1:** Thanks. Our core contribution resides not in proposing incremental adjustments to established frameworks, but rather in advancing systematic methodologies that demystify stochastic factors while enhancing holistic semantic comprehension for this research domain.
Firstly, the adoption of attention-based mechanisms to mitigate cropping randomness plays a pivotal role in zero-shot classification task, enabling consistent and robust performance improvements.
Moreover, our key insight lies not merely in employing attention-based selection to focus on critical regions, but also in being the first (to the best of our knowledge) to perform **feature cropping** that complement raw-space crops by integrating global semantic information. This dual mechanism proves crucial for aligning with LLM descriptions, while also establishing a novel paradigm for future research in multimodal alignment.
Additionally, our approach demonstrates high flexibility, enabling seamless integration with various advanced VLMs (please refer to **our answer A2 to Reviewer C2Mc and A3 to Reviewer dz4u**) to enhance their performance through plug-and-play adaptation.
**Q2:** Table 6 is not properly cited.
**A2:** Thanks for pointing it out. We will fix it in the future version of our paper.
**Q3:** Maintain “cos” consistency.
**A3:** Thanks for pointing it out. We will fix it in the future version of our paper.
**Q4:** Capitalization consistency.
**A4:** Thanks for pointing it out. We will fix it in the future version of our paper.
**Q5:** About hyperparameters set.
**A5:** Thanks. Our method involves three critical hyperparameters: crop_ratio, num_crops, and top-k, which we consistently set to 0.5, 60, and 20 respectively across all datasets. This unified configuration serves dual purposes: First, it demonstrates our approach's capability to achieve consistent performance improvements without dataset-specific tuning, and second, it facilitates convenient application in industrial deployments. As evidenced by the hyperparameter sensitivity analysis presented in the table below or in the Figure5 in our paper, our method exhibits remarkable robustness to parameter variations. In fact, alternative configurations (e.g. crop ratio=0.6, num_crops=30 and top-k=30) might potentially yield superior results to those reported in our paper. Nevertheless, we maintain fixed parameters throughout all experiments to ensure fair comparative evaluation and rigorous empirical validation of the proposed methodology.
| crop_ratio | 0.3 | 0.4 | 0.5 | 0.6 | 0.7 | 0.8 |
| --- | --- | --- | --- | --- | --- | --- |
| ABS | 71.75 | 71.87 | 71.92 (reported in paper) | **71.99** | 71.88 | 71.84 |
| **num_crops** | **10** | **20** | **30** | **40** | **50** | **60** |
| ABS | 71.72 | 71.88 | **71.98** | 71.97 | 71.93 | 71.92 (reported in paper) |
| **top-k** | **10** | **20** | **30** | **40** | **50** | **60** |
| ABS | 71.83 | 71.92 (reported in paper) | **71.98** | 71.97 | 71.69 | 71.56 |
**Q6:** About soft matching.
**A6:** Thanks. The soft matching mechanism is proposed to addresses the inherent mismatch issue in CLIP's original matching strategy, specifically the "description-crop misalignment" phenomenon where textual descriptions partially deviate from cropped image regions. This problem arises because our selection process emphasizes local object features - compared to using full images, these focused crops may induce partial mismatches with LLM descriptions during semantic alignment. The soft matching resolves this through adaptive weighting: it suppresses irrelevant LLM descriptions while amplifying semantically aligned ones. As demonstrated in the table below, the ablation studies confirm that removing soft matching causes performance degradation, verifying its critical role in mitigating mismatch effects. Notably, applying soft matching to WCA further improves accuracy, empirically proving its general effectiveness in filtering noisy descriptions.
| | ImageNet | DTD | ImageNetV2 |
| --- | --- | --- | --- |
| Ours w/o soft matching | 71.22 | 53.36 | 65.23 |
| Ours | **71.92** | **54.26** | **66.19** |
| WCA | 71.08 | 52.79 | 64.71 |
| WCA w/ soft matching | **71.37** | **53.60** | **65.67** | | Summary: This paper introduces ABS, a training-free Attention-Based Selection method that uses Vision-Language Pretraining (VLP) model’s attention maps (e.g., DINO and CLIP) to guide cropping in both raw image and feature space, effectively integrating local details with global semantic context via soft matching to achieve SoTA performance in some zero-shot classification tasks.
Claims And Evidence: The primary claims may not be supported by convincing evidence. Specifically, the effectiveness of the attention‐based raw space and feature selection components is not fully supported by the ablation study provided. In Table 4, these components contribute only a marginal average improvement (around +0.3%). It makes me concerns about whether these key modules significantly impact overall performance.
Methods And Evaluation Criteria: The paper leverages standard zero-shot visual classification and domain generalization benchmarks (i.e., various ImageNet variants, CUB, Oxford Pets, DTD, Food101, and Place365) which effectively assess both global and fine-grained performance.
Theoretical Claims: The paper offers only limited theoretical claims without detailed proofs, relying mostly on intuitive arguments.
Experimental Designs Or Analyses: The experimental design is generally sound with thorough ablation studies. However, given that the quality of the attention map significantly impacts performance, evaluating the method with a more advanced VLP model (e.g., BLIP-2) would better validate its robustness.
Supplementary Material: The supplementary material includes additional visualization experiments, more ablation studies and code.
Relation To Broader Scientific Literature: The paper builds on WCA (ICML, 2024), by incrementally enhancing its pipeline. Whereas WCA uses random cropping and LLM-generated descriptions, this paper integrates attention-based selection to more accurately focus on semantically important regions.
Essential References Not Discussed: The paper overlooks several key studies on attention‐based cropping methods [1,2,3] that are essential for highlighting its contributions.
[1] Chen J, Li H, Liang J, et al. Attention-based cropping and erasing learning with coarse-to-fine refinement for fine-grained visual classification[J]. Neurocomputing, 2022, 501: 359-369.
[2] Wang Y, Zhang Z, Feng L, et al. A new attention-based CNN approach for crop mapping using time series Sentinel-2 images[J]. Computers and electronics in agriculture, 2021, 184: 106090.
[3] Wang W, Shen J. Deep cropping via attention box prediction and aesthetics assessment[C]//Proceedings of the IEEE international conference on computer vision. 2017: 2186-2194.
Other Strengths And Weaknesses: Strengths
1. The experiment of this paper is extensive.
2. It is an interesting idea of attention-based feature selection to enhance the model's performance.
Weaknesses
1. Limited technical contribution. The proposed ABS closely resembles WCA (ICML, 2024) with only incremental changes, and the Soft Matching module appears to drive most of the performance gains (Please refer to “Relation To Broader Scientific Literature”).
2. Concerns about the performance on images with multiple objects (e.g., Food101) or complex backgrounds (e.g., Place365). For instance, the Food101 dataset shows lower performance compared to WCA and even negative gains on Place365.
3. Concerns about the reproducibility. the paper insufficient details on the LLM's prompt generation, alignment process between raw and feature spaces. It is a recommendation for including a pseudo-code.
4. Formatting issues in some formulas (e.g., Formula 8) that need optimization.
5. Overall language and clarity could be improved for better readability.
Other Comments Or Suggestions: My main concern remains the incremental contribution, particularly the limited gains from the attention-based selection compared to the soft matching component. Therefore, I give a "Weak Reject" recommendation and may improve my rating if the rebuttal satisfies.
Update:
I appreciate the authors' efforts in their rebuttal. It effectively addresses most of my concerns. I believe the proposed method is simple but efficient, and as a result, I decide to raise my rating to ``weak accept'' recommendation
Questions For Authors: Why does ABS perform worse on Food101? Is it related to the complexity of food images, the presence of multiple objects, or another factor?
Ethical Review Concerns: None
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: **Q1:** The concerns in Claims And Evidence.
**A1:** Thanks.
1. The table below compares applying soft matching alone vs. combined two selections to the baseline. Combined with the ablations in our paper, it shows that individual components yield improvement when used independently, but integration works best. It is noteworthy that the combined two selections outperforms using soft matching alone, proving these key modules significantly enhance overall performance.
2. The small improvement observed when using the raw space and feature selection individually because: Using either selection alone may lead to excessive focus on either local or global information. Moreover, employing cropping will focus on specific local regions. While this enables better alignment with LLM descriptions that match the currently focused regions, it weakens the alignment for those unrelated to these regions. Consequently, without soft matching to filter irrelevant descriptions, many unrelated descriptions would adversely affect the current crop's alignment. This phenomenon is also observed in the ablations in WCA, demonstrating that filtering or weighted integration of crops is crucial.
3. We replace the components in WCA with ours in the table below. The results prove that our components deliver performance gains compared to the original WCA, proving superiority of our design.
||ImageNet|DTD|ImageNetv2|$\Delta$Avg
|-|-|-|-|-
|Baseline|69.61|50.53|63.27|
|Baseline w/ soft m.|70.03|52.89|63.68|+1.06
|Baseline w/ two sele.|70.32|52.66|64.34|+1.30
|Ours|**71.92**|**54.26**|**66.19**|+2.98
|WCA|71.08|52.79|64.71|
|WCA w/ soft m.|71.37|53.60|65.67|+0.69
|WCA w/ two sele.|71.42|53.76|65.83|+0.81
**Q2:** More advanced VLP model.
**A2:** Thanks, as your suggestion, we employ the Blip-2 and compare with other baselines. The table below shows that ABS outperform all others across two datasets, demonstrating our effectiveness and adaptability. More advanced VLMs (e.g. ALIGN, AltCLIP and GroupViT) please refer to **our answer A3 to Reviewer dz4u.**
||Waffle|CuPL|WCA|ABS
|-|-|-|-|-
|DTD|45.64|50.74|54.47|**56.12**
|ImageNet-A|61.43|63.51|72.79|**74.39**
**Q3:** The comment of Broader Scientific Literature.
**A3:** Thanks. Please refer to **our answer A1 to Reviewer bJ6A.**
**Q4:** About attention‐based cropping methods.
**A4:** Thanks. [1] generates attention maps to crop and randomly erasing regions to force the model to focus on key areas. Although their method focus local regions, it fails to address the subsequent loss of global context. In contrast, our approach compensates by using feature selection. We experiment with [1] on our task (as shown in the table below), ABS demonstrate superior performance. This advantage stems from our global semantic compensation for cropped regions.
||ImageNet
|-|-
|ACEN [1]|61.62
|Ours|**71.92**
Although [2] and [3] are both attention-related works, [2] uses geographical information, making it only applicable to specific scenarios. [3] requires training for its modules, which contradicts zero-shot tasks. Moreover, neither method considers supplementing global information. In the revision, we will discuss and compare with these methods.
**Q5:** About technical contribution.
**A5:** Thanks. Please refer to **A1 and our answer A1 to Reviewer bJ6A.**
**Q6:** Concern about Food101.
**A6:** Thanks. ABS demonstrates performance improvements across multi-object or complex backgrounds datasets including Place365, only with the exception of Food101.
The Food101 differs from conventional multi-object datasets, it contains inherently multi-label images but provides only single-label annotations. For instance, an image labeled as "french fries" may actually contain multiple objects (e.g., fries, steak, and salad), where non-target objects could occupy a larger visual proportion than the labeled subject (We show several examples in our anonymous link: https://anonymous.4open.science/r/Submission_4487-1B78). Because all these objects fall within the predefined label set, the single-label assignment introduces ambiguity. These inherent properties could cause our method to identify unlabeled object categories within the images.
WCA’s randomness may inadvertently benefit from this properties. However, our experiments confirm substantial improvements in most of classification tasks including multi-object or complex backgrounds datasets.
**Q7:** About prompt and pseudocode.
**A7:** Thanks.
1. For the generation of LLM descriptions, we simply follow CuPL, utilizing their publicly released JSON files. The specific prompts can be found in the CuPL.
2. For details and pseudocode of the alignment process, please refer to **our answer A2 to Reviewer dz4u and A4 to Reviewer iUpr.**
We will supplement these in future versions of our paper.
**Q8:** Weakness 4&5.
**A8:** Thanks. We will revise our paper thoroughly.
**Q9:** Other comments and questions.
**A9:** Thanks. Please refer to the answer above. | null | null | null | null | null | null |
Hypothesis Testing for Generalized Thurstone Models | Accept (poster) | Summary: In this paper, the authors look at the problem of hypothesis testing of generalized thurstone models. The later models are used to model ranking among several entities based on pairwise comparisons. Extensive research has been done to learn the parameters of such a model. However, an important questions is given a set of empirical pairwise comparisons does the observations correspond to an underlying GTM? This hypothesis question apparently has not been looked so far. The authors initiate a formal theoretical study of this testing problem and came up with a formalism and test statistic which is the main contribution of the paper.
Claims And Evidence: The main claim is that the proposed hypothesis questions is useful in checking whether a given set of samples of pairwise comparisons correspond to a GTM or not. They also give experimental evidence to support the theoretical guarantees.
Methods And Evaluation Criteria: Yes
Theoretical Claims: Yes, in my opinion. The formalism of the testing problem is as follows
A good weight vector w must be orthogonal to the all ones vector and must have bounded values. The hypothesis testing problem distinguishes the following two cases.
- there exists a good weight vector w such that the probability of pairwise comparisons follow a cumulative probability according to some distribution F with respect to the difference of w values
- the pairwise comparisons is eps far in Frobenius norm from any such good weight vector
I didn't check the proof but here are the main theoretical claims.
- we roughly need n/eps samples to answer the above testing problem
- the upper bound is supported with a suitable lower bound based on LeCam method
- confidence intervals have been derived for the test statistic
Experimental Designs Or Analyses: The experiments were conducted on both synthetic and benchmark data. For both cases it shows that the proposed methods works well to determine the test threshold using a data-driven approach.
Supplementary Material: A bit.. I looked at the experimental part
Relation To Broader Scientific Literature: This works initiates the hypothesis testing of GTMs. However some special cases appeared in the literature before. The proposed method generalized beyond these special cases.
Essential References Not Discussed: NA
Other Strengths And Weaknesses: I think the proposed testing problem is novel and the techniques proposed are sound.
Other Comments Or Suggestions: NA
Questions For Authors: What happens if we define the testing problem with respect to other matrix norms such as the spectral norm?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for your insightful feedback and for dedicating time to review our paper! We respond to the specific questions as follows:
**Testing problem with respect to other norms**: We believe the Frobenius norm is a natural choice for our problem as it allows tractable analysis of maximum-likelihood-type methods. There is some precedent to utilizing such quadratic distances in hypothesis testing, such as the classical chi-squared test. Another popular choice for separation distance is the sum of total variation (TV) distances. Using the equivalence of norms ($||x||_1 \leq \sqrt{n} ||x||_2$), our results can be translated to TV distance, and they again turn out to be tight for complete graphs. For the TV separation distance $TV(P, \mathcal{T}_F)$, a simple calculation gives:
$TV(P, \mathcal{T}_F) =$
$\inf_{w \in \mathcal{W}_b }$
$\sum_{(i,j) \in \mathcal{E}}$
$\frac{1}{|\mathcal{E}|} |p_{ij} - F(w_i - w_j)| \leq \inf_{w \in \mathcal{W}_b } \frac{1}{\sqrt{|\mathcal{E}|} } ||P - F(w)||_F$
Recall that our test can distinguish whether $P = F(w)$ for some $w \in \mathcal{W}_b$ or
$\inf_{w \in \mathcal{W}_b} \frac{1}{n} ||P - F(w)||_F \geq c/\sqrt{nk}$
with a minimax risk at most 1/2. If $TV(P, \mathcal{T}_F) \geq \epsilon$, then using above equation, we can conclude that
$$\inf_{w \in \mathcal{W}_b } \frac{1}{n} ||P - F(w)||_F \geq \frac{\epsilon}{n} \sqrt{|\mathcal{E}| }$$
Thus our test has small minimax risk if $\frac{\epsilon}{n} \sqrt{|\mathcal{E}| } \geq c/\sqrt{nk}$, which is equivalent to $\epsilon \geq c\sqrt{n/(|\mathcal{E}| k)}$. This implies that the critical threshold for our test for the quantity $TV(P, \mathcal{T}_F)$ is $O(\sqrt{n/(|\mathcal{E}| k)})$ which reduces to $O(1/\sqrt{nk})$ for complete graphs. Interestingly, this bound matches the lower bound in [Seshadri & Ugander, 2020] for complete graphs, derived for the same notion of TV separation distance.
Moreover, using the inequality $||A||_2 \leq ||A||_F$ for any matrix $A$ and the same argument as above, we can translate our upper bounds to the spectral norm. However, we don't have lower bounds for the spectral norm.
We will incorporate these comments into the manuscript. | Summary: Covers “Generalized Thurstone models,” in which each player has a utility, and the probability of winning is a function of the difference in utilities – but this choice function is an arbitrary CDF. Nice motivation to observe that GTMs do not capture certain types of choice dynamics, so asking whether data are consistent with any GTM is a useful question. The general question regarding whether *any* GTM is consistent with a dataset is very interesting, and also technically intricate -- this is an excellent question to ask, and the authors make significant progress.
## update after rebuttal
Note that my questions below have been addressed in the authors' rebuttal.
Claims And Evidence: The abstract claims that the results are "validated" through experiments on synthetic and real-world datasets. I don't think is quite accurate. It seems that, instead, the synthetic experiments (basically just one in the main paper body) show empirically how the test statistic is distributed for a particular distribution over in-class tournaments, while the real-world datasets (also just one) also pursue the same methodology to estimate the test statistic, and show that the statistic is distributed roughly as expected for GTM models for the most popular models, but not for comparisons that involve less popular models. This is a suggestive finding, but does not seem to be explored in more detail.
Methods And Evaluation Criteria: I feel that the empirical evaluation is less thorough than the theoretical parts of the paper. There are some interesting findings, but I don't come away with a strong understanding of applying the techniques developed here to a broad range of settings. See some more specific points in the general comments and questions below.
Theoretical Claims: I did not check proofs. For the supplementary material in particular, I just scanned at a very high level.
Here is my rough understanding of the flow of the theoretical parts of the main paper body, with a few notes for suggestions inlined:
1. Model: each directed comparison (i,j) is either present or not. If present, the probability of winning is known fully. The graph is fixed in advance, not dependent on outcomes.
2. Note: Some confusion in notation: Definition 2.2 places no restrictions on F beyond R → [0,1], but then in Equation 3 it’s defined in terms of noise distribution G.
3. Pairwise comparison data is then (Equation 5) defined as bernoulli random variables parameterized by the winning probability of a competition.
4. The authors then define likelihood of observations, assume winning probabilities are bounded away from 0 and 1. The estimation problem is given with a bound b of magnitude of weights – seems unnatural, and shouldn’t be necessary with this assumption on winning probabilities, but later sections make clear that there are some technical issues for which this is necessary. Question for authors: is this restriction necessary because of the techniques, or is it fundamental?
5. Add some assumptions on strong log-concavity and bounded derivatives for F – this guarantees a unique solution for the likelihood estimation problem, and holds for some common GTMs.
6. Note: Section 2.3: why are the constants "universal" when they depend on F? Assuming it’s just \delta,\epsilon that are universal? Possible to clarify this in the text?
7. The authors then define their testing problem to differentiate between H_0, in which the winning probabilities come from some utilities under F, and H_1, in which any utilities result in a winning matrix bounded away from the actual one. They then show this is approximated by the frobenius norm difference between the true winning matrix, and the one under the likelihood-maximizing utilities.
8. From here, they define a test statistic, and ask what properties of the graph and observations are needed for the “minimax risk” (a measure of the probability of type-1 and type-2 errors) to be bounded by a constant.
9. They study the “critical threshold,” which is the distance lower bound in the H_1 null hypothesis. They show first there is an upper bound like c/sqrt(nk) on the critical threshold, where n is #players, and k is (half) number of games per observed pair. Their test uses half the data to estimate the utilities, and the other half to compute the statistic.
10. Their test holds even when the observation graph is disconnected – but I wonder what happens with their utility estimation procedure since it’s no longer identified? Possible to comment on this?
11. Next they consider lower bounds on the critical threshold. The lower bound is based on Seshadri&Ugander, but extends to GTM and more general observation graphs. These seem to be tight to within constants for complete graphs.
12. They also consider some upper bounds on type 1 and 2 error probabilities when comparisons arrive by “rounds” of games, each round containing a bernoulli draw per edge. I have to say, I’m not confident how to interpret the results of Theorem 7, including how tight the resulting confidence intervals might be. Perhaps the authors could include some more discussion about this -- I'd love to hear what is possible in the rebuttal.
Experimental Designs Or Analyses: See below for some comments.
Supplementary Material: I read the additional experiments regarding distribution of Frobenius error in figure 4, and the estimated multiplier for threshold in figure 5, and very quickly scanned the theorems presented in supplementary material.
Relation To Broader Scientific Literature: The authors do a good job of laying out the landscape for this area.
Essential References Not Discussed: Perhaps consider this reference at PNAS on sample complexity where your assumption of winning probabilities bounded away from {0,1} does not hold: https://www.pnas.org/doi/10.1073/pnas.2202116119
Other Strengths And Weaknesses: Please see below under comments and suggestions
Other Comments Or Suggestions: Slight confusion: equation 1) speaks to a specific choice function F, while main contribution 1) speaks to the distance to the family of GTMs. At this point in the draft, I was uncertain whether the focus was examining a null hypothesis regarding a single GTM, versus the entire family. This became clear later on.
My summary and some comments on the theoretical section is given above under "Theoretical Claims."
Here are some comments, questions, and thoughts regarding the Experiments section:
“Random skill scores” – does this mean uniform in [-b,b]? This is a good strawman, but not a broad coverage of what happens in settings where utilities are not drawn uniformly (eg, what happens if there are clusters of utilities, etc). Could the authors please comment about this assumption? I discuss next that the synthetic experiments are quite tightly tied to this assumption, as it induces the distribution over test statistic values (unless I am misunderstanding).
The first experiment as I understand it measures the distribution of the test statistic induced by the very specific underlying model (random skill scores) – I’m not sure how to read the finding from this experiment, as I can’t imagine an actual experimental setting in which this is a good probabilistic model of reality…? Related to this, on the idea of “repeating the process a sufficient number of times to build a distribution of test statistics” – is anything known about the true distribution of the test statistic for a GTM?
Perhaps my biggest question on the experiments is that I seem to be missing something high level. I don’t see the connection between the empirical test statistics and the various upper and lower bounds from the rest of the paper. Could the authors please clarify this, and whether anything more can be done experimentally to tighten the connection of the theoretical results to the questions that practitioners might face?
Related to this, there are no experiments that test whether the empirical quantile approach can actually distinguish between, say, a random skill scores GTM model, and a related model chosen to be a certain known distance from any GTM model. Is it possible to perform such an experiment? It’s hard to know how to interpret
For the LMSYS results, what does it mean that 60% of values are above the threshold, beyond the fact that the estimation procedure underestimates the critical value? Is this an issue of the increased variance of estimating p_{ij} due to sparsity of results for each (i,j) pair? Or, as I read it, is the idea that somehow less popular language models do *not* have a fundamental "quality" that can be used to estimate their likelihood of generating a better answer than a competitor? If the latter, this seems like a somewhat startling finding, and would benefit from more discussion (and analysis), as it now speaks more centrally to LLM testing, an issue of great importance right now.
Note: Figure 2 caption references LYMSYS (as does later text) -- is this supposed to be LMSYS? Otherwise, please clarify.
Questions For Authors: In addition to the questions above, two more things:
1. What is the intuition behind your test statistic? Is there some reason to think this is the best or approximately best (ie, variance-minimizing) test statistic for GTM or specific choice functions?
2. Are there other simplifications that would allow considering your bounds relative to other standard statistical tests? Perhaps a step function choice function?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for detailed feedback. Due to 5000 character limit, our responses are concise. We will incorporate the addressed points and new experiments in the final version
**Experimental Concerns**
* Experiments not explored in detail: Our focus was on theoretical aspects of the testing problem. To clarify, our first synthetic experiment shows that the threshold obtained via the empirical quantile approach follows the same high-level scaling as the theoretical threshold in Eq 37 (see Fig1). We also showed how to obtain a threshold using an asymptotic approximation in App F.2. **To address concerns, we added new experiments on real & synthetic data (see response to Reviewer smfn)**
* Interpreting Exp 1 findings: See response above
* Broader application: Validating the BTL model is crucial due to its wide applications(eg. in RLHF), where flexible ranking models are preferred. We believe our test could extend to RLHF where BTL scores are given by neural network/linear models.
* Connection b/w theory and practice: Our results on critical threshold and confidence intervals (CI), which follow from Type I & II error bounds, connect to our 1st synthetic experiment and App F.2 (see above).
* Validating empirical quantile approach: We have designed an experiment to validate its effectiveness in a synthetic setting. See Exp2 in response to Reviewer smfn
* Interpretation of LMSYS Results: The 60% above-threshold rate is a bootstrapped estimate of the test's power indicating ~40% chance that the model lies within 95% statistical deviations from BTL. The figure shows that as n increases, deviation from Thurstone increases, a top-9 batch size provides a statistically accurate fit to the Thurstone model, and the deviations are significant for $n\geq21$.
* Sparsity of $p_{ij}$: There is no sparsity as the graph is nearly complete
**Necessity of Bound b**: This restriction arises from our techniques for bounding separation distance. While we believe the bound b can be removed for certain cases (eg.complete graph) the analysis is significantly more complex. For general graphs, it is unclear whether b is fundamental; this is an interesting future problem. Additionally, assuming bounded weights is standard in literature on parametric models [Shah et al. 2016].
**Non-uniqueness of w in Disconnected Graph**: Our analysis uses error bounds in Laplacian semi-norm. When $G$ is disconnected, solutions $w^*,\hat{w}$ of Eq 7,8 may not be unique, but the error $||\hat{w}-w^*||_L$ is well-defined as the non-unique component lies in the null space of $L$. Thus, our upper bounds on critical thresholds still hold. Additionally, our lower bounds do not assume connectivity and hold for disconnected super-Eulerian graphs.
**Interpretation of Thm. 7 & Tightness of CIs**:
* Thm. 7 can be reduced from the sequential setting to the standard testing where data is available upfront.
* It implies Type I & II errors decay exponentially when separation distance $\gg1/\sqrt{nk}$.
* The bounds apply to any partition of data into $\mathcal{Z}_1$ and $\mathcal{Z}_2$, offering guidance on split-size based on graph topology (e.g., equal split for complete graphs, larger $k_1$ for better type I control in cycle graphs). See Appendix E for details
* To see tightness of CIs, we can compare Figs 1 and 5 for complete and grid graphs, with scaled threshold values of ~0.75 & ~0.45.
**Random Skill Scores**: Yes, the scores are drawn independently and uniformly in [-b,b] and translated to satisfy $w^T1=0$. While we acknowledge concerns about coverage with random sampling, in the context of finding thresholds, our experiments show that the resulting threshold exhibits the same scaling as theory predicts and achieves good empirical type I and II errors compared to a well-crafted threshold in a synthetic setting (see Exp2).
**Notational Confusion**:
* Definition 2.2: Sure, we will remark that F is a special CDF and add examples.
* Universal constant: Once graph $G$ choice function $F$, parameters $\delta,b$ are fixed, all the constants are universal as they depend only on these entities. We will remove 'universal' to avoid confusion. Note:$\epsilon$ is not constant as it can depend on $n,k$
* LYMSYS/LMSYS: Yes, it is LMSYS
**Test statistic**:
* Distribution: The distribution of $T$ is indeed hard to characterize, but using Prop. 3.8, we can asymptotically approximate its tail by a quadratic function of Gaussian random variables (see App F.2)
* Intuition: See response to Reviewer smfn. Our statistic may not be optimal in the sense you propose, but it is analytically tractable and does characterize the critical threshold.
**Essential References**: We will discuss it in final version.
**Other statistical tests** Our problem is a minimax composite hypothesis testing problem, which lacks a non-asymptotic theory in general. The only direct comparison of our bounds is with [Makur, Singh 2023] in the BTL case; both results have the same critical threshold scaling.
---
Rebuttal Comment 1.1:
Comment: Thank you for your detailed responses, they are very helpful | Summary: This work develops a hypothesis testing framework to determine whether pairwise comparison data follows a generalized Thurstone model for a given choice function, introducing a minimax separation distance to quantify deviations from such models. The study establishes theoretical bounds on the critical threshold based on the observation graph's topology, proposes a hypothesis test with confidence intervals, and establish time-uniform bounds on type I and II errors using reverse martingale techniques.
Claims And Evidence: My primary concern is the definition of the test statistic in Equation (15), as the paper lacks an intuitive explanation for its formalization. Furthermore, the relationship between this test statistic and those proposed in Rastogi et al. (2022) (Equation 8) and Makur & Singh (2023) (Equation 11) remains unclear, **requiring further clarification regarding its advantages in both theoretical analysis and experimental performance.**
References:
Rastogi, C., Balakrishnan, S., Shah, N. B., and Singh, A. Two-sample testing on ranked preference data and the role of modeling assumptions. Journal of Machine Learning Research, 23(225):1–48, 2022.
Makur, A. and Singh, J. Testing for the bradley-terry-luce model. In 2023 IEEE International Symposium on Information Theory (ISIT), pp. 1390–1395, 2023. doi:10.1109/ISIT54713.2023.10206450.
Methods And Evaluation Criteria: See Claims And Evidence part.
Theoretical Claims: The paper establishes a strong theoretical framework with rigorous proofs.
Experimental Designs Or Analyses: Lack of comparisons with state-of-the-art methods. All experiments present only test statistics and thresholds; explicitly reporting key evaluation metrics such as test power and Type-I error would be highly appreciated.
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: N/A
Questions For Authors: N/A
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your insightful feedback and for dedicating time to review our paper! We respond to the specific questions as follows:
**Intuitive explanation for definition of test statistic**: In addition to our existing discussion after Eq 15 in the paper, we provide here with an additional intuitive explanation: Consider the statistic
$$T^{\prime} = \sum_{(i,j)\in \mathcal{E}}\frac{Z_{ij}(Z_{ij}-1)}{k_{ij}'(k_{ij}'-1)}+F(w_i^*-w_j^*)^{2}-2F(w_i^* -w_j^*)\frac{Z_{ij}}{k_{ij}' }$$
obtained by substituting $w^*$ in place $\hat{w}$ in Eq. 15. Then, the expected value of $T'$ is $||P- F(w^*) ||_F^2$.
This is because the expected value of the first term is $p_{ij}^2$, and the last term is $-2 F(w_i^* - w_j^*) p_{ij}$. Hence, $T$ is constructed by plugging in $\hat{w}$ in place of $w^*$ in the unbiased estimator $T^{\prime}$ of $||P- F(w^*)||_F^2$.
We will add additional clarification in the manuscript.
**Relationship between this test statistic and those in [Rastogi et al. 2022] and [Makur, Singh 2023]**:
* The test statistic proposed in [Rastogi et al. 2022] is for a two-sample testing problem (i.e., testing whether two sets of samples are drawn from the same pairwise comparison model or not) which is a very different problem to that in our work.
* The test statistic in [Makur, Singh 2023] is for testing the BTL model, which is a special case of our model. Furthermore, their test statistic is based on spectral techniques, while ours is based on maximum likelihood techniques and is applicable for general Thurstone models
* There is some resemblance between the three test statistics since all three statistics are ``estimators” for squared Frobenius distances of pairwise comparison models. However, the techniques used to analyze them are very different. For example, our theoretical analysis crucially relies on sample splitting, while the other two do not. We will expand on this discussion in the final version. We comment on the experimental concerns below.
**Comparisons with state-of-the-art methods/Additional Experiments**: Except [Makur, Singh 2023], we are not aware of any work that addresses the same minimax problem as ours for a general Thurstonian model in a non-asymptotic regime. The tests based on likelihood ratio do not consider the general hypothesis testing problem considered in this work. However, we have performed following additional experiments for the BTL model. The figures for these experiments can be found at http://anonymous.4open.science/r/something-E6CB/ALLFigures.pdf
1. **Performance Comparison with [Makur, Singh 2023] (Exp1)**: We assume the observation graph to be complete and define the pairwise comparison matrix $P$ under the null and alternative hypothesis as the one used to prove the lower bound in Eq. 39. We set $\eta = 0.06$ and $k = 10$. We evaluate the empirical Type I and Type II errors for three methods: the proposed test statistic based on maximum likelihood estimation (Max. Likelihood), the same test statistic without sample splitting (Max. Likelihood2), and the spectral method from [Makur, Singh 2023] (Spectral). Our results in Fig. 1 indicate that the proposed method performs comparably to the spectral approach, while Max. Likelihood2 achieves even lower error. The threshold for all three methods is determined using the empirical quantile approach.
2. **Type I and II Errors: Empirical Quantile vs. Optimal Threshold (Exp2)**: We extend our previous experiment by comparing the empirical quantile threshold with the "optimal" threshold $\eta^2n(n-1)/2$. We evaluate Type I and II errors for $\eta\in[0.08,0.16], n\in[15,25,35,45], k=10$. Fig. 2 shows that the empirical quantile approach performs similarly to the optimal threshold, with Type I error control close to the nominal 0.05 level, despite the threshold being computed from randomly sampled skill scores.
To address Reviewer 3Nsw concerns regarding threshold computation using clustering, we also compare thresholds derived from random and clustered skill scores, where clustering is based on assigning half the player's scores randomly in [-0.7,-0.4] and the rest with their exact negative. Fig 3 shows that both approaches yield nearly identical thresholds.
3. **Experiment on real-world datasets**: In addition to our LMSYS dataset experiment, we also analyzed the NBA dataset from https://www.kaggle.com/datasets/nathanlauga/nba-games/data. Using data from 2022 onward, we applied our test to the 12 teams with the most matches since 2002. Each comparison involved a home and away team, and we tested on cumulative data over t recent years. Fig. 4 shows that for the first ~10 years, the BTL and Thurstone models fit well, but for larger intervals, the hypothesis is rejected, as a single BTL score cannot capture team strength over extended periods.
Various parameters, such as number of simulated datasets, are the same as those used in our paper for previous experiments. We will include these experiments in the final version
---
Rebuttal Comment 1.1:
Comment: Thank you for your response. The answers have addressed my questions and concerns. I will proceed to increase my rate. | Summary: The paper addresses the problem of hypothesis testing for whether a given pairwise comparison dataset follows a Generalized Thurstone Model (GTM), which is formally stated in equation (12). It proposes a test statistic along with a corresponding testing threshold that matches the lower bound on the critical threshold $\epsilon_c$ in the case of a complete observation graph, as defined in equation (14), thereby establishing its minimax optimality in this setting.
Additionally, the paper derives information-theoretic lower bounds on $\epsilon_c$ for different graph types, as shown in Table 1 and stated in Proposition 3.5. It also provides time-uniform bounds on Type I and Type II errors in a sequential testing framework, where at each time step, a single comparison is observed, as presented in Theorem 3.7. Furthermore, the paper constructs confidence intervals for the test statistic under the null hypothesis and validates the theoretical results through experiments on both synthetic and real datasets.
Claims And Evidence: yes
Methods And Evaluation Criteria: Yes, however, I think the experiment section could be improved by adding comparisons to other methods that perform hypothesis testing for Thurstone models, particularly in terms of Type I and Type II errors. For instance, some of the methods mentioned in the last paragraph of Section 1.2 could be included as baselines, even if they only apply to specific models, to provide a more informative comparison.
Theoretical Claims: I checked the general ideas in the proofs but I haven't verified each step.
Experimental Designs Or Analyses: yes, see the comment above in the methods evaluation and criteria
Supplementary Material: yes, I checked the general ideas in the proofs but I haven't verified each step.
Relation To Broader Scientific Literature: The key contribution is the proposed hypothesis test for the Generalized Thurstone Model using a maximum likelihood approach. This complements previous work in (1), which developed hypothesis tests for the Bradley-Terry-Luce (BTL) model based on spectral methods.
---
(1) Makur, A., and Singh, J. (2023). "Testing for the Bradley-Terry-Luce Model." In IEEE International Symposium on Information Theory (ISIT).
Essential References Not Discussed: no
Other Strengths And Weaknesses: Strengths:
- The paper addresses an interesting problem within a general framework that encompasses many Generalized Thurstone Models.
- The paper’s theoretical results are promising and well-developed, providing a thorough investigation into the minimax optimality of the proposed test. Additionally, it offers bounds within the sequential testing framework.
Weaknesses:
- I believe the experimental study could be enhanced by providing more informative results and comparing the proposed test with other methods.
- The approach used in Section 4 to estimate the threshold—by generating numerous simulated datasets under the null hypothesis to compute the testing threshold—can be computationally expensive.
Other Comments Or Suggestions: For completeness, it would be helpful to provide the expression for $F$ that was used in the experiments for the BTL and Thurstone models.
Questions For Authors: Is there a specific motivation for using the weighted log-likelihood in equation (6) instead of the typical log-likelihood, which I assume would involve $Z_{ij}$ instead of $p_{ij}$?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your insightful feedback and for dedicating time to review our paper! We respond to the specific questions as follows:
**Comparisons to other methods for testing of Thurstone models**: Minimax testing for generalized Thurstone models (for a fixed choice function $F$) has not been studied much in the literature. The case of logistic $F$, which corresponds to BTL models, is the only case that has baselines [Makur, Singh 2023]. So, it is difficult to provide accurate baselines for general functions $F$. However, to address this concern, we have included an additional experiment to compare the proposed method (Max. Likelihood) with [Makur, Singh 2023] for complete graphs (See response to Reviewer smfn for details). Our results show that the proposed method has a similar performance to the spectral method in [Makur, Singh 2023]. We have also added other experiments as outlined in the response to Reviewer smfn. We will add details of all experiments to the manuscript to make it more informative.
**Estimating threshold can be computationally expensive**: Yes, we agree that the computational complexity of estimating threshold will depend on the number of simulated datasets generated. However, we remark that:
1) This procedure is efficiently parallelizable.
2) Even with a naive implementation (without any parallelization), the running time is small as each of our experiments can be done within 5 minutes on a normal CPU for $n$ as large as $60$. To speedup computing $\hat{w}$ on the simulated dataset, one can initialize the iterates at the optimal values that generated the simulated dataset, followed by a few iterations of gradient descent.
3) Moreover, when all $k_{ij}$ are equal (or roughly the same), our simulation results in Figure 1 suggest that $0.75n/k$ as the threshold for complete graphs and $0.4n/k$ for 2D grid is a good approximation.
4) Using an asymptotic approximation and an intermediate result (Proposition 3.8), we can approximate the threshold as detailed in Appendix F.2. Approximating the threshold in this way is much faster than the empirical quantile approach.
**Motivation for using the weighted log-likelihood**: We chose to use weighted negative log-likelihood for the following reasons:
1) To define the minimax composite hypothesis testing problem, we first introduced a separation distance. For analytical purposes, we chose to represent this separation distance using the (unweighted) Frobenius norm. The weighted likelihood expression in Eq. 8 arises when we relate the separation distance in Frobenius norm to the cross-entropy term, as detailed in the Proof of Theorem 1. As a result, our definitions in Eq. 6,7 naturally inherited the weighted property.
2) If we were to use the unweighted version of maximum likelihood, we would need to employ a weighted Frobenius norm with weights $k_{ij}$ to define separation distance, which did not seem a natural choice to us. Alternatively, we would need to add an extra assumption that different $k_{ij}$ are within constant factors of each other, which we also chose not to do.
**Expression for F for the BTL and Thurstone models**: We remark that we have used $F(t) = \frac{1}{1 + e^{-t} }$ (sigmoid function) for the BTL model and $F(t) = \int_{-\infty}^t \frac{1}{\sqrt{2\pi}} e^{-x^2/2} dx$ (complementary-CDF of normal) for the standard Thurstone model. We will include this information in the revised manuscript.
---
Rebuttal Comment 1.1:
Comment: Thank you for your detailed response, and for running the additional experiments. | null | null | null | null | null | null |
Enhancing Spectral GNNs: From Topology and Perturbation Perspectives | Accept (poster) | Summary: This paper proposes a higher-dimensional sheaf Laplacian matrix based on perturbation theory and the theory of cellular sheaves. The perturbation is controlled from the block form of the normalized graph Laplacian matrix, and can contain more distinct eigenvalues. The paper provides theoretical analyses on the expressiveness of spectral GNNs and perturbation bounds for the eigenvalues. Node classification experiments demonstrate the efficacy of the proposed Laplacian.
Claims And Evidence: The claims seem clear and convincing.
Methods And Evaluation Criteria: The proposed method seems valid, but may have much larger complexity. The paper mentions the construction complexity for the Laplacian, but not the GNN complexity induced by using a more complex Laplacian.
Theoretical Claims: The theorems and propositions seem correct.
Experimental Designs Or Analyses: 1. Table 2 shares some information with Table 1, but with different performance values. Is this due to execution variation? Could you merge the table instead?
2. Why do you not compare your proposed PSL with the previous Sheaf Laplacian based GNNs mentioned in Sec. 7.2?
3. The ablation study part does not discuss model complexity (which may offer another angle of why PSL-GNN performs better, but may not be an advantage). I think adding runtime comparison may be useful.
Supplementary Material: I have a rough glacne through all of it.
Relation To Broader Scientific Literature: The contribution is related to the other Sheaf Neural Networks on graphs but seems to have some advantages (not numerically compared though).
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: The paper is generally well-written and flows well.
Other Comments Or Suggestions: It may be better if you first write out Proposition 5.1 to motivate the need of perturbation, then introduce perturbations.
Questions For Authors: 1. What is the relationship between Tables 1 and 2?
2. Why do you not compare your proposed PSL with the previous Sheaf Laplacian based GNNs mentioned in Sec. 7.2?
3. What is the model complexity in terms of GNN computation, not just construction of the Laplacian?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your valuable suggestion.
**Response to Q1**
We apologize for any confusion caused. To clarify: Table 1 demonstrates the performance gains achieved by integrating PSL into various models, while Table 2 highlights the comparison between PSL, GSL, and the conventional normalized graph Laplacian. Table 2 shares some information with Table 1, but with different performance values. It is because we retrained all the models separately under the same experimental environment. Therefore, although the experimental results differ slightly, these variations fall within the normal fluctuation range. As suggested by other reviewers, we reconducted comprehensive experiments by adding four new datasets (10 in total). All baselines use their optimal parameter settings as reported in their original papers. The new Table 1 is available at <https://anonymous.4open.science/r/exp1-DF26/exp1.pdf>, and the new Table 2 is available at <https://anonymous.4open.science/r/exp1-DF26/exp2.pdf>, ensuring the robust validation of the proposed method.
**Response to Q2**
Next, we will explain the reason for not comparing the previous Sheaf Laplacian-based GNNs in Sec. 7.2.
SheafNN by Hansen and Gebhart was designed under the settings with a known sheaf structure, but real-world datasets typically lack this information.
Bodnar et al. adapted the sheaf Laplacian into a learnable form that is suitable for graph learning, making it applicable for graph learning. Our GSL indeed follows Bodnar et al.'s approach, so we have already compared our approach with their proposed Sheaf Laplacian-based GNN.
The hypergraph sheaf Laplacian proposed by Duta et al. is explicitly designed for hypergraphs, making it inapplicable to our benchmark datasets.
Both Conn-NSD by Barbero et al. and D-TNN by Battiloro et al. impose restrictive assumption on high node degrees, which are not satisfied by most benchmark graph datasets.
**Response to Q3**
**Notation:**
- $n$: Number of nodes
- $f_1$, $f_3$, $f_4$: Feature dimensions
- $d$: Stalk dimension
- $c$: Number of classes
- $\text{nnz}_{\mathcal{B}}$: Number of nonzeros in the edge incidence matrix (approximately $2E$, where $|E|$ is the number of edges)
- $r$: Average number of nonzeros per row in the PSL matrix
- $f_{last}$: Feature dimension of the last layer
For PSL-GCN, we generate a new PSL every 10 epochs; therefore, for efficiency analysis per epoch, we consider the following two cases. In the first case we include PSL construction time. The preprocessing stage has a complexity of $O\big(n \cdot f_1 \cdot d \cdot f_3\big)$.
The PSL construction has a complexity of $O\big(\text{nnz}_{\mathcal{B}}^2\big)$.
The forward propagation for 2 layers has a complexity of $O\big(2 \cdot nd \cdot f_3 \cdot (r + f_4)\big)$ (with $r$ representing the average number of nonzeros per row in the PSL matrix).
The final output transformation has a complexity of $O\big(n \cdot d \cdot f_{last} \cdot c\big)$.
Thus, the total complexity is
$$O\Big(\text{nnz}_{\mathcal{B}}^2 + n \cdot f_1 \cdot d \cdot f_3 + 2 \cdot nd \cdot f_3 (r + f_4) + n \cdot d \cdot f_{last} \cdot c\Big).$$
In the second case, we exclude PSL construction time, and the complexity per epoch is
$$O\Big(n \cdot f_1 \cdot d \cdot f_3 + 2 \cdot nd \cdot f_3 (r + f_4) + n \cdot d \cdot f_{last} \cdot c\Big).$$
In order to empirically validate the efficiency of our method, we compare it with the representative work [4] *Neural Sheaf Diffusion: A Topological Perspective on Heterophily and Oversmoothing in GNNs*. We report the average epoch runtime (ms) and the total runtime per fold (s) in the table below:
| Datasets | Cora | Pubmed | Citeseer | Photo | Texas | Cornell | Actor |
|------------|------------|-------------|------------|------------|----------|----------|------------|
| Diag-NSD | 26.4/5.9 | 124.3/34.7 | 25.2/5.8 | 90.6/17.4 | 8.3/1.6 | 8.1/1.5 | 98.4/21.5 |
| O(d)-NSD | 57/12.3 | 204.5/66.3 | 64.1/13.6 | 143.5/26.3 | 26.8/6.7 | 27.4/7.2 | 128.2/31.9 |
| Gen-NSD | 85.3/17.6 | 231.1/74.3 | 92.4/20.6 | 166.7/34.6 | 34.3/14.4| 31.4/14.2| 177.6/45.2 |
| PSL-GCN | 16/4.6 | 83.7/17.4 | 18.3/5.2 | 65.3/15.8 | 6.3/1.1 | 6.4/1.1 | 72.7/17.3 | | Summary: This paper claims that the presence of repeated eigenvalues limits the expressive power of spectral GNNs. To address this issue, this paper proposes perturbed sheaf Laplacian, which achieves optimal model performance due to its more distinct eigenvalues.
Claims And Evidence: The occurrence of repeated eigenvalues does indeed limit the expression ability of spectral GNN, as evidenced by many previous literature. However, this paper claims that eigenvalue correction [1] damages the topological information of the original graph, but does not provide any analysis or basis.
[1]Lu, K., Yu, Y., Fei, H., Li, X., Yang, Z., Guo, Z., Liang, M., Yin, M., and Chua, T.-S. Improving expressive power of spectral graph neural networks with eigenvalue correction. In Proceedings of the AAAI Conference on Artificial Intelligence, volume 38, pp. 14158–14166, 2024.
Methods And Evaluation Criteria: Yes, the proposed method helps alleviate the problem of limited expressiveness caused by repeated eigenvalues.
Theoretical Claims: No
Experimental Designs Or Analyses: 1.According to Table 2, the performance of PSL-GNN is comparable to that of GSL-GNN. Does this indicate that PSL-GNN is sufficient to achieve optimal performance without the need for GSL-GNN?
2. Obviously, this paper improves based on eigenvalue correction, but does not compare it with eigenvalue correction.
3.Although this paper provides a complexity analysis, the actual runtime is helpful for readers to understand the scalability of the proposed method.
Supplementary Material: Yes, the supplementary materials only include code links.
Relation To Broader Scientific Literature: Previous literature has shown that repeated eigenvalues can limit the expressive power of spectral neural networks and hinder model performance. This paper adopts a novel approach (perturbed sheaf Laplacian) to solve this problem.
Essential References Not Discussed: The eigenvalue correction method [1] can also solve the problem of duplicate eigenvalues, but this paper did not compare it with it.
[1]Lu, K., Yu, Y., Fei, H., Li, X., Yang, Z., Guo, Z., Liang, M., Yin, M., and Chua, T.-S. Improving expressive power of spectral graph neural networks with eigenvalue correction. In Proceedings of the AAAI Conference on Artificial Intelligence, volume 38, pp. 14158–14166, 2024.
Other Strengths And Weaknesses: Compared to eigenvalue correction, this paper does not require expensive eigenvalue decomposition.
Other Comments Or Suggestions: No
Questions For Authors: 1.What are the advantages of this paper compared to eigenvalue correction? Although the paper mentions that eigenvalue correction damages the topological information of the original graph, it does not provide a detailed explanation. And this paper did not compare it with eigenvalue correction.
2.What is the training efficiency of the proposed method? Obviously, this paper introduces more intensive matrix operations, so providing actual training time is beneficial.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for your valuable suggestion.
**Response to Comment 1 in Experimental Designs or Analyses**
We reconducted the experiments by adding four new datasets (10 in total). All baseline algorithms use the best parameter settings in their original paper. Additionally, we also tuned the parameters in our proposed method.
Following are the partial experimental results, and the complete experimental results are available at <https://anonymous.4open.science/r/exp1-DF26/exp2.pdf>.
| Datasets | Cora | Pubmed | Citeseer | Photo | Texas | Cornell | Actor |
|-------------|--------------|--------------|--------------|--------------|--------------|--------------|--------------|
| Jacobi | 88.96±0.68 | 89.67±0.82 | 80.73±0.88 | 95.52±0.33 | 93.45±2.03 | 92.94±2.38 | 41.16±0.70 |
| GSL-Jacobi | 89.43±0.94 | 89.92±1.33 | 81.24±1.16 | 95.55±0.36 | 93.84±1.97 | 93.45±1.71 | 41.21±0.45 |
| PSL-Jacobi | **90.73±1.34** | **90.42±1.13** | **81.54±1.12** | **95.69±0.52** | **94.20±1.75** | **93.91±1.96** | **41.94±0.75** |
The results show that PSL performs better than GSL. Nonetheless, we believe that GSL merits further investigation, as it can theoretically learn a new operator with fewer or even no repeated eigenvalues. In this paper, PSL is a special case of GSL, which uses perturbation to achieve more distinct eigenvalues, effectively alleviating the problem of repeat eigenvalues. However, our current perturbation method is not refined enough to completely eliminate repeated eigenvalues—a task that would require a deeper understanding of the sheaf Laplacian's properties, a challenging problem we aim to address in future, as mentioned in the conclusion of our paper.
**Response to Comment 2 in Experimental Designs or Analyses**
We included the eigenvalue correction method in the baselines and compared vanilla GNN, EC-GNN, and PSL-GNN in the new experimental settings.The results can be found at <https://anonymous.4open.science/r/exp1-DF26/exp1.pdf>. The experiments show that our method improves all baselines including EC-GNN.
**Response to Comments 3 in Experimental Designs or Analyses**
Please refer to the following Response to Q2 in Questions For Authors.
**Response to Q1 in Questions For Authors**
Compared with the eigenvalue correction method, our proposed PSL does not compromise the original topological information encoded in the normalized Laplacian matrix. Here, we briefly explain why the eigenvalue correction method will lead to this issue. The spectral gap of the normalized Laplacian often measures the quality of graph connectivity. The eigenvalue correction method, however, reduces the spectral gap of the new operator H (i.e., u₁ = βλ₁ + (1-β)v₁< λ₁, when v₁ < λ₁), which in turn affects information propagation (please see [3]: Spectral Graph Pruning Against Over-Squashing and Over-Smoothing for details). We also experimentally validated this effect:
| | Cora | Pubmed | Citeseer | Photo | Texas | Cornell | Actor |
|-------------|-------|--------|----------|-------|-------|---------|-------|
| **n** | 2708 | 19717 | 3327 | 7650 | 183 | 183 | 7600 |
| **v₁** | 7e-4 | 1e-4 | 6e-4 | 2e-4 | 1e-2 | 1e-2 | 2e-4 |
| **λ₁** | 4e-3 | 1e-2 | 1e-3 | 1e-3 | 5e-2 | 7e-2 | 3e-2 |
| **λ̂₁** | 5e-3 | 1e-2 | 2e-3 | 1e-3 | 5e-2 | 7e-2 | 3e-2 |
Here, $\hat{\lambda}_1$ denotes the spectral gap of PSL. The comparison between EC-GNN and PSL-GNN is available at <https://anonymous.4open.science/r/exp1-DF26/exp1.pdf>. The results show that PSL-GNN outperforms EC-GNN, demonstrating the superiority of our work.
**Response to Q2 in Questions For Authors**
We compared the efficiency of PSL-GNN with a representative work ([4] *Neural Sheaf Diffusion: A Topological Perspective on Heterophily and Oversmoothing in GNNs*). Following the experimental setup in [4], we compared PSL-GCN with the three GCN-based sheaf models proposed in [4] and reported the average epoch runtime (ms) and the total runtime per fold (s). The results are shown in the table below:
| Datasets | Cora | Pubmed | Citeseer | Photo | Texas | Cornell | Actor |
|------------|------------|-------------|------------|------------|----------|----------|------------|
| Diag-NSD | 26.4/5.9 | 124.3/34.7 | 25.2/5.8 | 90.6/17.4 | 8.3/1.6 | 8.1/1.5 | 98.4/21.5 |
| O(d)-NSD | 57/12.3 | 204.5/66.3 | 64.1/13.6 | 143.5/26.3 | 26.8/6.7 | 27.4/7.2 | 128.2/31.9 |
| Gen-NSD | 85.3/17.6 | 231.1/74.3 | 92.4/20.6 | 166.7/34.6 | 34.3/14.4| 31.4/14.2| 177.6/45.2 |
| PSL-GCN | 16/4.6 | 83.7/17.4 | 18.3/5.2 | 65.3/15.8 | 6.3/1.1 | 6.4/1.1 | 72.7/17.3 |
As we can see our approach is significantly more efficient than the other sheaf models. | Summary: This paper aims to solve the repeated eigenvalues of graph Laplacian by proposing a novel perturbed sheaf Laplacian (PSL). The authors claim that PSL can increase the number of distinct eigenvalues and improve the expressive power of spectral GNNs. Experiments on the node classification task validate the effectiveness of PSL on different spectral GNNs.
Claims And Evidence: Some of the claims have been confirmed, but others remain unconvincing.
- C1: **It also compromises the original topological information encoded in the normalized Laplacian matrix.** It is unclear why previous methods fail to use the topological information. This paper claims that "PSL can retain the topological information of the normalized Laplacian matrix", implying that it has the same topological information of the original graph Laplacian. As a result, I think previous methods can also leverage the topological information.
- C2: **Comparion between PSL and GSL**. The proposed PSL is a perturbed version of the general sheaf Laplacian (GSL). However, in the ablation studies, the performance of PSL does not outperform GSL by a large margin. Therefore, the audience may doubt the effectiveness of PSL.
Methods And Evaluation Criteria: 1. This paper only conducts experiments on the node classificiation datasets, which is unconvincing. In practice, we often use graph-level tasks, such as structure counting, to evaluate the expressive power of GNNs. See [1] for more details.
2. This paper does not report the performance of Lu et al., 2024 [2], making the results less convincing.
[1] Graph as Point Set. ICML 2024.
[2] Improving expressive power of spectral graph neural networks with eigenvalue correction. AAAI 2024.
Theoretical Claims: Roughly checking but not confident.
Experimental Designs Or Analyses: This paper should add graph-level experiments. See Methods And Evaluation Criteria.
Supplementary Material: I reviewed the theoretical analysis part.
Relation To Broader Scientific Literature: This paper introduces PSL, which is a model-agnostic method to improve the expressive power of spectral GNNs. PSL consistently improves the performance of polynomial GNNs, which may benefit some downstream applications.
Essential References Not Discussed: This paper only applies PSL to the polynomial GNNs, which is a part of spectral GNNs. It would be better if the authors can try different architectures of spectral GNNs, such as Specformer [3].
[3] Specformer: Spectral Graph Neural Networks Meet Transformers. ICLR 2023.
Other Strengths And Weaknesses: See the above comments.
Other Comments Or Suggestions: See the above comments.
Questions For Authors: See the above comments.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your valuable suggestion.
**Response to C1**
We apologize for the confusion.
Briefly, the Laplacian spectrum measures graph connectivity. Cheeger's inequality $2h_G > \lambda_1 > \frac{h_G^2}{2}$ shows that a larger spectral gap $\lambda_1$ implies better connectivity (More details can be found in: Spectral Graph Pruning Against Over-Squashing and Over-Smoothing). The Cheeger constant $h_G$ quantifies the tightest connectivity bottleneck in a graph. In Lu et al.'s method, the new operator's ($H$) eigenvalues are defined as $u_i = \beta \lambda_i + (1-\beta)v_i$, where $v_i = 2i/n - 2$. When $v_1 < \lambda_1$, it follows that $u_1 < \lambda_1$ (because $u_1 - \lambda_1 = (1 - \beta)(v_1 - \lambda_1)$ with $\beta < 1$), which reduces the spectral gap and impairs information flow, especially in large graphs, where $v_1 = 2/n - 2$ is very, very small. However, our approach perturbs the normalized Laplacian in a way that maintains subtle eigenvalue differences regardless of graph size, thereby preserving the topological information.
Below, we verify our argument above by presenting the spectral gaps' orders of magnitude for the normalized graph Laplacian and PSL across various datasets. As shown in the following table, for each dataset, $v_1 < \lambda_1$, $u_1 < \lambda_1$ , and $\hat{\lambda}_1 \leq \lambda_1$, which indicates that Lu et al.'s approach indeed reduces the spectral gap, thus compromising the original topological information encoded in the normalized Laplacian matrix.
| | Cora | Pubmed | Citeseer | Photo | Texas | Cornell | Actor |
|-------------|-------|--------|----------|-------|-------|---------|-------|
| **n** | 2708 | 19717 | 3327 | 7650 | 183 | 183 | 7600 |
| **v₁** | 7e-4 | 1e-4 | 6e-4 | 2e-4 | 1e-2 | 1e-2 | 2e-4 |
| **λ₁** | 4e-3 | 1e-2 | 1e-3 | 1e-3 | 5e-2 | 7e-2 | 3e-2 |
| **λ̂₁** | 5e-3 | 1e-2 | 2e-3 | 1e-3 | 5e-2 | 7e-2 | 3e-2 |
**Response to C2**
According to Reviewer QU1C's suggestion, we reconducted comprehensive experiments by adding four new datasets (10 in total). All baseline algorithms use the best parameter settings in their original papers. The results demonstrate PSL achieves better performance than GSL, which are available at <https://anonymous.4open.science/r/exp1-DF26/exp2.pdf>.
**Response to Q1 in Methods And Evaluation Criteria**
It's insightful to point out the relevance of graph-level tasks in [1]. The primary focus of our paper was to address a specific known limitation inherent to spectral GNNs: the performance degradation and limited expressiveness caused by repeated eigenvalues in the standard graph Laplacian. We chose node classification to demonstrate direct evidence that our proposed PSL method successfully overcomes the targeted limitation in a practical application for spectral GNNs.
Standard spectral GNN approaches face inherent challenges when applied across datasets containing graphs of varying sizes and structures, which are common in graph-level tasks. It's difficult to directly learn a single spectral filter that works across different $\Lambda$ and $U$ matrices from different graphs.
Rigorously evaluating PSL's impact on graph-level tasks might involve developing novel ways to combine PSL-based spectral features with appropriate graph pooling mechanisms. While valuable, we considered this beyond the primary scope of introducing and validating the core PSL concept.
**Response to Q2 in Methods And Evaluation Criteria**
We included Lu et al.'s method in the baselines. The results in the following table show our method outperforms Lu et al.'s method. The full results are available at <https://anonymous.4open.science/r/exp1-DF26/exp1.pdf>.
| Datasets | Cora | Citeseer | PubMed | Computers | Photo | Chameleon | Actor | Squirrel | Texas | Cornell |
|-------------|---------------|---------------|---------------|---------------|---------------|----------------|---------------|---------------|---------------|---------------|
| Jacobi | 88.96±0.68 | 80.73±0.88 | 89.67±0.82 | 90.42±0.31 | 95.52±0.33 | 74.23±1.45 | 41.16±0.70 | 57.38±1.24 | 93.45±2.03 | 92.94±2.38 |
| EC-Jacobi (Lu et al.'s method) | 89.06±0.67 | 81.28±0.96 | 89.87±0.42 | 90.33±0.28 | 95.54±0.36 | 75.64±1.51 | 41.01±0.74 | 59.87±0.91 | 93.48±1.49 | 93.29±2.33 |
| PSL-Jacobi (Our method) | **90.73±1.34** | **81.54±1.12** | **90.42±1.13** | **90.83±0.61** | **95.69±0.52** | **75.87±1.44** | **41.94±0.75** | **61.47±0.98** | **94.20±1.75** | **93.91±1.96** |
**Response to comments in Essential References Not Discussed**
Specformer requires eigenvalue encoding. If PSL is integrated into Specformer, we have to encode the learned PSL, which implies the encoding process would involve training a PSL-GNN. The computation cost would be substantially increased.
---
Rebuttal Comment 1.1:
Comment: I have read the authors' rebuttal and checked other reviewers' comments. Although this paper does not provide experiments on graph-level tasks, it still brings a good idea and new content to GNNs. I raise my score to weak accept. | Summary: This paper presents a novel solution to the repeated eigenvalue problem in Spectral GNNs.
Through the formal definition of cellular sheaf on graphs,
the paper formally introduces the definition of cellular sheaf,
which essentially specifies that when a signal with dimension $d$ propagates from node $i$ along edge $(i,j)$ to another node $j$,
it is not directly added but first undergoes a linear transformation, which can be denoted as $Q_{ij}$.
Each $Q_{ij}$ contains $d\times 1$ learnable parameters.
Assuming this linear transformation is Identity, the operating matrix only changes from L to $L \otimes I_d$,
with the same number of distinct eigenvalues
(this operation can be viewed as expanding the dimension of $L$).
Now, since this linear transformation is not Identity, it actually brings a slight perturbation,
which increases the number of distinct eigenvalues.
The paper combines Weyl's theorem to show that when this perturbation is small enough, it guarantees an increase in distinct eigenvalues.
And through experiments, it verifies that indeed more eigenvalues are obtained.
The paper compares with state-of-the-art polynomial-filter-based GNNs with almost no hyperparameter tuning,
and shows that the Sheaf Laplacian method brings a slight advantage.
Claims And Evidence: - The part about introducing Sheaf Laplacian and the perturbation method to bring more distinct eigenvalues is very interesting and clear and convincing.
- It undoubtedly makes a contribution to the multiple eigenvalue problem.
- However, I'm not entirely convinced that the experiments sufficiently support the claim that ``solving the multiple eigenvalue problem can improve node classification performance''. Please see section (5. Experimental Designs Or Analyses) in the Review table.
Methods And Evaluation Criteria: Yes.
Theoretical Claims: I roughly checked Theorem 4.1 and Prop 5.2 - Corollary 5.4.
Experimental Designs Or Analyses: The paper's experiments are the common node classification tasks in the Spectral GNN series of work,
including both homophilic and heterophilic graph datasets.
However, I'm concerned that the way authors conducted the experiments seems too rough.
Spectral GNNs, including GCN, are sensitive to hyperparameters (of course, the tendency to over-tune hyperparameters is a bad problem),
but this paper, according to Appendix E.4., seems to have done no hyperparameter tuning at all.
Therefore, the experimental data reported in the paper is significantly **lower** than elsewhere.
Meanwhile, the method presented in the paper only brings quite **slight** improvements,
and the number of datasets compared is also relatively small.
So, although I appreciate the ideas in this work,
I'm skeptical about whether solving the repeated eigenvalue problem can truly bring improvements to downstream tasks, and think the experiments are insufficient.
Supplementary Material: I mainly looked at the Experimental Setup section. I didn't carefully review other parts.
Relation To Broader Scientific Literature: This paper mainly responds to the discussion about repeated eigenvalues' impact on spectral GNNs expressiveness in Wang & Zhang (2022).
Essential References Not Discussed: No.
Other Strengths And Weaknesses: Please check the former review form(2. Claims And Evidence)
Other Comments Or Suggestions: None.
Questions For Authors: I mainly care the issues raised in section (5. Experimental Designs Or Analyses).
1. I suggest the authors report the difference in response values of $g(\lambda)$ before and after perturbation.
2. I suggest the authors use Optuna for light hyperparameter tuning to confirm whether the method indeed has advantages (empirically).
3. Could the authors explain more on the correspondence between $\nu$ and $\|P\|$ in Thm.4.1? If there is theoretical justification, that would be great. If not, empirical evidence would also be helpful to understand this relationship.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your valuable suggestion.
**Response to the raised issues in Experimental Designs or Analyses**
We reconducted the experiments by adding four new datasets (10 total) and using a full-supervised split (60%/20%/20%), which follows Wang & Zhang’s (*How Powerful are Spectral Graph Neural Networks*). It is worth noting that our previous experiments use the split (48\%/32\%/20\%), which is only recommended by Bondar et al. in *Neural Sheaf Diffusion: A Topological Perspective on Heterophily and Oversmoothing in GNNs*.
The partial experimental results are as follows, in which each baseline algorithm uses the best parameter settings in their original paper. We also tuned the parameters in our proposed method. It shows that PSL-GNN still yields improvements over all baselines and performs better than EC-GNN.
The complete experimental results are available at <https://anonymous.4open.science/r/exp1-DF26/exp1.pdf>.
| Datasets | Cora | Citeseer | PubMed | Computers | Photo | Chameleon | Actor | Squirrel | Texas | Cornell |
|-------------|---------------|---------------|---------------|---------------|---------------|----------------|---------------|---------------|---------------|---------------|
| GPRGNN | 88.54±0.82 | 80.09±1.03 | 88.52±0.46 | 87.01±0.74 | 93.87±0.34 | 67.14±1.10 | 39.92±0.65 | 50.08±1.95 | 92.97±1.41 | 91.32±2.02 |
| EC-GPR | 89.41±0.69 | 80.66±1.01 | 89.64±0.53 | 89.91±0.68 | 94.76±1.02 | 74.24±1.06 | 40.42±0.77 | 62.48±2.03 | 92.27±1.92 | 90.79±2.22 |
| PSL-GPR | **90.13±0.92** | **81.11±0.76** | **89.82±1.89** | **89.93±1.70** | **94.87±0.96** | **74.78±1.34** | **41.17±0.96** | **63.65±0.87** | **94.74±1.65** | **92.44±1.85** |
| Jacobi | 88.96±0.68 | 80.73±0.88 | 89.67±0.82 | 90.42±0.31 | 95.52±0.33 | 74.23±1.45 | 41.16±0.70 | 57.38±1.24 | 93.45±2.03 | 92.94±2.38 |
| EC-Jacobi | 89.06±0.67 | 81.28±0.96 | 89.87±0.42 | 90.33±0.28 | 95.54±0.36 | 75.64±1.51 | 41.01±0.74 | 59.87±0.91 | 93.48±1.49 | 93.29±2.33 |
| PSL-Jacobi | **90.73±1.34** | **81.54±1.12** | **90.42±1.13** | **90.83±0.61** | **95.69±0.52** | **75.87±1.44** | **41.94±0.75** | **61.47±0.98** | **94.20±1.75** | **93.91±1.96** |
**Response to Question 1**
We design a metric $S(k,m)$ to quantify the difference in response values of $g(\lambda)$ before and after perturbation. Assuming the filtering coefficients for frequency components $U^T X_i W$ before and after perturbation are $k$ and $m$, respectively, the similarity metric is defined as:
$$
S(k,m)=
\begin{cases}
1, & \text{if } k = m = 0, \\
1 - 2\frac{|k-m|}{|k|+|m|}, & \text{otherwise}.
\end{cases}
$$
Specifically, $S(k,m)=1$ indicates identical coefficients ($k=m$), including when both are zero. We measured the response difference for PSL-GCN and PSL-GPR in the Cora dataset. The figure showing the results is at <https://anonymous.4open.science/r/exp1-DF26/response.pdf>. Only about 1/10 of all nodes exhibit no change ($S=1$) in their filtering coefficients before and after perturbation, which aligns with the results reported in Table 3 of our paper.
**Response to Question 2**
Please refer to Response to the raised issues in Experimental Designs or Analyses.
**Response to Question 3**
We guess you mean $\phi$. Recall that in Theorem 4.1, $\phi$ is defined as the minimum eigenvalue gap of the normalized Laplacian matrix before perturbation. When a perturbation matrix $P$ is applied, Weyl’s inequality tells us that the eigenvalue change is bounded by its spectral norm, $||P||_2$. So if $||P||_2 < \phi$, then the eigenvalue variation intervals do not overlap, resulting in no eigenvalue multiplicity. Otherwise, the new eigenvalues might coincide.
While Theorem 4.1 describes a strict condition for ensuring fully distinct eigenvalues, in practice, it is not required to adhere to this condition strictly. We only need $||P||_2$ to be sufficiently small (but not too small. $||P||_2$ approaching zero would alleviate the perturbation effects.).
To address this, we introduce the learnable perturbation restriction maps to achieve a controllable and appropriate perturbation matrix $P$. Empirically, this approach maintains a sufficiently small spectral norm such that more eigenvalues split without generating identical new eigenvalues.
---
Rebuttal Comment 1.1:
Comment: Thank you for the supplementary experimental details.
Regarding **Q3**, I would like to ask whether in your experiments, you actually demonstrated the $\phi$ in the Theorem through $\nu$?
---
Reply to Comment 1.1.1:
Comment: Thank you so much for prompting this clarification. Our paper uses the symbols $\phi$ and $\eta$, but just to confirm, $\nu$ does not appear in our work. That might reflect a misunderstanding in our previous response. Thinking about parameters that might be closely related to your query for this final response, we considered the potential relevance of $\eta$. We conducted an empirical study on $\eta$'s impact on eigenvalue perturbations and performance, and the findings are reported in Appendix F.2 and F.4 in our paper. We hope this addresses your question more fully! | null | null | null | null | null | null |
Token Coordinated Prompt Attention is Needed for Visual Prompting | Accept (poster) | Summary: This paper proposes a Token Coordinated Prompt Attention (TCPA) module to enhance the effectiveness of visual prompting in Vision Transformers (ViT). Existing methods use shared prompts for all tokens, overlooking the distinct roles of CLS and image tokens, leading to limited representational capacity. TCPA addresses this by assigning CLS and image-specific prompts for targeted attention interactions, improving their discriminative abilities. A matching function further assigns coordinated prompts to individual image tokens to enhance feature diversity and representation. Experiments show that TCPA significantly improves feature diversity and performance.
## update after rebuttal
I have reviewed the authors' rebuttal as well as the comments from my fellow reviewers. I remain inclined to maintain my positive assessment and will keep my current rating.
Claims And Evidence: The claims made in the submission are well-supported by clear and convincing evidence. The paper thoroughly validates the effectiveness of the proposed Token Coordinated Prompt Attention (TCPA) module through extensive experiments across multiple benchmarks. The authors provide detailed comparisons with state-of-the-art methods, demonstrating significant improvements in both feature diversity and overall performance. Additionally, ablation studies are conducted to isolate the contributions of CLS-specific and image-specific prompts, highlighting the effectiveness of each component.
Methods And Evaluation Criteria: The proposed methods and evaluation criteria (e.g., benchmark datasets) are appropriate and well-suited to the problem at hand. The chosen benchmark datasets are representative, providing valuable insights into the model's performance across various scenarios.
Theoretical Claims: The correctness of the theoretical claims in the paper is not in question. The paper relies on two established theories from existing literature to demonstrate that the self-attention matrix in current prompt learning methods is low-rank. Furthermore, through experimental analysis, it is validated that the proposed method enhances the diversity of the self-attention matrix, encouraging different tokens to focus on diverse discriminative information.
Experimental Designs Or Analyses: The experimental design and analysis in the paper are both reasonable and effective. The authors have selected appropriate comparative experiments to validate the proposed method, and the benchmarks and evaluation metrics used in the experiments are well-targeted, allowing for a comprehensive assessment of the model's performance. Additionally, ablation studies are included to verify the performance of each module. The paper also presents several visualization experiments, further supporting the theoretical claims made. These design choices significantly contribute to the reliability and validity of the research.
Supplementary Material: The authors did not provide supplementary materials but prepared an appendix. In the appendix, the authors present additional visualization experiments of features and attention maps to validate that the proposed method can extract more comprehensive discriminative information, and that the extracted features are more discriminative.
Relation To Broader Scientific Literature: This paper introduces a plug-and-play enhancement module, TCPA, designed for existing visual prompt learning methods (such as VPT, VP, VFPT, etc.). The module works by modifying the interaction between the CLS, image tokens, and prompts in the attention mechanism, encouraging different tokens to interact with only specific prompts. This, in turn, helps the model extract more comprehensive discriminative information.
Theoretically, the paper leverages two existing theories to demonstrate that the attention matrix in current prompt learning methods is low-rank. This is further validated through experiments, which also show that the proposed method enhances the diversity of the attention matrix, encouraging different tokens to focus on a broader range of discriminative information.
Essential References Not Discussed: No essential related works crucial for understanding the contributions of the paper have been omitted. The paper provides a comprehensive overview of related work in visual prompting, covering the core literature relevant to the proposed method. The authors have appropriately applied the relevant theories and provided a thorough introduction to them. These citations and discussions offer strong background support for understanding the key contributions of the paper.
Other Strengths And Weaknesses: Strengths:
1. The proposed method is novel. The paper introduces Token Coordinated Prompt Attention for the first time, which changes the way tokens and prompts interact in prompt learning methods. By selecting specific prompts for each token to interact with, this approach helps the model extract rich and comprehensive discriminative information.
2. The paper is well-structured and coherent. The logical flow is smooth, and the writing is clear. The accompanying figures effectively illustrate and validate the points made in the paper, making the arguments more accessible and convincing.
3. The paper provides comprehensive comparative experiments. The authors conduct experiments across multiple benchmark datasets and integrate the proposed module into several existing prompt learning methods, achieving consistent performance improvements. This demonstrates the effectiveness and generalizability of the proposed approach across different scenarios.
4. The ablation studies are well-designed. The authors include a wide range of ablation and visualization experiments, which help readers understand the role of each module and provide a clear visualization of how the proposed TCPA influences the attention maps and feature extraction process of the model.
Weaknesses:
1. The authors only show examples of 2D and 3D attention maps for a single sample. Providing additional examples across a wider range of samples would further strengthen the argument and offer additional validation of the method's effectiveness.
2. The authors should conduct hyperparameter experiments on more datasets to thoroughly analyze the impact of hyperparameters on the model's performance. This would offer a more comprehensive understanding of how different settings influence the results.
Other Comments Or Suggestions: It is recommended that the authors include pseudocode of the method to help readers better understand the process and flow of the proposed approach. This would make it easier for others to reproduce or build upon the work.
Questions For Authors: Could the authors clarify whether the proposed module is applicable to all visual prompting methods, or if it is specifically suited for certain types of methods, such as token-based prompting approaches?
Ethical Review Concerns: N/A
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for your appreciation of our **novelty**, **effectiveness** and **comprehensive experiments**.
(The images mentioned below are available at the anonymous link: https://anonymous.4open.science/r/ICML-2025-Paper35-Rebuttal-7E9E.)
### Q1: More Visualizations
1. Thank you for your valuable feedback. We have included additional 2D and 3D attention map visualizations with more samples in the appendix.
2. As shown in Fig.4.1 (https://anonymous.4open.science/r/ICML-2025-Paper35-Rebuttal-7E9E/4.1.png), the same trend is observed in the additional visualizations. In existing visual prompt methods, *the attention regions of prompts are highly similar*, leading to nearly identical features being extracted from the CLS and image tokens. In contrast, our proposed TCPA module *enhances more diverse attention across prompts, CLS tokens, and image tokens*.
3. This is because our method selects different prompts for different tokens and performs attention-based interactions, encouraging the model to extract more diverse and comprehensive discriminative information.
### Q2: Hyperparameter
1. As shown in Fig.4.2 (https://anonymous.4open.science/r/ICML-2025-Paper35-Rebuttal-7E9E/4.2.png), we have added hyperparameter experiments *on the Dog and GTSRB datasets*, which exhibit the same trend observed on the CUB dataset.
2. When the prompt pool is too small, prompt diversity is limited, causing high overlap in selected prompts and making the extracted features indistinguishable. On the other hand, an excessively large prompt pool increases learnable parameters, which can lead to overfitting and decreased performance. Optimal performance is achieved with a moderate pool size.
3. Additionally, we have included hyperparameter experiments for the weight parameters $\lambda_i
$ and $\lambda_c$. As shown in Fig.3.2 (https://anonymous.4open.science/r/ICML-2025-Paper35-Rebuttal-7E9E/3.2.png), the best performance is achieved when $\lambda_i=0.03$ and $\lambda_c=0.02 $. When $\lambda_i$ and $\lambda_c$ are too large, they *interfere with the learning of prompts and the classifier*, leading to performance degradation. When $\lambda_i$ and $\lambda_c$ are too small, *the indicators corresponding to the prompts cannot be effectively learned*, making it difficult to accurately match prompts to different tokens, which also results in performance degradation.
### Q3: Pseudocode of the Method
1. Thank you for your valuable suggestions.
2. We have added the pseudocode of the method in the appendix to clearly illustrate the proposed approach.
### Q4: Applicability of the Method
1. Existing visual prompt learning methods can be categorized into two types based on the prompt placement: image-based and token-based. *Our approach is compatible with both*.
2. For token-based visual prompt learning methods, our TCPA can enhance the attention interaction process, thereby improving performance.
3. For image-based methods, token prompts can be incorporated alongside the original approach, integrating our TCPA to provide continuous prompting during feature extraction. | Summary: The paper introduces Token Coordinated Prompt Attention (TCPA), a novel module for visual prompting in Vision Transformers (ViTs). TCPA assigns specific prompts to CLS and image tokens, enhancing their discriminative abilities through targeted attention interactions. It uses a matching function to dynamically allocate prompts to image tokens, improving feature diversity and representation. Experiments show TCPA outperforms state-of-the-art methods, validating its effectiveness in extracting comprehensive and discriminative features.
Claims And Evidence: Yes.
Methods And Evaluation Criteria: For the Token Coordinated Prompt Attention (TCPA) module, the authors propose a novel approach to disentangle prompts for CLS and image tokens, enhancing feature diversity and discriminability. However, the prompt assignment process relies on a cosine distance-based matching function, which can capture the complex relationships between tokens and prompts.
Theoretical Claims: Theoretical correct.
Experimental Designs Or Analyses: The paper demonstrates the effectiveness of TCPA through comprehensive evaluations on HTA and VTAB benchmarks, consistently outperforming state-of-the-art methods like VPT and DAMVP across diverse tasks. Ablation studies clearly highlight the contributions of R-TCPA (role-level) and T-TCPA (token-level) components, with an analysis of prompt pool size. Visualizations, including t-SNE and attention maps, show that TCPA extracts more discriminative and diverse features compared to baselines. Additionally, theoretical analysis based on the low-rank properties of self-attention (Theorems 4.1 and 4.2) provides a solid foundation for TCPA's design.
Supplementary Material: Supplementary material are well reviewed.
Relation To Broader Scientific Literature: This paper advances the field of visual prompting by introducing the Token Coordinated Prompt Attention (TCPA) module, which enhances feature diversity and discriminability in Vision Transformers through role-specific and dynamically assigned prompts, addressing a key limitation in existing methods.
Essential References Not Discussed: None
Other Strengths And Weaknesses: Incomplete Hyperparameter Sensitivity: Only prompt pool size is explored; other hyperparameters (e.g., weighting parameters in Sec. 3.4.) are not thoroughly analyzed.
Other Comments Or Suggestions: None
Questions For Authors: How would TCPA perform if extended to the base-to-novel task [1,2] in prompt learning? It is recommended that the authors consider this direction for further research.
[1] Khattak M U, et al. Self-regulating prompts: Foundational model adaptation without forgetting[C]//ICCV. 2023: 15190-15200.
[2] Wu G, et al. Cascade prompt learning for vision-language model adaptation[C]//ECCV 2024: 304-321.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your appreciation of our **novelty**, **effectiveness** and **comprehensive experiments**.
(The images mentioned below are available at the anonymous link: https://anonymous.4open.science/r/ICML-2025-Paper35-Rebuttal-7E9E.)
### Q1: Cosine Distance-based Matching Function
1. We conduct a visualization experiment on the image prompts selected by different image tokens. As shown in Fig.3.1 (https://anonymous.4open.science/r/ICML-2025-Paper35-Rebuttal-7E9E/3.1.png), tokens corresponding to different parts of an object select different prompts. This indicates that our matching mechanism can recognize the different semantic information contained in tokens to some extent and assign the corresponding prompts accordingly.
2. During the method design process, we explored various alternative matching strategies, including Euclidean distance, Kullback-Leibler (KL) divergence, and weight prediction through a learnable MLP. As shown in the table below, among these matching strategies, cosine distance achieved the best performance.
3. In future research, we will further optimize the prompt matching mechanism by incorporating neighborhood token information to achieve more accurate prompt assignment.
||CUB|Dog|GTSRB|
|-|-|-|-|
|Euclidean Distance|89.3|91.4|93.4|
|KL Divergence|89.2|91.3|93.6|
|MLP|89.0|91.2|93.7
|Cosine Distance|**89.5**|**91.5**|**94.1**|
### Q2: Hyperparameter
1. Thank you for your valuable suggestions. We conduct an ablation study on the weight hyperparameters $\lambda_i$ and $\lambda_c$ on the CUB dataset. As shown in Fig.3.2 (https://anonymous.4open.science/r/ICML-2025-Paper35-Rebuttal-7E9E/3.2.png), the best performance is achieved when $\lambda_i=0.03$ and $\lambda_c=0.02 $.
2. When $ \lambda_i $ and $ \lambda_c $ are too large, they *interfere with the learning of prompts and the classifier*, leading to performance degradation.
3. When $ \lambda_i $ and $ \lambda_c $ are too small, *the indicators corresponding to the prompts cannot be effectively learned*, making it difficult to accurately match prompts to different tokens, which also results in performance degradation.
### Q3: Base-to-novel Task
1. First, *for a fair comparison* with existing visual prompt learning methods, we conducted experiments on the HTA and VTAB benchmarks to validate the effectiveness of our approach.
2. Existing visual prompt learning methods typically use a ViT backbone. When adapting a pretrained ViT model to downstream tasks, a task-specific classifier must be learned *based on the number of categories in the target task*. Consequently, due to the constraints of the classifier, ViT models cannot conveniently train on base classes and generalize to novel classes as CLIP models do.
3. Additionally, we adapt several visual prompt learning methods, including VP, VPT, and VFPT, and our TCPA, to the CLIP model to evaluate their performance on the base-to-novel task. As shown in the table below, using the VFPT method as an example, our TCPA improves performance by **0.5%–0.9% on base classes** and by **0.5%–1.3% on novel classes**. Similarly, our TCPA also achieves consistent performance improvements on the VP and VPT methods. This improvement stems from our approach’s ability to assign different prompts to different image tokens, enabling the model to capture more comprehensive and fine-grained discriminative information for each category, thereby enhancing generalization to novel classes.
4. In future research, we plan to incorporate part-level modeling of learned categories to further improve the applicability and generalizability of our approach.
|Methods||Caltech101|OxfordPets|Stanford_Cars|Flowers102|
|-|-|-|-|-|-|
|VP|Base / Novel|97.0 / 93.5|92.3 / 94.1|68.4 / 72.8|89.5 / 70.2|
|**+TCPA**|Base / Novel|97.4 / 94.1|93.1 / 94.4|70.7 / 73.6|95.5 / 71.2|
|VPT|Base / Novel|97.3 / 93.9|95.3 / 94.3|72.4 / 74.1|96.2 / 71.1|
|**+TCPA**|Base / Novel|97.8 / 94.6|95.7 / **94.9**|73.7 / 74.7|96.5 / 72.3|
|VFPT|Base / Novel|97.6 / 94.4|95.9 / 94.2|73.4 / 74.6|96.6 / 71.3|
|**+TCPA**|Base / Novel|**98.1** / **94.9**|**96.3** / 94.8|**74.2** / **75.7**|**97.5** / **72.6**| | Summary: This paper proposes Token Coordinated Prompt Attention (TCPA) to enhance visual prompting for Vision Transformers. By disentangling and adaptively assigning prompts to different CLS and image tokens based on their distinct roles, this method effectively mitigates the limitations of conventional visual prompting and improves feature diversity and discriminability.
Claims And Evidence: Yes. Figure 1 supports the claim that existing visual prompting methods usually learn and leverage the same prompt for all tokens without considering the different functionalities of CLS and image tokens, as well as the varying discriminative information conveyed by different image tokens, leading to different tokens focusing on similar regions and extracting biased discriminative information.
Methods And Evaluation Criteria: Yes. The proposed method selects different prompts for different tokens and performs attention-based interactions, thereby improving the representation ability of ViT.
Theoretical Claims: In this paper, Theorem 4.1 and Theorem 4.2 do not involve specific proofs.
Experimental Designs Or Analyses: Yes. In Section 5.5.3., there is a lack of analysis of the two weight parameters \lambda_i and \lambda_c in Equation (14). Beside, the last part of Section 5.5.4. contains redundant experimental analysis.
Supplementary Material: Yes. The supplementary material provides more t-SNE visualization results of extracted features and more attention visualization results, which further demonstrate the effectiveness of the proposed TCPA.
Relation To Broader Scientific Literature: Prior methods use the same prompts for all tokens without considering the distinct roles of CLS and image tokens, as well as the differences in discriminative information extracted by various image tokens. This results in the features extracted by different tokens being neither distinguishable nor comprehensive, which limits the model's performance. This paper proposes TCPA to select different prompts for different tokens and performs attention-based interactions, thereby encouraging the model to extract more diverse and comprehensive discriminative information.
Essential References Not Discussed: No. The related work is enough to understand the research background of this paper.
Other Strengths And Weaknesses: Strengths:
The proposed TCPA addresses a key limitation of existing visual prompting methods, i.e., uniform prompt interaction, improving the diversity and representational capacity of the extracted features.
Weaknesses:
(1)The method description lacks sufficient clarity in Section 3.
(2)The use of mathematical notation is somewhat inconsistent, which hinders comprehension.
(3)The optimization objective lacks a detailed explanation, and the weight parameters are not supported by a thorough parameter analysis experiment.
Other Comments Or Suggestions: (1)Please revise Section 3 of the paper to ensure clarity in the methodology and consistency in notation.
(2)Please revise Section 5.5.4. of the paper to remove duplicate experimental analyses.
(3)It is recommended to provide a more detailed explanation of Equation (11) and Equation (14) and include a parameter analysis of the weight parameters in the experimental section.
Questions For Authors: (1)What is the purpose of the attention region corresponding to "Row 9, Column 8" in Figure 1?
(2)For the sentence “Through the equation above, we obtain the output for the image tokens (p_{j+1}^{i,d}, h_{1}^{j+1}, · · · , h_{M}^{j+1}), which, together with the previously obtained output of the CLS token c_{j+1}, serves as the input for the next MSA block B_{j+1}.” in Section 3.2, why is p_{j+1}^{i,d} not discarded.
(3)Are k_{k}^{i} and \kappa_{k}^{i} in Equation (9) representing the same notation?
(4)Does \hat{A}_{m,k} represent an element of the binarized matrix \tilde{A}?
(5)Please explain Equation (11) and Equation (14) in detail, and add a parameter analysis of the weight parameters in the experimental section.
(6)The sentence below Equation (11) in Section 3.3, “…, we obtain the mask M^{i} corresponding to the CLS token,” seems to contain a typo. M^{i} should be written as M^{c}.
(7)There are repeated experimental analyses in Section 5.5.4.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for your appreciation of our **motivation**, **effectiveness** and **comprehensive experiments**.
### Q1: Theorem
1. Theorem 4.1 and Theorem 4.2 mentioned in our paper are established theories from existing work, which we have *appropriately cited*.
2. In their original paper, these theorems were used to analyze the rank of the attention matrix in vision models. In our paper, we reference these theorems alongside Fig.3 to illustrate that existing prompt learning methods tend to focus on overlapping information, whereas our TCPA assigns different prompts to different tokens, *enabling a more comprehensive extraction of discriminative features*.
3. We have now included the proof of Theorem 4.1 and Theorem 4.2 in the appendix for completeness.
### Q2: Hyperparameter
Thank you for your valuable suggestions. We have included hyperparameter experiments for the weight parameters $ \lambda_i $ and $ \lambda_c $, as detailed in **Reviewer LMp2 Q2:Hyperparameter**.
### Q3: Section 5.5.4
1. In Section 5.5.4, we primarily present the t-SNE visualizations of the features extracted by both the baseline methods and our approach, further demonstrating that our method captures more comprehensive discriminative information.
2. We have revised and refined the last two sentences in this section to eliminate redundancy.
### Q4: Notations in Section 3
1. We have thoroughly checked the formulas in the paper. For example, we have standardized the use of *superscripts to indicate different attributes* of tokens, prompts, and indicators (i.e., whether they belong to the CLS token or image token), while *indices representing layer numbers and patch indices are consistently placed in subscripts*. For example, the notation $ \boldsymbol{h}^1_i $, which originally represented the first token in the $ i $-th layer, has been revised to $ \boldsymbol{h}_{i,1} $. Additionally, to improve clarity, we have changed $ M $, which originally represented the number of patches, to $ N $, and $ N $, which originally represented the number of network layers, to $ L $.
2. Furthermore, we have carefully reviewed other parts of the paper and corrected grammatical issues and typos. For example, in Eq.9, we have corrected $ \boldsymbol{k} $ to $ \boldsymbol{\kappa} $.
### Q5: Optimization Objective
1. The objective of Eq.14 is to *minimize* the distance between image tokens and their corresponding prompt indicators, ensuring that both $\sum{\mathcal{S}(\boldsymbol{h}_m, \boldsymbol{\kappa}^i_m)}$ and $\sum{\mathcal{S}(\boldsymbol{c}_j, \boldsymbol{\kappa}^c_j)}$ are as small as possible.
2. To enhance clarity, we have added an explanation of the optimization objective before Eq.14.
### Q6: Eq.11
1. The binarized matrix $\mathrm{\mathbf{\hat{A}}} \in \{0,1\}^{M \times N_i}$ has dimensions matching *the number of image tokens*, but in the actual model, **the CLS token needs to be considered**. In other words, the dimensions of $\mathrm{\mathbf{\hat{A}}}$ need to match *the number of image tokens plus one*. Eq.11 is designed to achieve this dimensional alignment.
2. To help readers better understand, we have added an explanatory note before Eq.11 in the paper.
### Q7: "Row 9, Column 8" in Figure 1
1. The first two are objects, and a background token is selected as a reference for comparison to make the experiment more comprehensive.
2. Existing methods focus on the same regions regardless of whether the tokens correspond to objects or the background, whereas in our approach, different object tokens attend to different object regions, and the background token focuses more on the background.
3. This is because our TCPA matches different prompts to tokens with different semantics for attention interactions, enabling more comprehensive extraction of discriminative information from the image.
### Q8: Notation $ p_{j+1}^{i,d} $ in Section 3.2
1. This is a typo on our part. The output $p_{j+1}^{i,d}$ for each layer should be discarded and not used for the next layer's output.
### Q9: Eq.9
1. Yes, $k_{k}^{i}$ and $\kappa_{k}^{i}$ in Eq.9 represent the same notation.
2. We have standardized it to $\kappa_{k}^{i}$.
### Q10: Notation $\hat{A}_{m,k}$
1. Yes, $\hat{A}_{m,k}$ represents an element of the matrix $\tilde{A}$.
2. We have standardized it to $\hat{A}$ and no longer use $\tilde{A}$ to represent it.
### Q11: Typo
1. We have revised $\mathrm{\mathbf{M}}^i$ to $\mathrm{\mathbf{M}}^c$ in the sentence below Eq.11 in Section 3.3.
2. We have also carefully checked and corrected other sections of the paper for grammatical issues and typos, such as changing "SPT" to "VPT" in Section 5.5.
---
Rebuttal Comment 1.1:
Comment: I have reviewed the authors' rebuttal and the comments from other reviewers. I would like to maintain my positive rating.
---
Reply to Comment 1.1.1:
Comment: Dear reviewer zc31
Thank you for your thoughtful feedback and for reconsidering our work. Your comments helped us refine the presentation and strengthen the manuscript. We truly appreciate the opportunity to clarify our approach and the time you spent reviewing our submission.
Best regards,
Authors | Summary: This paper introduces a token-wise prompt termed as TCPA to enrich discriminative information of tokens by assigning specific prompts to each different tokens. As a plug-and-play strategy，TCPA can be seamlessly integrate with existing prompt based methods. Experiments show that TCPA can achieve consistent performance gains across diverse benchmarks.
## update after rebuttal
The rebuttal has well addressed my concerns, so I changed my scores from 2->3. I recommend acceptance of this paper.
Claims And Evidence: The claims made in the submission are supported by clear and convincing evidence.
Methods And Evaluation Criteria: The proposed approach contains several unresolved technical issues. The motivation is supported by previous existing works, yet the reason the proposed methods can assign different prompt to different image tokens is unclear. There is no theoretical analysis or strategy to ensure the load balance of different prompts. The eq.14 that optimizes keys of prompts looks wrong.
Theoretical Claims: No theoretical claims.
Experimental Designs Or Analyses: Sound.
Supplementary Material: I have reviewed the supplementary materials, which include extra visualization of the method.
Relation To Broader Scientific Literature: Two existing works [1,2] served as theoretical support to this paper.
[1] Wang, S., Li, B. Z., Khabsa, M., Fang, H., and Ma, H. Linformer: Self-attention with linear complexity. arXiv preprint arXiv:2006.04768, 2020.
[2] Kim, Y., Li, Y., Moitra, A., Yin, R., and Panda, P. Do we really need a large number of visual prompts? Neural Networks, 177:106390, 2024.
Essential References Not Discussed: None.
Other Strengths And Weaknesses: See other parts.
Other Comments Or Suggestions: 1. Figure 3 is difficult to interpret due to unclear axis labels. It should be immediately discernible which axis represents keys and which represents values. Revisions to these figures may needed.
2. The notation throughout the paper is inconsistent and poorly defined. For example, M is used to represent both the number of tokens and the final mask, which can cause confusion. The subscript c represents layers, while the subscript h represents index, which is counterintuitive.
3. The paper contains several grammatical errors and awkward phrasings that impede clarity.
4. Typos in 5.5 (SPT).
Questions For Authors: I may raise my score if all my concerns are well addressed.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your appreciation of our **clearity**, **motivation** and **sound experiments**.
(The images mentioned below are available at the anonymous link: https://anonymous.4open.science/r/ICML-2025-Paper35-Rebuttal-7E9E.)
### Q1: Load Balance of Different Prompts
1. Since the number of CLS and image tokens varies across different semantics, some tokens share similar meanings, while others are more distinct. As a result, prompts associated with different semantics should be selected at different frequencies. Therefore, we did not impose a strict load-balancing design for different prompts.
2. To ensure that every prompt is optimized rather than some prompts never being selected, we *randomly choose prompts during the first 10 epochs of model training*. In the subsequent 90 epochs, prompt selection is guided by a prompt indicator, which adjusts selection based on semantic information. This design ensures that all prompts and their corresponding indicators are optimized while maintaining differing selection frequencies for prompts associated with different semantics.
3. Furthermore, we visualize the selection frequency of prompts, as shown in Fig.1.1 (https://anonymous.4open.science/r/ICML-2025-Paper35-Rebuttal-7E9E/1.1.png). The results indicate that different CLS prompts are selected at frequencies **ranging from 0.13 to 0.45**, while different image prompts are selected at frequencies **ranging from 0.05 to 0.24**. This verifies that all prompts in our method are effectively utilized, with none remaining unused.
### Q2: Eq.14
1. We have carefully reviewed Eq.14 and the related Eq.9 and confirmed that our formulations are **correct**.
2. Eq.9, $\mathcal{S}(\boldsymbol{h}_m^{j},\boldsymbol{\kappa}^i_k)=1-\mathrm{cos}(\boldsymbol{h}_m^{j}, \boldsymbol{\kappa}^i_k)$, computes the **cosine distance** between $\boldsymbol{h}_m^{j}$ and $\boldsymbol{\kappa}^i_k$. A *higher* similarity between $\boldsymbol{h}_m^{j}$ and $\boldsymbol{\kappa}^i_k$ results in a *larger* $\mathrm{cos}(\boldsymbol{h}_m^{j},\boldsymbol{\kappa}^i_k)$, leading to a *smaller* cosine distance $\mathcal{S}(\boldsymbol{h}_m^{j},\boldsymbol{\kappa}^i_k)$.
3. The objective of Eq.14 is to *minimize* the distance between image tokens and their corresponding prompt indicators, ensuring that both $\sum{\mathcal{S}(\boldsymbol{h}_m,\boldsymbol{\kappa}^i_m)}$ and $\sum{\mathcal{S}(\boldsymbol{c}_j,\boldsymbol{\kappa}^c_j)}$ are as small as possible.
4. To enhance clarity, we have added an explanation of the optimization objective before Eq.14.
### Q3: Fig.3
1. Figure 3 in our paper visualizes the attention map in ViT, defined as $A=\text{Softmax} \left(\frac{Q K^T}{\sqrt{d_k}}\right)$.
2. In (b) and (d), both the x-axis and y-axis are token indices, with the y-axis corresponding to queries and the x-axis to keys. The color variations indicate the attention weights.
3. In (a) and (c), the z-axis is the attention weights, while both the x-axis and y-axis correspond to token indices. The difference is that the x-axis represents queries, and the y-axis represents keys. Notably, for clarity, we did not visualize all queries but instead focused on CLS tokens and a subset of prompt and image tokens.
4. We have revised Fig.3, explicitly annotating the meaning of each axis. The updated figure is provided in Fig.1.2 (https://anonymous.4open.science/r/ICML-2025-Paper35-Rebuttal-7E9E/1.2.png).
### Q4: Notation
1. In our original paper, $M$ represents the number of patches. It is **italic**, **uppercase**, and **not bold**, used to denote a *scalar*. In contrast, $\mathrm{\mathbf{M}}$ represents the final mask. It is **upright**, **uppercase**, and **bold**, used to denote a *tensor*.
2. To improve clarity, we have changed $M$, which originally represented the number of patches, to $N$, and $N$, which originally represented the number of network layers, to $L$.
3. The paper does not use subscripts $c$ and $h$. Instead, superscripts $c$ and $i$ are used to differentiate between CLS token-related and image token-related prompts and indicators. These are **lowercase**, **italic**, and **not bold**. Meanwhile, $\boldsymbol{h}$ represents tokens in the network, which are *vectors* and are written in **lowercase**, **italic**, and **bold**.
4. To enhance readability, we have standardized the use of superscripts to indicate different attributes of tokens, prompts, and indicators (belong to CLS token or image token). Meanwhile, indices indicating layer numbers and patch indices are consistently placed in subscripts. For example, the notation $\boldsymbol{h}^1_i$, which originally represented the first token in the $i$-th layer, has been revised to $\boldsymbol{h}_{i,1}$.
### Q5: Typo
1. We have corrected "SPT" to "VPT" in Sec.5.5.
2. Additionally, we have thoroughly checked and revised other parts of the paper for grammatical issues and typos. For example, in Eq.9, we have corrected $\boldsymbol{k} $ to $\boldsymbol{\kappa}$. | null | null | null | null | null | null |
Lower Bounds for Chain-of-Thought Reasoning in Hard-Attention Transformers | Accept (poster) | Summary: This paper explores the use of CoT reasoning and scratchpads in enhancing the computational capabilities of transformers. The authors propose new lower bounds for the number of CoT steps required for various algorithmic problems, challenging optimistic bounds from circuit complexity.
Claims And Evidence: The claims are supported by clear and convincing evidence.
Methods And Evaluation Criteria: I believe the analysis method is overly restrictive, particularly with the use of hard transformers and 0-1 digit operations. It seems difficult to accurately represent real-world scenarios using these approaches.
Furthermore, I think the model completely neglects the logical progression inherent in CoT reasoning. Treating all outputs as equivalent tokens seems problematic, especially for long dialogues where the summary might be treated in the same way. This approach doesn't appear to be reasonable.
Theoretical Claims: I have examined the proof process. The proof contains numerous assumptions that are either arbitrary or difficult to relate to practical contexts. For example, the assumption |{i ≤ N : ρN (i) = ∗}| ≥ CN is completely unclear in terms of its rationale, and the corresponding proof seems to fail to justify this core inequality.
Additionally, there are many unexplained symbols, such as *, ρ|x|, and |{i ≤ N : ρN (i) = ∗}|.
Experimental Designs Or Analyses: The conclusion of this experiment does not seem to indicate that O(n) is the lower bound of the complexity. At the same time, the conclusions of these experiments appear to be similar to those in [1, 2].
[1] Towards revealing the mystery behind chain of thought: A theoretical perspective. NeurIPS 2023
[2] Unlocking the Capabilities of Thought: A Reasoning Boundary Framework to Quantify and Optimize Chain-of-Thought. NeurIPS 2024
Supplementary Material: No Supplementary Materials here.
Relation To Broader Scientific Literature: None.
Essential References Not Discussed: In fact, there has already been some detailed discussion on CoT Boundaries in previous work. Please analyze in detail the differences between the following works and your proposed boundary:
1. Towards revealing the mystery behind chain of thought: A theoretical perspective. NeurIPS 2023
2. Unlocking the Capabilities of Thought: A Reasoning Boundary Framework to Quantify and Optimize Chain-of-Thought. NeurIPS 2024
Furthermore, there is a lack of significant work focusing on the interpretability of CoT. Relevant works include:
1. Wang et al. How Large Language Models Implement Chain-of-Thought? Arxiv 2023.
2. Hanna et al. How does gpt-2 compute greater-than?: Interpreting mathematical abilities in a pre-trained language model. NeurIPS 2023.
3. Dutta et al. How to think step-by-step: A mechanistic understanding of chain-of-thought reasoning. TMLR 2024.
Other Strengths And Weaknesses: None.
Other Comments Or Suggestions: None.
Questions For Authors: - Could you please elaborate on the specific differences between this work and previous research mentioned above?
- The experimental results do not seem to conclusively demonstrate that O(n) is the lower bound of the complexity. It would be helpful to see a more rigorous argument or further evidence supporting this claim.
- The assumptions made in this work appear to be quite strong, potentially even stronger than those in the original work by Feng et al. [1]. It might be useful to provide additional justification or relax some of these assumptions, to ensure the findings are robust and applicable in a wider range of scenarios.
[1] Feng et al. Towards revealing the mystery behind chain of thought: A theoretical perspective. NeurIPS 2023
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank the reviewer for acknowledging that our claims are supported by clear and convincing evidence. We now address all the concerns mentioned in the review:
1. On the restrictiveness of our approach due to the use of hard attention and binary input/output format:
We agree that hard attention is a simplifying assumption, though it is amply supported by interpretability studies as we cited in Appendix E.1.
Perhaps even more importantly, recent results also show that hard attention has the *same expressiveness* as the real-world transformer setting -- that is, UHAT can simulate the output of finite-precision soft attention transformers with causal masking [3]. Hence, real-world transformers cannot have asymptotically shorter CoTs than UHAT transformers. Thus, our results *provably transfer to the real-world setup*. We will highlight this in the final version.
Regarding 0-1 digit operations, this is not a substantive restriction. The random restrictions technique has typically been applied to binary input strings in the past, which we follow for simplificity. However, the technique equivalently applies to strings over other alphabets, and, trivially, any finite alphabet can be encoded in binary. We will add explicit discussion, and a formal statement of the equivalence, in the final version of our paper.
2. On neglecting the logical progression in CoT reasoning:
Our bounds hold irrespectively of the contents of the CoTs, including their logical structure. If the concern of the reviewer is that some of the tokens in the CoT may be less important than others, then it is not a problem for our proofs, since we treat all tokens as important.
3. On arbitrary assumptions, specifically $|{i ≤ N : ρ_N (i) = ∗}| ≥ CN$:
We would like to point out that this is not an assumption; this is a property of a specific class of functions in Theorem 3.3. It formalizes the idea that a function stays constant on a set of strings "ignoring" many positions in those strings. Informally, if $|{i ≤ N : ρ_N (i) = ∗}| ≥ CN$ then with probability at least $C$ changing one bit in the input of $f$ won't affect the output; in other words, $f$ is insensitive. We will expand our informal explanation of the rationale behind the statement of the theorem. We will also be happy to add intuition on the meaning behind other assumptions if the reviewer clarifies which of them seem arbitrary.
4. On unexplained symbols:
Note that the * in Definition 3.2 is just a plain symbol in the output space of restrictions: $\rho_N : [1,N] \rightarrow \Sigma \cup \{*\}$, also used in the condition $\rho_{|x|}(i) \neq *$.
Other symbols are also either defined or standard notation, but we will take care to make the notation more accessible for a broader audience in the final version.
5. On experiments not supporting the statement that $O(n)$ is the lower bound of the complexity:
We assume that by the sentence "O(n) is the lower bound of the complexity" the reviewer references the group of our statements imposing the $\Omega(N)$ bounds on the length of CoT required to solve specific tasks. Generally, our experiments supporting this group of statements show that all successful CoT strategies for the tasks we consider require at least $\Theta(N)$ steps. We agree that it does not prove that no other successful sublinear CoT strategy exists; however, proving such statement experimentally is challenging since it isn't feasible to test all possible CoTs. We are happy to extend our experimental design if the reviewer has any suggestions.
6. On relation to [1] (Feng et al. 2023) and [2] (Chen et al. 2024):
The key difference to prior work on the theory of CoT is that our results provide provable lower bounds on the lengths of CoTs. This is the key advance compared to [1], which instead focused on showing that certain tasks require CoTs, but didn't study how many steps are minimally needed.
[2] shows the relationship between the type of the CoT and the maximum difficulty of the task that an LLM can solve with that CoT. While these results are important, they leave the concept of difficulty undefined, and they also do not provide the bounds on the required length of the CoT. Therefore, while the results of [2] are generally applicable to more tasks, our work offers much more precise and rigorous results for specific tasks.
7. On discussing interpretability of the CoT:
In the camera-ready version of the paper, we will include a discussion of the work on interpretability of CoT and cite the papers mentioned by the reviewer.
8. On excessively strong assumptions:
We ask the reviewer to clarify which assumptions are referenced in this concern and which of them are stronger than those in [1]. It is hard for us to give an answer to this question without knowing details.
---
[3] Jerad et al. "Unique Hard Attention: A Tale of Two Sides." arXiv preprint arXiv:2503.14615 (2025). | Summary: This paper establishes lower bounds on the required chain-of-thought (CoT) length that unique hard-attention (UHAT) transformers need for solving certain classes of problems.
In particular, lower bounds are established for PARITY ($\Omega(N)$), MULTIPLICATION ($\Omega(N)$), MEDIAN ($\Omega(N)$), and REACHABILITY ($\Omega(\lvert E \rvert \log \lvert V \rvert)$), where $N$ is the length of the input.
Empirical experiments on both synthetic setups and LLMs validate the paper's claims.
Claims And Evidence: Yes
Methods And Evaluation Criteria: Yes
Theoretical Claims: Yes
Experimental Designs Or Analyses: Yes
Supplementary Material: No
Relation To Broader Scientific Literature: This improves our understanding of LLM expressivity.
Essential References Not Discussed: None that I'm aware of.
Other Strengths And Weaknesses: Strengths:
* This paper is quite solid and improves our understanding of transformer expressivity.
* Complexity lower bounds are appreciated, as they tend to be harder to prove than upper bounds.
* The list of FAQs in Appendix A resolves many of the questions I initially had.
* This is a good paper.
Weaknesses:
* I do not see clear weaknesses in this paper.
Other Comments Or Suggestions: N/A
Questions For Authors: N/A
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We thank the reviewer for the positive assessment of our paper. We particularly appreciate the reviewer's point that complexity lower bounds, as shown in this paper, tend to be harder to prove than upper bounds.
If possible, we'd like to kindly ask the reviewer to provide more justification supporting their score. We are concerned that, as the review is rather brief, it might be disregarded by the AC and other reviewers. | Summary: This paper establishes that hard-attention transformers require chain-of-thought (CoT) sequences of length linear in the input size to solve high-sensitivity algorithmic tasks like MEDIAN, and REACHABILITY in layered DAGs, with bounds tight up to logarithmic factors. By leveraging sensitivity analysis and a novel application of random restrictions, the authors prove that sublinear CoT steps would render these functions reducible to constants, which is impossible due to their inherent sensitivity, and further show that "dot-by-dot" CoTs require super-polynomial lengths. Empirical validation on synthetic tasks confirms sharp accuracy declines with sublinear CoT, while tests on real LLMs corroborate the necessity of sufficient intermediate steps.
Claims And Evidence: All claims made in the submission are supported by clear and convincing evidence.
Methods And Evaluation Criteria: The experiments make sense.
Theoretical Claims: The theorems in paper make sense, and I believe they are correct. However, I didn't check the proof line by line.
Experimental Designs Or Analyses: The experimental designs are valid.
Supplementary Material: I didn't check the proof line by line.
Relation To Broader Scientific Literature: N/A
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: **Strengths**
1. **Theoretical Rigor**: The paper provides a foundational analysis using tools from circuit complexity (e.g., sensitivity, random restrictions) to derive lower bounds, rigorously extending prior work on transformer expressivity.
2. **Empirical Alignment**: Synthetic experiments validate theoretical predictions, with clear accuracy drops when CoT lengths are sublinear. Tests on real LLMs strengthen practical relevance, bridging theory and practice.
3. **Clarity**: The exposition is well-structured, with intuitive explanations of sensitivity and UHAT transformers, making complex theoretical arguments accessible.
### **Weaknesses**
1. **UHAT Assumption**: The reliance on *unique hard attention* limits direct applicability to real-world transformers, which use soft attention. While the authors justify UHAT for theoretical tractability, the practical implications for standard transformers remain limited.
2. **Scalability of Experiments**: Synthetic tasks use small inputs (e.g., 16-bit integers), raising questions about generalization to larger scales. While pragmatic for controlled validation, broader empirical tests (e.g., 64-bit MULTIPLICATION) could strengthen claims.
Other Comments Or Suggestions: The template seems to be wrong.
Questions For Authors: Please refer to the weakness.
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: We thank the reviewer for the positive assessment of our experiments and theorems and pointing out the strengths of our paper. We now address the concerns raised in the review.
1. In Appendix A, we explain in detail why our results for hard attention are relevant for real-world transformers, especially concerning CoT. We briefly reiterate the arguments below.
First of all, many existing CoT constructions for soft attention in the literature (e.g., [1]) can be expressed in UHAT. Hence, even if lower bounds for soft attention don't directly follow from the lower bounds for UHAT, our impossibility results show that any sublinear solutions for considered tasks would likely to be hard to find.
Second, prior work [2] established a correspondence between the unlearnability of certain classes of tasks for soft attention and their impossibility for hard attention. Thus, our lower bounds for UHAT expressivity shed light on lower bounds for learnability in soft attention (and those are directly supported by our experiments).
2. In addition to our arguments in Appendix A, there is new substantial evidence proving a correspondence between hard and soft attention that has not yet been mentioned in our paper. Recent work, published after we had submitted our paper to ICML, rigorously establishes that some versions of UHAT are functionally equivalent to real-world Transformer setup (finite-precision causal soft attention) [3]. That result expands prior work that had already established that finite-precision soft attention is contained in $AC^0$ [4]. This directly establishes the relevance of our results for the real-world LLMs, as they *directly imply corresponding lower bounds for finite-precision soft-attention transformers*. We will make this implication explicit in the final version.
3. Regarding the scalability of our experiments, we agree that scaling our experiments would further illustrate our conclusions. Initially, we limited our multiplication experiments to 16 bits due to computational resource limitations. We will scale up our experiments, and include the results in the camera-ready version of the paper.
4. The reviewer has also mentioned that our template is wrong. We are not aware of any mismatch between our template and the official ICML template recommendations. We ask the reviewer to clarify what exactly is wrong with the template, and we can fix those issues in the final version of the paper.
Finally, we kindly ask the reviewer to reconsider the score given to our paper. We would like to point out that the reviewer agrees that the paper is clear, experiments and theoretical results are thorough, and the claims are supported by convincing evidence. The only weaknesses mentioned are the UHAT assumption and the recommended scaling of the experiments, and we address those weaknesses above. Thus, we believe that the negative score assigned by the reviewer is unjustified given this list of strengths and weaknesses.
---
[1] Abbe et al. "How far can transformers reason? the globality barrier and inductive scratchpad." NeurIPS 2024.
[2] Hahn and Rofin. "Why are Sensitive Functions Hard for Transformers?" ACL 2024.
[3] Jerad et al. "Unique Hard Attention: A Tale of Two Sides." arXiv preprint arXiv:2503.14615 (2025).
[4] Li et al. "Chain of thought empowers transformers to solve inherently serial problems" ICLR 2024 | null | null | null | null | null | null | null | null |
CALM: Consensus-Aware Localized Merging for Multi-Task Learning | Accept (poster) | Summary: The authors introduce a novel model merging approach called CALM to address multi-task learning integration. The core idea involves identifying localized parameters aligned with global task consensus through three key components:
1. Class-Balanced Entropy Minimization Sampling (CB-EMS): A method to extract reliable unsupervised datasets while preserving class balance.
2. Efficient-Aware Framework: A sequential merging strategy that reduces computational complexity.
3. Consensus-Aware Mask Optimization: A binary mask mechanism to extract effective localized parameters, where global consensus is optimized using CB-EMS datasets.
Experiments across diverse vision and language multi-task scenarios validate the method’s robustness and effectiveness.
Claims And Evidence: 1. From the insight, the author proposes that local parameters with global task consensus are the effective information in model merging. The author provides explanations and experiments, and I hope the author will further explore this global task consensus, which will be elaborated later.
2. The author proposes using Class-Balanced Entropy Minimization Sampling to build reliable unsupervised datasets. This part has sufficient proof.
3. The author proposes an Efficient-Aware Framework to achieve more efficient model merging. The explanation here is adequate but requires more experimental support.
4. The author introduces the Consensus-Aware Mask Optimization method to extract local parameters with global consensus. I agree with the value of masks in model merging, and the experimental results prove its effectiveness, since the improvement mainly comes from this method.
Methods And Evaluation Criteria: The authors offer a detailed explanation in the method section, including effective figures and algorithm workflows. CB-EMS originates from the classic Entropy Minimization Sampling approach and can be seen as an improvement on the Adamerging entropy.
The Efficient-Aware Framework is a serialized framework, with the final Mask Optimization stage aimed at refining task-specific binary masks applicable to all tasks. The method itself has no critical flaws, but the written of Mask Optimization and its corresponding algorithm do not precisely align. I believe the evaluation criteria are appropriately set.
Theoretical Claims: I have reviewed the formulas and equations in the method section. The paper's theoretical claims focus on explaining the method workflow, with no clear issues.
Experimental Designs Or Analyses: The authors followed existing experimental setups, testing on standard visual and NLP benchmark datasets, and achieved significant results. However, some existing model merging methods have expanded to more tasks—further exploration on these benchmarks is warranted. The analysis of CB-EMS and Efficient-Aware is complete, but the authors should add more analysis for the Consensus-Aware Mask Optimization module.
Supplementary Material: The supplementary material is fairly thorough. The authors first introduced the experimental data, baselines, and setup comprehensively. Next, they performed ablation studies on hyperparameters and showed results on the ViT-L/14 architecture. Lastly, they briefly analyzed the binary mask. It’s recommended to expand on this part and place it in the main text.
Relation To Broader Scientific Literature: From a broader scientific perspective, model merging is similar to fields like federated learning and model fusion, but differs in that its multi-task training needs to be based on the same pretrained model. Existing methods fully leverage this characteristic by proposing task vectors [1], and how to optimally utilize these task vectors has become a key focus across approaches. The optimization strategy proposed by the authors – using an unsupervised test set to identify more effective parameter points (working points) for task vectors – builds upon existing research [2,3,4] and applies the optimization strategy to local parameters.
[1]Ilharco, G., Ribeiro, M. T., Wortsman, M., Schmidt, L., Hajishirzi, H., and Farhadi, A. Editing models with task arithmetic.
[2]Yadav, P., Tam, D., Choshen, L., Raffel, C. A., and Bansal, M. Ties-merging: Resolving interference when merging models.
[3]Yang, E., Wang, Z., Shen, L., Liu, S., Guo, G., Wang, X.,and Tao, D. Adamerging: Adaptive model merging for multi-task learning.
[4]He, Y., Hu, Y., Lin, Y., Zhang, T., and Zhao, H. Localize-and-stitch: Efficient model merging via sparse task arithmetic.
Essential References Not Discussed: Maybe [1] can be added into discussion.
[1] Model breadcrumbs: Scaling multi-task model merging with sparse masks.
Other Strengths And Weaknesses: ## Strengths
1. This paper presents clear and impactful insight, with strong introductory explanations that offer valuable insights for model merging.
2. The introduction of EMS and sequentialized merging is innovative. While not entirely novel, to my knowledge, these ideas are the first proposed in the context of model merging, marking an exploratory contribution.
3. The proposed global task consensus is conceptually related to "task-shared information" but distinct: global consensus focuses on non-conflicting parameters, whereas task-shared information emphasizes parameter fusion. This distinction is thought-provoking.
## Weaknesses
However, I still have some questions that, if addressed, would significantly strengthen the work:
1. The Efficient-Aware Framework is innovative and proven effective. However, whether this framework applies to existing model merging methods requires further investigation.
2. The authors should provide a clearer explanation and brief exploration of how global task consensus is captured through Mask Optimization in practice.
3. Some existing model merging methods have expanded to more tasks， such as 14- 20 visual tasks—further testing on these benchmarks would solidify the claims.
4. Additional analysis of the Consensus-Aware Mask Optimization module is necessary such as the other two modules.
Other Comments Or Suggestions: Ensure alignment between the main text and algorithm diagrams, or provide more prominent explanations.
Questions For Authors: My questions have been comprehensively outlined in the Weaknesses.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: ***Question 1: Does the Efficient-Aware Framework apply to existing model merging methods?***
***Answer:*** Thanks for the inspiring question.
The Efficient-Aware Framework (EAF) introduces a novel serialized merging approach for model merging, which impacts existing methods as follows:
- **For task quantity/order-insensitive methods**: EAF does not directly affect merging results and can be naturally applied to methods like Task Arithmetic and Localize-and-Stitch. These approaches typically disregard global task information during merging.
- **For task quantity/order-sensitive methods**: Existing techniques (e.g., Ties-Merging, Adamerging) can adopt EAF through pairwise merging substitution. However, their performance will significantly degrade due to EAF's inability to comprehensively integrate multi-task information. Experimental validation appears in **Reviewer oEok Question 2**. This limitation further constrains their scalability for new tasks.
---
***Question 2: How is global task consensus captured through Mask Optimization in practice?***
***Answer:*** Thank you for the valuable question. We would like to explain it as follows:
- **Theoretical perspective**: The Mask Optimization process extracts gradient directions beneficial for global tasks, aligning with the global task consensus principle. Detailed theoretical analysis is provided in **Reviewer y6gA Question 1**.
- **Empirical perspective**: Mask Optimization effectively compresses task-relevant information while eliminating inter-task interference. Experimental results are available in **Reviewer Rsjn Question 3**.
---
***Question 3: Additional experiments on extensive visual tasks.***
***Answer:*** Thanks for the constructive comments.
We supplement six new datasets (**CIFAR100, Flowers102, OxfordIIITPet, STL10, KMNIST, FashionMNIST**), expanding the vision tasks to 14 in total, to validate CALM's stability under increased task diversity. Results are as follows.
|Method|SUN397|Cars|RESISC45|EuroSAT|SVHN|GTSRB|MNIST|DTD|
|-|-|-|-|-|-|-|-|-|
|CALM ($\|S\|=13, \|\overline{S}\|=1$)|69.6|68.6|89.2|97.7|93.6|93.2|98.2|67.5|
|CALM ($\|S\|=12, \|\overline{S}\|=2$)|71.4|73.4|91.0|98.3|94.6|95.2|98.4|70.4|
|CALM ($\|S\|=11, \|\overline{S}\|=3$)|72.0|74.1|91.4|98.1|94.7|95.4|98.5|71.0|
|CALM ($\|S\|=10, \|\overline{S}\|=4$)|72.3|74.0|91.5|98.1|94.9|95.5|98.6|71.7|
|**Method**|**CIFAR100**|**Flowers102**|**OxfordIIITPet**|**STL10**|**KMNIST**|**FashionMNIST**|**Avg Acc**||
|CALM ($\|S\|=13, \|\overline{S}\|=1$)|79.4|83.4|91.5|97.6|84.4|90.7|**86.0**||
|CALM ($\|S\|=12, \|\overline{S}\|=2$)|81.9|85.0|91.4|97.9|87.1|90.8|**87.6**||
|CALM ($\|S\|=11, \|\overline{S}\|=3$)|82.6|84.8|91.6|97.9|85.6|90.6|**87.7**||
|CALM ($\|S\|=10, \|\overline{S}\|=4$)|83.2|84.7|91.8|97.9|86.2|90.7|**87.9**||
**Key Findings from Experiments on 14 Visual Tasks:**
- **Scalability:** CALM achieves robust performance (average accuracy ≈87% for the original 8 tasks) through sequential merging of a minimal task subset, demonstrating sustained effectiveness under task scaling.
- **Flexibility:** Superiority over existing methods is attained even with limited merging steps, highlighting its efficiency in resource-constrained scenarios.
- **Robustness:** The ordering of sequential merging tasks shows negligible impact on final performance, confirming task-agnostic stability.
---
***Question 4: Additional analysis of the Consensus-Aware Mask Optimization module.***
***Answer:*** Thanks for the practical comments.
In the review, we provided a more detailed analysis of the Consensus-Aware Mask Optimization module, including:
- **The definition of global consensus**: refer to **Reviewer Rsjn Question 1**;
- **Experimental analysis of the binary mask**: refer to **Reviewer Rsjn Question 3**;
- **Ablation Study of Consensus-Aware Mask Optimization**: refer to **Reviewer oEok Question 3**.
---
***Question 5: Essential References Discussion.***
***Answer:*** Thank you for your constructive advice.
**Comparison between CALM and ***Model Breadcrumbs: Scaling Multi-Task Model Merging with Sparse Masks:*****
- **Commonality:**
Both methods leverage task vectors and acknowledge the significance of local parameters for multi-task model merging.
- **Divergence:**
Model Breadcrumbs filters anomalous parameter values based on local prior characteristics (e.g., magnitude distribution thresholds), whereas CALM dynamically extracts task-agnostic knowledge to identify optimal local parameters that align with global task consensus.
- **Advantage of CALM:**
CALM more effectively resolves conflicts among local parameters by integrating cross-task knowledge. The consensus-aware optimization ensures that selected parameters exhibit enhanced reliability and generalizability across diverse tasks, thereby offering a more principled and robust solution.
---
Rebuttal Comment 1.1:
Comment: Thank you to the authors for the detailed and thoughtful response. After carefully reviewing the rebuttal, I find that it satisfactorily addresses my main concerns and provides additional clarity on several key aspects of the work. Specifically, the clarification of the Efficient-Aware Framework’s current scope and its potential applicability to other model merging methods is appreciated. The expanded analysis of the CAMO module also offers a deeper understanding of its contribution to the overall design. Accordingly, I have raised my score to 4. | Summary: The paper introduces a test-time adaption method named CALM, which optimizes an equally-sized mask on pre-fine-tuned task-specific models through a reliable unsupervised dataset. The mask aims to extract locally shared parameters with global task consensus, offering a new perspective for model merging by exploring how to identify more effective local parameters. Furthermore, CALM implements a serialized merging framework that achieves remarkable efficiency in scenarios requiring individual merging of new tasks.
Claims And Evidence: The paper focuses on addressing the question: "How to identify and extract effective information in model merging to enhance performance on all tasks?" The authors propose that effective information can be represented through localized parameters and aligned with a global task consensus.At first glance, this claim appears reasonable. The authors support their arguments through two primary approaches: first, by analyzing the limitations of existing global and localized model merging methods; second, by experimentally demonstrating the feasibility of extracting global consensus. Although the paper lacks further theoretical validation, the authors emphasize that due to the inherent difficulty in interpretability within model merging, their claims can still be supported experimentally.
Methods And Evaluation Criteria: The three contributions of this method hold good novelty and practical value for the model merging community. CB-EMS can serve as a general and feasible approach for unsupervised data in model merging; the Efficient-Aware Framework introduces a new serialized merging approach; while binary mask training follows Localize-and-Stitch, employing global task optimization is indeed more reasonable. Therefore, this method demonstrates clear advantages over previous approaches. If the authors further develop interpretable theories, it would be more beneficial to the community. For experiments, the paper provides sufficiently comprehensive tests, and its evaluation criteria align with classical model merging works.
Theoretical Claims: Eq.2-Eq.5 in the paper provide the derivation of CB-EMS, and Eq.6-Eq.9 outline the optimization process of Consensus-Aware Mask Optimization. There is no proof process, so no proof errors exist.
Experimental Designs Or Analyses: The main experiments consist of four parts: Visual multi-task, NLP multi-task, CB-EMS analysis, and Efficient-Aware Framework analysis. The core experiments largely validate CALM’s feasibility, showing strong performance on both visual and NLP tasks. The analysis sufficiently examines the robustness and effectiveness of each proposed module. One question: since the CB-EMS method does not exhibit stable sampling rates, how should sampling be handled in practice?
Supplementary Material: Yes, the supplementary material details the multi-task datasets and baselines. It also includes more ablation study results. Most importantly, it analyzes the binary mask and identifies which parameters are effective parameters—this is very helpful for model merging.
Relation To Broader Scientific Literature: As for research on model merging, there are mainly two approaches. One is data-free methods, which do not require additional task data and rely on experience and strategies to merge models. The other is data-based methods, which utilize extra task information to achieve better merging results. Obviously, the CALM method falls into the latter category, but it fully learns from the former approaches by using task information to develop merging strategies. This combination offers a useful perspective for model merging research.
Essential References Not Discussed: I think the references in this paper are comprehensive.
Other Strengths And Weaknesses: Strengths:
(1) The authors present a novel perspective by addressing the fundamental challenges of model merging, proposing a method that balances global task consensus with local parameter alignment.
(2) The framework of the proposed method is exceptionally clear, with each component being structurally complete and innovating upon existing model merging approaches in all three modules.
(3) The experimental results demonstrate substantial performance improvements over baselines, even compared to data-based methods.
Weaknesses:
(1) The sampling rates of CB-EMS in experiments appear inconsistent; how would this be resolved in practical applications?
(2) A detailed ablation study on global consensus is limited. The authors should explore the concept of global task consensus more deeply.
Other Comments Or Suggestions: Ensure minimal overlap among elements in figures, as exemplified in Figure 1.
Questions For Authors: See weakness
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: ***Question 1: The sampling rates of CB-EMS in experiments appear inconsistent; how would this be resolved in practical applications?***
***Answer:*** Thanks for the practical comments. We would like to explain it as follows:
- **CB-EMS Sampling Rates Show Cross-Task Generalizability.**
Experimental results demonstrate that CALM exhibits consistent performance trends across language and visual benchmarks: accuracy first increases then decreases with higher sampling rates, peaking at 0.8 (language) and 0.9 (visual). This validates CALM's cross-domain adaptability and task-agnostic performance patterns.
- **Optimal Sampling Rates Depend on Unsupervised Data Properties.**
The choice of optimal sampling rates is dynamically determined by the scale and quality of unsupervised data. For small datasets, higher rates (0.8-0.9) help mitigate data scarcity through increased sample diversity. When individual task models show high prediction confidence on the unsupervised data, high sampling rates remain viable despite potential noise. Conversely, lower rates (0.4-0.5) are recommended for unreliable predictions to prioritize data credibility.
- **Supervised Data Guides Sampling Rate Optimization.**
Supervised data enables adaptive sampling: set sampling rate equal to task models' accuracy on the supervised set. This balances data trustworthiness and utilization by filtering noise while keeping useful data. **Below we demonstrate the performance improvements enabled by this method. Setting the sampling rate to match the accuracy of the supervised dataset significantly enhances data credibility.**
||SUN397|Cars|RESISC45|EuroSAT|SVHN|GTSRB|MNIST|DTD|
|-|-|-|-|-|-|-|-|-|
|Individual(Full Data)|75.3|77.7|96.1|99.7|97.5|98.7|99.7|79.4|
|Sampling Rate|75.3|77.7|96.1|99.7|97.5|98.7|99.7|79.4|
|Individual(Sampled Data)|88.3|87.3|97.4|99.9|98.5|99.2|99.8|87.5|
---
***Question 2: A detailed ablation study on the individual components of CALM.***
***Answer:*** Thanks for the very constructive comments.
- **Ablation Study of CB-EMS.**
**As shown in Figure 5, we present ablation study results of CB-EMS.** The experimental results demonstrate that adding the CB-EMS method achieves performance comparable to supervised learning results and is significantly better than unsupervised EM methods using entropy.
**Below, we provide the "Class-balanced" ablation results.** Incorporating the Class-balanced component effectively avoids class imbalance and shows significant performance improvement.
|Method|SUN397|Cars|RESISC45|EuroSAT|SVHN|GTSRB|MNIST|DTD|**Avg Acc**|
|-|-|-|-|-|-|-|-|-|-|
|CB-EMS|72.6|74.8|91.9|98.6|95.2|96.4|99.1|72.8|**87.7**|
|EMS|70.6|73.0|88.2|93.3|88.1|75.9|93.7|70.0|**81.5**|
- **Ablation Study of Efficient-Aware Framework.**
**We conduct additional ablation studies by adding the Efficient-Aware Framework (EAF) to existing model merging methods and removing it from CALM.** EAF has no effect on order-insensitive methods (e.g., Task Arithmetic) but effects order-sensitive methods (AdaMerging). Without EAF, CALM reduces to randomly selecting a task for mask learning, with results as follows.
**Existing methods exhibit significant performance degradation under the Efficient-Aware Framework** since they require simultaneous consideration of all task vectors.
**Without this framework, CALM still maintains robust performance.** Notably, CALM still requires EAF for large-scale task merging.
|Method|SUN397|Cars|RESISC45|EuroSAT|SVHN|GTSRB|MNIST|DTD|**Avg Acc**|
|-|-|-|-|-|-|-|-|-|-|
|AdaMerging (+EAF)|70.7|55.3|61.3|66.5|74.0|58.1|99.1|36.2|**65.2**|
|AdaMerging (-EAF)|64.5|68.1|79.2|93.8|87.0|91.9|97.5|59.1|**80.1**|
|CALM (+EAF)|72.6|74.8|91.9|98.6|95.2|96.4|99.1|72.8|**87.7**|
|CALM (-EAF)|71.9|74.1|91.6|98.7|95.2|96.2|98.9|71.2|**87.3**|
- **Ablation Study of Consensus-Aware Mask Optimization.**
Consensus-Aware Mask Optimization contributes most performance gains as our core component and cannot be fully ablated. We instead conduct ablation studies on our core insights and key components.
- **Ablation Study of Localized Information and Global Consenus**
As core insights, CALM degenerates into Localize-and-Stitch (extracting localized task-specific information) when focusing solely on localized patterns, and degenerates into TW AdaMerging (applying identical masks to all parameters) when only global consensus is considered.
- **Ablation Study of Regularization**
Evaluating the impact of regularization in the optimization equation.
- **Ablation Study of Binary Mask**
Please refer to **Reviewer Rsjn Question 2**.
|Method|SUN397|Cars|RESISC45|EuroSAT|SVHN|GTSRB|MNIST|DTD|**Avg Acc**|
|-|-|-|-|-|-|-|-|-|-|
|Local-only|67.2|68.3|81.8|89.4|87.9|86.6|94.8|62.9|**79.9**|
|Global-only|58.0|53.2|68.8|85.7|81.1|84.4|92.4|44.8|**71.1**|
|W/o Regularization|70.1|72.4|90.8|97.6|94.2|95.3|98.2|70.5|**86.3**|
|CALM|72.6|74.8|91.9|98.6|95.2|96.4|99.1|72.8|**87.7**|
---
Rebuttal Comment 1.1:
Comment: Thank you for your detailed answer. I agree with the concept of integrating local information with global consensus in model merging, which offers valuable insights for the field. The authors provide comprehensive ablation studies that validate the effectiveness of their approach and address my concerns. I have no further questions and recommend maintaining my original score. | Summary: This paper focuses on model merging in multi-task learning, aiming to identify locally shared information with global task consensus while addressing existing limitations of parameter conflict in global information and diluted local features during merging.
The method comprises three components: 1) Class-Balanced Entropy Minimization Sampling constructs a reliable unsupervised dataset; 2) An Efficiency-Aware Framework enables resource-effective model merging; 3) Consensus-Aware Mask Optimization designs mask refinement with global consensus.
Experiments on both vision and language datasets demonstrate the method's effectiveness, outperforming state-of-the-art approaches.
Claims And Evidence: Most claims made in the submission are clear. However, the authors should further clarify the exact definition of "global consensus" and explain how CALM specifically achieves it.
Methods And Evaluation Criteria: Yes
Theoretical Claims: No errors in theoretical claims. However, whether character subscripts should be italicized needs consistency.
Experimental Designs Or Analyses: The experiments include 8 visual classification tasks and 12 NLP tasks, which aligns with most model merging methods. However, the lack of analysis on the binary mask—such as whether it captures global consensus or the properties of this consensus—weakens the support for the authors’ key insight.
Supplementary Material: Yes. Experimental results and Visualizations
Relation To Broader Scientific Literature: The main contribution of this paper lies in applying the global optimization approach from Adamerging to localized model merging methods, such as Ties-Merging, and Localize-and-Stitch, thereby avoiding the issue where these data-free methods struggle to precisely capture task-specific characteristics.
Essential References Not Discussed: The author should add a comparison between CALM and some of the latest model merging-related papers, like [1] and [2].
[1] Mitigating Parameter Interference in Model Merging via Sharpness-Aware Fine-Tuning
[2] Model merging with SVD to tie the Knots
Other Strengths And Weaknesses: Other Strengths:
1. The paper is well-structured and well written, and the figures and tables are detailed, clearly conveying the authors' insights and methodology.
2. I agree that the issue the authors focus on is significant in model merging.
3. The proposed method achieved state-of-the-art experimental results, and the experiments are thorough.
Other Weaknesses:
1. The experiments based on language multi-task benchmarks could be more comprehensive to check if the findings align with those in visual benchmarks.
Other Comments Or Suggestions: Please refer to Other Strengths And Weaknesses and Questions For Authors
Questions For Authors: The following are the questions and concerns I hope the authors can address further:
1. The authors need to provide a clearer definition and explanation of global task consensus to establish the core idea of this work.
2. Can CALM adapt to existing frameworks without an efficiency-aware framework?
3. Does the binary mask capture global consensus? The authors need to explore this further.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: ***Question 1: The authors need to provide a clearer definition and explanation of global task consensus to establish the core idea of this work.***
***Answer:*** Thanks for your valuable question. We clarify the concept of global task consensus as follows:
- **Definition:** Global task consensus refers to shared and generalizable knowledge patterns or parameter adaptation directions among multiple independently fine-tuned models during model merging.
- **Key Properties:**
- **Cross-Task Validity:** Consistent parameter adaptation directions across tasks during fine-tuning.
- **Task-Specific Feature Preservation:** Avoidance of significant performance degradation on any task after model merging.
- **Validation:** Due to length limitations, we provide theoretical error analysis to validate its effectiveness. For details, please refer to **Reviewer y6gA Question 1**.
---
***Question 2: Can CALM adapt to existing frameworks without an efficiency-aware framework?***
***Answer:*** Thank you for your valuable question.
The efficiency-aware framework enables CALM to achieve efficient model merging with strong scalability. Our method can also adapt to scenarios without this framework, maintaining compatibility with existing approaches. Below we present two feasible solutions:
- **Single-Task Merging: Randomly select one task for model merging.** As shown in Figure 6, the results demonstrate that applying CALM to a single task achieves comparable or even better performance than sequential multi-task merging. Thus, CALM can be applied to a single task without requiring sequential merging.
- **Multi-Task Simultaneous Merging: Utilize multiple binary masks to merge all tasks simultaneously.** We can slightly modify the CALM method to align with existing model merging frameworks, with the following optimization objective. Within a single optimization equation, we optimize a binary mask for each task and enforce that the sum of binary masks equals an all-ones matrix. This allows simultaneous extraction of information from all tasks while maintaining global consensus. During optimization, we still employ real-valued masks $R$ and classify each parameter to tasks via softmax.
$$
\min_{\{M\}} \ \sum_{t=1}^T\mathcal{L}(\theta_{mtl})+\alpha\sum_{t=1}^T||M_t||_1
$$
$$
s.t. \ \theta_{mtl}=\theta_{pre}+\sum_{t=1}^TM_t\odot\tau_t,\ \sum_{t=1}^TM_t=\textbf{1}_{n \times n}.
$$
---
***Question 3: Does the binary mask capture global consensus?***
***Answer:*** Thanks for the practical comment.
In Appendix D, we provide visualizations and analysis of the binary mask properties. Here, we present a concise experiment to demonstrate the effectiveness of binary mask.
For each task, we apply CALM with the following definitions: $\theta_{pre}$ denotes the pre-trained model, $\tau_{1}$ is the task vector from the remaining seven tasks via task arithmetic, $\tau_{2}$ is the target task vector, and $M$ is the optimized binary mask. We evaluate the target task performance under five configurations:
|Model Parameters|SUN397|Cars|RESISC45|EuroSAT|SVHN|GTSRB|MNIST|DTD|
|-|-|-|-|-|-|-|-|-|
|$\theta_{pre}$|62.3|59.6|60.3|45.7|31.6|32.6|48.3|44.4|
|$\theta_{pre}+\tau_1$|48.8|54.9|46.3|35.4|46.7|32.9|74.8|35.0|
|$\theta_{pre}+(1-M)\odot\tau_1$|60.4|64.8|69.8|85.6|76.5|68.6|89.5|54.0|
|$\theta_{pre}+\tau_2$|79.2|77.7|96.1|99.8|97.5|98.7|99.7|79.4|
|$\theta_{pre}+M\odot\tau_1$|69.9|69.5|80.0|88.1|72.7|71.7|90.4|59.7|
|$\theta_{pre}+(1-M)\odot\tau_1+M\odot\tau_2$|71.9|73.9|88.3|96.9|93.4|93.9|98.0|69.0|
CALM extracts task vectors with approximately 5% parameters. We have the following conclusions:
- **Interference suppression** (Rows 2-3): Removing 5% parameters from $\tau_{1}$ via $(1-M)\odot\tau_{1}$ significantly improves target task adaptation, demonstrating effective identification of interference parameters.
- **Task-specific preservation** (Rows 4-5): Confining $\tau_{2}$ to 5% masked parameters $M\odot\tau_{2}$ maintains strong performance, indicating precise capture of essential transfer signals.
- **Conflict-free merging** (Rows 3,5,6): Simultaneous application of $(1-M)\odot\tau_{1}$ and $M\odot\tau_{2}$ achieves performance gains without parameter conflicts, verifying CALM's effective multi-task merging capability.
---
***Question 4: Additional experiments of language multi-task benchmarks.***
***Answer:*** Thanks for the very constructive comments.
**CALM demonstrates consistent behavior across language and visual benchmarks.** We give an example, shown in the table below. Both domains exhibit nearly identical trends in average accuracy versus CB-EMS sampling rates - initially increasing then decreasing with higher sampling. Additional experiments confirm this cross-domain consistency.
|Sampling Rates|0.1|0.2|0.3|0.4|0.5|0.6|0.7|0.8|0.9|1.0|
|-|-|-|-|-|-|-|-|-|-|-|
|language benchmarks|80.1|80.8|81.0|81.2|81.2|81.3|81.3|**81.7**|81.4|81.5|
|visual benchmarks|83.8|84.9|85.7|86.1|86.4|86.8|87.1|87.4|**87.7**|87.5|
---
Rebuttal Comment 1.1:
Comment: Thanks for the rebuttal. Most of my concerns have been addressed. I will keep my score | Summary: Localized Information with Global Consensus: CALM proposes a method to extract localized parameters that align with global task consensus, ensuring that the merged model maintains effectiveness across all tasks.
* A new sampling technique that leverages unsupervised data more effectively by balancing class representation and minimizing entropy.
* A scalable and efficient framework for merging models sequentially, reducing computational complexity while maintaining performance.
* A method to optimize binary masks that align with global task consensus, enabling conflict-free merging of task-specific parameters.
* The authors demonstrate the superiority of CALM through extensive experiments on both vision and NLP tasks, showing that it outperforms existing global-aware and localized-aware methods, and approaches the performance of traditional MTL without the need for retraining.
Claims And Evidence: Yes, most claims are support by empirical evidence.
Methods And Evaluation Criteria: The evaluation criteria follows existing works and is reasonable in practice.
Theoretical Claims: No theoretical claims.
Experimental Designs Or Analyses: Yes, the experimental designs are sound.
Supplementary Material: I briefly reviewed the supplementary material.
Relation To Broader Scientific Literature: N/A
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: **Strengths**:
* The authors provide extensive experimental results across multiple datasets, demonstrating that CALM consistently outperforms existing baselines and achieves performance close to traditional MTL.
* The efficient-aware framework is a practical contribution, especially in scenarios where tasks are completed asynchronously or computational resources are limited. The sequential merging approach reduces the complexity of merging multiple tasks.
**Weaknesses**:
* While the empirical results are strong, the paper lacks a deeper theoretical analysis of why localized information with global consensus leads to better performance. A more formal theoretical framework or proof could strengthen the paper.
* Although the paper includes some ablation studies (e.g., comparing CB-EMS with other sampling methods), it would benefit from a more detailed analysis of the individual components of CALM (e.g., the impact of the efficient-aware framework vs. the consensus-aware mask optimization).
* The paper does not discuss the sensitivity of CALM to hyperparameters (e.g., the regularization parameter
$\lambda$ or the sampling rate for CB-EMS). A discussion on how sensitive the method is to these choices would be useful for practitioners.
* efficient-aware-> efficiency-aware?
Other Comments Or Suggestions: N/A
Questions For Authors: N/A
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: ***Question 1: A more formal theoretical analysis of the effectiveness of localized information with global consensus***
***Answer 1***: Thanks for the inspiring question. We perform a theoretical analysis of the following three aspects based on error.
- **Localized information reduces interference in model merging. Such interference arises from intra-task noise and conflicts across task vectors (e.g., cancellation due to opposing parameter values).**
Denote the interference by $\epsilon$, so that task vector$$\tau_j = \Delta\tau_j+\epsilon,$$ where $\Delta\tau_j$ is the effective information for the global optimal update (nonzero in dimensions $I$) and $\epsilon$ is concentrated in the complementary set $J$. Define the binary mask $M_L$ such that $(M_L)_i=1$ if $i \in I$ and
$(M_L)_i=0$ if $i \in J$. Thus, the merged task vector becomes $$\Delta \tau_L = M_L\odot\tau_j = \Delta\tau_j+M_L\odot\epsilon,$$
reducing the interference energy from $||\epsilon||^2$ to $E_L=||M_L\odot\epsilon||^2.$
Although methods like Ties-Merging and Consensus TA aim to lower interference, their effectiveness is limited by the absence of global task information.
- **Global consensus enables the update to closely align with the optimal direction common to all tasks, reducing the overall loss.**
For all visible tasks $S_v$, we utilize global consensus to optimize a mask $M_G$ by minimizing
$$
\min_{M_G} \sum_{t_v \in S_v} L_{t_v}(\theta_{pre} + \tau_{seq}^{(j-1)} + M_G \odot \tau_j).
$$
Assuming a quadratic approximation near $\theta_{pre} + \tau_{seq}^{(j-1)}$, we have
$$
L_{t_v}(\theta_{pre} + \tau_{seq}^{(j-1)} + M_G \odot \tau_j) \approx L_{t_v}(\theta_{pre} + \tau_{seq}^{(j-1)}) + \langle g_{t_v}, M_G \odot \tau_j \rangle + \frac{1}{2}(M_G \odot \tau_j)^T H_{t_v} (M_G \odot \tau_j),
$$
where $H_{t_v}$ is the Hessian. Assume $H_{t_v}$ is the identity matrix and $\Delta\tau_j$ denote the global optimal update. The update error is
$$
E_{G} = ||M_G \odot \tau_j - \Delta\tau_j||^2.
$$
The gain from global consensus is defined as
$$
\Delta_{G} = ||\tau_j - \Delta\tau_j||^2 - ||M_G \odot \tau_j - \Delta\tau_j||^2.
$$
The optimization process shows that global consensus effectively reduces the overall loss.
- **Our CALM method integrates localized information and global consensus to effectively mitigate local parameter interference while capturing information beneficial for global tasks.**
Let the obtained binary mask be $M^*$; then the update error is
$$
E_{CALM} = ||M^* \odot \tau_j - \Delta \tau_j||^2.
$$
Based on the optimization objective, the error can also be expressed as
$$
E_{CALM} = \min(E_{loc}, E_{glob}) - \Delta_{syn},
$$
where $\Delta_{syn} > 0$ represents the additional error reduction from joint optimization.
**Thus, CALM achieves both local and global gains, effectively reducing the overall error.**
---
***Question 2: Additional ablation studies on the individual components of CALM.***
***Answer:*** Thank you for your valuable question.
Due to length limitations, we will present additional ablation study results in **Reviewer oEok Question 2**.
---
***Question 3: The sensitivity of CALM to hyperparameters (the regularization parameter $\lambda$ and the sampling rate for CB-EMS).***
***Anwser:*** Many thanks for the insightful suggestions.
Below are the model merging results on eight vision datasets under different regularization parameters $\lambda$ and sampling rates.
|$\lambda$|SUN397|Cars|RESISC45|EuroSAT|SVHN|GTSRB|MNIST|DTD|Avg Acc|
|-|-|-|-|-|-|-|-|-|-|
|0.5|72.9|75.2|92.3|99.0|95.3|96.3|99.1|72.9|**87.8**|
|2|72.5|74.8|91.8|98.7|95.3|96.3|99.1|72.1|**87.6**|
|1|72.6|74.8|91.9|98.6|95.2|96.4|99.1|72.8|**87.7**|
CALM is insensitive to $\lambda$, with merging performance remaining stable.
**Thus, $\lambda$ between 0.5 and 2 is acceptable**.
|Sampling Rate|SUN397|Cars|RESISC45|EuroSAT|SVHN|GTSRB|MNIST|DTD|Avg Acc|
|-|-|-|-|-|-|-|-|-|-|
|0.1|69.7|69.0|88.6|97.1|93.9|94.1|96.8|61.4|**83.8**|
|0.2|70.8|70.3|89.2|97.4|94.0|94.7|97.2|65.4|**84.9**|
|0.3|71.5|71.8|89.9|97.9|94.3|95.0|97.5|67.5|**85.7**|
|0.4|71.9|72.4|90.2|98.0|94.3|95.1|97.8|69.1|**86.1**|
|0.5|72.2|73.3|90.8|98.2|94.6|95.6|98.0|68.8|**86.4**|
|0.6|72.6|73.5|91.0|98.2|94.5|95.6|98.1|70.9|**86.8**|
|0.7|72.4|74.5|91.2|98.4|94.8|95.8|98.2|71.7|**87.1**|
|0.8|72.7|74.9|91.7|98.6|95.0|96.0|98.5|71.8|**87.4**|
|0.9|72.6|74.8|91.9|98.6|95.2|96.4|99.1|72.8|**87.7**|
|1.0|72.9|75.3|91.8|98.6|95.2|95.9|98.8|71.8|**87.5**|
Performance first increases then decreases with the sampling rate, peaking at 0.9. This aligns with our theory.
**In practice, the optimal sampling rate depends on data quantity and quality; for high-quality data, a higher rate (e.g., 0.8–0.9) is preferred, otherwise a lower rate is recommended**.
---
***Question 4: efficient-aware-> efficiency-aware.***
***Answer:*** Thank you for your constructive advice.
**We will seriously consider making changes in the final version.** | null | null | null | null | null | null |
Internal Causal Mechanisms Robustly Predict Language Model Out-of-Distribution Behaviors | Accept (poster) | Summary: Understanding the behavior of complex black-box models has always been a challenge since the inception of deep neural networks (DNNs). This problem has worsened after the introduction of large language models (LLMs). In this paper, the authors investigate whether understanding the internal causal mechanisms of LLMs can improve the prediction of output correctness. In particular, they show that the most robust features for correctness prediction are those that play a causal role in the model's behavior using two proposed methods --
Counterfactual Simulation and Value Probing. The methods are evaluated on diverse tasks like symbol manipulation, knowledge retrieval, and instruction following, where causal features consistently perform better, particularly under out-of-distribution settings. In addition, the methods improve model safety and reliability by providing more accurate correctness estimates.
## update after rebuttal
The authors addressed all my concerns and I vote for the acceptance of this paper.
Claims And Evidence: While the paper provides substantial evidence to support its claims, it lacks some key details that raise questions about the effectiveness of the proposed method.
i) While the methods perform well on the selected tasks, the paper does not extensively address how well these findings generalize to other, more complex real-world language model applications.
ii) The success of the methods relies on identifying causal variables, which may require domain-specific knowledge. It would be great if the authors could comment on the applicability of the approach in scenarios where causal structures are not well understood.
Methods And Evaluation Criteria: While the proposed method and evaluation criteria make sense within the context of understanding the internal causal mechanisms of LLMs, there are several questions concerning the methodology and evaluation of the proposed methodology.
i) The benchmark tasks are diverse but they are relatively controlled and lack the full complexity of real-world scenarios (e.g., complex multi-hop reasoning or dialogue systems). This raises concerns about generalizability.
ii) The methods rely on identifying causal subspaces, which may require domain expertise or prior knowledge. This dependency limits the approach’s scalability to more opaque or less understood tasks.
iii) It would be great if the authors could comment on the computational bottleneck of counterfactual simulation, which involves multiple forward passes to assess causal stability. Would this prohibit the use of the proposed method for large-scale language models like GPT-4?
iv) While the paper compares causal vs. non-causal features in Sec. 5.2, a more granular ablation study (e.g., the impact of individual layers or attention heads) could reveal which specific components contribute most to correctness prediction.
v) Will the selection of hyperparameters and causal subspaces for a given task inadvertently lead to overfitting on specific benchmarks?
Theoretical Claims: NA
Experimental Designs Or Analyses: Yes, I read the experimental setup and thoroughly reviewed the analysis.
Supplementary Material: Yes, the prompt templates and additional results are well described in the Appendix.
Relation To Broader Scientific Literature: The paper presents a novel perspective to understand the correctness of language model predictions.
Essential References Not Discussed: NA
Other Strengths And Weaknesses: By leveraging internal causal features rather than relying on output probabilities, one key strength of the proposed method is that it can effectively handle distribution shifts and hallucinations.
Other Comments Or Suggestions: NA
Questions For Authors: Please refer to the "Claims And Evidence" and "Methods And Evaluation Criteria" for more details.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We are grateful that the reviewer found our perspective on correctness prediction novel, and we appreciate the opportunity to discuss the practical value of our work!
---
### Q1. Generalizability to complex real-world tasks
We believe it's helpful to take a step back to examine the source of generalizability concerns and its relation to the broader goal of this work. Specifically, our framework comprises two key components: (1) finding causal mechanisms in LLMs, and (2) leveraging these mechanisms to predict model behaviors, particularly in OOD settings.
**Generalizability questions fall in the design space of problem (1)**, e.g., how to identify the high-level causal model without a strong human prior, how to scale to more complex tasks, etc. These are indeed important problems that mechanistic interpretability community has been focused on. However, even if we could *perfectly* identify the mechanisms underlying every GPT-4 prediction, **it remains an open question whether such mechanisms are actually useful for predicting model behaviors** (Mu et al. 2021; Wang et al. 2023; Sharkey et al. 2025).
Therefore, the focus of this work is to examine this under-explored but crucial step (2). As a result, **we choose to build upon existing tools developed by the interpretability community for problem (1)**. This means we naturally inherit the limitations of these tools.
With this context in mind, we would like to further address limitations of these interpretability tools we used!
**1.1 Reliance on human priors to identify causal mechanisms**
This is indeed a recognized limitation of concept localization methods. We discussed solutions in our response to reviewer uRDA Q3.
**1.2. Scale to real-world complex tasks**
We totally agree that there are many real-world tasks whose complex causal structures are not (yet) fully understood. However, **our method remains applicable when the causal structure is *partially* known, and a surprising number of real-world applications fall into this category.**
In fact, our experiments already include such tasks, e.g., MMLU contains 57 tasks to evaluate production-grade LLMs. While we may not know the exact causal mechanisms behind answering abstract algebra or international law questions, we can still leverage the shared multiple-choice format as high-level structure for correctness prediction.
Below, we highlight two additional practical domains where our methods are directly applicable:
- **LLM evaluation.** Constructing benchmarks typically requires expensive human annotations. A reliable correctness estimator allows benchmark creators to prioritize uncertain or error-prone examples. Moreover, systematic evaluation often requires structured inputs, e.g., SQuAD adversarial (Jia et al., 2017), GSM-symbolic (Mirzadeh et al., 2024), which inherently reflect high-level task structures that our framework can readily exploit.
- **Verifiable text generation.** In high-stakes domains like medical records generation, ensuring factual and referential accuracy. One strategy is to have LLMs generate symbolic references to structured source data that are easy to verify (Hennigen 2024). These symbolic references act as templated prompts, which can be converted to high-level models. Our methods allow estimating the correctness of texts generated using these decoding algorithms.
### Q2. Computation cost of counterfactual simulation
We have provided the computation cost in Table 1. Counterfactual simulation is K times more expensive than greedy decoding, where K is the number of counterfactual samples. Empirically, a relatively small set of counterfactual samples, e.g., K=16, is sufficient to achieve high AUC-ROC.
The cost can be further reduced by caching representations before the intervention site. For $Q$ queries from the same task, assume the intervention site is at the middle layer, the average cost per query is $(K+Q+QK)/2Q$, i.e., about $K/2$ times more expensive than greedy decoding when $Q$ is large.
### Q3. Which components contribute most to correctness prediction
Thanks for the suggestion! It indeed aligns with our discussion in Section 6.4 on using correctness estimation as an evaluation task for interpretability methods.
We have experimented with attention heads vs residual streams using GPT-2 on IOI task. The original IOI paper localizes the position variable in the outputs of S-Inhibition heads. These sets of heads produce an AUC-ROC around 0.8, while random heads have an AUC-ROC of 0.5. They underperform residual subspaces, likely because the manually identified heads do not fully capture the causal variable.
### Q4. Risk of overfitting causal subspaces
As with any supervised method, causal subspaces or probes may overfit to the training distribution. This is exactly why we see a slight drop from ID (Table 2) to OOD settings (Table 3) across all tasks/methods. However, **methods using causal features are more robust, i.e. consistently show smaller ID–OOD gaps.** | Summary: This paper presents a method for estimating whether a language model’s output is correct by examining “causal” internal representations. It studies both symbolic tasks and open-ended tasks, finding that features which directly mediate model behavior are more reliable than simpler methods. The authors claim that causally grounded features remain robust under prompt changes and distribution shifts.
Claims And Evidence: Yes
Methods And Evaluation Criteria: Yes
Theoretical Claims: N/A
Experimental Designs Or Analyses: Yes
Supplementary Material: Yes
Relation To Broader Scientific Literature: It is well-aligned with work on correctness estimation and the causal mechanism in language models.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: Strengths
1. The authors provide a thorough evaluation across multiple datasets.
2. The paper covers a broad range of tasks under both ID and OOD settings.
Weaknesses
1. The rationale for calling the method “causal” is unclear. The paper never formally defines “causality,” despite it being central to the proposed approach.
2. Several core notions—causal features, causal mechanisms, causal interpretability, and causal role—are mentioned but not defined. The term “causal” appears throughout without a clear theoretical foundation.
3. Some terms, such as “causal representation” and “causal structure,” have precise definitions in existing research. However, the paper neither references nor appears to adopt those definitions. Specifically, the conclusion highlights the assessment and use of “causal representation” and “causal structure” as central contributions, yet neither term is introduced in the main text. In the literature of causal representation learning, a “causal representation” refers to latent variables and the structure among them, while in causal discovery, a “causal structure” is the causal graph whose edges denote structural equations between variables.
Other Comments Or Suggestions: N/A
Questions For Authors: 1. What are the precise definitions of these terms related to causality?
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: We very much appreciate the reviewer’s suggestion to clarify what is distinctively *causal* about our methods, and also how what we are doing relates to important neighboring areas of search, like **causal discovery** and **causal representation learning (CRL)**.
We see this as an opportunity to further clarify the nature of our contribution using the additional space we would get in our next version.
---
### Q1. Clarification on the definition of “causal”
Our paper is grounded in the literature on **mechanistic interpretability**, and more specifically in techniques that perform interventions on networks to understand how they represent data and make predictions. This is in many respects easier than causal discovery or CRL, since the network is a closed deterministic system.
Nonetheless, the field does not yet have clarity on how networks make predictions, and approaches like ours are seeking to address that limitation. (For additional details on causal abstraction, the family of techniques we draw on, please see our response to **reviewer uRDA Q2.4**).
As we agree that using some of these terms which have technical meanings in important literature (especially “causal representation”) may be confusing to many readers, we intend to reword our summaries of the paper’s main contributions. In particular, we will replace the mention of “causal representation” in the text “assessing stability of causal representations” to “assessing the ability to simulate counterfactual behaviors under causal interventions”. This strikes us as a chance to clarify the diverse ways that causal methods are contributing to AI right now.
---
Rebuttal Comment 1.1:
Comment: Thank you for your response. However, my concerns regarding the definitions of key causality-related terms remain unaddressed. As mentioned in Q2 of my review, could you please explicitly clarify the definitions of the following terms within the manuscript?
- Causal features
- Causal mechanisms
- Causal interpretability
- Causal role
I appreciate your emphasis on mechanistic interpretability, but I’d like to note that it is conceptually distinct from causality: the former typically concerns understanding model predictions (as you mentioned), while the latter centers on intervention and counterfactual reasoning. In my view, if the manuscript's focus is on mechanistic interpretability, it would benefit from significant restructuring, as the current framing and terminology are largely couched in causal language (and the term "mechanistic interpretability" does not appear in the paper).
If the intended focus is indeed causality, then I believe it's essential to define the relevant terms precisely to avoid conflating correlation and causation at a conceptual level. Clarifying this would significantly strengthen the clarity and impact of the work.
---
Reply to Comment 1.1.1:
Comment: We are grateful to the reviewer for their continued engagement with our work!
- **Causal**: Our use of the word “causal” is the one adopted in standard texts on the subject, e.g., Pearl 2009, Peters et al. 2017, and so on.
- **Causal structure**: What might be less familiar is the type of causal structure we are dealing with. Instead of investigating *partially unobserved* causal structures in the world (as is typical in economics, biology, epidemiology, and so on), we are interested in the causal structure of **a (trained) neural network**. There is a sense in which we have the ground truth for this causal structure: we know exactly what **structural model** characterizes this system.
- Its **variables** are the neurons in the network and the **functional mechanisms** are given by weight matrix multiplications, non-linear transformations, and so on, across the layers that comprise the neural network.
The work in mechanistic interpretation on which we are building asks the simple question: is there a **more abstract** causal model that adequately captures the structure of the network when it comes to a particular task that the network successfully performs?
There is a growing literature within the study of causality concerned with this general question of *when one causal model can be said to **abstract** another.* Answering such questions involves precisely the notions the reviewer identified: interventions, counterfactuals, etc., all understood in the standard way in the field (as in the texts mentioned above). A paradigmatic example of such work on **causal abstraction** is, e.g., this paper by Rubinstein, Weichwald, et al.: https://arxiv.org/abs/1707.00819. In our original submission, we referred directly only to the work in mechanistic interpretability that invokes this subarea of causality research.
But we would gladly include further clarification of how that line of work relates to the broader field of causality, including references to a broader array of literature, if the reviewer feels that would help allay unnecessary confusion. | Summary: This paper focuses on correctness prediction of large language models. It separates internal features into causal features and background features and suggests two approaches for predicting the correctness of model outputs. In one, permutations are used to determine whether predictions are robust against changes in non-causal features. Another one learns a linear model and checks how close predictions are to the decision boundary.
## update after rebuttal
The authors addressed my concerns and clarified some misunderstandings. Therefore, I have raised my score to accept.
Claims And Evidence: The paper claims that causal representations are beneficial for correctness prediction. There is experimental evidence to support this claim.
It is not fully clear how much these features model meaningful causal relations; however, they improve performance in the experimental evaluation. There is no comparison to any other approach for correctness prediction.
Methods And Evaluation Criteria: The evaluation makes sense. However, additional experiments would be beneficial to further support the claims made in this paper (see "Claims and Evidence"). There is also no comparison to any other methods. Further information on the experimental setup would be helpful, such as the number of samples considered for each experiment.
Theoretical Claims: There are no theoretical claims.
Experimental Designs Or Analyses: The experimental design is sound and valid.
Supplementary Material: The appendix is not very large. I skimmed over all parts. It gives more details on the evaluation by showing more information on the datasets, as well as some additional results. However, there is no text accompanying the tables. More context and information on what is presented in the appendix would improve the structure and readability.
Relation To Broader Scientific Literature: To the best of my knowledge, this is the first paper that considers correctness prediction in large language models under a causal perspective. Both the idea and implementation make sense, and the results look promising. However, there is no experimental comparison of other approaches for correctness prediction and how this approach would compare to them.
Essential References Not Discussed: There are no essential related works missing that I am aware of.
Other Strengths And Weaknesses: **Strengths**
The idea of using causal features for correctness prediction is promising since predictions based on non-causal features should be less reliable. This should, in particular, help when making predictions on out-of-distribution data, when predictions based on non-causal features that were informative before fail to be useful. The mathematical formalization of the problem is good. Considering output features, last prompt token features, and internal background features as alternatives to the causal features in the experimental evaluation helps highlight the benefit of the proposed approach.
**Weaknesses**
For weaknesses regarding the experimental evaluation, see the fields above.
Clarity and Presentation: The paper illustrates the methodology sufficiently well to understand their approach. However, there is also much room for improvement to make understanding easier. For one, the paper would benefit from a figure on the methodology, outlining the approach in a visually understandable manner. Adding intuition on steps in the methodology would also be helpful. In particular, what do the background variables represent? And what is the causal graph that is assumed by the authors? I understand that $X \rightarrow X_\mathcal{T} \rightarrow Y$, but where does $\mathcal{B}$ fit in? To me, the most sense considering the methodology would be that $X \leftarrow \mathcal{B} \rightarrow Y$ (B acting as a kind of confounding feature), but this is not entirely clear from the paper. Concepts such as distributed alignment search and interchange intervention accuracy would also benefit from more details in this paper to reduce the reliance of readers to be familiar with the corresponding papers.
Other Comments Or Suggestions: - There is no reference to Figure 1 in the text.
- The evaluation (Section 3.2) should be placed after the methodology and at the start of section 5 since they are not essential to understand the methodology but only matter for the experimental evaluation.
- Should $x$ in Equation 3 not be $x_L$?
- "Since the model’s behavior can vary widely as the input distribution shifts, a reliable correctness prediction method should be able to robust under behavior changes." There is a small grammar mistake in here (Section 3.2).
Questions For Authors: 1. What is the intuition and what are the causal assumptions regarding the background variables? What are examples of what should be causal and what background?
2. Can the causal and background variables found by the method be analyzed such that they are understandable for humans?
3. How exactly is the balanced dataset constructed?
4. Under "Value probing", the paper states "...when the causal relation between $\mathcal{X}_\mathcal{T}$ and $\mathcal{Y}$ holds." What does this mean, i.e., when does the causal relation hold and when does it not hold?
5. Why does the counterfactual dataset only consist of samples where the model prediction is correct? Is this sufficient to learn to predict correctness? Why?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We thank the reviewer for the thoughtful feedback! We are especially glad that the reviewer recognizes our work as the first to address correctness prediction in LLMs from a causal perspective.
---
---
### Q1. Comparison with strong baselines in correctness estimation
A major concern is that
> there is no comparison to any other approach for correctness prediction.
**We respectfully disagree with this characterization, as we have compared with two of the strongest baselines in the literature: confidence scores and correctness probing**. We do realize that these methods are not explicitly labeled as “baselines” in our result tables, which may have caused some confusion. We will revise the manuscript to make the baseline labels more prominent.
To recap our baselines, we have reviewed existing methods (L160) in Section 4.1 (**Confidence Scores with Temperature Scaling**) and Section 4.2 (**Correctness Probing**). These baselines were chosen because they are *widely adopted and representative of state-of-the-art techniques* in correctness estimation (see Section 2.1 for the line of work, and also Kadavath et al., 2022; OpenAI 2023; Chen et al 2024; Orgad et al 2025 for the most relevant SOTA). We have reported their performance in Table 2 and Table 3 in Section 5.2.
---
### Q2. Presentation: Clarification on background variables
**2.1 Where does the background variable fit into the causal graph**
Please see our responses to **reviewer uRDA 2.1 and 2.2**
**2.2 Are causal and background variables understandable for humans**
This is a valuable question from the explainability perspective–namely, how to explain complex models to humans. In our experiment, **all causal variables correspond to human-interpretable concepts**, as these high-level models were manually specified by interpretability researchers. However, we want to emphasize that **our approach to correctness prediction does not require the causal variables to be human-interpretable**. The causal role of a variable in predicting model behavior is sufficient, even if it is not directly intelligible.
---
### Q3. Details on dataset construction
- For details on **split generation**, please see our response to **reviewer w7xm Q1**.
- For **label balancing**, we perform stratified sampling: we first partition all prompts into two groups based on the correctness of the target model predictions. We then randomly sample 1024/512/512 examples from each group.
---
### Q4. Clarification: when does the causal relation $X_T → Y$ hold and when does it not hold
As discussed in our response to **reviewer uRDA 2.1**, the causal relation $X_T → Y$ is an abstraction of low-level neural networks.
**This abstraction is faithful when $X_T$ mediates the model’s behavior.** However, neural networks often fail to generalize beyond their training distributions, where the model’s actual behaviors might diverge from what the high-level causal model $H$ predicts. **When this occurs, we say the high-level causal relation $X_T → Y$ no longer holds**, i.e., it is no longer a faithful abstraction of the low-level neural network model. These cases correspond precisely to our out-of-distribution settings.
---
### Q5. Clarification: Why does the counterfactual dataset consist only of correctly predicted samples
This is indeed one of the interesting findings from our work: **it is sufficient to learn a strong correctness predictor using only correctly predicted examples.** This finding might make more sense if we consider confidence score methods, where correctness predictions are made using the probabilities output alone without using any additional samples.
The question of why Counterfactual Simulation works is in fact tied to the core question we are asking in this work: does understanding the internal causal mechanisms allow us to better predict model behaviors, especially under distribution shift?
Intuitively, if we know that (1) for all correctly predicted examples, the model behaves according to a high-level causal model $H$ (i.e. implements a systematic solution), and (2) for an unseen example, the model does not implement the same solution, **then it is very likely that the model is predicting something abnormal and so the prediction is likely wrong**. Mathematically, this intuition is formalized in Eq 7-9, where the counterfactual simulation measures whether the model implements the same solution as we have observed on the correct samples.
---
### Q6. Presentation
We appreciate the reviewer’s suggestion to clarify the definitions of "Distributed Alignment Search" and "Interchange Intervention Accuracy."
We will include preliminary explanations of these terms in the revised manuscript! | Summary: This paper investigates the use of internal causal mechanisms within language models (LMs) to predict the correctness of their outputs. Rather than relying on traditional confidence scores or heuristic probing of internal activations, the authors propose two methods grounded in causal interpretability, Counterfactual Simulation and Value Probing.
These methods are evaluated across a diverse suite of tasks under both in-distribution and OOD settings. The authors demonstrate that causal features yield more robust correctness estimates than non-causal baselines, particularly under distribution shifts.
The work builds upon the causal abstraction framework and introduces a correctness estimation benchmark using known causal variables in some tasks.
Claims And Evidence: The central claim of the paper is that **internal causal mechanisms are more robust predictors of correctness than non-causal heuristics**, particularly under distribution shift. This claim is supported by:
- Comprehensive experiments across five tasks and ten OOD settings (Tables 2 & 3).
- Comparisons between causal and non-causal features (confidence scores, probing) under consistent evaluation metrics (AUC-ROC).
- Correlations between Interchange Intervention Accuracy (IIA) and correctness AUC (Figure 2), suggesting a link between causal alignment and predictive robustness.
However, one problematic claim is the general applicability of the linear decomposition assumption (Eq. 5). The paper acknowledges limitations but does not provide direct evidence or diagnostics when this assumption fails (e.g., in tasks with entangled representations).
Methods And Evaluation Criteria: Counterfactual simulation and value probing are appropriate for the problem of correctness estimation. The use of interchange interventions to isolate causal variables is well-motivated by prior interpretability literature (e.g., Geiger et al., 2021, 2024).
Each task is evaluated under both in-distribution and OOD prompts, with OOD shifts chosen to stress test causal robustness.
Theoretical Claims: The key theoretical claim is that internal model representations can be linearly decomposed into task-relevant (causal) and background (nuisance) components, enabling causal inference via projection.
This is not formally proven in the paper. The decomposition in Eq. (5) is derived from prior work on causal abstraction and DAS, but:
- No formal conditions for identifiability are given.
- No proofs of convergence or uniqueness of the causal basis Q.
- The assumption that task behavior is mediated by a single variable X_T is strong and underspecified.
- No formal causal graph given.
Experimental Designs Or Analyses: Overall solid, tasks cover different scenarios.
Why value probing not performing well in a lot scenarios?
Supplementary Material: No
Relation To Broader Scientific Literature: The paper is directly based on the causal abstraction and mechanistic interpretability literature:
- Geiger et al. (2021, 2024a, 2024b) on DAS and interchange interventions
- Wu et al. (2023), Huang et al. (2024), and others on task-specific circuit discovery
- Work on LLM trustworthiness via internal probes (e.g., Azaria & Mitchell, 2023; Ferrando et al., 2024)
Novelties including:
- Reframing causal representations as predictors of correctness, not just explanatory tools
- Demonstrating improved robustness under shift over confidence scores and surface-level probes
Essential References Not Discussed: NA
Other Strengths And Weaknesses: Strengths
- Strong empirical benchmark with real OOD variation
- Introduces novel causal predictors (simulation + value probing)
- Bridges interpretability and evaluation
Weaknesses
- Causal assumptions (e.g., disentanglement, uniqueness of $X_T$) not deeply validated
- Theoretical work directly based on prior work (DAS)
- Method assumes knowledge of task structure to define $X_T$
Other Comments Or Suggestions: Page 5:
> “We empirically study whether these low-confidence predictions correspond to incorrect predictions in Section 4.3.”
“Section 4.3” may be a typo. Based on context, the relevant content likely appears in Section 5 (Experiments). Please confirm and update accordingly.
Page 5:
> “We evaluate four correctness predictions methods over a suit of five language modeling tasks.”
“We evaluate four correctness prediction methods over a **suite** of five language modeling tasks.”
---
Explicitly present the assumed structural causal model (SCM) as a diagram or formal figure.
The implicit model appears to be:
$X \rightarrow X_T \rightarrow Y, X \rightarrow B \rightarrow Y$
Questions For Authors: See comments above
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We thank the reviewer for their insightful comments! We are encouraged that they recognized the novelty of our methods, the strength of our empirical results, and the significance of bridging the explanatory and predictive aspects of interpretability analysis.
---
---
### Q1. Clarification on the linear decomposition assumption
Linearity is indeed an assumption made in DAS. We have discussed its implications in the presence of non-linearity and potential remedies in our response to **reviewer w7xm 2.4** and offer additional evidence in **Q4** below.
---
### Q2. Clarification on the causal assumptions and causal model
**2.1 Causal structures in causal abstraction**
We also appreciate the reviewer’s request to clarify the causal aspects of our approach, which we recognize does rely on previous work on causal abstraction. **There are in fact several causal structures at play, and causal abstraction is about the relationship between different causal structures.** Most basically, there is the causal structure of the neural network itself: a sequence of layers of variables with each layer depending functionally on the previous. But there is also a second causal structure given by the “high level” model $H$ that, in our running example, is given by just three variables, $X, X_T$, and $Y$. **The variable B does not occur in $H$. Moreover, $X_T$ is not unique in the sense that we can have different high-level models representing different levels of abstraction.**
DAS then involves searching for $X_T$ somewhere in the network, such that the interchange interventions are successful. When that happens, we say that H is an approximate abstraction of the network, in the sense that $X_T$ mediates the transformation from task $T$ input to output. In the limit, DAS is guaranteed to find this encoding of $V_T$, provided it exists. **But note that basis $Q$ is not guaranteed to be unique.**
**2.2 The background variable $B$**
With this much, we can say exactly what $B$ is. $B$ is just the orthogonal complement of the identified representation of $X_T$ (e.g., somewhere in the residual stream). It lives outside the simple high-level structure $H$ and is determined by the structure of the network, namely how it encodes $X_T$. **We call it a background variable because it encompasses everything about the input that does not feed into $X_T$** (and ultimately determine the output $Y$).
**2.3 Identifiability** Please see our response to **reviewer w7xm 2.3.**
**2.4 Modeling more complex task structures**
We totally agree that this three-variable high-level structure can be overly restrictive. Indeed, **most tasks studied in our paper involve significantly more complex structures.** For instance, in the IOI task, at least 6 causal variables are involved (Figure 2, Wang et al. 2023), including 3 input variables (IO, S1, S2), 2 position variables (outputs of the Induction and the S-Inhibition Heads), and the output. We use the second position variable as $X_T$ to perform counterfactual simulation. We will clarify in the revised manuscript that the three-variable model is for *illustrative purposes*, and our methodology generalize to more complex settings as demonstrated in our experiments.
---
### Q3. Method assumes knowledge of task structure to define $X_T$
This is a valid concern, and indeed a known limitation. However, the interpretability community has proposed auto-interp methods to reduce the reliance on human priors (Mu et al. 2021; Hernandez et al., 2022; Bills et al., 2023; Conmy et al., 2023; Rajaram et al., 2024).
Our proposed methods work well with these methods.
For example, an auto-interp pipeline produces a natural language description of a feature subspace, which can be translated into a high-level causal model $H$: input → concept → output. We can then (i) verify whether $H$ is faithful via interchange interventions, and (ii) use $H$ to perform the counterfactual simulation defined in Eq (7).
---
### Q4. Reasons for why value probing underperform in many settings
We hypothesize two reasons:
- **Incomplete coverage of the causal pathway.** Unlike Counterfactual Simulation, value probing does not cover the full causal mechanism from X to Y and thus might fail to detect errors in the $X_T→Y$ computation.
- **Complexity of decision boundaries.** Linear probe requires not only that the variable can be encoded in a linear subspace, but also that the individual values of variables be linearly separable (L222-225)--a stronger assumption than DAS’s (Eq. 5). Non-linearity and high-dimensional variables generally make the geometry of the decision boundaries more complex and harder to learn. A great example is the country variable in RAVEL, which has over 200 unique values. Although the most frequent countries are linearly separable (as visualized via PCA), the long tail distribution makes learning the complete decision boundaries challenging. This likely explains Value Probing’s underperformance on RAVEL.
---
Rebuttal Comment 1.1:
Comment: I thank the authors for clarifying my concerns. Therefore I raise my score. | Summary: For this paper the authors try to identify internal features of LLM that mediate causal effects on the final prediction output. In settings where LLM predictions align with the actual real-world causal process, causal features are assumed to resemble the ground-truth mechanism and, therefore, allow for predictions which are invariant to external disturbances or out-of-distribution queries.
Towards the goal of identifying causal features, the authors present two methods which work on finding features which are invariant under counterfactual inputs ('counterfactual simulation') or learn a decision boundary from the extracted activations ('value probing'). In both cases the authors first localize features that model an intermediate variable by finding a minimal linearized subspace and decompose this into causally relevant and background variables.
Experiments are conducted over several datasets symbolic manipulation, retrieval, instruction following inspecting AUC-ROC for in-distribution tasks and robustness under OOD settings. Through their experiments the authors find that their proposed methods are capable to identify causal features relevant to the given tasks. This results in high AUC-ROC values for in-distribution settings and superior prediction performance in OOD settings, compared to prior baselines.
Please note, this is an emergency review.
**Update after rebuttal.** In their rebuttal the authors were able to further clarify implications and limitations of their made linearity assumptions in their work. While I acknowledge possible concerns regarding the formal handling of causality, causal representations and structure, I find the concepts to be sufficiently handled for this type of work, and the presented results of figs. 1 and 2 convincing and in line with already existing literature (e.g. the particular positions of decision making within LLMs). I therefore remain with my recommendation to accept the paper.
Claims And Evidence: The authors claim that their proposed methods are able to identify internal model features that are causally relevant to predict the final outcome of the model. To this, the authors conjecture that a linear decomposition of layer residuals into subspaces of causally relevant and irrelevant background features yields the desired representations. While linearity assumptions might not hold under all settings, extensive prior work on feature space linearization exists, supporting the presented claims. From the presented evidence in Figures 1, 2 and tables 2 and 3 it can be furthermore concluded that the presented methods indeed identify causally relevant features as OOD performance remains stable and the visualized identified feature activations align well with the predicted outcome.
Methods And Evaluation Criteria: The specific proposed methods of counterfactual simulation and value probiing are well described and formalized in equations 7-11. The general approach appears to be sound and handles correctly handles implementation of causal considerations for identifying features.
The utilized datasets of Indirect Object Identification, PriceTag, RAVEL, MMLU and UnlearnHP are known or seem to be suited to test the claimed effects. The authors test on an in-distribution and an out-of-distribution setting by altering prompts and utilized concepts. Here, the construction of interventions on the datasets and prompts are well described. The presented prompts are reasonably designed and their rephrased version are suited to evoke OOD behavior by altering sentence phrasing or adding distracting artifacts. Performance is measured in terms of AUC-ROC, task accuracy and interchange intervention accuracy. The individual metrics are suited to assess the respective effects.
Theoretical Claims: Apart from assuming linear decomposability in Eq. (5), the authors present no direct theoretical claims or proofs. Causal relations from inputs variables, intermediate representations to the model output are straight forward and correctly formalized.
Experimental Designs Or Analyses: The authors describe the overall experimental setup and use of metrics well and seem setup conduct a proper evaluation. The paper, however, severely lacks in terms of experimental details with regard to the training setup of the proposed method and hyperparameter tuning of prior methods. The authors mention (hyper)parameter optimization and training setup, e.g. for the $\tau$-classifier, but do not specify the exact model setup, optimization method, learning rate or number of samples/iterations. While the proposed methods incorporate additional steps which make reasonable effort to enhance results, there is currently no way of assessing whether or not the evaluation has been setup properly and fair from the current state of the paper.
The evaluation over different datasets, along with results in tables 2 and 3 and the figures 1 and 2, seem to indicate a proper working of the methods with alternating, but constantly better, performance than the compared baselines. The presented visualization generally support the claims of the paper and indicate a good identification of causally relevant features from the internal residual activations for the methods.
Supplementary Material: I reviewed the whole Appendix, consisting of different prompts for the different dataset in appendix A.1, further results of the RAVEL OOD setting (A.2) and variations on different model variant (A.3). Overall, the prompts and results are well presented and seem to align with the main paper.
Relation To Broader Scientific Literature: LLMs have classically been found to generally struggle with direct causal reasoning [1-5]. Nonetheless, as of today, LLM are utilized in an abundant number of tasks. Recent interest on mechanistic interpretability and circuit extraction techniques pose desirable guarantees in terms of robustness and scalability. The identification of causally relevant features might help establish particularly strong theoretical quarantees and help scaling and generalization to previously unseen OOD queries.
[1] Jin, Zhijing, et al. "Cladder: Assessing causal reasoning in language models." *Thirty-seventh conference on neural information processing systems*. 2023.
[2] Kıcıman, Emre, et al. "Causal reasoning and large language models: Opening a new frontier for causality." *arXiv preprint arXiv:2305.00050* (2023).
[3] Zečević, Matej, et al. "Causal parrots: Large language models may talk causality but are not causal." *arXiv preprint arXiv:2308.13067* (2023).
[4] Gao, Jinglong, et al. "Is chatgpt a good causal reasoner? a comprehensive evaluation." arXiv preprint arXiv:2305.07375 (2023).
[5] Ashwani, Swagata, et al. "Cause and Effect: Can Large Language Models Truly Understand Causality?." arXiv preprint arXiv:2402.18139 (2024).
Essential References Not Discussed: The authors general motivate and embed their presented work well within the existing literature. The presented work builds on a series of prior work on causal feature extraction from LLM by Geiger et al. . The authors expect extensive knowledge on this line of work, which hinders comprehension and self-enclosedness of the work. Key concepts on the localization process of finding causal mechanisms in LLM or extracting feature subspaces, such as "distributed alignment search" or evaluation metrics such as the "interchange intervention accuracy", are only briefly referred to. The presented methodology seems to rely on linearity assumptions of latent representations which, however, are only insufficiently discussed. In this regard, the paper might be improved by more explicitly discussing identifiability of model representations [1,2], possibilities of non-linear mechanisms identification or their non-identifiability [3,4] and general (causal) perspectives on linearity and subspaces in LLM activations [5].
[1] Mikolov, T., Yih, W. T., & Zweig, G. (2013, June). Linguistic regularities in continuous space word representations. In Proceedings of the 2013 conference of the north american chapter of the association for computational linguistics: Human language technologies (pp. 746-751).
[2] Park, K., Choe, Y. J., & Veitch, V. (2023). The linear representation hypothesis and the geometry of large language models. arXiv preprint arXiv:2311.03658.
[3] Leemann, T., Kirchhof, M., Rong, Y., Kasneci, E., & Kasneci, G. (2023, July). When are post-hoc conceptual explanations identifiable?. In Uncertainty in Artificial Intelligence (pp. 1207-1218). PMLR.
[4] Friedman, Dan, et al. "Interpretability Illusions in the Generalization of Simplified Models." *International Conference on Machine Learning*. PMLR, 2024
[5] Rajendran, Goutham, et al. "From Causal to Concept-Based Representation Learning." *Advances in Neural Information Processing Systems* 37 (2024): 101250-101296.
Other Strengths And Weaknesses: **Strengths**
The paper is generally well written and motivated. The presented approaches soundly incorporate the notion of causality and build up existing feature extraction methods. The presented theory and working of the methods is well formalized in the equation.
The identified representation hold desirable properties in terms of robustness and OOD behavior. The authors are able present convincing evidence towards the correct identification of such features.
Finally, the experiments seem to be generally well setup and support the claims made. From the visualizations of identified features the authors are able to demonstrate correct identification of causally relevant factors.
**Weaknesses**
The mentioned weaknesses concern the lack of clarity and insufficient discussion on possible assumptions as mentioned before. Specifically:
1) The lack in clarity on the experimental evaluation makes it impossible to judge the correct setup and comparison of the methods. The authors might want to provide the necessary details, as discussed in the section above.
2) By the decomposition of residual activations in Eq. (5) the authors assume a simplified linear representation of model residual activations. Since the authors are furthermore concerned with causal interactions, they only consider the high-level causal chain of input, intermediates and output. Both assumptions are simplifications to the true working of the model and might lead to a simplified regression towards only the direct parents intermediates of Y. While prior works have shown that linear interpretations might exist, the authors might discuss possible implications and limitations of their approach in setting of more complex causal structures and composed or non-linear behaviour.
3) The authors might improve their paper, by briefly describing the key ideas of the localization process and distributed alignment search, in particular with regard to the necessary assumptions for the utilization of the methods and applicability to the presented setting.
Other Comments Or Suggestions: * typo l.120 "desire[d] behavior"
Questions For Authors: Questions mainly concern the weaknesses above:
1) Could the authors provide further details on the experimental setup, such as training parameters and hyper parameter search?
2) Could the authors discuss the required assumptions with respect to linearization of the residual feature space?
3) What are the implications for the methods in terms of expressiveness and variable identifiability of intermediate values which are no direct causes of the final model output? Would the presented methods be able to identify such variables?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We thank the reviewer for their detailed feedback! We are glad they found our proposed methods “well formalized” and “soundly incorporate the notion of causality” and appreciated our task design, metrics, and supporting results.
---
### Q1. Experimental Details
We provide detailed experimental setup below to further assure reviewers that our baseline comparisons are fair.
- **Datasets**
- For each task, we randomly sample 3 folds from all prompts (i.e. the Cartesian product between templates and variable values). Each fold has 2048/1024/1024 examples for train/val/test sets (1024/512/512 for UnlearnHP due to limited source texts). Our dataset sizes are comparable to prior work on truthfulness prediction (e.g., Orgad et al 2025, Gottesman et al 2024).
- **Training setup and hyperparameters** (selected based on val set accuracy)
- **Confidence Score**
- Temperature scaling: Search over T = 0.5, 1, 2, 3 and report results for the best two (T = 1, 2).
- Output token selection: Search over first-N, N ∈ [1, 100] and answer tokens. Answer tokens are identified via regex.
- Aggregation: Experiment with mean (Kadavath et al., 2022; Guerreiro et al., 2023) and min (Varshney et al. 2023), reporting mean as it outperforms min on most tasks.
- **Probing**:
- Model: Experiment with `sklearn.linear_layer.LogisticRegression` with default settings (follow Orgad et al. 2025) and `sklearn.svm.LinearSVC` (which has lower accuracy)
- Feature location: Search across all layers and tokens.
- **Counterfactual simulation**:
- Training data: 10K pairs randomly sampled from 1024x1024 correct examples
- Intervention dimension: Search over powers of 2; Use 1/256/1024/4/4 for the five tasks.
- Intervention location: Use locations identified in prior work or search over variable tokens, their immediate successors, chat template tokens, and the last token across layers.
- Optimizer: AdamW with constant LR = 1e-4, no weight decay; trained for one epoch.
### Q2. Linearity Assumptions on Representations
**2.1 Presentation of assumptions**
We fully agree and have made the linearity assumption for value probing explicit in L222-228. We also take this opportunity to clarify the assumptions behind counterfactual simulation below.
**2.2 Counterfactual simulation does not require linearity**
We would like to clarify that Eq. (7) does *not* rely on any assumption of linearity in model representations. The linearity assumption appears only in Eq. (5), which defines *one possible* localization method. Crucially, our formulation in Eq. (7) is designed to be general and agnostic to the choice of localization methods. It remains valid even when using localization methods that operate in non-linear spaces.
**2.3 Causal abstraction assumes access to the full causal structure, and is not subject to the identifiability concerns raised in [3–5]**
The identifiability problems in causal settings arise when some fundamental aspects of the causal structure is unknown, as in the important literature references by the reviewer [3, 4, 5]. By contrast, in our setting, the relevant causal structure--the neural network itself--is assumed to be fully accessible to use. The task of DAS, and related techniques for finding causal abstractions, is simply to check whether a "high-level" causal structure is implicitly implemented in the network. This is not an inference or identification problem, but rather a search problem whose goal is to help us understand how the model represents examples and makes predictions. We will clarify this important distinction at the beginning of the paper.
**2.4 Generalizability to non-linear representations: Transformer representations are not fully linear, yet localization methods like DAS can still have partial success**
We thank the reviewer for raising this point. We agree that the linear subspace approach in Eq. (5) has limitations when high-level concepts are non-linearly encoded. In this case, we can switch to a more suitable localization method (e.g., involving non-linear mappings) and our method in Eq. (7) remains compatible.
If we stick with current linear methods like DAS, generalizability becomes an empirical question. Since Transformer-based LLM representations are neither fully linear nor fully non-linear (Park et al. 2024; Smith 2024; Engels et al. 2024), our results already offer empirical insights—we expect a *partial* success rather than a complete failure with non-linear representations.
### Q3. Generalizability to more complex causal structures
**3.1 Expressiveness** Please see our response to **reviewer uRDA Q2.4**.
**3.2 Variable identifiability** Please see our response to **Q2.3**
### Q4. Presentation
We sincerely thank the reviewer for the suggestions on engaging the broader audience who are less familiar with the interpretability literature. We will add a preliminary on localization methods and evaluation metrics.
---
Rebuttal Comment 1.1:
Comment: I thank the authors for providing details on the experimental evaluations, which where the most pressing issue in my opinion.
I, furthermore, agree with the comments on the linearity assumptions in that paper. While the authors rightly argue that Eq. 5 only poses a particular possible implementation, it is the only one shown and tested in this paper. I would like to recommend that the authors include the provided comments regarding possible implications of their choice in the final version.
Q2.3 / Variable Identifiability: What I meant in my initial review, was whether the presented method can identify and validate the correct working of intermediate mechanisms that might be, in turn, relevant for the final model output? While in their particular setting the authors are primarily concerned with the causal correctness of the final target variable, considerations on *how* models come to their conclusions might further strengthen explanations on the identified mechanisms.
The remaining points only pose minor concerns. I have, therefore, raised my score to an accept.
---
Reply to Comment 1.1.1:
Comment: We want to thank you again for your detailed feedback that has helped sharpen the presentation of our work!
---
> I would like to recommend that the authors include the provided comments regarding possible implications of their choice in the final version.
Thank you for the suggestion! We will clarify our assumptions and implications of our methods in the final version of the paper.
> Q2.3 / Variable Identifiability: What I meant in my initial review, was whether the presented method can identify and validate the correct working of intermediate mechanisms that might be, in turn, relevant for the final model output? While in their particular setting the authors are primarily concerned with the causal correctness of the final target variable, considerations on how models come to their conclusions might further strengthen explanations on the identified mechanisms.
This is a great point, and we share the reviewer’s enthusiasm about the possibility of gaining further clarity about how models are generating final outputs, especially in the “open-ended” tasks where we currently have only partial understanding.
For instance, in MMLU we rely purely on specific multiple-choice mechanisms from Wiegreffe et al. (2025). Notably, this is already enough to show an improvement in correctness prediction. But a fuller understanding of the mechanism mediating between inputs and outputs could potentially lead to even greater improvements, in addition to other benefits. | null | null | null | null |
EnIGMA: Interactive Tools Substantially Assist LM Agents in Finding Security Vulnerabilities | Accept (poster) | Summary: This paper presents EnIGMA, an LM agent enhanced with Interactive Agent Tools (IATs) to solve CTF challenges, achieving state-of-the-art results. Their experiments use 390 challenges from diverse benchmarks to evaluate EnIGMA with different LLMs. They also provided several ablation studies and analyses to demonstrate the effectiveness of EnIGMA and model behaviors.
Claims And Evidence: Partially.
I wonder about their claim about SOTA performance.
In Section 3.2 and Table 2, they include the previous best methods without a clear demonstration of the comparison. I wonder what the particular method used in previous best methods and if they used the same LLM as the agent? Does the superiority come from the better LLMs or the proposed framework?
Methods And Evaluation Criteria: Yes.
1. I would like to ask for more clarification of tool design: In Section 2.1, specify why only gdb and pwntools were chosen for IATs. Are tools like tshark or nikto (mentioned in Appendix D and Figure 10) accessible to the agent?
2. It is not clear to me how the cost metric is calculated. Did you count the API cost for GPT models? How about LLaMA?
Theoretical Claims: The paper doesn't have theoretical claims.
Experimental Designs Or Analyses: Yes.
I found some experimental results that need more analysis and discussion.
1. Table 1: The LM summarizer improves performance by 2.6% over the simple summarizer, but removing both summarizers only reduces performance by 1.3%. This paradox is unexplained.
2. Table 1 shows that ablating IATs reduces overall performance by 2.1%, but in the web category, performance improves by 3.45% (Table 10). This suggests the current IATs may be suboptimal for web challenges.
3. For their criteria for solution leakage, I do not agree with the second condition. The LLM may have learned a large number of flags and found the solution by method of exclusion.
4. Line 431, the experiment with unseen changes is unclear and doesn't cite the data source appropriately. I wonder what the tasks are and what the differences are between the unseen task and existing benchmarks.
Supplementary Material: Yes, appendix.
Relation To Broader Scientific Literature: Lack of novelty. The tool use of agent and conversation summarization have been explored in previous works. I didn't find new methodology contributions, although I acknowledge the engineering contributions of this paper.
As the main contributions are the engineering aspect, I expect that the paper has more discussion about the code release and ethical considerations.
Essential References Not Discussed: None.
Other Strengths And Weaknesses: Strengths:
1. They evaluate their proposed framework with 390 challenges on four benchmarks (NYU CTF, CyBench, etc.) and diverse LLMs. It shows the generalizability of their framework.
2. The discussion of "soliloquizing" and leakage quantification provides useful insights into LM evaluation pitfalls.
Weaknesses:
Please see the comments in the above sections.
Other Comments Or Suggestions: Please see the comments in the above sections.
Questions For Authors: Please see the comments in the above sections.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you so much for your time and consideration. You’ve brought up excellent points in your feedback that we address below.
**Q1: Previous best methods comparison - does the superiority come from the better LLMs or the proposed framework?**
To address your concern, we present agent performance across different benchmarks while using the same LMs: On the NYU CTF benchmark with GPT-4 Turbo, EnIGMA achieves a 7% solve rate vs. NYU Agent’s 4%. On CyBench with Claude 3.5 Sonnet, EnIGMA reaches 20%, outperforming CyBench’s 17.5%. With Llama 3.1 405B Instruct, EnIGMA scores 10% vs. CyBench’s 7.5%. All agents use a ReAct framework with access to a Linux terminal in a Dockerized environment. CyBench, specifically, runs on Kali Linux, where the agent can benefit from a lot of pre-installed security tools. These gains, across benchmarks and models, show that EnIGMA’s framework – not just LM choice – drives performance improvements. We will clarify it in Section 3.
**Q2: Why only gdb and pwntools were chosen for IATs? Are tools like tshark or nikto accessible to the agent?**
We selected the most common tools which were unsupported in current LM agents based on our experiments on the development set. Tools like `tshark` and `nikto` remain accessible but are not part of IATs because they already have well-structured CLIs that can be invoked directly as shell commands without requiring interactivity. We will clarify this in the paper.
**Q3: How is the cost metric calculated?**
The cost metric is calculated per solved challenge based on API calls, taking into account input & output tokens and model-specific pricing. OpenAI and Anthropic models use their official pricing, while Llama models follow Together AI's API rates. Details are in Appendix C.2, and we will further clarify the cost calculation in the paper.
**Q4: The LM summarizer improves performance by 2.6% over the simple summarizer, but removing both summarizers only reduces performance by 1.3%.**
The LM summarizer and the simple summarizer are actually two distinct modules. The LM summarizer condenses the previous action’s output into a short summary (so that the agent can process long outputs from tools such as a decompiler). The simple summarizer shows the first 100 lines of the last action’s output. We show the results of the simple summarizer, which degrades the baseline agents performance by 2.6%, just to show that a simple approach to summarizing doesn’t perform well. On the other hand, our LM summary tool improves performance by 1.3% over the baseline. We apologize for the confusion this caused and will remedy this in the next version of our paper by clarifying the role of the simple summarizer as a baseline summarizer, that should not actually be used in practice.
**Q5: IATs may be suboptimal for web challenges.**
This is correct. As noted in Section 4.1 (Line 316), the performance increase in the web category suggests that the current IATs may be less suited for these types of challenges. At the same time, this result highlights the effectiveness of interactive tools in the categories where they are most relevant - crypto, pwn, and rev - where their presence contributes to the agent’s success. There are a large number of ways to further expand IATs to handle a wider variety of tasks, and so we leave that for future work.
**Q6: Solution leakage criteria and finding the solution by method of exclusion.**
Our second condition specifically assesses whether the flag appears in any observations, which are the outputs generated by the environment. In the scenario you described the flag would not appear in any of the environment’s outputs. According to our definition, this case would indeed be classified as solution leakage.
**Q7: Unseen challenges - data source and differences with existing benchmarks.**
Thank you for bringing this to our attention. We will cite the GitHub repository with these new challenges, which were part of the qualification round of the 2024 CSAW competition, following the same competitions as the NYU CTF benchmark but from different years. These challenges span the same six categories: 5 crypto, 4 forensics, 3 web, 4 rev, 4 pwn, and 1 misc. The key difference is their release date – September 2024, after all models’ training cutoffs. EnIGMA with Claude 3.5 Sonnet solves 2 of 21 challenges suggesting that it can extrapolate to new problems that the underlying LM has not encountered during training.
**Q8: Novelty.**
Please see reviewer FRVw, Q5.
**Q9: Code release and ethical considerations.**
We are committed to open-sourcing our code and have included an anonymized repository with all experimental artifacts in the supplementary materials. Given the cybersecurity focus, we address ethical considerations in the Impact Statement (page 9) and have disclosed our findings to model providers to ensure awareness of potential safety implications.
Thank you again, your constructive feedback is valuable in refining our work.
---
Rebuttal Comment 1.1:
Comment: Thanks for the response.
I found many of my concerns have been addressed. I hope the authors can incorporate these into the final version of the paper.
For Q1, I hope the author can summarize the SoTA comparison results in a table.
---
Reply to Comment 1.1.1:
Comment: We thank reviewer FxPC for their response and score increase.
> I hope the authors can incorporate these into the final version of the paper.
For Q1, I hope the author can summarize the SoTA comparison results in a table.
We are committed to incorporate these changes into the final version of the paper. We will also include a table summarizing the SoTA comparison between our agent and previous best methods using the same LMs.
Thank you for your valuable feedback. | Summary: The paper proposes EnIGMA, an LM agent designed for CTF challenges. EnIGMA is built based on SWE-agent for code generation, which is based on the ReAct framework. On top of SWE-agent, EnIGMA incorporates actions and tools specially designed for the CTF challenges, including a debugger and a remote connection server tool. EnIGMA is evaluated on four CTF challenges (3 public and 1 self-created) and demonstrates clearly better performance than previous state-of-the-art.
Claims And Evidence: I didn't find faulty claims.
Methods And Evaluation Criteria: The proposed method makes sense in general. The evaluation is also rigorous from my point of view.
Theoretical Claims: There are no theoretical claims in this paper.
Experimental Designs Or Analyses: The experimental design follows the standards for CTF challenges.
Supplementary Material: I didn't review the supplementary material.
Relation To Broader Scientific Literature: The application of ReAct-based agent to the CTF challenges is reasonable, demonstrating the power of LM agents in solving complex tasks. The results are expected, as LM agents with tools should perform better than naive LLM prompting.
Essential References Not Discussed: I didn't find important missing references.
Other Strengths And Weaknesses: The paper is generally well-written and the results are convincing.
My major concern is the novelty of the method. Incorporating specially designed tools is a typical design when adapting generic agents to specific tasks. In this work, it is hard to claim that the performance gain is due to the agent workflow design rather than harnessing the power of the tool.
Other Comments Or Suggestions: The system can implement a memory module to store previously solved cases. The memory entries can be retrieved to further enhance the performance.
Questions For Authors: If for the previous methods, the same debugger is hardcoded into the system, will they achieve much better results than they did before?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We sincerely thank the reviewer for their feedback on our work and for finding our results convincing. We address each of your concerns below.
**Q1: Novelty of the method and whether the performance gain due to the agent workflow design or harnessing the power of the tools.**
In EnIGMA, we are the first to show how to enable an LM agent to utilize ***interactive tools***, such as a debugger and a server connection tool. To facilitate the use of such tools, we developed the IATs framework, which also provides extendability for future research on other interactive tools (Section 2). This approach allows the agent to perform tasks it previously could not, even when tools are directly installed on the environment. As a result, EnIGMA achieves state-of-the-art performance on three out of the four benchmarks we tested, even when using the same LMs and methods as in previous approaches (see reviewer FxPC, Q1). Our comprehensive empirical analysis (Section 4) explores how the LM agent utilizes the framework, where we demonstrate the agent’s effective use of interactive tools. Lastly, we also ***uncover the surprising soliloquizing phenomenon***, which provides valuable insights into the design and evaluation of future LM agents. We hope this clarifies the novelty and impact of our method, and we are grateful for your feedback.
**Q2: The system can implement a memory module to store previously solved cases. The memory entries can be retrieved to further enhance the performance.**
This is a valuable suggestion. Prior research on LM agent frameworks has shown that a memory module can improve performance. We leave this as a direction for future research.
**Q3: If for the previous methods, the same debugger is hardcoded into the system, will they achieve much better results than they did before?**
In the reverse engineering (rev) category – where the debugger is most frequently used (Figure 9) – Table 10 indicates a 3.84% drop in solve rate when the interactive tools (debugger and server connection) are removed. We know that the debugger was invoked in 8.1% of these tasks, and the server connection was used just in 3.3% of cases, we can therefore summarize that removing only the debugger would harm performance.
In addition, Table 1 shows that removing both the debugger and server connection tools reduces the overall solve rate by 2.1% across all categories in all four benchmarks.
In the initial paper we didn’t have an ablation study that just ablates the debugger away, but we agree that this is an important number to have and will run these experiments for the final version of the paper.
Thank you once again for your valuable feedback. | Summary: The paper describes a new and improved agent for solving computer security Capture the Flag challenges.
Claims And Evidence: Mostly. There is one claim about interactive tools that I think is overstated (see Other comments below). The evaluation of leakage has some limitations.
Methods And Evaluation Criteria: Yes. I think the benchmarks and evaluations are reasonable and appropriate and support the paper's goals.
Theoretical Claims: No theoretical claims made.
Experimental Designs Or Analyses: The experimental designs seem reasonable. I would have been interested if there was a more convincing way to evaluate leakage, but that's challenging to do, so it's not a surprise that it is difficult to get a solid grip on it.
Supplementary Material: No
Relation To Broader Scientific Literature: This continues a line of work exploring using LLM agents to solve CTF puzzles, and improves upon past work. It finds that better design of tool bindings improves overall performance.
Essential References Not Discussed: Not that I know of.
Other Strengths And Weaknesses: This work is helpful, because it helps us understand the risks of LLM agents and the balance of power between attackers vs defenders (do stronger agents help attackers more, or help defenders more?).
This work might also be useful in the future for system defenders, because solving CTF puzzles is related to finding vulnerabilities. These techniques might improve effectiveness of agents at finding vulnerabilities, and system defenders could use those methods to find and then patch vulnerabilities in their systems.
The paper is well-written and easy to follow.
Other Comments Or Suggestions: I don't understand what "main shell" means. Does this mean a connection to a Unix shell (e.g., bash)? Or does this mean an agent running a REACT loop?
Fig 2: I don't understand how this demonstrates a session running in parallel with the main shell. What part of Fig. 2 is the main shell and what part is the separate session? What does "bash-\\$" mean? Does that prompt mean that the FTP connection has terminated and now the session involves the agent interacting with bash? Or is the FTP connection still open and the agent is still interacting with it? If so, why provide input like "bash-\\$" that normally indicates back to the command-line shell rather than in a program like a FTP client?
Sec 2.2: What is the input to the summarizer? Does the summarizer receive the prior thought and action (e.g., "Let's start by decompiling...")? Does it receive the initial context about the problem (e.g., the text of the problem statement for this CTF problem)? Or does it only receive the tool output and nothing else?
Sec 2.3: Please provide more detail on this. How many demonstrations per step? How were they selected? Can you report the average number of guidelines and a histogram on them, and show some randomly selected examples of guidelines?
Table 1: On what dataset is this measured?
Table 2: I recommend showing Table 2 earlier, and moving Table 1 later. First, show the main overall results on effectiveness of your method. Save the ablations for later.
Sec 4.1: Could we achieve a higher pass rate, if we halt the process after 20 steps (if it hasn't succeeded yet), reset everything, and restart anew? In other words, if in one run, the agent never succeeds, might there be another luckier trajectory that does succeed, and if we try multiple trajectories, does it increase the probability that at least one succeeds? It might be better to try 5 times, each for only steps, than to try once, for 100 steps.
Sec 4.1: I don't agree with the conclusions here. The quantitative results don't support the claim that "Proper interactive interfaces are crucial". The performance drop with IATs is only 2 percentage points (about 10%). That's not "crucial".
Sec 4.2: The criteria used to measure leakage seems a bit too narrow to me. I can imagine that if the challenge was in the training set, the LLM might not have memorized the flag but might have memorized the solution approach. (For instance, maybe the LLM training data included a writeup from one of the contest participants on their blog.) I think it would be helpful if you had a way to measure leakage in a more convincing way.
Sec 4.2, unseen challenges: It might help to mention which of the 4 datasets has the most similar distribution to the set of 21 unseen challenges, so we know what to compare to.
Typos: "miscallaneous", "challenges.."
Questions For Authors: I have no particular prioritization
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thanks for finding our work helpful. Your thorough review of the paper and suggestions has been helpful to clarify several details.
**Q1: What "main shell" means. Does this mean a connection to a Unix shell (e.g., bash)? Or does this mean an agent running a REACT loop?**
“Main shell” is a connection to a unix shell, specifically in our case it is a bash shell. We will clarify this in the revised paper.
**Q2: Fig 2: How does this demonstrate a session running in parallel with the main shell?**
In our setup, the agent always has access to the main shell, which is represented as `bash $-`. The interactive tool runs as a separate process in the environment and is displayed to the agent as a distinct line, labeled `(Interactive session …)`. The agent can interact with this parallel process through special interfaces, which are accessible from the main shell. These interfaces are described in detail in Table 7. In Figure 2, the agent demonstrates accessing the parallel process by using the `connect_sendline` interface to send a command to the FTP server. Then, the agent uses the `decompile` within the main shell to decompile a binary, while the FTP connection is still maintained. We will update the caption of Figure 2 to better reflect this interaction.
**Q3: Sec 2.2: What is the input to the summarizer?**
As outlined in Section 2.2, the input to the simple summarizer consists of the long observation, which is saved to a file and then opened using SWE-agent's file viewing interface. This allows the agent to view the first 100 lines, and the agent can then scroll or search through the file as needed. For the LM summarizer, the input includes the challenge context – the challenge's name, category, and the CTF problem text – as well as the last action performed by the main agent and its resulting output. More detailed information about all the prompts can be found in Appendix G, with the LM summarizer prompts specifically described in Appendix G.2.
**Q4: Sec 2.3: Demonstrations and guidelines details**
Each challenge category (crypto, rev, misc, web, forensics, pwn) has its own demonstration, where the crypto category has two demonstrations, while the other categories have one demonstration each. These demonstrations were selected randomly from the failed challenges in the development set. Specifically, we ran our agent without any demonstrations on the challenges in the development set, then we randomly selected failed challenges to include in the demonstrations and manually created successful trajectories to include as demonstrations. The guidelines, which were derived through trial and error from runs on the development set, are based on manual observations from failed attempts. We have a total of 9 general guidelines, along with 5 additional guidelines specifically for the debugger. All of these guidelines are provided in Appendix G.1, Figure 12 (Line 1516).
**Q5: Table 1: On what dataset is this measured?**
The results are aggregated results on all four benchmarks - NYU CTF, CyBench, InterCode-CTF and HTB.
**Q6: Table 2: I recommend showing Table 2 earlier, and moving Table 1 later.**
Thank you for pointing this out - we will change this in the revised paper for a more streamlined reading.
**Q7: Sec 4.1: Could we achieve a higher pass rate, if we halt the process after 20 steps (if it hasn't succeeded yet), reset everything, and restart a new?**
As our pass@1 results suggest, our agent succeeds fast and fails slow (Figure 4). The proposed suggestion to restart the trajectory after X steps, given our results, may be helpful as the agent is unlikely to succeed when it reaches an impasse in one trajectory. We leave this as a future research direction.
**Q8: Sec 4.1: The quantitative results don't support the claim that "Proper interactive interfaces are crucial".**
Thanks for the observation, we will change this to “Proper interactive interfaces enhance performance”.
**Q9: Sec 4.2: The criteria used to measure leakage, and whether the agent memorizes a solution approach from training data rather than the flag.**
The leakage issues are something that we address extensively in Section 4.2, using solution leakage quantification, uncovering soliloquizing phenomena which relates to solution approach leakage and by measuring our agent using new challenges released after training cutoff date of all of the models used in our evaluations. Please refer to reviewer FRVw, Q1.
**Q10: Sec 4.2, unseen challenges: It might help to mention which of the 4 datasets has the most similar distribution to the set of 21 unseen challenges, so we know what to compare to.**
Thanks for observing the missing information, please refer to reviewer FxPC, Q7.
**Q11: Typos: "miscallaneous", "challenges.."**
Thank you for catching the typos, we will fix these in the next version of the paper.
We hope to have addressed the concerns raised and will update the paper accordingly. We appreciate your thoughtful review.
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Rebuttal Comment 1.1:
Comment: Thank you for your response about data leakage. I had indeed missed that experiment, and I think it is responsive and helpful. I appreciate how you have dealt with data leakage; ruling out data leakage is very challenging, but I think the analysis here has done a good job of addressing the concern, or as good as is reasonably possible given the challenges in this area. I also appreciate the addition of detailed comparison to state-of-the-art schemes. I think that will further strengthen the paper. I continue to recommend accepting this paper.
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Reply to Comment 1.1.1:
Comment: We thank reviewer t5tU for their response and for finding the data leakage analysis and experiments helpful.
We will incorporate the valuable feedback raised during the rebuttal in the final version of the paper. | Summary: This paper presents EnIGMA, an LM agent designed for autonomously solving Capture The Flag (CTF) challenges.
- The authors introduce Interactive Agent Tools (IATs), which enable the LM agent to execute interactive cybersecurity tools such as debuggers and remote server connection utilities. These tools address key limitations in prior LM-based cybersecurity agents, which lacked the ability to use interactive command-line utilities.
- The authors evaluate EnIGMA on 390 CTF challenges across four benchmarks (NYU CTF, InterCode-CTF, CyBench, and a collected HackTheBox (HTB) dataset), reporting state-of-the-art performance on three of these benchmarks.
- Additionally, they introduce a method for quantifying data leakage and identify a novel phenomenon termed soliloquizing, where the LM hallucinates entire challenge solutions without environmental interactio
Claims And Evidence: - EnIGMA achieves state-of-the-art performance on multiple CTF benchmarks.
- The paper provides empirical results comparing EnIGMA to prior LM-based agents, showing significant improvements in solved challenges. However, it is unclear whether the performance gain is due to genuine advancements in reasoning or data leakage from training corpora.
Methods And Evaluation Criteria: The paper adopts CTF benchmarks to evaluate cybersecurity-focused LM agents, which is a reasonable choice for testing the agent’s practical problem-solving ability. However, the evaluation lacks sufficient details on dataset splits, agent hyperparameters, and exact experimental conditions.
Theoretical Claims: The paper does not introduce new theoretical foundations but instead focuses on empirical improvements through tool integration.
Experimental Designs Or Analyses: strengths:
- Ablation studies show that IATs, summarizers, and demonstrations contribute to performance improvements.
- Diverse benchmarks ensure broad evaluation across different cybersecurity challenges.
Weaknesses:
- Unclear statistical significance: The paper lacks confidence intervals or statistical tests to validate improvements.
- Data leakage analysis is incomplete: The authors attempt to quantify leakage but cannot verify whether training data contamination influenced results.
Supplementary Material: yes. the detail of methods
Relation To Broader Scientific Literature: The paper extends work on LM agents for cybersecurity by introducing interactive tools.
Essential References Not Discussed: no
Other Strengths And Weaknesses: strengths:
The integration of IATs for debugging and server interaction is a meaningful addition to LM agent capabilities.
weakness:
- The paper is difficult to follow, with unclear explanations of contributions and inconsistent structuring.
- The work is mostly engineering-driven rather than presenting new conceptual frameworks.
Other Comments Or Suggestions: see weakness
Questions For Authors: see weakness
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your interest in our research and the acknowledgment of IATs as a meaningful addition to LM agents. We greatly appreciate your feedback and insights which will help us improve our work. We’ve addressed your concerns below:
**Q1: Data leakage analysis is incomplete + It is unclear whether the performance gain is due to genuine advancements … or data leakage from training corpora.**
Addressing whether agents solve problems through reasoning or by relying on memorization remains a challenge in LM evaluations. Yet, we tackle this issue extensively (Section 4.2, Table 3 and Appendix E) by quantifying solution leakage where the flag is submitted without appearing in prior observations and by uncovering the soliloquizing phenomenon (hallucinated observations), which relates to data leakage of the solution approach (Figure 7).
Moreover, results on challenges released after the training cutoff of all models used in our evaluations (Section 4.2, Line 431) shows that EnIGMA is able to solve 2 out of 21 challenges that it *could not* have seen before. Combined with comparison between EnIGMA to other agents using the same LM versions (see reviewer FxPC, Q1) we can attribute EnIGMA’s performance gain to the novel agent improvements that we introduced in this work and not to solution leakage.
**Q2: The evaluation lacks sufficient details on dataset splits, agent hyperparameters, and exact experimental conditions.**
Our evaluation involves four test benchmarks: NYU CTF, CyBench, InterCode-CTF, and HTB, as well as a self-created development benchmark. We discuss each of these benchmarks in Section 3, and we provide further details on the benchmarks and experimental conditions in Appendices B and C, including the LM parameters (model versions, temperature, and nucleus sampling values). For the LM agent configuration, we outline the interfaces and environment used during evaluations in Appendix D, and we also provide all the prompts used in the evaluation in Appendix G. We adopted the default parameters from SWE-agent. Demonstrations were provided per challenge category: two for the crypto category, and one for each of the other categories. We appreciate your comment on this and will ensure this information is presented more clearly in the next version of our paper.
**Q3: Unclear statistical significance.**
We fully agree that measuring statistical significance is important. As you mentioned in the strengths, our ablation studies (Table 1) along with the analysis in Section 4.1 demonstrate that the performance improvements can be attributed to the IAT framework we introduced. Specifically, using these interactive tools, the agent solves challenges in an average of 11.5 turns, which is 22.8% faster than the 14.9 turns required when they are not used (p-value: 0.019). Combined with the results shown in Figure 4, which highlight that the agent is more likely to succeed quickly and fail slowly, we can claim the performance gain to the proposed interactive agent tools framework. We will incorporate this statistical analysis in the revised paper.
**Q5: The work is mostly engineering-driven rather than presenting new conceptual frameworks.**
Our primary contribution is the introduction of a novel agent for the cybersecurity domain, designed with specialized tools and interfaces that enhance its ability to solve CTF challenges.
We are the first to demonstrate how an agent can utilize ***interactive tools***, such as a debugger and a server connection tool. We developed the IATs framework to facilitate future research in enabling LM agents to use such tools (Section 2.1). These new tools allow EnIGMA to achieve state-of-the-art performance across three of the four benchmarks.
Lastly, we provide a comprehensive empirical analysis of the agent's behavior (Section 4), where we ***uncover the unexpected soliloquizing phenomenon***. This finding provides valuable insights that can inform the design and evaluation of future LM agents. We hope this clarifies the contributions of our work.
**Q6: The paper is difficult to follow, with unclear explanations of contributions and inconsistent structuring.**
We apologize for any confusion caused by the structure of the paper. Our contributions are outlined in both the introduction and conclusion, and as an answer to Q5 above. These contributions are elaborated in the relevant sections of the paper: Section 2 introduces our agent, including the IATs and summarizers; Section 3 details the development set and experimental setup; and Section 4 presents the empirical analysis including solution leakage and soliloquizing phenomenon. We are not sure what you mean by inconsistent structuring, and would be happy to remedy this if you briefly explain the concern.
We appreciate your insights once again and are committed to improving the clarity of the paper.
---
Rebuttal Comment 1.1:
Comment: Thanks for the response. I found many of my concerns have been addressed. I will update my final score! | null | null | null | null | null | null |
Q-VDiT: Towards Accurate Quantization and Distillation of Video-Generation Diffusion Transformers | Accept (poster) | Summary: This paper proposed a quantization method named Q-VDiT tailored specifically for video Diffusion Transformers. The proposed Q-VDiT aims to address severe model quantization information loss in video models. Specifically, the authors proposed Token-aware Quantization Estimator to compensate for quantization errors from both token and feature dimensions. Temporal Maintenance Distillation is used to optimize each frame from the perspective of the overall video. Extensive experiments demonstrate the superiority of the proposed Q-VDiT over baseline and other previous quantization methods.
Claims And Evidence: This paper claims that "Quantization can reduce storage requirements and accelerate inference by lowering the bit-width of model parameters. Yet, existing quantization methods for image generation models do not generalize well to video generation tasks.". The claims are supported by experimental results.
Methods And Evaluation Criteria: The authors proposed Token-aware Quantization Estimator to compensate for quantization errors from both token and feature dimensions. Temporal Maintenance Distillation is used to optimize each frame from the perspective of the overall video. Extensive experiments demonstrate the superiority of the proposed Q-VDiT over baseline and other previous quantization methods.
Theoretical Claims: Yes. Proof of Theorem 3.2 is reasonable.
Experimental Designs Or Analyses: Yes. Quantization Estimator to compensate for quantization errors from both token and feature dimensions. Temporal Maintenance Distillation is used to optimize each frame from the perspective of the overall video.
Supplementary Material: Yes. The demo video part.
Relation To Broader Scientific Literature: This paper proposed a quantization method named Q-VDiT tailored specifically for video Diffusion Transformers. The proposed Q-VDiT aims to address severe model quantization information loss in video models. Specifically, the authors proposed Token-aware Quantization Estimator to compensate for quantization errors from both token and feature dimensions. Temporal Maintenance Distillation is used to optimize each frame from the perspective of the overall video. Extensive experiments demonstrate the superiority of the proposed Q-VDiT over baseline and other previous quantization methods.
Essential References Not Discussed: No
Other Strengths And Weaknesses: Pros:
1. a quantization method named Q-VDiT tailored specifically for video Diffusion Transformers is proposed.
2. Token-aware Quantization Estimator is proposed to compensate for quantization errors from both token and feature dimensions.
3. Temporal Maintenance Distillation is used to optimize each frame from the perspective of the overall video
4. Experimental results verify the effectiveness of the proposed method.
Cons:
1. More optimization details of Temporal Maintenance Distillation should be included such as training data and resources.
2. The video demos generated by the proposed method, included in the supplementary material, show observed artifacts and temporal flicking, the authors should give some deeper explanations.
3. The original videos generated by the open-sora model are not displayed, and it seems that the proposed Quantization method can not preserve the performance of the original models.
Other Comments Or Suggestions: My major concern is the unsatisfied video generation performance.
Questions For Authors: Please refer to Weaknesses for more details.
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: We thank the reviewer for the constructive comments on our paper. Regarding the concerns, we provide the following responses.
> Q1: Optimization details.
Sorry for the misunderstanding, **we have reported optimization details including training data in Appendix Sec. B. and show the training cost in Tab. 4**. We will make this more prominent in revised version.
> Q2: Original videos.
We apologize for our negligence and we have released all original videos in [[https://anonymous.4open.science/r/Generated_videos]](https://anonymous.4open.science/r/Generated_videos-EB77). **We also have shown more generated critical video frames under W3A6 setting comparison with FP model in Appendix Sec. H. In W3A6 setting, current methods cannot even produce meaningful videos. Our method is significantly closer to FP in terms of generation quality than existing methods.**
> Q3: Some temporal flicking.
The OpenSora model we experimented in paper inevitably has some temporary flicking. But our method is significantly better than existing methods in terms of metrics (see Tab. 1 and Tab. 2) and closer to the FP model in terms of visual effects (see Fig. 5, Appendix Sec. H). **We further conducted W4A6 quantization experiments on larger models HunyuanVideo and CogVideoX, and demonstrated the generated video effects in [[https://anonymous.4open.science/r/Generated_videos]](https://anonymous.4open.science/r/Generated_videos-EB77). The videos we generate do not have issues such as temporary flicking and the visual quality is closer to the full precision model. We also has notable improvement compared to the baseline method ViDiT-Q.**
We also present quantitative comparisons in the table below：
|Model|Method|Imaging Quality($\uparrow$)|Aesthetic Quality($\uparrow$)|Overall Consistency($\uparrow$)|
|-|-|-|-|-|
|CogVideoX|FP|61.80|58.88|26.46|
|CogVideoX|ViDiT-Q|46.03|45.31|21.65|
|CogVideoX|**Ours**|**52.13**|**49.86**|**23.75**|
|Hunyuan|FP|62.30|62.49|26.85|
|Hunyuan|ViDiT-Q|52.28|55.25|24.81|
|Hunyuan|**Ours**|**57.42**|**57.04**|**25.49**|
Our method is closer to the FP model in terms of metrics and visual effects, and has a significant improvement compared to the baseline method ViDiT-Q.
> Q4: Performance of our quantized model compared with FP model.
**1. Some performance gap under lower bit setting.** We have reported the same higher bit setting (e.g. W6A6) with ViDiT-Q in Appendix Tab. 5 and our method can achieve lossless performance compared with FP model. Since the performance gap is minor in higher bit settings, we further explore the performance improvement on lower bit settings (e.g., W3A6). Under this low bit setting, we have achieved state-of-the-art and **significantly outperform existing methods and existing methods can hardly generate reasonable videos under low bit setting.** We show more visual comparison in Fig. 5 and Appendix Sec. H.
**2. Choice for mainly focus on lower bit.** Naturally, lower bit quantization brings more memory saving and acceleration for real-world deployment, but often faces more severe performance degradation which is a harder situation under exploration. Since existing methods like ViDiT-Q have achieved almost lossless performance at higher bits (e.g., W4A8), we want to further explore the performance improvement at lower bits. Compared to W4 quantization, W3 usually faces severe performance degradation which is commonly discovered in LLM quantization [1][2]. So we chose lower bit quantization settings (e.g., W3A6) in Tab. 1 and Tab. 2, under which existing methods can hardly generate reasonable videos as shown in Fig. 5. Our method has greatly improved in terms of metrics and visual effects compared to existing methods. **We want to note that we also reported same higher bit settings as ViDiT-Q in Appendix Tab. 5**, and our method still has improvement compared to existing methods and **achieves lossless**.
[1].GPTQ: Accurate Post-Training Quantization for Generative Pre-trained Transformers.
[2].Quarot: Outlier-free 4-bit inference in rotated llms.
**3. Main contribution.** We would like to further highlight our contribution by investigating the limitations of current quantization methods in video generation models and solving them from both quantization (Sec. 3.2) and optimization (Sec. 3.3) perspectives. With almost the same calibration cost with current methods (Tab. 4), our method brings significant relatively performance improvement at lower bit compared to existing methods in terms of metrics (Tab. 1 and Tab. 2) and visual effects (Fig. 5 and Appendix Sec. H) while maintaining lossless performance at higher bit (Appendix Tab. 5). Meanwhile, our method can bring 2.4x reduction in memory cost and 1.35x actual acceleration for inference (Appendix Tab. 7) with no extra burden compared with baseline ViDiT-Q. | Summary: This paper addresses the issue of information loss and misalignment of optimization objectives that arise when applying existing quantization methods to video generation models. Current quantization techniques, which are primarily designed for image generation models, may not be directly suitable for video generation due to the temporal dependencies inherent in videos. To address this challenge, the paper proposes a Token-aware Quantization Estimator (TQE) and a Token-aware Quantization Estimator (TQE). The former aims to reduce information loss by considering token-wise importance during quantization, while the latter focuses on minimizing the temporal distribution discrepancy between the full-precision model and the quantized model. Experimental results demonstrate that the proposed approach effectively mitigates information loss compared to existing quantization methods when applied to video generation models.
Claims And Evidence: yes
Methods And Evaluation Criteria: yes
Theoretical Claims: yes, the formulas and proofs seem correct.
Experimental Designs Or Analyses: yes, I have reviewed all the experiments presented in the paper, which are all necessary. However, the analysis of the experiments is not sufficiently detailed.
1. Although the proposed method outperforms state-of-the-art methods in terms of final generation metrics, it remains unclear whether the improvements genuinely stem from the reduction in quantization error or from other factors. Further analysis is needed to verify the source of the performance gains.
2. In the experiment, the paper mainly compares the video generation performance at different bit-widths but does not provide a thorough analysis of the acceleration effect or memory savings. This lack of evaluation makes it difficult to assess the actual efficiency improvements brought by the proposed method.
3. In Table.4, as ViDiT-Q is a calibration-free method, why does it still have training cost? In this table, it would be better to show the memory consumption of the full-precision and the fp16 models, which would help demonstrate the efficiency of the proposed method.
Supplementary Material: Yes, experiment details, additional experiments, and visualization results.
Relation To Broader Scientific Literature: Current quantization methods are primarily designed for image generation models, whereas the method proposed in this paper introduces a quantization approach specifically for compressing and accelerating video generation models.
Essential References Not Discussed: No
Other Strengths And Weaknesses: Strengths:
1. The writing in the paper is relatively clear, making it easy to follow the motivation and the proposed method.
2. The proposed method outperforms the state-of-the-art methods on public datasets. Additionally, the ablation study validates the effectiveness of each component.
Weaknesses:
please see the comments and questions in different sections.
Other Comments Or Suggestions: In Figure 2, some symbols or notations appear to be missing, which may affect the clarity and completeness of the illustration. It would be helpful to ensure all necessary symbols are properly displayed.
Questions For Authors: What similarity function is used in Eq. 9
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you very much for your high recognition of our work and the valuable suggestions you provided. Our response is as follows:
> Q1: Quantitative analysis on quantization error.
We add quantitative experiments on W3A6 model last layer weight's quantization error and information entropy mentioned in the proposed TQE (Sec. 3.2)：
|Method|Quantization Error($\downarrow$)|Entropy($\uparrow$)|VQA-Aesthetic($\uparrow$)|
|-|-|-|-|
|FP|-|6.98|66.91|
|ViDiT-Q|73.7|4.46|39.82|
|**Ours**|**56.0**|**5.49**|**53.53**|
**Consistent with our claim, our method indeed reduces quantization errors and improves the information entropy of the quantized weights.** From quantitative metrics, TQE has indeed improved the performance of the model by reducing quantization error and increasing entropy. Theorem 3.2 states that the quantization error of weights has lower information entropy compared to the original weights. This is also proved by the quantitative results.
> Q2: Actual inference efficiency and memory consumption.
We have reported the inference efficiency of W4A8 model compared with FP model in Appendix Tab. 7. We also display the data here.
|Method|Memory Cost($\downarrow$)|Latency Cost($\downarrow$)|VQA-Aesthetic($\uparrow$)|VQA-Technical($\uparrow$)|
|-|-|-|-|-|
|FP|10.9G|51.3s|66.91|53.49|
|**Ours**|**4.5G (2.4$\times$)**|**38.0s (1.35$\times$)**|**71.32**|**55.56**|
Compared to FP model, our method achieves complete lossless performance while bringing 2.4$\times$ reduction in memory cost and 1.35$\times$ inference acceleration. In the revised version, we will modify our layout to make this more prominent.
> Q3: In Tab. 4, why ViDiT-Q has training cost?
ViDiT-Q requires calculating quantization sensitivity between layers to allocate different bit-widths, which incurs additional time consumption. This is also reported in their paper. We will modify our wording to avoid ambiguity.
> Q4: Fig.2 misses some notations.
We will fix the problem in the final version.
> Q5: Similarity function used in Eq. 9.
We use cosine similarity. | Summary: The paper introduces Q-VDiT, a quantization framework for video DiT to reduce computational complexity while preserving video quality. It addresses two key challenges: quantization error compensation through a Token-aware Quantization Estimator (TQE) and spatiotemporal consistency via Temporal Maintenance Distillation (TMD).
## update after rebuttal
Thanks to the authors for addressing my concerns and providing additional results. I will keep my score. The videos on Hunyuan/opensora look great.
Claims And Evidence: The statement that existing approaches fail to calibrate quantization from a video-wide perspective, leading to degraded video quality is too strong. ViDiT-Q does incorporate video tokens and reports results on video datasets, making it inaccurate to claim that it does not consider the entire video. The distinction should focus on how Q-VDiT improves over ViDiT-Q rather than dismissing prior work outright.
Methods And Evaluation Criteria: The Token-aware Quantization Estimator (TQE) is introduced to approximate quantization errors across two orthogonal dimensions: token and feature space. However, its quantization error reduction is not directly evaluated. While Figure 3 provides an example and Table 3 includes an ablation study, the effectiveness of TQE in minimizing quantization error remains unclear. A more explicit quantitative evaluation of the error reduction would strengthen the argument.
Theoretical Claims: Proposition 3.1 and Theorem 3.2 establish that quantized weights retain less information entropy than the original weights. However, the link between this theoretical result and the practical benefits of TQE is not clearly articulated. It remains unclear which specific error terms TQE reduces and by how much. Providing quantitative results on TQE’s impact on entropy reduction would help substantiate its contribution.
Experimental Designs Or Analyses: - The paper adopts a different quantization setting from ViDiT-Q but lacks a clear justification. The claim that "we mainly focus on harder settings" does not sufficiently explain the reasoning behind the choice. Further insights into why these settings are chosen, particularly regarding their relevance to real-world deployment and model robustness, would improve the clarity of the paper.
- The paper does not explicitly discuss the performance gap between W3A8 and W4A8 (in ViDiT-Q). Given the significant differences in VBench scores between this paper and ViDiT-Q, a more detailed comparison is necessary. Clarifying whether W3A8 introduces substantial quality degradation compared to W4A8 would help readers interpret the reported results.
Supplementary Material: Yes, videos
Relation To Broader Scientific Literature: not related
Essential References Not Discussed: n/a
Other Strengths And Weaknesses: n/a
Other Comments Or Suggestions: n/a
Questions For Authors: - why the generated videos exhibit low motion dynamics? Do we observe this before using quantization?
- The paper does not evaluate on larger video generation models, such as Hunyuan (https://github.com/Tencent/HunyuanVideo), why? The results could be more meaningful on these SOTA models.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your detailed review of our work. Here are our responses to your concerns:
> Q1: Statement of our Q-VDiT.
We apologize for the misunderstanding caused by our statement. **We absolutely do not deny ViDiT-Q's contribution. ViDiT-Q is the first method to explore quantization for video generation models and an important baseline method for our paper. We greatly appreciate the contribution of ViDiT-Q.** What the statement wants to emphasize is that we hope to consider the correlation between different frames in the video information during the optimization process and further improve the quality of the quantized video generation model. We will modify our wording in the revised version to avoid this ambiguity.
> Q2: Quantitative analysis on quantization error and information entropy introduced in TQE.
We add quantitative experiments on W3A6 model last layer weight's quantization error and information entropy mentioned in the proposed TQE (Sec. 3.2)：
|Method|Quantization Error($\downarrow$)|Weight Entropy($\uparrow$)|VQA-Aesthetic($\uparrow$)|
|-|-|-|-|
|FP|-|6.98|66.91|
|ViDiT-Q|73.7|4.46|39.82|
|**Ours**|**56.0**|**5.49**|**53.53**|
**Consistent with our claim, our method indeed reduces quantization errors and improves the information entropy of the quantized weights.** From quantitative metrics, TQE has indeed improved the performance of the model by reducing quantization error and increasing entropy. Theorem 3.2 states that the quantization error of weights has lower information entropy compared to the original weights. This is also proved by the quantitative results.
> Q3: Explanation of quantization settings.
Naturally, lower bit quantization brings more memory saving and acceleration for real-world deployment, but often faces more severe performance degradation, which is a harder situation under exploration. Since existing methods like ViDiT-Q have achieved almost lossless performance at higher bits (e.g., W4A8), we want to further explore the performance improvement at lower bits. Compared to W4 quantization, W3 usually faces severe performance degradation, which is commonly discovered in LLM quantization [1][2]. So we chose lower bit quantization settings (e.g., W3A6) in Tab. 1 and Tab. 2, under which existing methods can hardly generate reasonable videos as shown in Fig. 5. Our method has greatly improved in terms of metrics and visual effects compared to existing methods. **We want to note that we also reported the same higher bit settings as ViDiT-Q in Appendix Tab. 5**, and our method still has improvement compared to existing methods and **achieves lossless**.
[1].GPTQ: Accurate Post-Training Quantization for Generative Pre-trained Transformers.
[2].Quarot: Outlier-free 4-bit inference in rotated llms.
> Q4: Performance gap between W3A8 and W4A8.
Compared to W4, the significant loss of weight information in W3 (only 2\**3=8 representation candidates for a single value) leads to a serious performance degradation as we discussed in Q3. This also highlights the importance of our proposed TQE in compensating for the weight quantization errors. **Our method outperforms current quantization methods in both W3 and W4 (Tab. 1 and Tab. 2)**.
> Q5: Motion dynamics before and after quantization.
Existing methods like ViDiT-Q have also found that the quantized model exhibits a certain degree of dynamic decline. We can also see from the metrics Motion Smoothness and Dynamic Degree in Tab. 1 that this is particularly severe after W3 quantization. **Our method has the same level of motion dynamics as the full precision model in terms of metrics**, which can be seen from the Motion Smoothness and Dynamic Degree metrics in Tab. 1. And our method also shows significant improvement in dynamics compared to existing methods. More generated videos in [[https://anonymous.4open.science/r/Generated_videos]](https://anonymous.4open.science/r/Generated_videos-EB77) also prove the dynamic retention ability of our method at the same level as the FP model.
> Q6: Evaluation on larger video generation models.
We add W4A6 quantization experiment on larger SOTA models CogVideoX-5B and HunyuanVideo-13B:
|Model|Method|Imaging Quality($\uparrow$)|Aesthetic Quality($\uparrow$)|Overall Consistency($\uparrow$)|
|-|-|-|-|-|
|CogVideoX|FP|61.80|58.88|26.46|
|CogVideoX|ViDiT-Q|46.03|45.31|21.65|
|CogVideoX|**Ours**|**52.13**|**49.86**|**23.75**|
|Hunyuan|FP|62.30|62.49|26.85|
|Hunyuan|ViDiT-Q|52.28|55.25|24.81|
|Hunyuan|**Ours**|**57.42**|**57.04**|**25.49**|
**We also provide more generated video comparisons in [[https://anonymous.4open.science/r/Generated_videos]](https://anonymous.4open.science/r/Generated_videos-EB77). Our method is closer to the FP model in terms of metrics and visual effects, and has notable improvement compared to the baseline method ViDiT-Q.** | Summary: Diffusion transformers (DiT) are powerful for video generation but face deployment challenges due to large parameter sizes and high computational complexity. To tackle the issues of information loss and mismatched objectives during quantization, the authors propose Q-VDiT, introducing the Token aware Quantization Estimator (TQE) to mitigate quantization errors and the Temporal Maintenance Distillation (TMD) to preserve spatiotemporal correlations across frames. Their W3A6 Q-VDiT achieves a scene consistency score of 23.40, surpassing current state-of-the-art quantization methods by 1.9.
Claims And Evidence: Yes. The claims are supported by clear and convincing evidence.
Methods And Evaluation Criteria: Make lots of sense but missing some love level comparisons.
Theoretical Claims: Yes, I have checked the proofs for theoretical claim regarding all equations.
Experimental Designs Or Analyses: Yes, I verified that the experimental designs and analyses were sound. The main findings rely on high-level metrics.
Supplementary Material: Yes. I checked the video resutls and codes.
Relation To Broader Scientific Literature: The paper makes a valuable contribution to the field of video generation by addressing the issue of large, slow models, and demonstrating how quantization can significantly speed up inference.
Essential References Not Discussed: NA
Other Strengths And Weaknesses: Strengths:
The idea is both good and novel.
The quantitative results are notably strong.
The writing is easy to follow.
Weaknesses:
The supplementary material does not show the original model’s qualitative results, and overall quality does not seem improved compared to other methods.
Although the high-level metrics are strong, the presented video exhibits noticeable blurriness; reporting additional lower-level metrics (e.g., FVD) could provide a more comprehensive evaluation.
Inference speed comparisons are missing, making it difficult to assess practical efficiency.
The motivation for concatenating each frame with all frames for temporal distillation is unclear, especially given potential alternatives (e.g., temporal differences).
Other Comments Or Suggestions: NA
Questions For Authors: Please see above parts
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for reviewing our manuscript and providing valuable suggestions. Here are our responses to some of the concerns you raised:
> Q1: Original model’s qualitative results.
We apologize for our negligence and we have released all original videos in [[https://anonymous.4open.science/r/Generated_videos]](https://anonymous.4open.science/r/Generated_videos-EB77). We have also shown more generated critical video frames under W3A6 setting comparison with FP model in Appendix Sec. H. In W3A6 setting, current methods cannot even produce meaningful videos. Our method is significantly closer to FP model in terms of generation quality than existing methods.
> Q2: Overall quality improvement.
We have reported the same higher bit setting (e.g. W6A6) with ViDiT-Q in Appendix Tab. 5 and our method can achieve lossless performance compared with FP model. Since the performance gap is minor in higher bit settings, we further explore the performance improvement on lower bit settings (e.g., W3A6). Under this low bit setting, we have achieved state-of-the-art and **significantly outperform existing methods and existing methods can hardly generate reasonable videos under low bit setting.** We show more visual comparison in Fig. 5 and Appendix Sec. H.
**We further conducted W4A6 quantization experiments on larger models HunyuanVideo and CogVideoX, and demonstrated the generated video effects in [[https://anonymous.4open.science/r/Generated_videos]](https://anonymous.4open.science/r/Generated_videos-EB77)**. The visual quality of our method is closer to the full precision model. We obtained better results than baseline method ViDiT-Q.
We also present quantitative comparisons in the table below：
|Model|Method|Imaging Quality($\uparrow$)|Aesthetic Quality($\uparrow$)|Overall Consistency($\uparrow$)|
|-|-|-|-|-|
|CogVideoX|FP|61.80|58.88|26.46|
|CogVideoX|ViDiT-Q|46.03|45.31|21.65|
|CogVideoX|**Ours**|**52.13**|**49.86**|**23.75**|
|Hunyuan|FP|62.30|62.49|26.85|
|Hunyuan|ViDiT-Q|52.28|55.25|24.81|
|Hunyuan|**Ours**|**57.42**|**57.04**|**25.49**|
Our method is closer to the FP model in terms of metrics and visual effects, and has a significant improvement compared to the baseline method ViDiT-Q.
> Q3: Additional lower-level metrics (e.g., FVD).
We have reported FVD on UCF-101 dataset in Appendix Tab. 6. We also report FVD on OpenSORA prompt set used in Tab. 1 and Tab. 2:
|Method|Bit|FVD($\downarrow$)|VQA-Aesthetic($\uparrow$)|
|-|-|-|-|
|FP|16|101.9|66.91|
|ViDiT-Q|W4A6|132.6|54.66|
|**Ours**|W4A6|**103.6**|**67.05**|
|ViDiT-Q|W3A6|251.8|39.82|
|**Ours**|W3A6|**191.1**|**53.53**|
Compared to baseline method ViDiT-Q, our method achieved lower FVD, demonstrating the consistent superiority of our method on both high and low level metrics.
> Q4: Inference speed comparison.
We have reported the inference efficiency of W4A8 model compared with FP model in Appendix Tab. 7. We also display the data here.
|Method|Memory Cost($\downarrow$)|Latency Cost($\downarrow$)|VQA-Aesthetic($\uparrow$)|VQA-Technical($\uparrow$)|
|-|-|-|-|-|
|FP|10.9G|51.3s|66.91|53.49|
|**Ours**|**4.5G (2.4$\times$)**|**38.0s (1.35$\times$)**|**71.32**|**55.56**|
Compared to FP model, our method achieves complete lossless performance while bringing 2.4$\times$ reduction in memory cost and 1.35$\times$ inference acceleration. In the revised version, we will modify our layout to make this more prominent.
> Q5: Motivation for temporal distillation.
We quantitatively compare our distillation method with temporal differences:
|Method|VQA-Aesthetic($\uparrow$)|VQA-Technical($\uparrow$)|
|-|-|-|
|No distillation|45.67|38.42|
|Temporal differences|46.15|53.81|
|**Ours**|**54.92**|**61.59**|
As we discussed in Sec. 3.3, our motivation is **to perceive the inter-frame information of the whole video in distillation process. We hope to consider the overall information of the video while optimizing single frame information.** But direct MSE calculates different frame information separately as shown in Eq. 12. Although temporal differences can improve performance to some extent, our method achieved better results. **Concatenating all frames together can directly model the information of different frames in the whole video, which actually includes temporal differences between frames.** Our method can directly model the relationship matrix between all frames instead of simply the gap between two frames, so it can capture the global optimization information of the video well and achieve better performance.
---
Rebuttal Comment 1.1:
Comment: Thanks for addressing my concerns and for raising my score. The newly added visual comparisons are clear and significantly enhance the contribution of paper. It would be great to include comparisons with additional models—especially visual ones—in the main paper, although this might require major revisions.
---
Reply to Comment 1.1.1:
Comment: Dear reviewer,
We sincerely appreciate your time and constructive feedback throughout the review process. We are delighted to hear that our rebuttal has addressed your concerns and that you now recommend acceptance. Your insightful comments have significantly strengthened our paper, and we are grateful for your valuable contribution to improving our work. We will include comparisons with additional models during rebuttal in the revised version.
Best wishes,
All authors | null | null | null | null | null | null |
Reinforced Learning Explicit Circuit Representations for Quantum State Characterization from Local Measurements | Accept (poster) | Summary: The paper introduces a novel approach termed "explicit circuit representations" for quantum state characterization. Unlike traditional implicit representations, this method allows for direct experimental reconstruction of quantum states. The representations are designed to predict quantum properties accurately based on local measurement data alone. A reinforcement learning-based framework called QCrep is developed to learn these explicit circuit representations. QCrep relies on a local fidelity-based reward function to train an agent, circumventing the barren plateau problem common in gradient-based quantum optimization. The framework uses a Transformer-based measurement feature aggregation block to capture global features of quantum states from local measurements.
Claims And Evidence: 1.The claim regarding local and global fidelity is well supported by rigorous proof.
2.The effectiveness of the proposed representation is well supported by numerics.
Methods And Evaluation Criteria: Yes.
Theoretical Claims: Yes, i have checked the correctness of the proof in appendix, i.e. Proposition 2.1.
Experimental Designs Or Analyses: I have checked all the experimental designs and they are the main way to validate their proposed framework.
Supplementary Material: There is no supplementary material submission for this work.
Relation To Broader Scientific Literature: The application of reinforcement learning to the quantum problem (tomography) falls within the scoop of AI for Science.
Essential References Not Discussed: I think the related works are all currently disussed in the paper.
Other Strengths And Weaknesses: Strengths:
1. The authors introduce local fidelities as reward function, resulting in polynomial sample complexity and claim to mitigate barren plateau.
2. The authors bound the global fidelity well with averaged local fidelity, giving rise to a theoretical guarantee for the RL-based optimization.
Weaknesses/Suggestions are listed below.
Other Comments Or Suggestions: 1. Obviously, the tables and plots are too small, and hard to read the content inside, which significantly affect the quality of this submission.
2. The structure of the paper is not outlined well, e.g., the Discussion section reads like an extension to the former Experiment section.
3. It is claimed that measuring local observables can mitigate BP; however, this is only supported by a single numerical experiment, with no rigorous proof quantifying the extent of its effectiveness. Moreover, the proposed mitigation approach appears to align with the method described in [1], making the result unsurprising.
[1]. Cerezo, Marco, et al. "Cost function dependent barren plateaus in shallow parametrized quantum circuits." Nature communications 12.1 (2021): 1791.
Questions For Authors: 1. From what it is shown in Figure 1., QCrep framework is a strategy using RL-based method for choosing an appropriate ansatz for quantum state learning (or decoding) at each layer, it looks like an architecture search optimization problem, what’s the core advantage of using transformer-based layers in learning the local measurement data? What’s the sample complexity of the local measurement?
2. When using many-body Hamiltonian for learning task, how is the generalization ability of QCrep in learning the circuit representations in the region of critical behaviors?
3. Several confusions are raised in the comparison of ising model’s evolution. In section 3.2, the time-evolution parameter notation t overlaps the learning step t in the QCrep. And the authors said: “To exhibit the results, we average the performance on different parameters g for each evolution time t.”, is it meaning that QCrep treat the states with different ‘g’ and ‘t’ are notations ‘s’ from the set S, then the framework will learn the circuit representation for each ‘s’, resulting in storing V_{s,t} for them? What is the trotter step when showing first-order Trotter-Suzuki decomposition in Figure 3(b), and what’s the global fidelities of first-order trotter decomposition state?
4. It is with particular interesting to learn a quantum stabilizer codes and their decoding process to respective logical codes. Can QCrep learn the decoding process efficiently? For example, take 5-qubit stabilizer code as training set, how many steps do QCrep need to approximate a perfect decoder?
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: **1. Suggestion 1. Refinement of tables and plots.**
To improve readability, we will refine the tables and figures by moving the legends to the top or embedding them within the figures and abbreviating some metrics in tables. The figures in current paper is in PDF format thus can be scaled larger without loss of resolution.
**2. Suggestion 2. Refinement of the Discussion section.**
The discussion section primarily focuses on evaluating the scalability of our method in more challenging scenarios. The experiments presented in this section shows potential challenges and solutions. We will refine this section by clarifying the topic of discussion and incorporating an exploration of the practical adaptation of our method.
**3. Suggestion 3. Proof on mitigating BP.**
We would like to highlight that our proposed approach is not specifically targeting on mitigating BP, but state characterization (also not tomography). Our main focus is generating circuits for target family of states **locally**, which allows for computing the properties via measuring the output states, and for handling downstream tasks by directly decoding the learned representations without touching the underlying states.
*Therefore, even though the result seems not surprising, it doesn't affect our contribution. In turn, the prior works have provided rigorous guarantee on on mitigating BP with local cost function, which empowers the effectiveness of our reward.* Local cost function has guaranteed trainability for larger systems [1–3]. However, **good trainability does not directly imply good global fidelity and the relation between local cost function and global fidelity remains unclear from the prior works**. Hence, we leverage the advantage of local cost function to design our reward for characterizing large scale quantum systems, and further show how global fidelity can be lower-bounded when the agent learns high local fidelity. Additionally, beyond the numerical experiment we present to demonstrate the mitigation of BP, our extraordinary performance in scaling to much larger systems (e.g., 50 qubits) compared to gradient-based methods also indirectly supports the mitigation of BP.
[1] Sack et al. "Avoiding barren plateaus using classical shadows." PRX Quantum 3.2 (2022): 020365.
[2] Uvarov, A. V., and Jacob D. Biamonte. "On barren plateaus and cost function locality in variational quantum algorithms." Journal of Physics A: Mathematical and Theoretical 54.24 (2021): 245301.
[3] Cerezo, et al. "Cost function dependent barren plateaus in shallow parametrized quantum circuits." Nature communications 12.1 (2021): 1791.
**4. Q1. The advantage of transformer. The sample complexity of local measurement.**
For the advantage of transformer, please refer to the reply 2 to reviewer 9UgW.
A key advantage of our framework over architecture search is that it requires no gradient computation with respect to the circuit parameters, thus can explore more regions during optimization. This feature ensures robustness against noise (see Appendix G), and is natural suitable for tensor network backend, which can simulation large-scale quantum systems. The back-prop from SVD layer is ill-defined when containing zero or repeated singular values if using gradient-based optimizer.
Regarding sample complexity, please refer to Appendix F, and the reply 2 to Reviewer 5m67.
**5. Q2. The generalization ability in the region of critical behaviors for many-body Hamiltonian task.**
To the best of our knowledge, accurately characterizing quantum states in critical region is an open problem of quantum state learning and is not the target of our approach. We use DMRG to simulate many-body ground states, which cannot approximate the real ground state well in the phase transition region. Nonetheless, our method could provide a means to detect phase transition by comparing the fidelity between the reconstructed state and the actual ground state.
**6. Q3. Clarification on the comparison of Ising evolution.**
Your understanding is absolutely correct. There's a misuse of notation of $t$ and we will correct this in a revised version. The trotter step is set to 0.1, as demonstrated in Appendix E. We compare the state fidelity between the learned state and first order trotter decomposed state as shown in Figure 3 (a) and Table 3, where the trotter decomposed state is can approximate the actual evolved state with error rate within 1e-6, but is less efficient if small error is allowed.
**7. Q4. Learning quantum stabilizer codes.**
This is a very interesting topic. However, we note that for a QEC decoder, the output varies according to the input, which is not a quantum state characterization task. It is not compatible with our framework that maps a family of states towards a single state. Extending our framework to support quantum channel characterization could be important yet non-trivial during the short period of rebuttal and we would leave this for future work. | Summary: The paper uses a deep reinforcement learning algorithm to construct quantum circuits in a manner that avoids barren plateaus by not requiring gradients with respect to the circuit parameters. The approach appears to outperform alternative approaches, including VQE and QAQA.
A nice addition to the work is the use of a transformer architecture that the authors explicitly tie to the modelling of entanglement between qubits in the circuit. Further, as the circuit is built from local rewards, it appears that the algorithm is scalable.
## Update after rebuttal
I was happy to see the rebuttal from the authors and was happy to raise my score. I am confident that the authors will update the relevant parts of the manuscript and it will make a great contribution to the conference.
Claims And Evidence: The claims the authors wish to explore are well validated. They demonstrate that their algorithm works and, under certain conditions, outperforms alternative approaches.
Methods And Evaluation Criteria: It would be more convincing if the authors discussed/demonstrated scaling to larger circuits or perhaps, more complex problems. However, the chosen benchmarks are relevant.
Theoretical Claims: There are not many/any theoretical claims made in this manuscript.
Experimental Designs Or Analyses: I had no issue with the experimental design or analysis.
Supplementary Material: The supplementary material was complete and useful.
Relation To Broader Scientific Literature: The approach to building quantum circuits using reinforcement learning is becoming more popular, so this paper aligns well with the emerging field. Further, using transformer architectures to encode entanglement is a novel concept.
Essential References Not Discussed: I am not familiar enough with the specific literature to discuss whether essential literature is complete. However, the authors do have a comprehensive state-of-the-art and related work section in both the main manuscript and the supplementary information.
Other Strengths And Weaknesses: The idea is novel and interesting to the broader community. A possible weakness is the extension to more complex problems but, possibly more importantly, larger circuits. Further, the claims regarding capturing of entanglement were not well validated. Would a simpler architecture have sufficed?
Other Comments Or Suggestions: Some of the figures were quite small, 6 and 7 in particular.
Questions For Authors: 1. Can you validate that the transformer architecture is a benefit here? Was there enough data to truly use this complexity and is there any way to explore the capturing of entanglement or correlation effects after training?
2. Can you scale this arbitrarily to large circuit and expect good fidelity?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: **1. Suggestion 1. Refinement of figures.**
We will adjust the legend position and font size. Current figures are in PDF format and can be enlarged without loss of resolution.
**2. Q1. Benefits of transformer architecture. Capture of entanglement.**
Compared to simpler architecture like MLP, the transformer in our framework has two main advantages: 1. It allows for capturing entanglement (long-term relation in the measurement data) **without increasing the number of parameters** of the neural network. 2. It enables transfer learning ability to different system sizes. We did further ablation study on learning 50-qubit Ising model to validate our claim. First, we use MLP to replace the transformer block. The input data is flattened and fed into MLP with $49\times 9$ input neurons, which increases with the system size unlike the transformer that is size-agnostic. Note that this formulation doesn't directly allow transfer to a different system size since the architecture is fixed. Second, we perform zero-shot transfer learning of this MLP-based to 10-qubit system, by concatenating 0 to the measurement data. The table below records the performance.
| Model | Local | Global |
| ---------------------- | ------------------- | ------------------- |
| Transformer | 0.9986 $\pm$ 0.0003 | 0.9673 $\pm$ 0.0083 |
| Transformer (transfer) | 0.9876 $\pm$ 0.0032 | 0.9391 $\pm$ 0.0160 |
| MLP-fix | 0.9985 $\pm$ 0.0002 | 0.9560 $\pm$ 0.0041 |
| MLP-fix (transfer) | 0.7311 $\pm$ 0.0271 | 0.1617 $\pm$ 0.0456 |
The local fidelity learned by transformer and MLP are essentially the same, but for global fidelity, transformer outperforms MLP. This reveals that **transformer is better at modeling the correlation in measurement data compared to MLP**. More importantly, transformer enables flexible transferability to quantum system of different sizes.
For architectural complexity, we highlight that our transformer encoder is relatively shallow. It has 2 blocks, each of which contains one 4-head MHA layer and the embedding dimension is only 128. Thus, the architecture is not complex compared with modern LLM. We just utilize its self-attention mechanism, a benefit for modeling quantum data as shown above. More implementation details can be found in the reply 2 to Reviewer cAXj.
**3. Q2. Scalability to larger circuits.**
It's hard to guarantee the scalability to arbitrary large circuit with good global fidelity. Consider a simple case, where your goal is to learn a product state $\bigotimes_{i=1}^n|\psi_i\rangle$. The agent learns to construct a circuit that maps this product state to $|0\rangle^{\otimes n}$ by maximizing the global fidelity, computed as $F=\prod_i |\langle\psi_i|0\rangle|^2$. Suppose the agent is good enough to fit every local term $|\langle\psi_i|0\rangle|^2$ up to accuracy $1-\epsilon$. The total accuracy of $F$ is $(1-\epsilon)^n$, which decays exponentially with the system size. Intuitively, **the difficulty of maintaining good global fidelity would exponentially increase with the system size, even for learning such easy product states**. Nevertheless, in our experiment, we have shown that for learning states like Ising ground states, the performance of zero-shot transfer learning on 70 and 100 qubit systems **remains stable**, as shown in Figure 3(c) and Figure 4(b). This indicates that the agent can capture some underlying pattern of the quantum system that is transferable to another scale, thus we can expect a promising fidelity on relatively large system.
We further did experiments on learning 120 and 150 qubit Ising model. The following table records the results of local and global fidelity.
| System size | Local | Global |
| ----------- | ------------------- | ------------------- |
| 120 | 0.9985 $\pm$ 0.0006 | 0.9180 $\pm$ 0.0333 |
| 150 | 0.9984 $\pm$ 0.0007 | 0.8927 $\pm$ 0.0446 |
This shows that even though the fidelity drops with the increase of system size, it doesn't show an exponential degrade, validating the effectiveness of our model.
**4. W1. Extension to more complex problems.**
In the following experiment, we consider learning 50-qubit random rotated maximally entangled states (GHZ), where the reduced density matrices are maximally mixed states. The agent has freedom to choose to apply Hadamard, CNOT and $R_z(\theta)$ where $-\pi / 4 < \theta < \pi / 4$. The table below shows the local and global fidelity between the reconstructed and target state.
| Local | Global |
| ------------------- | ------------------- |
| 0.9927 $\pm$ 0.0151 | 0.9275 $\pm$ 0.1511 |
We can see that **although the states are maximally entangled, the agent can still successfully reconstruct them using the local fidelity reward function if choosing an appropriate action space**. This again highlights the flexibility and applicability of our framework.
---
Rebuttal Comment 1.1:
Comment: I thank the authors for their comments. I found the results on transferability quite interesting and certainly in favor of the transformers. I would be curious to see how graph networks handled the problem also using attention. In general though, this feedback was helpful. I will raise my score to an accept. | Summary: This work develops explicit quantum state representations by generating surrogate preparation circuits through reinforcement learning. The approach uses a local fidelity reward function and a quantum measurement feature aggregation block that extracts global features from local measurement data. The paper attempts to establish theoretical analysis of the relationship between local approximation and global fidelity. Experiments demonstrate successful learning of special classes of quantum states up to 100 qubits.
Claims And Evidence: The claims and evidence are basically fine. One concern is about the implementation of the algorithm, as the loss function involves calculation of the fidelity function of density matrices, which is difficult to estimate. The impact of samples and their inaccurate estimation on the overall method is unclear.
Methods And Evaluation Criteria: The methods and evaluation criteria are less convincing due to insufficient description of the algorithm details, circuit ansatz, sample cost, and input assumptions.
Theoretical Claims: There are no major proofs.
Experimental Designs Or Analyses: The experimental design does not provide sufficient evidence to show whether the method is practical and efficiently implementable for near-term quantum computers.
Supplementary Material: The supplementary material is not checked in details.
Relation To Broader Scientific Literature: The relation to broader scientific literature is basically reasonable.
Essential References Not Discussed: The reference is reasonable.
Other Strengths And Weaknesses: The work shows an interesting attempt for learning quantum states. But I have some concerns:
1. The algorithm relies on fidelity calculations of density matrices, which are difficult to estimate accurately. As this is a key subroutine, the accuracy vs. sample cost of fidelity needs more analysis. A more careful analysis concerning the whole implementation is needed.
2. When reading the paper, I feel that I need clearer details on the algorithm specifics, circuit ansatz design, optimization, sample complexity, and input requirements or assumptions.
3. For the large-scale solution, the work lacks rigorous proofs to support its claims and theoretical analysis.
4. Experimental results don't sufficiently demonstrate the method's practicality or efficient implementation on near-term quantum hardware.
5. It would be better to provide the detailed methodology of numerical simulations for the experimental part.
Other Comments Or Suggestions: The comments are shown above.
Questions For Authors: 1. How does your algorithm handle the accuracy-sample cost tradeoff when estimating density matrix fidelity, and what analysis have you done to validate its practical implementation?
2. Could you provide more specific details about your algorithm implementation, circuit ansatz design, optimization procedure, sample complexity requirements, and the input assumptions your method makes?
3. What rigorous proofs support your theoretical claims, particularly for the large-scale quantum state learning solution you propose?
4. What evidence demonstrates that your method is practical and efficiently implementable on near-term or future quantum hardware?
5. Can you elaborate on the detailed methodology used for your numerical simulations (up to which level) in the experimental section?
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: **1. W1 & Q1. The accuracy-sample cost tradeoff, estimation of density matrix fidelity.**
The impact of finite sampling (inaccurate expectation value estimation) to the accuracy has been discussed in Appendix G1.
We would like to clarify that while estimating density matrix fidelity is difficult in general, our framework ensures accurate and efficient estimations due to following reasons:
(1) In our framework, instead of evolving the product state 0 towards the target state, we construct circuits to evolve the target state to 0. The two approaches are equivalent because quantum gates are invertible, but our approach only needs to estimate the **local** fidelity between an arbitrary state (density matrix) and 0. This can be done efficiently because it only requires measuring Pauli Z observables.
(2) We only need to compute the local fidelity rather than global fidelity as the reward function for training, which can be estimated by applying local Pauli Z operators to the output state, demonstrating the practical implementation of our framework.
**2. W2 & Q2 & Q5. More implementation details.**
(1) For the **algorithm implementation**, the policy network of the agent contains a 2-layer 4-head Transformer encoder with hidden dimension 128. The positional encoding follows the standard procedure in [1]. The final MLP has 3 linear layers with ReLU activation, and the feature dimension is 512.
(2) The **circuit ansatz design** has been detailed in section 2.3 and section 3, the circuit layout is brickwork shown in Figure 1.
(3) The **input assumptions** to the network has been discussed in section 2.2, where we exclusively measure expectation values of two-local Pauli observables, i.e., XX, XY, YX, YY, YZ, ZX, ZY, ZZ. The impact of inaccurate measurement is discussed in Appendix G1, showing that 1024 measurement shots is enough to obtain a relevantly accurate estimation of expectation values and attain no degrade of performance.
(4) To **optimize** the policy network, we use Adam optimizer with learning rate 0.001. We use stable baselines3 [2] for the implementation of PPO. The batch size is set to 1000. We set a cutoff KL divergence 0.05 between two updates of the network to enhance training stability.
(5) The **numerical simulation details**, including the Tensor Network simulation of quantum systems, and the resource requirement for training and inference are presented in Appendix E and F.
[1] Vaswani, Ashish, et al. "Attention is all you need." Advances in neural information processing systems 30 (2017).
[2] Raffin, Antonin, et al. "Stable-baselines3: Reliable reinforcement learning implementations." Journal of machine learning research 22.268 (2021): 1-8.
**3. W3 & Q3. Proofs for the large-scale quantum state learning.**
Please refer to the reply 3 to Reviewer 9UgW, where we briefly analyze that **even for learning product states, the global fidelity naturally degrades exponentially with the system size, but the performance of our framework remains stable when transferring to larger systems**.
**4. W5 & Q4. Evidence of practicability and efficient implementability on near-term or future quantum hardware.**
First, the measurement settings for our framework is efficient and practical that only require nearest-neighbor measurements, including the input data acquisition and the reward computation. These resources can be easily obtained in real experiments. Second, the action set only contains single-qubit or two-qubit local gates. This means that our framework is implementable even on a quantum hardware without long-term qubit connections. Moreover, our framework follows naturally the spirit of Sim-to-Real [1] learning. The agent could first be trained in the simulation environment, where the expectation values can be accurately and efficiently computed. Then the agent is transferred to a real quantum hardware to conduct state reconstruction.
Furthermore, we have demonstrated the impact of circuit noise in Appendix G2, where the agent is first trained in noiseless environment and transferred to a quantum circuit suffered from depolarizing noise. The output states affected by the
noise become mixed states. The results shows that the agent can tolerate noise strength below 0.2 and maintain good performance. We anticipate this to be a natural advantage owing to the reinforcement learning pipeline. Because during training, rather than greedily selecting the action that maximizes the reward, the agent makes explorations in different gate combinations and gate parameters, thus becomes aware of how to adjust the action when the observation (the input measurement data) deviates from the ideal case.
[1] Zhao, Wenshuai, Jorge Peña Queralta, and Tomi Westerlund. "Sim-to-real transfer in deep reinforcement learning for robotics: a survey." 2020 IEEE symposium series on computational intelligence (SSCI). IEEE, 2020. | Summary: This paper introduces QCrep, a novel reinforcement learning framework for quantum state characterization that generates explicit circuit representations rather than implicit neural encodings. The innovation lies in using local measurements from neighboring qubits to learn circuit descriptions that can faithfully reconstruct quantum states of interest. This represents a significant departure from existing approaches that either require exponentially many measurements or produce black-box neural representations that lack physical interpretability.
The authors developed a transformer-based measurement feature aggregation architecture to extract global quantum features from local measurement data, coupled with a local fidelity reward function that mitigates the notorious barren plateaus problem. Their theoretical analysis establishes a formal relationship between local and global fidelity, providing mathematical justification for their approach. Empirically, they demonstrate QCrep's effectiveness on diverse quantum states up to 100 qubits, including IQP circuit states, time-evolved Ising model states, and many-body ground states, while also showing its utility for downstream tasks like Hamiltonian learning.
Claims And Evidence: The paper's primary claims are generally supported by their theoretical analysis and experimental results:
The claim that QCrep can learn explicit circuit representations for quantum states using only local measurements is convincingly demonstrated across multiple experiments. The authors show they can achieve high fidelity with only $O(N)$ observables instead of the exponential number typically required.
The authors claim their reinforcement learning approach with local fidelity rewards avoids barren plateaus. This is supported indirectly by their ability to scale to systems much larger (50-100 qubits) than what's typically achievable with gradient-based methods, though direct landscape analysis would strengthen this claim.
Their claim regarding zero-shot transfer to different system sizes is compellingly validated by their experiments showing a model trained on 50-qubit systems can generalize to systems ranging from 10 to 100 qubits.
The usefulness of the circuit representations for downstream tasks is demonstrated through Hamiltonian learning experiments, where the learned representations enable parameter prediction with high accuracy.
The paper's evidence for robustness to finite sampling and noise (in the appendix) supports practical applicability, showing the method works with as few as 512 measurement shots and moderate levels of depolarizing noise.
One claim that could use more thorough validation concerns the method's performance on highly entangled states, as the current experiments focus on states with moderate entanglement.
Methods And Evaluation Criteria: The paper's methodological approach represents a creative combination of techniques from quantum computing and machine learning. The key insight is inverting the typical state preparation problem: rather than learning circuits that prepare target states from $|0⟩^{\otimes N}$, they learn circuits that evolve target states toward $|0⟩^{\otimes N}$. This enables handling multiple states from a family.
The evaluation criteria are comprehensive and appropriate:
1. Global and local fidelity measure how well the reconstructed states match targets
2. Renyi entropy evaluates the reconstruction of entanglement properties
3. Two-point correlations assess how well quantum correlations are captured
4. Spin-Z values verify the reproduction of local observables
Their comparative analysis against TQS, VQE, QAOA, and QAS consistently demonstrates QCrep's superior performance across all metrics, especially for larger systems.
The ablation studies examining finite sampling effects and circuit noise are crucial for assessing practical viability, though these results would benefit from inclusion in the main paper rather than the appendix.
Theoretical Claims: The paper's theoretical foundation is sound, particularly Proposition 2.1. This provides a mathematical justification for using local fidelity as a reward function.
The proof using spectral decomposition of the local fidelity observable is correct and insightful, showing why local optimization can yield good global properties - a question of fundamental importance in quantum many-body physics.
The theoretical analysis connects to broader questions about the information content of local reduced density matrices and the conditions under which they uniquely determine global states.
The paper doesn't explicitly analyze the representational power of bounded-depth quantum circuits, which would strengthen the theoretical foundation given the empirical success of relatively shallow circuits for complex states.
Experimental Designs Or Analyses: The experimental design is comprehensive, covering diverse quantum state families:
For each experiment, the authors clearly describe the system configurations, parameters, and evaluation metrics. The comparisons with baseline methods are fair and thorough.
The zero-shot transfer experiments demonstrating generalization across system sizes are particularly valuable, as is the out-of-distribution generalization test for Heisenberg ground states.
The Hamiltonian learning experiments effectively showcase the downstream utility of the circuit representations, showing they encode physically meaningful information that can be extracted with simple linear models.
The appendix experiments on universal gate sets and mixed-state families demonstrate the method's flexibility beyond the specific configurations in the main paper.
Additional analysis of how performance scales with entanglement complexity would strengthen the experimental component.
Supplementary Material: The supplementary material is relative comprehensive.
Relation To Broader Scientific Literature: The paper distinguishes itself from neural quantum states (like GQNQ and NQS) by producing explicit rather than implicit representations, addressing a key limitation of previous ML approaches.
The connection to quantum process tomography could be elaborated further, as circuit representation learning has parallels to process reconstruction.
Essential References Not Discussed: The paper's literature review is thorough, but more discussion on relation to NQS could be beneficial
Other Strengths And Weaknesses: Weaknesses:
The paper focuses primarily on states with moderate entanglement. The limits of the approach for highly entangled states remain unclear.
The computational complexity analysis could be more thorough, particularly regarding how training costs scale with system size and entanglement.
The paper doesn't fully explore which architectural components contribute most to performance. Additional ablation studies on the model architecture would provide deeper insights.
Other Comments Or Suggestions: No other comments.
Questions For Authors: 1. How does performance degrade with increasing entanglement entropy of target states? Is there an entanglement threshold beyond which the method becomes ineffective?
2. is it worth exploring more sophisticated reinforcement learning algorithms beyond PPO? Off-policy or model-based RL might further improve sample efficiency.
3. How would using higher n-local fidelity rewards affect results and computational costs? Your theory suggests this could tighten global fidelity bounds.
4. Could the framework be extended to directly optimize for specific quantum properties rather than state fidelity?
5. How does the method perform on mixed states rather than pure states? Many experimental quantum systems produce mixed states due to decoherence.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: **1. W1. Exploration in highly entangled states.**
Although fully reconstructing the target states for highly entangled states using local fidelity is generally difficult, our framework would work if the state characterization task is to estimate some properties of interests like correlations, which is the primary focus of our proposal. High local fidelity can be obtained even if the target states have higher entanglement like the states generated from random brickwork-like circuits in section 4. Besides, full reconstruction of highly entangled states is not entirely out of reach. For example, prior knowledge on how target states are formed can be leveraged to guide the agent’s learning process. Please refer to reply 4 to Reviewer 9UgW where we learn random rotated GHZ states.
**2. W2. Computational complexity analysis on training cost.**
The training cost depends on the number of observables, the maximum episode length $T$ and the iterations required for convergence. The first two components are analyzed in the main text, where the number of observables scales linearly with the system size regardless of entanglement; 1024 total measurement shots suffice to estimate the expectation values of local observables, and $T$ is fixed for each family of states regardless of system size. The convergence rate, however, is more difficult to analyze theoretically. We provide empirical evidence using the task of learning ground states of the Ising model. We train the agent to learn on 10- and 50-qubit states. The total number of iterations are set to 1740 and 1880. The agent achieves average global fidelity 0.9691 and 0.9673 respectively. This result aligns with the zero-shot transferability of the agent across different system sizes.
**3. W3. Additional ablation studies on the model architecture.**
The policy network is composed of one transformer encoder and one MLP for decision making. For the impact of the transformer encoder, please refer to the reply 2 to Reviewer 9UgW.
**4. Q1. Performance degrade with increasing entanglement entropy.**
For estimating local properties, e.g., Renyi Entropy and two-point correlations, entanglement does not matter much, since the agent can approach high local fidelity for higher entangled states like Figure 7. The degradation of global fidelity is related to the entanglement entropy, if one chooses 1-local fidelity as reward function and chooses a relatively general action space. Consider the Ising evolution as an example, where the circuit depth grows with the evolution time thus entanglement increases. The following table records the scaling of global fidelity with respect to evolution time $t$. The system size is 50 qubits.
| t | Fidelity |
| ---- | -------- |
| 1.2 | 0.9933 |
| 3.4 | 0.9934 |
| 5.6 | 0.9816 |
| 7.8 | 0.6284 |
The performance stays **stable for a relatively long time** before degradation. This is primarily because the bond dimension of the Tensor Network is not enough to accurately represent the state, which is a **limitation of the simulation** rather than our agent. In practice, if we can sample from a large scale quantum computer, we would expect better results.
**5. Q2. Exploring other reinforcement learning algorithms.**
PPO is a **robust and scalable** method that has successfully guided LLM across corpora comprising billions of texts [1], making it a good choice for learning quantum states. While off-policy methods could be explored, the potential inefficiency caused by inferior history actions remains a concern. As for model-based reinforcement learning, our framework already aligns with this paradigm. The simulator we use to evolve the quantum states could be regarded as a surrogate to the real quantum device.
[1] Ouyang, Long, et al. "Training language models to follow instructions with human feedback." Advances in neural information processing systems 35 (2022): 27730-27744.
**6. Q3. Influence of higher n-local fidelity rewards on results and computational costs.**
Higher n-local fidelity will result in barren plateaus problem thus the agent becomes harder or even unable to train if $n$ is too large. The number of observables required scales exponentially with $n$. However, for smaller $n$, e.g., $n\leq 5$, increasing $n$ would help obtain a higher global fidelity in practice, as shown in Figure 7.
**7. Q4. Extendability to directly optimizing specific quantum properties instead of state fidelity.**
Yes. Many properties can be computed by measuring the quantum state using some specific observables like Pauli X, Y and Z. Since the neural network agent can be optimized using local fidelity, obtained by measuring subsystems of the state with Pauli Z, we anticipate that the agent can also be optimized if changing Z to other observables that corresponds to some specific properties of interest.
**8. Q5. Perform on mixed states.**
Please refer to the reply 4 to Reviewer cAXj.
---
Rebuttal Comment 1.1:
Comment: Thanks for the detailed rebuttal. I would like to keep my recommendation for the paper. | null | null | null | null | null | null |
M+: Extending MemoryLLM with Scalable Long-Term Memory | Accept (poster) | Summary: The paper proposes an LLM memory-augmentation method called M+. By building on MemoryLLM, it improves the long-context understanding and information retention of a base LLM. They introduce what they call long-term memory vectors that are extracted by a trained retriever. M+ outperforms the base model and other existing baselines on long-context QA and knowledge retention benchmarks.
Claims And Evidence: M+ improves the long-context understanding and information retention of LLMs. This has been validated by the experiments in section 4.1 and 4.3. M+ also claims to be an efficient method but this is not clearly supported by the evidence presented in the paper. It has higher memory consumption and latency than the original base model. Adding CPU offloading to Table 1 is a bit misleading. It could be applied to any model and it is not specific to M+.
Methods And Evaluation Criteria: The benchmark datasets used in the paper are appropriate as they evaluate the long-context memory capabilities of models. However, the models were not evaluated on standard long-context benchmarks like the classic Needle-in-a-Haystack test and LongBench.
Theoretical Claims: None
Experimental Designs Or Analyses: Concerning analysis, not much is said about the memory vectors. It would greatly help the community to study what kind of information is contained in the memory vectors.
Supplementary Material: There is no supplementary material which hinders the reproducibility of the work. As the paper proposes a method that alters model architecture, access to the implementation would improve the evaluation of the work.
Relation To Broader Scientific Literature: The paper studies the long-context extension of LLMs. It also builds on an existing approach called MemoryLLM.
Essential References Not Discussed: Reccurrent Memory Transformers and their variants (https://proceedings.neurips.cc/paper_files/paper/2022/hash/47e288629a6996a17ce50b90a056a0e1-Abstract-Conference.html
, https://arxiv.org/abs/2304.11062) were not discussed in the paper. They also study latent-space memory.
The MemoryPrompt (https://aclanthology.org/2024.lrec-main.976/) paper analyzes the content of these memory vectors.
Other Strengths And Weaknesses: None
Other Comments Or Suggestions: Figure 3 is a bit hard to read. The scales on the 2 sides are different but combined in the same figure.
A Limitations section would help better delineate the actual contributions of the paper.
Questions For Authors: 1- What is the performance on the following standard long-context benchmarks: Needle-in-a-Haystack test and LongBench?
2- What is the memory consumption of MemoryLLM in your experiments?
3- Is the performance of the base Language Model affected by the introduction of the long-term latent-space memory? (perplexity and other metrics on standard LM benchmarks)
4- What is the performance of a simple RAG baseline?
5- Can you provide an estimate of how the memory consumption and latency would behave for very big models?
6- FLOPs was never reported. What is the FLOPs compared to the base model and other baselines? What are the results if you do FLOP-matched comparisons?
7- From an interpretability perspective, what kind information is contained in these memory vectors? How do they differ across layers? What distinguishes the long-term memory vectors from the short-term ones?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: **Claims And Evidence:**
We would like to clarify that by “CPU offloading,” we specifically mean **offloading the memory vectors** present in each layer of the model. In our setup, each layer contains 12,800 memory vectors, and it is unnecessary to keep all of them simultaneously in GPU memory. Instead, we can store them on the CPU and load them into GPU memory only when the corresponding layer is being computed. **It is important to note that other models such as LLaMA 3.1–8B do not have memory vectors, so our CPU offloading can only be applied on MemoryLLM and M+**. We will add more clarifications.
**Supplementary Material:**
We will publish the code and model upon acceptance and make sure of the reproducibility.
**Essential References Not Discussed:**
Thank you for bringing these up, we will add these works ([1], [2], [3]) into our paper.
**Comments, Suggestions and Questions:**
**Figure 3**: We will revise the scales to ensure consistency across subplots.
**Limitation Section:**: We briefly mentioned our plan to reduce CPU-GPU communication overhead in future work, we will add a section to discuss this.
**[Q1]**
(1) **Evaluations on LongBench**: We would like to note that our evaluations on LongBench are included in Section 4.4.
(2) **Experimental Results on NIAH**: We would like to emphasize two key points:
- **The scope of this paper goes beyond NIAH**: Our primary goal is to capture and reason over global information, rather than focusing solely on retrieval. Thus we focus on on longbook question answering and introduce a new dataset, Longbook-Event-QA (Section 4.1.1), which requires the model to understand a broader part of the book. In contrast, NIAH primarily evaluates retrieval ability, regardless of whether the model comprehends the broader story.
- **Our knowledge retention experiments share similarities with NIAH**: In Section 4.5 (Figures 5 and 6), the model is tasked with recalling information from a context it encountered long ago and answering related questions. This setup resembles document-level retrieval and aligns conceptually with the goals of NIAH, suggesting that our work addresses similar challenges from a different perspective.
**[Q2]**
We add the following two rows to Table 1 to report the GPU memory consumption of MemoryLLM: MemoryLLM-8B, 21176.24MB; MemoryLLM-8B (offload): 17967.47MB. These results show that MemoryLLM-8B has comparable GPU memory usage to M+.
**[Q3]**
On 1,000 unseen examples from Fineweb-Edu (2048-token limit), M+ achieves a perplexity of 1.9828 vs. 1.9734 for LLaMA-3.1-8B, showing no degradation in base model performance.
**[Q4]**
Using BM25-based RAG (retrieving up to 4 chunks of 4,096 tokens), we observe limited gains: LLaMA-3.1-8B + BM25 achieves 0.1623 on LongbookQA and 0.2065 on LongBook-Event-QA, slightly improving over LLaMA-3.1-8B-16k (0.1514 / 0.2362) on one task but worse on the other. In contrast, M+ achieves the best scores: 0.1755 / 0.2470. This shows RAG offers no consistent benefit and may hurt performance when global context is needed.
**[Q5]**
Retrieval latency scales as $\text{latency} \propto d_r \cdot s \cdot L \propto d \cdot s \cdot L$, where $d_r$ is the retriever hidden size ($d/20$), $s$ is the memory size (maximum 150k, independent of model size), and $L$ is the number of layers. Since $s$ is constant, latency simplifies to $\text{latency} \propto d \cdot L$. Given $M \propto d \cdot L$, we have $\text{latency} \propto M$. As for the memory consumption, Memory vectors overhead also scales linearly with $d$ and $L$.
**[Q6]**
M+ and LLaMA-3.1-8B have similar FLOPs (e.g., 6.92e13 vs. 5.68e13 at 2k, 1.94e15 vs. 1.75e15 at 64k). At 128k, LLaMA-3.1-8B runs out of memory, while M+ runs property and has the total FLOPs as 3.78e15.
**[Q7]**
Our memory vectors can be viewed as hidden states within the transformer layers, with miner differences being that they may store more **compressed** information. Thus the information they capture should be similar to the representations seen in the intermediate layers of a transformer when processing text.
Across layers, we hypothesize that the memory vectors follow a similar pattern to what has been observed in prior work on transformer interpretability [4, 5]:
- **Lower layers** tend to encode more **surface-level features**,
- **Higher layers** tend to encode more **semantic or abstract information**.
Regarding long-term memory, it is constructed by **randomly dropped** vectors from the short-term memory and storing them for extended use. Importantly, long-term memory vectors are structurally **identical** to short-term ones.
References:
[1] Recurrent Memory Transformer
[2] Scaling Transformer to 1M tokens and beyond with RMT
[3] MemoryPrompt: A Light Wrapper to Improve Context Tracking in Pre-trained Language Models
[4] How Many Layers and Why? An Analysis of the Model Depth in Transformers
[5] What does BERT learn about the structure of language?
---
Rebuttal Comment 1.1:
Comment: The authors have helped clarify all the ambiguous aspects of the paper. They also provided detailed answer to almost all the questions. I will update my score accordingly. It is important to include all the details in the paper for better clarity and reproducibility. However, the paper still lacks a proper quantitative analysis of the memory vectors from an interpretability perspective. The answer to Q7 are only speculations that are not properly substantiated.
---
Reply to Comment 1.1.1:
Comment: We sincerely thank the reviewer for raising the score and are extremely grateful for their constructive feedback. We will definitely include all relevant details and clarifications in the final version of the paper.
As for the concerns regarding interpretability, we acknowledge that the current version lacks a thorough interpretability analysis of M+ and we sincerely thank the reviewer for bringing this up. We would like to provide some more clarifications here: Our primary focus in this work is on exploring the model structures and demonstrating the model’s performance. We would like to respectfully note that this approach aligns with the trajectory of several influential works in the field. For example, seminal papers such as BERT: Pre-training of Deep Bidirectional Transformers for Language Understanding [1] and Attention Is All You Need [2] initially prioritized performance and introduced novel architectures, with interpretability analyses and theoretical insights following in subsequent research and other papers.
We hope this “performance-first, analysis-later” approach can be seen as a valid path for impactful contributions, and we fully intend to explore the interpretability of M+ in future work.
[1] BERT: Pre-training of Deep Bidirectional Transformers for Language Understanding
[2] Attention Is All You Need | Summary: This paper presents M+, an enhanced memory-augmented language model that extends long-term memory retention beyond conventional limits. Building on MemoryLLM, M+ integrates long-term memory with a co-trained retriever. Extensive experiments across long-context understanding, question answering, and knowledge retention benchmarks demonstrate that M+ consistently outperforms prior baselines, offering a robust and efficient solution for processing extremely long documents.
## update after rebuttal
Most of my concerns are addressed so I have raised my reviewing score.
Claims And Evidence: Yes. Most of the claims are supported by a range of quantitative experiments and ablation studies. For example, the paper demonstrates through long-book QA, Event QA and knowledge retention benchmarks that M+ outperforms baselines like MemoryLLM and Llama families. Detailed GPU memory cost comparisons and latency analysis further back the claim that M+ achieves extended retention with efficient resource usages.
Methods And Evaluation Criteria: Yes. The propose method M+ for integrating a long-term memory module into MemoryLLM match the stated goal of extending context retention beyond 20k tokens, and the chosen evaluation benchmarks (e.g., LongBook-QA, Event QA, and knowledge retention tasks) effectively measure whether the model can recall and use information from far in the past.
Theoretical Claims: The paper primarily focuses on an empirical framework rather than on detailed proofs of novel theorems.
Experimental Designs Or Analyses: Yes. The knowledge retention experiments and ablation studies are well suited to testing M+’s ability to remember and retrieve distant information.
While the paper’s approach to evaluating memory retention is well designed, the evaluation dataset and task types are limited. More complex datasets or practical applications are needed to demonstrate the effectiveness of the method [1, 2].
[1] Maharana, Adyasha, et al. "Evaluating Very Long-Term Conversational Memory of LLM Agents." Proceedings of the 62nd Annual Meeting of the Association for Computational Linguistics (Volume 1: Long Papers). 2024.
[2] Lu, Junru, et al. "Memochat: Tuning llms to use memos for consistent long-range open-domain conversation." arXiv preprint arXiv:2308.08239 (2023).
Supplementary Material: No additional supplementary material was provided.
Relation To Broader Scientific Literature: The paper builds on research in memory-augmented language models, particularly latent-space memory approaches (e.g., MemoryLLM) that store and retrieve hidden-state representations instead of raw tokens. The authors go a step further by co-training a retriever with their model, in contrast to attention-based retrieval from key-value caches. Their method also connects with work on long-context modeling by pushing context windows into the 100k+ range. By demonstrating improved knowledge retention and efficient retrieval on challenging long-QA tasks, the paper contributes to broader efforts of making LLMs handle truly extensive contexts while remaining computationally feasible.
Essential References Not Discussed: No
Other Strengths And Weaknesses: The core ideas of this paper build on existing latent-space memory approaches and chunk-based processing techniques. While the practical enhancements (e.g., CPU offloading to keep GPU usage low and adding a co-trained retriever for selective recall) are valuable, these methods can be viewed as incremental refinements, and I found them limited in originality and novelty, despite the paper’s clear demonstration of utility.
Other Comments Or Suggestions: 1. In the comparison experiments (Sections 4.1 and 4.2), since M+ is largely based on MemoryLLM, it would be beneficial to include direct comparisons showing how much M+ actually improves over MemoryLLM. Observing that margin explicitly could clarify the advantages of the proposed enhancements.
2. In Table 2, the authors report results on shorter-document tasks, yet M+ still outperforms MemoryLLM by a noticeable margin. Given that M+’s primary benefit appears to be in handling extremely long contexts, it would be helpful to clarify why it achieves such gains even with relatively small datasets.
Questions For Authors: No
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We are sincerely grateful for Reviewer v8Qd’s recognition of our work. Below, we address the reviewer’s questions in detail:
**[Q1] Direct Comparison between M+ and MemoryLLM: ** Thank you for raising this important point. In developing M+, we incorporated a number of significant improvements over MemoryLLM-7B, including: (1) a multi-LoRA architecture, (2) refined dataset selection (Fineweb-Edu and SlimPajama), and (3) a carefully designed data curriculum. These enhancements led to substantial performance gains, and as a result, we consider M+ to be in a different performance tier compared to MemoryLLM-7B.
That said, to provide a fair and controlled comparison of the architectural differences—specifically the benefits introduced by M+ – we retrained the original MemoryLLM with: (1) The LLaMA3-8B backbone; (2) The same multi-LoRA design; (3) More advanced datasets (Fineweb-Edu and SlimPajama). The retrained versions are included in our ablation study in Section 4.5, where we have two variants:
MemoryLLM-8B: We switch the backbone to Llama-3.1-8B and use multi-LoRA design and Fineweb-Edu dataset to continually train the model. This is exactly Stage 1 mentioned in Section 3.2.4.
MemoryLLM-8B-Long: After obtaining MemoryLLM-8B, we apply Stage 2 with long documents extracted from SlimPajama to enhance the model’s long document understanding abilities.
Although this section is titled “Ablation Study,” it effectively serves as a direct comparison between the MemoryLLM architecture and M+, isolating the effect of long-term memory while controlling for backbone model and training data. The comparison includes the following aspects:
1. **Perplexity (Figure 5):** M+ demonstrates lower perplexity than both MemoryLLM-8B and MemoryLLM-8B-Long. The performance gap between M+ and MemoryLLM-8B-Long is smaller, reflecting the benefits of the long-input training in both models.
2. **Knowledge Retention (Figure 6):** M+ shows a significant advantage over MemoryLLM-8B-Long in retention tasks. Notably, we observed that MemoryLLM-8B and MemoryLLM-8B-Long perform similarly on this task, underscoring the importance of the architectural changes in M+.
3. **Performance on Relatively Short Documents:** To further address your question, we have conducted additional experiments on shorter documents (8k tokens), and we will include these results in the paper. The results are as follows:
| Model | 2wikimqa | hotpotqa | qasper | musique | multifieldqa\_en | narrativeqa | Avg |
|------------------------|----------|----------|--------|---------|---------------|----|--------------|
| MemoryLLM-8B (8k) | 32.30 | 33.39 | 23.88 | 12.37 | 35.91 | 21.46 | 26.55 |
| MemoryLLM-8B-Long (8k) | 32.23 | 37.86 | 31.62 | 20.35 | 42.16 | 23.49 | 31.29 |
| M+ (8k) | 33.12 | 37.99 | 29.91 | 20.68 | 40.11 | 24.18 | 31.00 |
These results show that while M+ and MemoryLLM-8B-Long perform similarly on shorter documents (as expected), M+ provides significant gains on long-context tasks (as shown in Figure 6). This further supports our claim that the long-term memory architecture in M+ is beneficial primarily for extended contexts. Additionally, the improved performance of MemoryLLM-8B-Long over MemoryLLM-8B on short documents can be attributed to the inclusion of longer training examples in Stage 2 (4k–64k), whereas Fineweb-Edu (used in Stage 1) contains very few examples longer than 4k.
In summary, **Section 4.5 provides a direct and controlled comparison between M+ and MemoryLLM**, where the primary architectural difference is the inclusion of long-term memory. We will explicitly clarify this point in the paper and include the new short-document comparison results for completeness. | Summary: Memory model: memory pool (based on MemoryLLM) and a long-term memory with additional temporal information. Every time, the memory pool is updated, and a subset of tokens is dropped to the Long-term memory. For recall from memory, a small subset of the long-term memory vectors is retrieved according to the dot product with the query from input. The search in the long-term memory uses a low dimensional projection of the vectors (keys) and the input query for such recall. These projectors are trained separately as part of the retrieval mechanism for the long-term memory. The M+ model is fine-tuned with 2 sets of weights based on LoRA: for reading and for updating the memory. Also, it was trained in 3 stages. The first stage fine-tunes Llama-3.1-8B following the MemoryLLM setup to incorporate the memory pool. This process is done on shorter documents. The second stage extends this to a balanced set of documents of various lengths. The last stage introduces the long-term memory and adapts the model to it on a new subset of long context documents. The M+ model is then evaluated on the LongBook-QA, a synthetically generated extraction of events called LongBookEvent-QA, SQuAD, NaturalQA, and LongBench. The baselines are Llama3.1-8B-16k, a similar version with SnapKV, and a Llama3.1 3B model with 128k context length. The results show that M+ has higher performance with lower or comparable memory consumption. The authors include ablation study comparing M+ after each fine-tuning stage for validation loss convergence and knowledge retention (SQuAD and NaturalQA).
## update after rebuttal
I appreciate the authors replying to my questions. There is no additional evidence that leads me to update my score.
Claims And Evidence: The claims made in this work seem appropriately supported with convincing evidence.
Methods And Evaluation Criteria: The methods and the evaluation criteria make sense for the presented application.
Note that no metric is described for the LongBench results (Table 2). Moreover, given those results, it is unclear what the authors want to convey with that experiment.
Also, it is worth mentioning that there are existing datasets that aim to test the quality of memory augmented models like M+ (see [1]).
[1] “Assessing Episodic Memory in LLMs with Sequence Order Recall Tasks” by Pink et al., 2024.
Theoretical Claims: N/A
Experimental Designs Or Analyses: Mostly, the design and the analyses look sound. I would encourage the authors to test on datasets that evaluate for long context, instead of selecting documents from a general dataset. The intention behind the ablation study is valuable, however, it is not evident that the long-term memory is the one helping to obtain better results in stage 3. A more correct version of the experiment would be to ablate the tokens retrieved from the memory (i.e., change to padding, zero vectors, or noise). This would diminish any effect of the additional training in Stage 3.
Supplementary Material: Reviewed the additional results on NaturalQA.
Relation To Broader Scientific Literature: The contributions in this work are relevant to this community and valuable. We should note that similar solutions have been proposed and have been shown to work similarly. This work doesn’t compare results beyond its predecessor (MemoryLLM).
Essential References Not Discussed: To the best of my knowledge the authors cite many previous work on memory-augmented LLMs. They appropriately introduce the predecessor MemoryLLM.
Other Strengths And Weaknesses: * The work is clearly written and nicely presented
* The experiments evaluate a vast amount of details about the model
Other Comments Or Suggestions: * Line 156: “tokens with the largest ages” -> “oldest tokens”
* Figure 3 shows “Llama-3.2-3B…” while the text mentions “Llama-3.1-3B”.
Questions For Authors: * What is the metric used for LongBench?
* What is the performance of M+ on the task of [1]?
[1] “Assessing Episodic Memory in LLMs with Sequence Order Recall Tasks” by Pink et al., 2024.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We sincerely thank reviewer f5Uz for their recognition of the value of our work. We address the reviewer's concerns below:
**Relation To Broader Scientific Literature:**
To the best of our knowledge, following MemoryLLM, the most recent works on parametric memory include Titans [3] and Memory at Scale [4], which scale models to 760M and 1.3B parameters respectively. However, these efforts remain exploratory and have not yet been evaluated on real-world tasks such as long-context question answering, which is the focus of our paper. As a result, there are currently few parametric memory approaches that offer a meaningful comparison to our work.
As for the questions:
**[Q1] Evaluation Metric in LongBench:**
Thank you for pointing this out. Following LongBench [1], we use the QA-F1 Score as the evaluation metric for all six benchmarks included in our paper. We will add this clarification in the revised version of our manuscript.
**[Q2] Related Work and Comparison with [2]:**
We appreciate you highlighting [2]—Assessing Episodic Memory in LLMs with Sequence Order Recall Tasks. It is indeed a relevant and important contribution. We note that it is conceptually similar to our newly proposed Longbook-Event-QA task (Section 4.1.1). While [2] evaluates models by asking them to sort two segments after reading an entire book, Longbook-Event-QA requires selecting the next event given a sequence of events. Both tasks emphasize the model’s comprehension of the narrative and its ability to reason about event order. Given their shared focus, we anticipate consistent results between Longbook-Event-QA and [2], and we will consider incorporating [2] as an extended benchmark in future work.
References:
[1] LongBench: A Bilingual, Multitask Benchmark for Long Context Understanding.
[2] Assessing Episodic Memory in LLMs with Sequence Order Recall Tasks.
[3] Titans: Learning to Memorize at Test Time.
[4] Memory Layers at Scale. | Summary: **Main Findings:**
Equipping large language models (LLMs) with latent-space memory has gained significant interest, as it extends the effective context window of existing models. However, preserving and retrieving information from distant past contexts remains challenging. To address this, this paper proposes M+, an enhancement of the existing MemoryLLM model, introducing a latent-space retrieval mechanism designed specifically for long-term memory retention.
**Main Algorithmic/Conceptual Ideas:**
M+ incorporates a co-trained retriever within the MemoryLLM framework, enabling dynamic retrieval of relevant latent space information during text generation. This allows the model to effectively leverage long-term contextual memories.
**Main Results:**
Empirical evaluations on several long-text benchmarks (including Longbook, SQuAD, and LongBench) demonstrate that M+ outperforms MemoryLLM.
Claims And Evidence: Yes, the claims are clear and convincing.
Methods And Evaluation Criteria: Yes, the proposed methods make sense for the target problems.
Theoretical Claims: Not applicable. No theoretical claims.
Experimental Designs Or Analyses: Yes, I have checked the experimental designs.
Supplementary Material: Yes, all supplementary materials are reviewed.
Relation To Broader Scientific Literature: Introducing a retrieval mechanism into MemoryLLM can effectively address the challenges associated with extremely long-context content.
Essential References Not Discussed: [1] is one of the earliest works to discuss the design of extra long-term memory. [2] [3] are closely related and up-to-date works that design memory modules for long-context ability in LLMs.
[1] Hybrid computing using a neural network with dynamic external memory
[2] Titans: Learning to Memorize at Test Time
[3] Scaling Transformer to 1M tokens and beyond with RMT
Other Strengths And Weaknesses: **Strengths:**
The proposed method clearly demonstrates improvements over the original MemoryLLM by introducing an effective retrieval mechanism (M+) for handling extremely long-context content.
The paper provides detailed descriptions of algorithms and experimental setups, facilitating straightforward reimplementation by the research community.
**Weakness**:
1. The novelty of this paper is incremental. The proposed long-term memory mechanism closely resembles existing retrieval-based designs for long-context processing, such as SnapKV, into MemoryLLM. The primary difference is utilizing KV or latent states for long-term memory, which has not been clearly demonstrated as crucial for improving performance.
2. The paper lacks a rigorous analysis or ablation study comparing KV and latent states as long-term memory.
Other Comments Or Suggestions: No additional comments.
Questions For Authors: 1. Could you elaborate further on any additional conceptual or algorithmic insights beyond introducing a retrieval mechanism into MemoryLLM? Specifically, what distinct advantages or innovations does your method offer compared to existing retrieval-based approaches (e.g., SnapKV)?
2. It would be beneficial to explicitly compare the effectiveness of leveraging KV cache versus latent states as long-term memory. Providing experimental results or ablation studies on this comparison could clarify the significance and necessity of your design choice.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: **Essential References Not Discussed:**
Thank you for highlighting these important works. We will incorporate [1], [2], and [3] into our related work section. Specifically, [1] aligns with the core motivation behind incorporating memory into language models. Both [2] and [3] explore architectural modifications to enable memory mechanisms in transformers. However, these approaches remain exploratory, as they have not been scaled beyond small models or applied to real-world tasks such as long-context question answering. In contrast, M+ is implemented at the 8B parameter scale and is designed to be scalable with additional GPU resources. We will update our related work section accordingly and include a discussion of these points in the paper.
**Weaknesses**:
**[W1] Similarity to Attention-Based Retrieval Methods:** We acknowledge that our method shares some similarities with prior approaches that use attention to retrieve keys and values. However, there are critical differences that make our approach unique and practically advantageous:
**(1) Efficiency:** Methods such as SnapKV maintain and retrieve key-value pairs per head, which becomes extremely costly when scaled. In our setting—with 32 layers and 32 attention heads per layer—this requires 1024 retrievals per query, resulting in significant latency (as noted in line 59 of our paper). In contrast, M+ uses a co-trained retriever to retrieve memory tokens, which are compressed hidden states. This results in only 32 total retrievals—one per layer—dramatically reducing both computational cost and latency.
**(2) Performance:** In Figure 6, the curve labeled MemoryLLM-8B-Attn follows the SnapKV-style approach of retrieving key-value pairs using attention per head. As shown in the figure, it performs substantially worse than M+, highlighting that our co-trained retriever not only improves efficiency but also yields better results in practice compared with attention-based retrievals.
**(3) Design:** Note that our training setup includes both relevant and irrelevant documents (See details in Appendix D), making it well-suited for contrastive learning. This allows us to effectively train the retriever, which integrates naturally into our overall training framework.
**[W2] Representation of Long-Term Memory (Hidden States vs. KV):**
We appreciate the reviewer’s insightful comment regarding the form of long-term memory. We advocate for the use of hidden states over key-value (KV) caches based on two key considerations:
**Compression Efficiency:** As detailed in the paper, we compress each 512-token chunk into 256 memory vectors per layer in a lossless manner. In contrast, KV-based methods often require downsampling—e.g., dropping half the keys and values—to control memory size, resulting in unavoidable information loss.
**Retrieval Efficiency and Performance:** As described in [W1], hidden states can be effectively retrieved using our co-trained retriever, requiring only 32 retrievals for each query. In contrast, a KV-cache approach would demand up to 1024 retrievals, significantly increasing computational cost. Furthermore, as shown in Figure 6, using hidden states yields better performance compared to using KV caches.
We believe these benefits make hidden states a more efficient and effective choice for long-term memory representation in our system.
[1] Hybrid computing using a neural network with dynamic external memory.
[2] Titans: Learning to Memorize at Test Time.
[3] Scaling Transformer to 1M tokens and beyond with RMT.
---
Rebuttal Comment 1.1:
Comment: I acknowledge the explanation provided in the text. However, I still believe that an apple-to-apple numerical comparison is necessary to demonstrate the effectiveness clearly. Although the authors state that “Furthermore, as shown in Figure 6, using hidden states yields better performance compared to using KV caches,” the comparison in Figure 6 is between MemoryLLM-8B and M+, which does not make it clear to the audience which part corresponds to an apple-to-apple comparison between KV cache and latent states. More explanations are necessary.
---
Reply to Comment 1.1.1:
Comment: We appreciate the reviewer’s suggestion regarding an apple-to-apple comparison between key-value caches and latent states.
**[TL, DR] We would like to highlight that we provide the comparison between key-value caches and M+ in Figure 3, which is the comparison between Llama-3.1-8B-SnapKV and M+ (For Longbook-QA, M+ vs Llama-3.1-8B-SnapKV is 0.1752 vs 0.1625, For Longbook-Event-QA, M+ vs Llama-3.1-8B-SnapKV is 0.2476 vs 0.2297).**
Specifically, we offer more explanations below:
Based on our understanding, the comparison the reviewer is requesting can be framed through the following four settings:
- Setting 1: Save the hidden states of $x_1, \cdots, x_n$, and use the question $q$ to retrieve some of these hidden states.
- Setting 2: Save the keys and values of $x_1, \cdots, x_n$, and retrieve relevant keys and values per head using $q$. (**key-value caches applet-to-apple** comparison with **M+**)
- Setting 3: Compress $x_1, \cdots, x_n$ into hidden states, and use a co-trained retriever to fetch relevant hidden states given $q$. (**M+**)
- Setting 4: Compress $x_1, \cdots, x_n$ into hidden states, transform them into keys and values, and use $q$ to retrieve keys and values.
We hope this breakdown aligns with the reviewer’s intent. If there are additional settings the reviewer would like us to consider, we would be happy to incorporate them.
Below, we explain how each of these settings corresponds to the methods evaluated in our paper:
- Setting 1 is primarily used in early work such as KNN-LM [1], and has since been superseded by methods like H2O [2] and SnapKV [3]. While we did not include Setting 1 in our comparisons, we note that it is no longer used in recent literature, and thus we followed this trend.
- Setting 2 corresponds to SnapKV, i.e. **Llama-3.1-8B-SnapKV** in Figure 3, where we implemented SnapKV on Llama-3.1-8B, and we present a direct comparison between SnapKV and our method (Llama-3.1-8B-SnapKV vs M+).
- Setting 3 corresponds to M+, which is compared with both key-value cache baselines and MemoryLLM.
- Setting 4 corresponds to our model MemoryLLM-8B-Attn, as shown in Figure 6.
To summarize, our paper includes:
- A comparison between Setting 2 and Setting 3 (key-value caches vs. M+), and
- A comparison between Setting 3 and Setting 4 (M+ vs. MemoryLLM).
Therefore, we believe the paper covers all meaningful and contemporary comparisons between key-value caches and latent state representations. We acknowledge the reviewer’s request and hope this clarification addresses the concern.
Finally, we would like to clarify that the “hidden states” saved in our system are not equivalent to those in Setting 1. In our case, the hidden states are outputs of an encoder that is trained jointly with the rest of the system. As a result, these are compressed representations and contain less redundant information compared with traditional decoder-side hidden states in a language model.
We thank the reviewer again for the thoughtful feedback and are happy to provide additional clarifications if needed. Meanwhile, if the reviewer finds our response adequately addresses the concern, **we would be sincerely grateful if they would consider reassessing the evaluation and potentially raising their score.**
[1] Generalization through Memorization: Nearest Neighbor Language Models.
[2] H2O: Heavy-Hitter Oracle for Efficient Generative Inference of Large Language Models.
[3] SnapKV: LLM Knows What You are Looking for Before Generation. | null | null | null | null | null | null |
Task-Gated Multi-Expert Collaboration Network for Degraded Multi-Modal Image Fusion | Accept (poster) | Summary: In this paper, authors proposes a framework, TG-ECNet, for degraded multi-modal fusion by unifying restoration and fusion. The key design involves task-gated routing and expert collaboration. The paper conduct a series of experiments to demonstrate the effectiveness of TG-ECNet.
Claims And Evidence: Yes, the claims is supported by evidence.
Methods And Evaluation Criteria: Yes, it makes sense for the problem.
Theoretical Claims: There are not theoretical claims in the paper.
Experimental Designs Or Analyses: I have checked the experimental designs. There are some problems and please see more details in the following questions.
Supplementary Material: I have reviewed the Supplementary Material, including more qualitative and quantitative results.
Relation To Broader Scientific Literature: The key contributions of the TG-ECNet framework are connected to advancements in three areas of the broader literature: multi-modal image fusion, degradation-aware restoration, and dynamic network architectures.
Essential References Not Discussed: The key references for image restoration are not included in Sec. 2.2, such as Restormer[1], Prompt IR[2], DGUNet[3], etc.
[1] Zamir, Syed Waqas, et al. "Restormer: Efficient transformer for high-resolution image restoration." Proceedings of the IEEE/CVF conference on computer vision and pattern recognition. 2022.
[2] Potlapalli, Vaishnav, et al. "Promptir: Prompting for all-in-one image restoration." Advances in Neural Information Processing Systems 36 (2023): 71275-71293.
[3] Mou, Chong, Qian Wang, and Jian Zhang. "Deep generalized unfolding networks for image restoration." Proceedings of the IEEE/CVF conference on computer vision and pattern recognition. 2022.
Other Strengths And Weaknesses: Strengths:
1. A novel framework to unifiy image restoration and fusion via a task-gated router and multi-expert collaboration.
2. Extensive experiments by authors.
3. The framework demonstrates competitive performance under four degradation scenarios (noise, haze, blur, stripe noise).
4. The paper also conducts experiments on object detection.
---
Weaknesses:
1. This work is still a two-stage method, where the first stage is to restore clean visible images and clean infrared images, and the second stage is to perform image fusion. So why don't I use advanced image restoration algorithms for the first stage? Then, I only need to care about the fusion.
2. How does the "Degradation-Aware Gating" in Figure 2 for the degraded visible and infrared image work? Is this the same as "Task-Gated Router" in Figure 3?
3. According to Figure 2, two U-shaped Transformer network are used for visible and infrared images, respectively. Is this understanding right? The details about this Transformer network are missing.
Other Comments Or Suggestions: Please polish this paper and then seek for possible publication. The current version is somewhat coarse.
Questions For Authors: 1. There are some errors in Figure 1. From Figure 1, the "Train Stage 1" doesn't involve the loss. But according to Sec. 3.3, the first training stage optimizes the parameters through the restoration loss. Then the fused image ground truth $\boldsymbol{I^C_F}$ is missing in the figure.
2. Again for Figure 1, the symbols are not consistent with the text parts. For example, degraded input $\boldsymbol{I^d_V}$, $\boldsymbol{I^d_I}$ in Figure 1 and $I^d_V$, $I^d_I$ in Sec. 3.3.
3. For Figure 2, what does "Prompt Components" mean? It is not mentioned in any sections. Then, what do the dotted line and solid line from "Weights" represent?
4. In Sec. 4.1 "Experimental Setting", "the number of experts K and the hyperparameter l balance were heuristically set to 2 and 0.0001 respectively." What is the hyperparameter l, which can not be found in Method. Then, why K is set as 2, where there are at least four degradations involved in the paper.
5. For evaluation metrics, why choosing CC, MSE, PSNR, $N_{abf}$ and MS-SSIM, what do these mean and how they are calculated? In Text-IF and EMMA, they both apply EN, SD, VIF and SCD.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thanks for recognizing our contributions in this work. We will reply to your questions in order.
---
## Response to the essential references
#### Concerning the references you suggested, we will incorporate them into our bibliography. Furthermore, our experimental configuration utilizes state-of-the-art image restoration algorithms, AdaIR (ICLR 2025), for preprocessing purposes.
---
## Response to the doubts towards our two-stage method
#### The traditional two-stage approach (image restoration followed by fusion) may be contradictory. Image restoration tends to eliminate noisy information while image fusion tends to integrate more valid information, but the restoration model may eliminate information of interest for image fusion in the first stage, leading to sub-optimal fusion performance. In our work, the proposed unified framework realizes the divide-and-conquer treatment of different degradation tasks by arranging the corresponding experts to process dynamically through Degradation-Aware Gating performing task routing, while the multi-expert system guided by Fusion-Aware Gating dynamically equilibrates the degree of information retention between the fusion and restoration tasks to realize the better restoration and fusion results.
#### In comparative evaluations, even when incorporating state-of-the-art network AdaIR (ICLR 2025) for preprocessing and advanced fusion algorithms in cascaded networks ([NewFig3](https://anonymous.4open.science/r/TG-ECNet/NewFig3.png)). Such a setting still underperforms our approach. Our method demonstrates significant advantages through comprehensive experimental validation. Primarily, it effectively minimizes feature loss induced by network cascading while fully exploiting the shared characteristics between image fusion and restoration tasks.
#### Furthermore, to ensure rigorous validation, we conducted generalization tests using non-degraded images, which consistently showed that dual-network architectures achieve suboptimal performance compared to our method. These results collectively highlight the technical superiority and robustness of our proposed framework.
---
## Response to the "Degradation-Aware Gating" and "Task-Gated Router"
#### The "Task-Gated Router" in Fig. 3 is an internal component of the "Degradation-Aware Gating" and "Fusion-Aware Gating" in Fig. 2. The Task-Gated Router operates by dynamically integrating input features with task-specific prompt components to generate adaptive routing weights, effectively bridging the gap between task requirements and feature representation.
#### Meanwhile, the "Degradation-Aware Gating" and "Fusion-Aware Gating" modules work in tandem to perform intelligent expert gating, where the computed weights selectively filter and combine the outputs from different experts. This dual-gating design not only maintains task-relevant feature propagation but also ensures optimal expert utilization based on both degradation characteristics and fusion objectives, thereby enhancing the model's capability to handle complex multi-task scenarios.
---
## Response to the U-shaped Transformer network
#### The two U-shaped Transformer networks shown in Fig. 2 share identical parameters. During the first-stage training, we developed a base network capable of simultaneously handling degradations in both visible and infrared modalities. It should be noted that such network architecture is quite common in image restoration tasks and does not represent the core innovation of our work. We have added the details of the model architecture in the revised manuscript.
---
## Response to Questions
#### 1. We apologize for the unclear presentation. First, the loss of Stage 1 is noted in Stage 2 in Fig.2. Second, in the visible-infrared image fusion task, we do not have the ground truth $I_{F}^{C} $.
#### 2. We thank the reviewers for pointing out the difference in bolding, which we will correct in the revised manuscript.
#### 3. The components you mentioned are all integral parts of the MoE system. The "Prompt Components" are derived by compressing features into task-specific prompts that encapsulate relevant task information. The ''weight'' is used to combine the outputs from different experts.
#### 4. Thanks for correcting this typo. In our work, we select the top 6 experts from 11 experts to cope with different degradations.
#### 5. These five metrics are all classic evaluation indicators in image fusion. Since our method focuses on utilizing expert systems to identify and eliminate degradations rather than directly removing degradations through text prompts and LLMs like Text-IF, it is essential for us to compute PSNR, a metric shared by both image restoration and fusion tasks. This calculation demonstrates the robustness of our experimental results. Also, the other four metrics are commonly adopted in other fusion algorithms as well.
---
Thanks for your suggestions.
---
Rebuttal Comment 1.1:
Comment: After rebuttal, my concerns have been addressed. And I recommend acceptance. | Summary: The paper introduces Task-Gated Multi-Expert Collaboration Network (TG-ECNet), a novel framework designed to address the challenges of degraded multimodal image fusion. The key innovation lies in its task-gated router, which integrates degradation-aware gating in the encoder and fusion-aware gating in the decoder to dynamically adapt to various degradation types (e.g., noise, blur, haze, stripe noise) and selectively aggregate features from multiple modalities (e.g., visible and infrared images). The framework also employs a multi-expert collaborative network and a two-stage training strategy to balance restoration and fusion tasks, ensuring high-quality fusion results in complex real-world scenarios. The authors demonstrate the effectiveness of TG-ECNet through extensive experiments on both synthetic and real-world datasets, showing superior performance compared to state-of-the-art methods in terms of restoration and fusion quality.
Claims And Evidence: The claims made in the paper are well-supported by both quantitative and qualitative evidence. The authors provide:
- Quantitative Results: Metrics such as CC (Correlation Coefficient), MSE (Mean Squared Error), PSNR are used to evaluate the performance of TG-ECNet on synthetic and real-world datasets. The results consistently show that TG-ECNet outperforms state-of-the-art methods across various degradation scenarios.
- Qualitative Results: Visual comparisons demonstrate that TG-ECNet effectively removes noise, haze, and stripe noise while preserving fine details and improving fusion quality. The fusion results are clearer and more informative compared to other methods.
- Downstream Task Evaluation: The authors evaluate the impact of TG-ECNet on object detection tasks using YOLOv5, showing that the fused images generated by TG-ECNet lead to higher detection accuracy (mAP and AP(0.5:0.95)) compared to other methods.
However, there are a few areas where the evidence could be strengthened:
- Real-World Generalization: While the synthetic dataset is well-constructed, the evaluation on real-world data is limited. More diverse real-world scenarios (e.g., outdoor scenes, different lighting conditions) should be tested to further validate the robustness of TG-ECNet.
Methods And Evaluation Criteria: The proposed methods and evaluation criteria are appropriate for the problem at hand. The use of degradation-aware gating to dynamically adapt to different degradation types and fusion-aware gating to selectively aggregate multimodal features is well-motivated and effectively addresses the ambiguity of degraded image fusion.
Theoretical Claims: The paper does not make strong theoretical claims, so there are no theoretical proofs to evaluate. The focus is primarily on the empirical validation of the proposed method.
Experimental Designs Or Analyses: The experimental design is sound, with both synthetic and real-world evaluations. The synthetic dataset is well-constructed, and the real-world experiments demonstrate the practical utility of TG-ECNet. However, there are a few areas where the experimental analysis could be improved:
- Real-World Data Diversity: The real-world experiments are limited to a few scenarios. Testing on a wider range of real-world data (e.g., outdoor scenes, different flicker frequencies) would strengthen the claims of generalizability.
- Downstream Task Evaluation: While the paper shows improvements in object detection, it would be beneficial to evaluate the impact of TG-ECNet on other downstream tasks (e.g., segmentation, SLAM) to further demonstrate the versatility of the framework.
Supplementary Material: NA
Relation To Broader Scientific Literature: The paper is well-situated within the broader literature on multimodal image fusion and degraded image restoration. The authors discuss related works in both conventional video deflickering and event signal filtering, highlighting the unique challenges posed by degraded multimodal images. The proposed method builds on existing ideas (e.g., attention mechanisms, spatio-temporal modeling) but introduces novel components (e.g., task-gated router) to address the specific problem of degraded image fusion.
Essential References Not Discussed: The paper covers most of the relevant literature, but there are a few areas where additional references could strengthen the discussion:
- Transformer-Based Fusion: The paper could discuss more recent transformer-based approaches for multimodal image fusion (e.g., SwinFuse, TransFuse) in more detail, as these methods are relevant to the problem of degraded image fusion.
Other Strengths And Weaknesses: - Limited Real-World Evaluation: The real-world experiments are limited in scope, and more diverse scenarios should be tested to validate the generalizability of TG-ECNet.
Other Comments Or Suggestions: - Expand Ablation Study: The ablation study could be expanded to include more variations of the network architecture to better understand the contribution of each component.
Questions For Authors: Please refer to the above parts.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thanks for recognizing our contributions in this work. We will reply to your questions in order.
---
## Response to the real-world experiments
#### We utilize real-world data from AWMM dataset to validate the robustness of our method in [Newfig2](https://anonymous.4open.science/r/TG-ECNet/NewFig2.png). The dataset consists of images with snow and haze. In our experiment, the results of our method have improved clarity and contrast.
---
## Response to the downstream tasks
#### In [NewFig6](https://anonymous.4open.science/r/TG-ECNet/NewFig6.png), we employed the unified segmentation network GroundingSAM to evaluate segmentation performance.
#### For the noisy scenario with $\sigma$=50, we segmented cars in the image, demonstrating that our method produces no false detections.
#### For infrared images with stripe noise, we segmented humans in the image, showing that our method accurately extracts the contours of all three individuals without missed detections or misclassifying the e-bike as part of the targets.
---
## Response to essential references
#### We conducted a series of experiments using SwinFuse, with the corresponding results presented in [NewFig1](https://anonymous.4open.science/r/TG-ECNet/NewFig1.jpg), [Newfig2](https://anonymous.4open.science/r/TG-ECNet/NewFig2.png), [NewFig3](https://anonymous.4open.science/r/TG-ECNet/NewFig3.png), [NewFig4](https://anonymous.4open.science/r/TG-ECNet/NewFig4.png), [NewFig5](https://anonymous.4open.science/r/TG-ECNet/NewFig5.png) and [Newfig6](https://anonymous.4open.science/r/TG-ECNet/NewFig6.png). Our method outperformed MGDN across all tasks, and we have also included this literature in our references.
---
## Response to limited ablation studies on critical components
#### in [NewFig7](https://anonymous.4open.science/r/TG-ECNet/NewFig7.png), we have conducted two other ablation experiments. First, since we use a learnable mask in the fusion stage, we compare this setting with visible modality dominant(VIS Major), infrared modality dominant(IR Major), and direct VIS-IR modality addition(plus). The result demonstrates that our setting is suitable for different scenarios. Second, since we use the multi-expert collaboration module in both stages, we conduct experiments in which only one stage uses the multi-expert collaboration module. In the experiments, we demonstrate that the module is instrumental in both stages.
---
Thanks for your suggestions.
[r1] Li, et al. AWFusion. arXiv:2402.02090,2024.
[r2] Guan, et al. Mutual-guided dynamic network for image fusion. ACM MM, 2023.
[r3] Wang, et al. SwinFuse. IEEE Transactions on Instrumentation and Measurement, 2022. | Summary: This paper presents TG-ECNet, a unified framework that concurrently addresses restoration and fusion of degraded visible images (affected by noise, blur, and haze) and infrared images (with stripe noise) through a task-gated router and multi-expert collaboration mechanism. The proposed integration of restoration and fusion processes enhances model robustness, demonstrating improved performance in real-world scenarios. Furthermore, the authors introduce a new benchmark dataset containing degraded multi-modal images.
Claims And Evidence: Insufficient substantiation:
1. The use of only two experts in the multi-expert collaboration module raises questions about the efficacy of this core design compared to conventional multi-expert architectures.
2. No analysis is provided regarding the impact of MoE configurations on model parameters and computational overhead.
Methods And Evaluation Criteria: Not sufficiently justified:
1. Inadequate specification of degradation parameters and data characteristics for both proposed benchmark datasets.
2. Experimental details on the detection task implementation remain unclear.
Theoretical Claims: The paper primarily makes the following theoretical claims:
1. Multi-modal image fusion must account for potential degradations in both RGB and infrared modalities
2. Existing multi-modal fusion methods underperform when processing degraded input images
3. The task-gated router enables adaptive handling of degraded features during fusion
4. The multi-expert collaborative network achieves robust restoration and high-quality fusion simultaneously
5. A two-stage training strategy optimizes joint handling of restoration and fusion tasks
Experimental Designs Or Analyses: Please refer to previous comments.
Supplementary Material: All supplementary materials have been thoroughly reviewed.
Relation To Broader Scientific Literature: This work connects to:
All-in-one image restoration approaches.
Multi-modal image fusion methodologies.
MoE (Mixture of Experts) techniques.
Dynamic network architectures.
Essential References Not Discussed: While the core methodology relates to dynamic networks for image fusion, the authors omit discussion of Mutual-guided Dynamic Network for Image Fusion (ACMMM 2023), a directly relevant contemporaneous work.
Other Strengths And Weaknesses: Strengths:
- Introduction of novel benchmark dataset for degraded multi-modal restoration/fusion
- Comprehensive experiments demonstrating SOTA performance on proposed and existing datasets
- Persuasive visual comparisons showing qualitative improvements
Weaknesses:
- Limited ablation studies on critical components
- Insufficient analysis of computational efficiency
Other Comments Or Suggestions: - Lines 211-213 and 213-215 contain repetitive content
- Discrepancy exists between table organization (recent methods first) and visual/metric presentation order
- Typographical error in Line 531 ("table()") requires correction
Questions For Authors: Please refer to previous comments.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thanks for recognizing our contributions in this work. We will reply to your questions in order.
---
## Response to the selection of experts
#### In our work, we select the top 6 experts from 11 experts to cope with different degradations. In our paper, there is a typo in Line 218. We utilize degradations of three types of Gaussian noise, haze, defocus blur, and stripe noise. The number of types is aligned with the number of experts we select. In [NewFig4](https://anonymous.4open.science/r/TG-ECNet/NewFig4.png), we compare the efficiency and performance of different methods and different expert selections in our method, which demonstrates that our selection is reasonable.
---
## Response to the impact of MoE configurations
#### In [NewFig4](https://anonymous.4open.science/r/TG-ECNet/NewFig4.png), we have shown that our method has a medium standard of FPS and Params and achieves a great performance. As the number of experts increases, the tasks each expert needs to complete are reduced, allowing them to focus on features specific to a particular degradation. Although the computational difficulty is somewhat heightened, it increases the granularity of the experiments.
---
## Response to the datasets
#### Our dataset includes six types of degradation: Noise15, Noise25, Noise50, Haze, DefocusBlur, and StripeNoise, with quantities of 726, 723, 724, 909, 3094 and 2443 respectively. Since we consider the DefocusBlur task to be more challenging and the infrared modality only involves one type of degradation StripeNoise, these two tasks have a larger volume of data. Additionally, we have created multi-degraded scenarios where a single image pair may contain 2 to 6 types of degradation, with 25 images allocated for each configuration.
---
## Response to the setting of the object detection
#### For each test set containing different degradations, we split the images in an 8:2 ratio and input them into the YOLOv5 network. The training was configured with 50 epochs, an image size of [640, 640], and we calculated both AP and mAP@0.5:0.95. The entire training process was completed on a single RTX 3090 GPU.
---
## Response to essential references
#### We conducted a series of experiments using MGDN [r2], with the corresponding results presented in [NewFig1](https://anonymous.4open.science/r/TG-ECNet/NewFig1.jpg), [Newfig2](https://anonymous.4open.science/r/TG-ECNet/NewFig2.png), [NewFig3](https://anonymous.4open.science/r/TG-ECNet/NewFig3.png), [NewFig4](https://anonymous.4open.science/r/TG-ECNet/NewFig4.png), [NewFig5](https://anonymous.4open.science/r/TG-ECNet/NewFig5.png) and [Newfig6](https://anonymous.4open.science/r/TG-ECNet/NewFig6.png). Our method outperformed MGDN [r2] across all tasks. We will incorporate a citation to this work in the revised manuscript.
---
## Response to ablation studies on critical components
#### In [NewFig7](https://anonymous.4open.science/r/TG-ECNet/NewFig7.png), we have conducted two other ablation experiments. First, since we use a learnable mask in the fusion stage, we compare this setting with visible modality dominant(VIS Major), infrared modality dominant(IR Major), and direct VIS-IR modality addition(plus). The result demonstrates that our setting is suitable for different scenarios. Second, since we use the multi-expert collaboration module in both stages, we conduct experiments in which only one stage uses the multi-expert collaboration module. In the experiments, we demonstrate that the module is instrumental in both stages.
---
## Response to the analysis of computational efficiency
#### We have responded to it above. Related results can be seen in [NewFig4](https://anonymous.4open.science/r/TG-ECNet/NewFig4.png).
---
## Response to other comments or suggestions
#### 1. Lines 211-213 and 213-215 don’t contain repetitive content. Lines 211-213 denote the setting of the first stage of the network, while lines 213-215 denote the setting of the second stage of the network.
#### 2. Thanks for this suggestion. We have adjusted the order in time order both in the table and in the visualization.
#### 3. Thanks for correcting this typo.
---
Thanks for your suggestions.
[r2] Guan, et al. Mutual-guided dynamic network for image fusion. ACM MM, 2023.
---
Rebuttal Comment 1.1:
Comment: I have carefully reviewed the authors’ rebuttal, which resolves most of my concerns. That said, I urge the authors to take the final revision seriously, addressing all reviewer comments with responsibility to the community. I also strongly encourage the authors to release the code and dataset, which would significantly enhance the reproducibility of the work and benefit the broader research community. | Summary: This paper introduces TG-ECNe, a novel framework designed to address the challenges of degraded multimodal image fusion. Multimodal images, such as visible and infrared images, often suffer from degradations like noise, blur, haze, and stripe noise, which negatively impact fusion quality. TG-ECNet tackles these issues by incorporating a task-gated router that includes degradation-aware gating in the encoder and fusion-aware gating in the decoder.
Claims And Evidence: Yes
Methods And Evaluation Criteria: Yes
Theoretical Claims: Yes
Experimental Designs Or Analyses: Yes
Supplementary Material: No Supplementary Material
Relation To Broader Scientific Literature: No
Essential References Not Discussed: No
Other Strengths And Weaknesses: 1. The experiments lack visualization results in combined degradation scenarios. Furthermore, since existing All-in-One image fusion algorithms are incapable of handling composite degradation, it is necessary to compare them with image restoration algorithms used as pre-processing steps to ensure the fairness of the experiments.
2. The article lacks detailed information about the proposed dataset, DeMMI-RF. The haze and noise scenarios do not align with real-world degradation conditions. Firstly, infrared images often suffer from varying degrees of degradation in adverse weather conditions, which the DeMMI-RF dataset does not seem to account for. Secondly, infrared images are more susceptible to noise than visible light images, yet the paper does not include experiments where both modalities are affected by noise.
3. In haze scenarios, comparisons should be made with current image fusion algorithms designed for adverse weather conditions, such as AWFusion.
4. The authors employ a multi-expert network to handle different types of degradation. However, could this lead to high computational complexity for the proposed algorithm? An analysis of computational efficiency is lacking.
5. The proposed framework does not appear to introduce any theoretical innovations at the module level. A more in-depth analysis is needed to explain why the proposed framework can effectively address challenges in complex scenarios.
6. Experiments in non-degraded scenarios are lacking, which are necessary to validate the generalization capability of the proposed algorithm.
Other Comments Or Suggestions: No
Questions For Authors: See the Weaknesses
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thanks for recognizing our contributions in this work. We will reply to your questions in order.
---
## Response to visualization results in combined degradation scenarios
#### In Fig.1, we’ve shown the performance of some methods like Text-if and DRMF in combined degradation scenarios. We use AdaIR(ICLR2025) as pre-processing before fusion algorithms to ensure the fairness of the experiments and show the visualization results and quantitative comparisons in [Newfig1](https://anonymous.4open.science/r/TG-ECNet/NewFig1.jpg), where our method outperforms all other methods.
---
## Response to the proposed dataset
#### In our DeMMI-RF dataset, the haze scenarios are generated by the atmospheric scattering model(ASM), where we change the parameter $A$ to adjust the intensity close to real situations. From the traditional ASM, we know:
#### $$J(x)=\frac{1}{t(x)}I(x)-A\frac{1}{t(x)}+b$$
#### Where $t(x)$ indicates image with haze, $J(x)$ indicates image without haze, $A$ indicates atmospheric light intensity. In our work, we set $A$ as $\overline{A}=MEAN(J(x))$, which avoids the image being too bright and makes it close to reality.
#### The noise scenarios are aligned with other Restoration Model settings.
#### Besides, we utilize real-world data from the AWMM dataset[r1] to validate the robustness of our method in [Newfig2](https://anonymous.4open.science/r/TG-ECNet/NewFig2.png). In [Newfig2](https://anonymous.4open.science/r/TG-ECNet/NewFig2.png), we show the visualization comparison among related works and ours. The dataset consists of images with snow and haze. In our experiment, the results of our method have improved clarity and contrast.
---
## Response to the methods designed for adverse weather conditions
#### Comparisons with AWFusion [r1] have been made in [NewFig1](https://anonymous.4open.science/r/TG-ECNet/NewFig1.jpg), [Newfig2](https://anonymous.4open.science/r/TG-ECNet/NewFig2.png), [NewFig3](https://anonymous.4open.science/r/TG-ECNet/NewFig3.png), [NewFig4](https://anonymous.4open.science/r/TG-ECNet/NewFig4.png), [NewFig5](https://anonymous.4open.science/r/TG-ECNet/NewFig5.png) and [Newfig6](https://anonymous.4open.science/r/TG-ECNet/NewFig6.png). Our method demonstrates superior performance across various scenarios. We will duly incorporate a citation to this work in the revised manuscript.
---
## Response to the computational efficiency
#### Although our multi-expert network inevitably increases the computational complexity, our method has a smaller parameters than some of the other methods. As for the number of experts, we show the quantitative comparisons between related works and other MoE settings in our work on the performance and efficiency in [NewFig4](https://anonymous.4open.science/r/TG-ECNet/NewFig4.png), which shows our choice is best when considering the efficiency and performance. Compared with other methods, our method has a medium cost but shows a good performance. In the selection of the number of experts, our selection shows the best performance.
---
## Response to innovations
#### The traditional two-stage approach (image restoration followed by fusion) may be contradictory. Image restoration tends to eliminate noisy information while image fusion tends to integrate more valid information, but the restoration model may eliminate information of interest for image fusion in the first stage, leading to sub-optimal fusion performance. In our work, the proposed unified framework realizes the divide-and-conquer treatment of different degradation tasks by arranging the corresponding experts to process dynamically through Degradation-Aware Gating performing task routing, while the multi-expert system guided by Fusion-Aware Gating dynamically equilibrates the degree of information retention between the fusion and restoration tasks to realize the better restoration and fusion results. Our framework reduces the contradiction between the restoration and fusion tasks and minimizes the information loss in the cascaded structure. Also, the structure doesn’t need text guidance, which is a must for Text-if and is more adaptive for multitasks than DRMF. Such a network can recognize different degradations and extract effective features.
---
## Response to experiments in non-degraded scenarios
#### We’ve shown the results in non-degraded scenarios in [NewFig5](https://anonymous.4open.science/r/TG-ECNet/NewFig5.png). From the results, we can know that our method is immune to the loss of features between cascaded networks.
---
Thanks for your suggestions.
[r1] Li, et al. AWFusion. arXiv:2402.02090,2024. | null | null | null | null | null | null |
Understanding the learned look-ahead behavior of chess neural networks | Reject | Summary: The paper analyzes the behavior of a transformer model trained on chess games using activation patching, probing, and attention ablation, as originally proposed in [1]. The paper finds that the model considers up to the 7th future move when selecting the best next move, and its lookahead behavior is highly context-dependent (on the puzzle set). Additionally, it shows that the model considers multiple possible move sequences.
[1] Jenner et al., Evidence of Learned Look-Ahead in a Chess-Playing Neural Network, 2024
Claims And Evidence: The main claims of the paper are as follows:
1. The model exhibits lookahead behavior up to the 7th move.
2. Its behavior is highly dependent on the puzzle set.
3. The model can choose an alternative move.
The first claim is well supported by Figure 3 but lacks novelty, as it is merely an extension of [1]. The second claim is not surprising, given that [1] already states, "the results of all our experiments are noticeably different on puzzles." The final claim appears to be original compared to [1], but its significance is unclear.
[1] Jenner et al., Evidence of Learned Look-Ahead in a Chess-Playing Neural Network, 2024
Methods And Evaluation Criteria: The proposed method is nearly identical to [1], but it is not self-contained. Regardless of its validity, the authors should have provided a more detailed explanation, as understanding it required constant reference to [1]. This lack of clarity makes it difficult to fully assess whether the method and evaluation criteria are appropriate for the problem.
[1] Jenner et al., Evidence of Learned Look-Ahead in a Chess-Playing Neural Network, 2024
Theoretical Claims: N/A
Experimental Designs Or Analyses: The presentation of the experimental results could be improved, as the figures take too long to understand. The authors should introduce key concepts, such as “log odds reduction” or "residual stream," in Section 2.3 to enhance clarity.
Supplementary Material: I attempted to review the supplementary material, but it was difficult to understand as it is too specific to the chess game.
Relation To Broader Scientific Literature: The scope of this paper is limited to chess, making its connection to the broader scientific literature rather weak.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: N/A
Other Comments Or Suggestions: I believe the authors should clearly explain how their work differs from [1]. In its current form, the paper shows very few distinctions from [1], and even the format of the figures is identical.
[1] Jenner et al., Evidence of Learned Look-Ahead in a Chess-Playing Neural Network, 2024
Questions For Authors: Please refer to the sections above.
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: Thank you for your review highlighting concerns about the paper's distinctiveness from Jenner et al. and its self-containedness. We would make substantial revisions in an updated version:
1. **Novelty vs. Jenner et al.**: We would revise the introduction to more clearly articulate how our work differs from and builds upon Jenner et al. Specifically, we would emphasize that we extend the analysis to the 5th and 7th future moves, reveal the network's use of distinct but consistent internal mechanisms for different move sequences, and demonstrate its ability to consider multiple possible move branches simultaneously. This would address your concern about insufficient distinction.
2. **Self-contained methods**:
- We would enhance the methodology section with clearer explanations of activation patching, log odds reduction, and corrupted boards, so readers don't need to constantly reference Jenner et al.
- We would add an explanation of log odds reduction, defining it as the decrease in log-probability that the model assigns to the correct move after patching. This would address your concern that key concepts weren't introduced in our methodology section.
- We would significantly expand the appendix with detailed descriptions of the implementation details, making the paper less dependent on consulting the Jenner et al. paper.
3. **Presentation improvements**:
- We would improve Figure 2's caption with detailed explanation of what each element represents (log odds reduction, "corrupted" label), addressing your concern that figures took too long to understand.
- We would enhance the clarity of puzzle set notation, making it more intuitive for readers.
4. **Broader implications**: We would strengthen the connection to broader literature in the introduction, emphasizing how the emergence of pattern-sensitive mechanisms suggests neural networks can develop generalized planning strategies applicable to novel situations, challenging the view that transformer systems merely memorize patterns without structured reasoning capabilities. This would address your concern about the limited connection to broader scientific literature.
5. **Differentiation from prior work**:
- We would highlight our unique contributions in the introduction and reiterate them throughout the paper to clearly distinguish our work from Jenner et al.
- We would reiterate specific findings about pattern-sensitive mechanisms (from the Results section) in the Conclusion, which weren't present in Jenner et al.
These proposed revisions would directly address your concerns about the paper's distinctiveness and self-containedness while maintaining our core contributions.
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Rebuttal Comment 1.1:
Comment: Thank you for the detailed response. It would be very helpful if you could provide a more thorough explanation of the methodology, so that readers who are unfamiliar with mechanistic interpretability (including myself) can understand your paper without needing to refer to external sources. That said, I still have some concerns regarding the novelty of the paper. While some of the results are original, others appear to be straightforward extensions of prior work. I think the paper would have been stronger if it had focused more on its ability to consider multiple possible move branches simultaneously, which is not explored in prior work. As the authors responded to my question in a constructive manner, I increase my score from 1 to 2.
Dear AC, although I personally do not find the extension of the analysis to the 5th and 7th future moves particularly novel, I recognize that it may be viewed as a meaningful contribution within the mechanistic interpretability field. I hope this context is taken into account in the evaluation of my score.
---
Reply to Comment 1.1.1:
Comment: Thank you for your additional feedback and the score change. You raise good points about the methodology explanation and novelty of our work.
For the methodology, you're right that we should make it more self-contained. We were constrained by space limitations in the main paper, but we can definitely add clearer definitions of concepts like "log odds reduction" and "residual stream" in the main text while expanding Appendix H to provide better background for readers not familiar with mechanistic interpretability.
On the novelty front, we agree that the alternative branch analysis (showing that the model considers multiple possible move sequences) is our most original contribution beyond Jenner et al. We didn't feature it as prominently in the main paper because we had a smaller dataset for this analysis (609 puzzles vs. 22k for the main analysis), so for that section we focused on the findings with stronger empirical support. We do explore this in more detail in Appendices F and G.
In a revised version, we would do a better job highlighting the multiple branch analysis and what it tells us about planning in neural networks, and expanding the methodological description, especially in Appendix H.
Thanks for engaging with our work and helping us improve it. | Summary: This paper builds on Jenner et al.'s work investigating the look-ahead capabilities of chess-playing neural networks, specifically the Leela Chess Zero policy network. The authors employ patching, probing, and ablation techniques to demonstrate that: 1) Chess models can consider moves up to 7 steps ahead, 2) Models evaluate alternative move sequences simultaneously, and 3) Specialized attention heads handle different aspects of chess puzzle solving tasks (e.g., L12H12 is implicated in transferring information about checkmate scenarios). The paper presents rigorous experimental evidence with detailed analyses across different puzzle types and introduces a novel notation system to classify chess positions.
Claims And Evidence: The claims are well-supported by multiple empirical methods. For each main claim (look-ahead depth, simultaneous consideration of alternatives, and specialized head functions), the authors provide evidence using complementary techniques: activation patching demonstrates causal relationships, probing shows information encoding, and ablation identifies specific components responsible for behaviors. The experimental design is thorough, with careful curation of relevant puzzle subsets and controlling for confounding factors.
Methods And Evaluation Criteria: The methods are appropriate for the mechanistic interpretability questions being investigated. The authors curate subsets of the Lichess dataset specifically targeting different aspects of look-ahead behavior. Their novel notation system for reasoning about multi-step chess sequences effectively manages the combinatorial complexity of possible move sequences, enabling clearer analysis of the model's behavior across different scenarios.
Theoretical Claims: There are no theoretical claims requiring proof in the main paper.
Experimental Designs Or Analyses: The experimental designs are sound and well-executed. The separation of puzzles into different sets based on move square patterns is particularly clever, allowing for disentangled analysis of how the model processes different types of positions. The combination of activation patching, probing, and ablation provides multiple lines of evidence for the claims, strengthening their validity.
Supplementary Material: I reviewed figures in the supplementary material directly referenced in the main paper, which provide additional evidence for the main claims and detailed ablation studies of specific attention heads. The appendices are *very* extensive.
Relation To Broader Scientific Literature: This work fits naturally within the growing field of mechanistic interpretability, a rapidly expanding subfield of AI alignment/interpretability research. It applies techniques previously applied to language models to understand strategic planning in a well-defined domain with clear evaluation metrics. The findings contribute to our understanding of how neural networks may develop planning capabilities, albeit in a toy setting.
Essential References Not Discussed: The references are sufficient, though many lack complete bibliographic information such as URLs or conference details. This is a minor issue that could be addressed in the final version.
Other Strengths And Weaknesses: No additional strengths or weaknesses beyond those already mentioned.
Other Comments Or Suggestions: * On line 84 you write "due to peculiarities of this particular model, explained in Jenner et al. 2024" - if these are not too complex, it would be good to briefly state what they are.
* On line 105 you describe your dataset. You say the solvable levels used for 3 and 5-move analysis were solvable by the Leela model. Were the additional 2.2k and 609 datasets also solvable? What percentage?
* I had difficulty understanding what the "corrupted" line in Figure 2 referred to. This could be clarified in the caption.
* On line 164, column 2 - "we particular" should be "in particular".
## Updates after rebuttal
Thank you for addressing the minor concerns raised in my review. I maintain my score of 4 as I believe this paper deserves to be accepted as a thorough extension of interesting work on the mechanistic interpretability of chess transformers; though it is not ground-breaking enough to warrant a 5.
Questions For Authors: None
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for your positive review and helpful suggestions for improving clarity. We would implement all your recommended changes in a revised version of the paper:
1. **Peculiarities of model**: We would clarify in Section 2.1 that Leela originally takes in past board states in addition to the current one, and that for our analysis, we use the finetuned version from Jenner et al. (2024) that only considers the current board state. This simplifies the generation of corrupted states for activation patching while maintaining equivalent performance to the original model.
2. **Solvability of datasets**: The additional 2.2k puzzles follow the same generation principles as the original 3- and 5-move dataset, and they are also solvable by Leela. However, by design, the 609 puzzles for the alternative branch analysis require Leela to be ambivalent about two different branches (with different move choices) when picking the next move, so Leela assigns a probability of around 50% (in practice, between 30-60%) to the optimal move. Therefore, these puzzles are more difficult for the Leela model to solve.
In a revised version, we would:
- Add text to Section 2.2 mentioning that additional details on the dataset generation and their difficulty level can be found in the appendices.
- Expand the "Dataset generation" section in the appendix to thoroughly explain how the new datasets are generated, and how they differ from the original dataset.
3. **"Corrupted" line clarification**:
In a revised version, we would:
- Enhance the Figure 2 caption to explain that "Corrupted" indicates the square where a piece was (re)moved on the corrupted board, compared to the original board, and that higher values indicate greater importance of that square for the model's decision. This would clarify what the "corrupted" line refers to, as you requested.
- Clarify in the activation patching section that we slightly shift piece positions or remove non-essential pieces to create a position where the originally correct move is no longer optimal, creating a controlled comparison where most board features remain identical except for critical tactical elements.
- Significantly expand the "Generating corrupted puzzles" section in the appendix to explain in detail the creation of the corrupted puzzles.
4. **Grammatical issue**: We would fix "we particular" to "in particular" on page 5, line 258, as you correctly pointed out.
These proposed changes would improve the clarity and completeness of our paper without altering our core findings, following your helpful suggestions. | Summary: This paper extends findings by Jenner et al (2024), which is a mechanistic interpretability paper examining how a chess network--specifically the Leela model, which has transformer architecture--"looks ahead" of game play by several moves. Specifically, the authors examine longer move sequences and possible branching behavior (i.e., alternative possible futures). They adopt a combination of patching, probing, and ablation to identify mechanisms for decision sequences. To do so, they construct a dataset (composed of three different chess puzzle sets, including the Lichess puzzles, for 3-move, 5-move, and 7-move puzzles, and cases with multiple valid move branches. By patching 3rd, 5th, and even 7th move squares, they show you can change Leela’s output — suggesting Leela considers these future moves.
Claims And Evidence: The premise of this paper is exciting, though I have a few concerns with regards to experimental procedure and evaluation.
1. The patched square might be affecting behavior indirectly--via co-adapted features or general heuristics--not because the model is simulating deep future play. In Othello-GPT (Li et al., 2023), and elaborated in Nanda et al. (2023), we see that the the idea that activation interventions like patching can be compensated for by the rest of the network unless you do them carefully--usually by coordinated interventions across layers. This doesn't seem to be addressed in this experimental framework, which may be confounding the results. Specifically, they do not appear to be patching entire sequences of activations (like full attention patterns or residual streams across layers), patching across multiple layers, or compensating mechanism or propagation of the patch forward. As probing and patching show the info is encoded and can affect output, but not necessarily that the model is deliberately using it for decision-making, it would be helpful to know if the authors did address this in some way that was unclear. In other words, "The model can encode 7-move futures" is not the same as "the model plans 7 moves ahead."
2. I didn't notice any adversarial testing or statistical robustness shown--e.g., how many patching cases don’t cause change? This is somewhat important for interpreting results.
3. The introduced notation in Section 2 is oddly complex, making it challenging to interpret results and other parts of the paper. While the notation is intended to categorize chess puzzles based on possible future moves, but reliance on sequences like 112XY or AABCD makes the results and figures harder to interpret without flipping back constantly to decode what each label means. The use of capital letters as placeholders (A, B, X, Y) for “distinct” or “arbitrary” digits is not standard and adds a symbolic burden without offering proportional clarity, and I spent some time wondering where in the alphabet the split occurs (i.e., which letters mean "distinct" versus "wildcard").
4. The binning of the dataset is follows from the notation and is reasonable, though hand-crafted, but is not evaluated statistically. The authors group puzzles using a custom binning scheme based on move destination square patterns (e.g., 112, 12345), but its unclear if there has been validation that these groupings align with meaningful model behavior or chess structure. While the bins are used extensively to interpret activation patching and attention patterns, it seems that their relevance is assumed rather than demonstrated. But this organization is the primary framework used to organize and interpret experimental findings. In other words, the binning may actually align with patterns the authors expect to find, making the results look more structured than they are. Specifically, I am concerned that there is some amount of cherry picking happening. The authors observe strong effects within a specific bins, but never test whether those effects persist across bins or on randomized groupings.
4. I also had the following questions: does the model generalize these look-ahead patterns to unseen or weird positions? Can they compare these results to a randomized or untrained version of the network?
5. The paper relies heavily on activation patching to infer causal importance of future move squares. However, the process used to generate corrupted board states--from which activations are patched--is somewhat unclear to me how it produces minimally changed board states. Is only a modification to one board placement modified? And is it validated that the assumed single patching targets only the intended feature?
Methods And Evaluation Criteria: See above
Theoretical Claims: see above
Experimental Designs Or Analyses: See above!
Supplementary Material: Appendix F provides a compelling extension of the main patching setup, using puzzles with two plausible branches of play to show that the model’s output is sensitive to future move squares from alternative lines. This is a thoughtful design that strengthens the case that the model considers downstream consequences in its reasoning. However, the overall dataset is quite small due to strict filtering, and the patching remains single-layer and local. It would be helpful to test whether the observed effects generalize beyond this niche subset, and whether coordinated interventions across layers confirm that these activations are actually part of a causal planning circuit, rather than salience-driven or compensable signals.
Relation To Broader Scientific Literature: This paper introduces a novel set up for exploring future branch planning in a game setting. While it has some limitations, the findings offer interesting directions for e.g., planning through transformer-based architecture.
Essential References Not Discussed: The citations are reasonable.
Other Strengths And Weaknesses: This paper combines a number of interventions into a more complete suite of interpretability tools. Some of the claims are relatively big, but depending on their responses to my above questions and concerns can be supported.
Other Comments Or Suggestions: See above
Questions For Authors: see above
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your detailed review. We address each point below:
1. **Regarding indirect effects in patching**: We agree that coordinated interventions could strengthen our conclusions, though in this work we restricted our focus to patching at the layer or head level. During our initial preliminary tests, we did perform multi-head patching (possibly heads from different layers) but we did not observe notably different results from the single-head case that would warrant a deeper investigation.
In a revised version, we would:
- Add a limitation in methodology discussion acknowledging that activation patching captures direct causal paths but may miss indirect effects distributed across multiple components
- Acknowledge in the conclusion that we cannot definitively determine whether the observed behavior represents true planning or sophisticated pattern matching, which would explicitly address your concern about distinguishing between encoding information and using it for planning
2. **Statistical robustness**: All puzzle sets shown contained at least 50 puzzles, which we deemed sufficient for statistical reliability. Exceptions are two puzzle sets (with 36 and 49 examples) for the alternative branch analysis, where dataset constraints limited our samples. Our appendix includes results for all qualifying puzzle sets, including those where activation patching shows no meaningful effect on log odds reduction (e.g., set 122 in Figure 8), demonstrating we didn't cherry-pick only positive results.
In a revised version, we would explicitly state that we analyzed all puzzle sets with at least 50 examples to ensure statistical reliability, covering the full range of move patterns in our dataset.
3. **Notation and binning**: We appreciate your feedback on the notation. While we developed it to manage the combinatorial complexity of move sequences, we recognize it could be clearer. Our notation followed the common convention that initial alphabet letters (A, B, C, ...) denote constants, while final letters (X, Y, Z) denote variables. We understand that our use of capital letters and the additional usage of M and N might have contributed to the confusion. In practice, we only use the letters A, B, C, D, X, Y, and Z. The letter M was chosen as shorthand for "mate", and N for "non-(check)mate".
Our binning approach stems from two key considerations:
- As patching is applied to board squares associated with residual stream dimensions, different puzzle sets naturally show qualitatively different behaviors. For example, in set 112, patching cannot distinguish between first and second moves (same square), while in set 123, all moves use distinct squares.
- Our preliminary experiments revealed marked different patching behavior for checkmate versus non-checkmate positions, leading to our M/N prefixes.
We note that some puzzles within sets show behaviors deviating from the typical pattern, suggesting potential additional meaningful categorizations. For instance, in set M112 (Figure 5), most puzzles respond strongly to ablation, but about a quarter present minimal changes.
In a revised version, we would restructure the puzzle set notation section with a clearer explanation of how we categorize puzzles based on the pattern of squares pieces move to.
4. **Generalization to unseen positions**: We use an untrained chess model as a baseline for probing results (dashed lines in Figure 3), showing that Leela encodes future move information that random models don't. In Appendix G, we tested handcrafted positions with two possible checkmates in 2 moves - a scenario absent from the 4 million Lichess puzzles. Despite being unlikely to appear in training data, attention head L12H12 still moves information "backward in time" as expected, suggesting generalization of look-ahead behavior.
5. **Corrupted board state generation**: Our corruption process minimally modifies the board state by changing a single piece's position, which changes the optimal move while preserving most board features. We verify that this process mainly affects the intended feature by showing localized changes in attention patterns.
In a revised version, we would:
- Clarify that we slightly shift piece positions or remove non-essential pieces to create positions where the originally correct move is no longer optimal, creating controlled comparisons where most board features remain identical except for critical tactical elements
- Expand the appendix explanation of corrupted puzzle generation methodology
We believe these proposed changes would directly address your methodological concerns while acknowledging the limitations of our approach. Our multi-faceted analysis using complementary techniques (patching, probing, and ablation) helps mitigate the limitations of any single approach, allowing us to build a more comprehensive understanding of the model's look-ahead behavior. | Summary: The authors use an existing technique for examining chess model internal states to expand the analysis of chess games to more complex positions.
Claims And Evidence: This paper has a common issue for interp papers, the authors don't make strong claims.
Of the three key contributions two (first and last) are not surprising or relevent without generazliation to other domains, while the middle one is an hypothesis without complete support.
Methods And Evaluation Criteria: The methods make sense, but the dataset is similar to the previous work so the results are accordingly narrow.
Theoretical Claims: They present no theorems, and the theory used is from other papers (Jenner et al., 2024).
Experimental Designs Or Analyses: I don't find these methods very convincing, but as they rely on previous papers that is not the question for this review.
The experiments appear to be a direct expansion on the previous work, but without presenting any new theoretical results. This might be relevant to a more specialized community, but the details of Leela's look ahead are not enough to support the claims of larger insights.
Supplementary Material: Briefly all of it
Relation To Broader Scientific Literature: I think there is significant merit in understanding the inner workings of NNs, but this paper does not contribute to the broader understanding. Another venue might be considered by the authors
Essential References Not Discussed: No
Other Strengths And Weaknesses: The expansion of on the previous Jenner paper is good, and maybe will lead to deeper insights in time
Other Comments Or Suggestions: I apologize for my short review, due to circumstances my verbosity is hampered
Questions For Authors: No
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: Thank you for your review. We appreciate your feedback on our paper's contributions and their broader relevance.
We wish to clarify that our work makes several substantive contributions beyond Jenner et al. (2024):
1. While Jenner et al. showed evidence of look-ahead to the 3rd move, we demonstrate that the network can process information up to the 7th move and analyze the mechanisms involved, representing a significant extension of the original work's scope.
2. Our analysis of the model's ability to consider multiple possible move sequences (alternative branches) is entirely novel and not covered in Jenner et al. This finding has important implications for understanding how neural networks can develop tree search-like capabilities without explicit programming.
3. Our identification of specialized attention heads for different types of positions (e.g., checkmate vs. non-checkmate scenarios) provides new mechanistic insights into how neural networks develop specialized components for different strategic contexts.
Regarding broader relevance, our findings about emergent planning capabilities in neural networks extend beyond chess. They contribute to our understanding of how models can learn to simulate future states and alternative possibilities through training—a capability relevant to autonomous systems, robotics, and any AI that needs to plan multiple steps ahead in complex environments.
We understand your concern that our paper may not make strong claims beyond Jenner et al., and that the generalization to other domains is limited. We would address these issues in a revised version of the paper as follows:
1. **Strengthen our claims with additional supporting evidence**:
- In the introduction, we would clarify our contributions beyond Jenner et al., emphasizing that we not only extend to higher move counts but also identify pattern-sensitive mechanisms that operate across different time horizons.
- We would add a section highlighting that our observed attention patterns represent meaningful structure rather than cherry-picked examples, providing evidence that our findings represent general mechanisms rather than isolated observations, strengthening the validity of our claims.
2. **Improve generalization**:
- We would emphasize more clearly that the specific patterns attention heads respond to appear to be time-insensitive, suggesting the model has learned general pattern-matching mechanisms across time rather than timing-specific heuristics. This directly addresses your concern about generalization by showing that the patterns we've identified are not specific to particular time steps but represent general strategies.
- We would revise the conclusion to emphasize the claim of pattern-sensitive mechanisms that could generalize beyond chess, making our contribution more broadly relevant to AI reasoning.
3. **Clarify theoretical importance**:
- We would enhance the introduction to connect the emergence of pattern-sensitive mechanisms to broader questions about how neural networks can develop generalized planning strategies applicable to novel situations.
- We would strengthen the conclusion about challenging "simplistic views of neural networks as merely statistical pattern matchers," highlighting the theoretical significance of our findings beyond the narrow domain of chess.
While our work builds on Jenner et al., we believe these proposed revisions would highlight our novel contributions to understanding how neural networks develop sophisticated look-ahead capabilities that could inform AI research beyond chess. | null | null | null | null | null | null |
Algorithms with Calibrated Machine Learning Predictions | Accept (spotlight poster) | Summary: This paper introduces calibration as a tool to enhance learning-augmented algorithms, focusing on two problems: ski rental and online job scheduling. The authors propose algorithms that leverage calibrated predictions to achieve instance-specific competitive ratios, theoretically and empirically outperforming methods like conformal prediction. Experiments on real-world datasets (Citi Bike rentals and sepsis triage) validate their approach.
Claims And Evidence: The claims made in the submission are supported by clear and convincing evidence.
Methods And Evaluation Criteria: The proposed methods make sense for the problem.
Theoretical Claims: I checked the correctness of some claims but didn't go through all the proofs. The proofs that I have checked are reasonable and sound.
Experimental Designs Or Analyses: I only made a quick pass on experimental designs, and it looks reasonable. Note that the main contribution of this paper is theoretical.
Supplementary Material: I didn't review the supplementary material.
Relation To Broader Scientific Literature: The key contribution of this paper is a new concept of the learning-augmented algorithm, i.e., using calibration to enhance the prediction. This is new and does not exist in the literature.
Essential References Not Discussed: All necessary related works are discussed in the submission.
Other Strengths And Weaknesses: Strengths:
1. The paper proposes a new concept (i.e., calibrated prediction) for learning-augmented algorithms; this bridges the gap between global uncertainty assumptions in learning-augmented algorithms and modern ML models with local uncertainty estimates. Calibration is framed as a practical, instance-specific alternative to conformal prediction. This concept looks more practical compared to the existing prediction concepts.
2. From the theoretical view: for ski rental, the proposed algorithm achieves an expected competitive ratio bounded by calibration error and mean-squared error (Theorem 3.1). The authors also provide the lower bound (Theorem 3.4) shows near-optimality. For job Scheduling: By analyzing finer-grained calibrated predictors, the paper demonstrates reduced inversion costs (Theorem 4.3), improving upon prior work that relied on binary predictions.
3. This paper also includes the experimental results. They did experiments on real data (Citi Bike and sepsis) to demonstrate performance gains, linking theory to real-world applications.
Weakness:
There are some weaknesses in the results that were obtained. For ski rental, the ratio of the proposed algorithm (theorem 3.3.) is related to alpha, which is the calibrated error. This makes the algorithm lose its robustness. In the worst case, alpha can be very large. As the authors show in the lower bound theorem (theorem 3.4), the lower bound does not rely on alpha. For job scheduling, the obtained results rely on the iid assumption for features; this may not be true in reality.
Overall, although there are some weaknesses in the paper, I am still happy to see this paper in the proceeding since the paper proposes a new concept in learning-augmented algorithms, which might lead to some future works. Besides this, I also think that the theoretical understanding of this calibrated prediction concept would have a positive impact on reality. Thus, I recommend the acceptance.
Other Comments Or Suggestions: n/a
Questions For Authors: n/a
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We’re glad that the reviewer shares our excitement about calibration as a novel and practical prediction concept for algorithms with predictions with lots of theoretical potential!
**“The expected performance bound for ski rental scales with max calibration error, which can be large, so the algorithm is non-robust.”**
We thank the reviewer for the opportunity to clarify this point — while our global (Theorem 3.1) and prediction-level (Theorem 3.3) performance bounds degrade with larger calibration error, we note that the expected competitive ratio of our algorithm for ski rental will never exceed 3. This fact is not immediately obvious, and we will add an explanation to our discussion on worst-case expected performance in line 211 of Section 3.3 to help contextualize the 1.8 bound when calibration error is zero. The idea is that when the max calibration error is larger than ⅓, the algorithm executes a worst-case renting strategy that is 2-competitive. For max calibration error of at most ⅓, the bound from Theorem 3.3 can be no larger than 3.
**“The results for job scheduling rely on an IID assumption that may not hold in reality”**
Though prior work in ML-augmented scheduling (Cho et al., 2022) also assumes independence for the sake of simplifying the prediction task, we agree that features are likely to exhibit some level of correlation in real-world job scheduling contexts. The difficulty of the prediction task grows exponentially in the number of jobs when arbitrary correlations are allowed, but we see allowing for limited correlations as an interesting direction for future work to continue narrowing the gap between theory and practice. | Summary: The paper studies how calibrated machine learning predictions can improve online algorithms. The paper focuses on two settings: the ski rental problem and online job scheduling.
In the ski rental problem, the predictions is about whether the skier will ski for more than a given threshold $b$ days using a calibrated binary predictor $f(X)$ where a calibrated $f(X)\in[0, 1]$ prediction means that it matches the actual likelihood of skiing more than $b$ days. The calibration error is the max calibration error, which measures the largest deviation from perfect calibration for any prediction.
In job scheduling, the model predicts the priority of each job using a calibrated probability score rather than a binary label, which allows for a finer-grained job ordering. Jobs are then scheduled using a threshold-based rule. In this setting, the authors consider the predictors to be perfectly calibrated.
In both settings, the authors show that the algorithm performance can be improved using calibrated predictors.
Claims And Evidence: Yes
Methods And Evaluation Criteria: Yes
Theoretical Claims: Yes
Experimental Designs Or Analyses: Yes
Supplementary Material: No
Relation To Broader Scientific Literature: The paper may relates to broader literature in AI-assisted decision-making where AI provides predictions for decision-making tasks.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: I like the idea of bringing the calibration to ensure the trustworthy property of provided predictions to the decision-makers. Unlike prior work that assumes global uncertainty of predictions, this approach uses instance-specific calibrated predictions, which can lead to more refined decision-making in the considered both ski rental and job scheduling problems. The authors also run a some experiments and it is good to see that the results indeed matches the theoretical findings.
Perhaps one of the weakness is the calibration metric considered in the paper. In the ski rent problem, the paper considers the max calibration error (i.e., a worst-case perspective), which sounds a bit weird to me, especially given that the authors have already assumed the underlying uncertainty is from distribution. One natural metric here should be expected calibration error, right?
Also, in the job schedule problem, the authors consider perfectly calibrated predictions, which is strong assumption. Could the results be generalized to a setting with predictors that may have certain calibration error here?
Other Comments Or Suggestions: See above
Questions For Authors: See above
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We appreciate the reviewer’s feedback and are glad that they value our high-level goal of using calibration as a tool to ensure the trustworthiness of predictions provided to decision makers.
**“Do the job scheduling results generalize to predictors with non-zero calibration error?”**
Yes, our results extend beyond perfectly calibrated predictors. We presented our results in terms of perfectly calibrated predictions to highlight the intuition that finer-grained predictions reduce sequencing errors, but they generalize to any predictions that are monotonically calibrated. Monotonic calibration is the weaker condition that the empirical frequencies $\Pr(Y=1 \mid f(X))$ are non-decreasing in the prediction $f(X)$. This property holds trivially for perfectly calibrated predictors, but zero calibration error is not required. In fact, many calibration approaches used in practice (e.g. Platt scaling (Platt 1999) and isotonic regression (Zadrozny and Elkan 2002; 2003)) fit a monotonic function to data of the form $(f(X), \Pr(Y=1 \mid f(X))$, leading to a monotonically-calibrated predictor with non-zero calibration error.
Thanks for pointing out that the statement of Theorem 4.3 appears brittle due to the assumption on perfect calibration. We’ll add a note that the result generalizes to predictors with non-zero calibration error and include full details for the more general case in the appendix.
**“For ski rental, is an average error metric like expected calibration error (ECE) more thematically appropriate than a worst-case metric like max-calibration error (MCE)?”**
Designing an algorithm that relies on ECE instead of MCE is an interesting direction for future work, and we will add it as an open question to Section 6. We suspect a global performance bound similar to Theorem 3.1 may still be recoverable in that setting. To the reviewer’s point, when MCE is significantly larger than ECE, Algorithm 1 makes conservative decisions, which suggests room for improvement. The fundamental challenge is that under ECE, prediction-specific performance bounds like those from Theorem 3.3 would only hold for predictions which are not “too miscalibrated,” rather than for all predictions.
Nonetheless, MCE aligns with our goal of providing prediction-specific performance guarantees based on practical error metrics. Importantly, MCE is only worst-case with respect to the finite set of predictor outputs and not the distribution over instances. This means that MCE can be estimated from data, allowing for practical, data-driven guarantees. | Summary: The paper introduces a novel idea of leveraging calibrated predictors to design learning-augmented algorithms. Instead of proving consistency, robustness, and smoothness guarantees, which are worst-case guarantees, the authors derive bounds that depend on the predictor's maximum calibration error. They apply this approach to the ski-rental problem and a variant of the single-machine scheduling problem where all the jobs have unit sizes but different priorities. They also support their theoretical findings with extensive experiments (in Section 5 and Appendix C).
## update after rebuttal
The authors addressed most of my major concerns and questions during the rebuttal period. I am now convinced that the paper, after including the improvements discussed with the authors during rebuttal, would make a nice contribution to the literature of learning-augmented algorithms, and I have increased my score accordingly.
Claims And Evidence: Yes
Methods And Evaluation Criteria: Yes
Theoretical Claims: I read the proofs in the main paper (first 8 pages) and checked their correctness. I did not read the proofs in the appendices, but the proof sketches explained in the paper seem correct and convincing.
Experimental Designs Or Analyses: The experiments are well explained and their results are sound.
Supplementary Material: I briefly read some proofs in the supplementary material, and reviewed the experiments in Appendix C.
Relation To Broader Scientific Literature: The paper contributes to the literature on learning-augmented algorithms. Instead of assuming that the predictions given to the algorithms can be arbitrary, the authors propose to leverage predictors with bounded calibration errors to prove new bounds, that improve upon prior works in some settings.
Essential References Not Discussed: The setting studied in this paper appears related to algorithms with distributional predictions, where predictions correspond to probability distributions rather than specific realizations. However, the paper does not reference or compare with this line of work. Relevant papers include:
- "Binary Search with Distributional Predictions" (Dinitz et al., 2024)
- "Contract Scheduling with Distributional and Multiple Advice" (Angelopoulos, 2024)
- "Learning-Augmented Binary Search Trees" (Lin et al., 2022)
Additionally, in Section 3.3, the discussion on the tradeoff between worst-case guarantees (consistency/robustness) and the average performance is related to the paper "On Tradeoffs in Learning-Augmented Algorithms" (Benomar et al., 2025), which considers, for the ski-rental problem, a predictor of the form **1**$(z > b)$ that is accurate with probability q and studies trade-offs between consistency, robustness, smoothness, and the average-case performance of the algorithm.
Other Strengths And Weaknesses: The idea of using the calibration of the predictor to improve the bounds of learning-augmented algorithms is interesting and might inspire future work. However, unfortunately, the paper has many weaknesses, some of which can easily be addressed but others raise more serious concerns
**Inaccurate claims for motivating the setting:**
- The abstract mentions that the framework of learning-augmented algorithms "often
assumes uniform reliability across all predictions". This is inaccurate, or at least not clearly stated. The theoretical framework of learning-augmented algorithms makes no assumptions on the reliability of the predictions, and this is why its objective is to prove consistency and also robustness guarantees.
- (First page, first paragraph of the right column) The authors claim that most prior work focuses on extreme settings where predictions are either entirely accurate or completely uninformative. This is again not true. Most prior work also examines how algorithm performance scales with the sum of all errors, providing bounds that hold even when predictions are imperfect (smoothness). These results allow for performance guarantees when some predictions are accurate while others are not, and induce such bounds when the problem variables and predictions are stochastic.
**Unconventional/Inadequate notation and terminology**.
- The competitive ratio, as defined in the paper, is instance-dependent (it depends on the distribution D), whereas the standard definition refers to the worst-case ratio over all possible instances.
- The "additive competitive ratio" introduced in the paper is also instance-dependent and **is not even a ratio**. Calling it a competitive ratio is very inadequate and misleading. Moreover, it is not a suitable performance measure for the online scheduling problem (discussed further later).
- The notation ALG(A,I) to denote the output of algorithm A on instance I is unconventional. The standard notation would simply be A(I) (or ALG(I) if the algorithm is denoted ALG), as used for the optimal offline algorithm, denoted OPT(I), not ALG(OPT, I).
- The paper consistently uses the term "prediction-aided algorithms" instead of the standard term "learning-augmented algorithms".
**Inadequate performance measure: "additive competitive ratio"**.
In the online scheduling problem, what the authors refer to as a "competitive ratio" is actually a regret term E[ALG - OPT]. This terminology is very inadequate and misleading.
Standard performance evaluation for online algorithms typically uses the competitive ratio, defined as the worst-case ratio ALG/OPT, which provides a scale and size-independent comparison to the optimal solution.
It serves as a multiplicative approximation factor to the optimal solution. This is a standard approach in broader fields of algorithm design, where attaining optimal performance is either impossible or complex, and the aim becomes instead to have algorithms approximating the optimal output up to a multiplicative factor (NP-hard problems, heuristic algorithms,...).
Regret terms like E[ALG - OPT] are more common in online learning, where the goal is to analyze the rate at which ALG/OPT approaches 1. A more relevant regret measure in online algorithms would be E[ALG - CR * OPT].
Prior work on online scheduling in the learning-augmented setting (e.g., Cho et al., cited in the paper) evaluates algorithms using the standard competitive ratio.
The paper’s use of regret makes it difficult to compare results with existing literature and raises concerns about the relevance of the findings since regret analysis is not adapted for the considered setting.
**No robustness**
- The setting of the paper can be viewed as the standard learning-augmented setting with a different error measure, which is a combination of the calibration error and the instance-wise prediction error ($\eta$ in ski-rental). While their algorithms for both ski-rental and scheduling are 1-consistent, the authors do not prove any robustness bounds on their performance, that hold independently of the error (i.e. even if the error is arbitrarily large).
Other Comments Or Suggestions: Minor comment:
- L 144 (right column): $k$ is introduced but it is not yet defined at this point.
Questions For Authors: - For the ski-rental problem, the paper considers a binary target variable and derives bounds based on the mean squared error (MSE) of the predictor $f$. However, in binary classification, binary cross-entropy is the default error measure and is commonly used for training calibrated classifiers. Can the authors justify why MSE is an appropriate choice in this context?
- MSE and calibration errors are presented as unrelated error measures. Are there any correlations/bounds between them? Are there any existing classifiers that minimize both the MSE and the max-calibration error? (i.e. is it indeed possible to have both $\alpha$ and $\eta$ close to 0)
- In Section 3.3., it is mentioned that the bound of Theorem 3.3 shows that the algorithm always has an expected competitive ratio of at most 1.8 when the classifier is calibrated. If the classifier is calibrated, i.e. $\alpha = 0$, then the bound becomes $1 + \min(\mathbb{E}[f(X)], 2\sqrt{\eta})$. Could the authors explain why this is always less than 1.8?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We sincerely thank the reviewer for their detailed feedback. However, we believe there may have been a significant misunderstanding regarding key aspects of our paper. Below, we address each concern in detail and respectfully ask that the reviewer reconsider their evaluation based on these clarifications and feedback from other reviewers.
**Motivation of the setting.**
We believe the reviewer’s concerns stem from a misunderstanding of our motivation for calibrated predictions:
- When stating that learning-augmented algorithms “often assume uniform reliability across all predictions” in the abstract, our intention was to highlight a reliance on global parameters that reflect a user's trust in the predictions in aggregate (e.g., often denoted $\lambda \in [0,1]$ in prior work, with $\lambda = 1$ indicating no trust and $\lambda = 0$ full trust). Our approach uses prediction-level uncertainty from calibration to eliminate the need for parameter tuning. We will revise line 015 of the abstract accordingly. Reviewer eD7y recognized this distinction, stating "this paper bridges the gap between global uncertainty assumptions in learning-augmented algorithms and modern ML models with local uncertainty estimates."
- The reference to “extreme settings” on page 1 was meant only to illustrate the endpoints of the global uncertainty parameter, not to imply that existing work studies these extremes. We will clarify this in line 015, column 2 to avoid ambiguity.
**Essential references.**
We appreciate the reviewer’s insightful connection to distributional predictions. We will cite the suggested references (and “Learning Online Algorithms with Distribution Advice” (Diakonikolas et al., 2021)) in Section 2.1, noting that they are conceptually related but do not study uncertainty quantification.
Regarding the **concurrent work** (posted on arXiv on 1/22/25) by Benomar et al. (2025), their approach gives average-case bounds for ski rental assuming access to a predictor that correctly guesses $I(Z > b)$ with known probability for any input. This type of assumption — often called “conditional coverage” in the ML literature (see, e.g., “Distribution-free Prediction Bands for Nonparametric Regression” (Lei and Wasserman 2012)) — enables better bounds, but is much stronger than our calibration assumptions.
**Performance measures.**
We strongly disagree that our performance measures are inadequate.
- As Reviewer v9Cf stated, “in theory, the expected competitive ratio is the most common objective and evaluation criterion for these types of algorithms,” supporting our methodology. Indeed, the expected competitive ratio we employ has precedent in sample-based learning-augmented algorithms (e.g., Diakonikolas et al., 2021; Anand et al., 2022), which align closely with our approach.
- We will update our terminology from “additive competitive ratio” to “regret,” as suggested. Many prior works on learning-augmented scheduling algorithms employ regret, with results given as explicit additive bounds (e.g., “Learning-Augmented Algorithms with Explicit Predictors” (Elias et al., 2024); “Non-clairvoyant Scheduling with Predictions (Im et al., 2023)), or later converted to competitive ratios (e.g., “Permutation Predictions for Non-Clairvoyant Scheduling” (Lindermayr and Megow 2022). Though Cho et al. (2022) follow the second approach, bounding expected regret is a core component of their analysis.
We will add this context to the third paragraph of Section 2.
**Robustness.**
We agree that our paper differs from traditional robustness analyses. Our primary objective is bounding expected performance degradation based on calibration error (CE), which captures robustness in our distributional setting. We will clarify this after the definition of CE in Section 2. Please see the responses to Reviewers wjo6 and eD7y for discussion on performance guarantees when CE may be large.
**“How are MSE and CE related, and can both be 0?”**
A classic result from “On Subjective Probability Forecasting” (Saunders 1963) decomposes MSE into a sum of non-negative refinement and calibration terms. This means $MSE=0$ implies $CE=0$. We will note this after the definition of CE in Section 2.
**“Why MSE and not binary cross entropy (BCE)?”**
We use MSE because its refinement term arises naturally in our analysis, and its calibration term is a standard error measure. While a similar decomposition holds for BCE, its refinement and calibration terms are not well-suited to our setting. We thank the reviewer for highlighting this mismatch between the error metrics used to train an ML model vs provide performance guarantees; it is a gap that remains between theory and practice, and an interesting question for future work that we will add to Section 6.
**“Why is the expected CR at most 1.8 when CE is zero?”** When $\alpha=0$, the prediction-level upper bound from Theorem 3.3 achieves a maximum value of 1.8 at $v=0.8$. We will add this brief explanation to Section 3.3.
---
Rebuttal Comment 1.1:
Comment: I thank the authors for their detailed response.
**Competitive ratio.**
Regarding performance measures, the competitive ratio is indeed the standard measure for analyzing online algorithms, and I did not claim otherwise. My point was that the competitive ratio is defined as the **worst-case** ratio over all possible instances, whereas the definition you consider in the current paper is instance-dependent (it depends on the distribution $D$). For example, in "Learning Online Algorithms with Distributional Advice" (Diakonikolas et al.), which you cited in your response, the authors establish **worst-case** guarantees on the ratio $\text{cost}(A, D)/\text{OPT}_D$ over all distributions $D$ in a given class $\mathcal{C}$, independent of the specific distribution.
**Regret.**
Regarding the regret analysis, I agree that using it is reasonable. I guess my main concern was with the terminology: referring to it as an "additive competitive ratio" was highly misleading.
### **Robustness**
The major remaining weakness is the lack of robustness guarantees. As I noted in my review, while the authors introduce calibration error as their chosen error measure, which is well-motivated, it does not replace the need for robustness guarantees.
- For the ski-rental problem, the authors stated in their response to reviewer eD7y that the ratio $\text{ALG}/\text{OPT}$ is always at most 3. However, this holds only because their algorithm assumes knowledge of the max-calibration error $\alpha$. In the context of learning-augmented algorithms, an algorithm is considered robust if it can still perform reasonably well without any knowledge of prediction quality. This is why I am not convinced by the robustness claimed in the authors response.
- Additionally, in prior work, if the maximum prediction error (under any given error measure) is known, the parameter $\lambda$ can be chosen optimally, eliminating the need for tuning it. Thus I also don't agree with the claim that the approach of the paper eliminates the need for tuning the levels of robustness and consistency.
- The same issues arises in the scheduling problem, where no robustness bounds are provided. The authors’ explain in their response that their bounds capture robustness based on calibration error. However, error-dependent bounds, which indeed ensure bounded performance degradation for bounded error, indicate "smoothness" rather than "robustness". Robustness, on the other hand, requires guarantees that hold even under arbitrary prediction errors.
### **Other comments**
I am satisfied with the authors’ responses to my other comments and questions, and encourage them to include the corresponding discussions in the paper.
I have slightly raised my score, but I still do not recommend acceptance, as robustness remains a fundamental requirement (alongside consistency and smoothness) when designing algorithms with predictions. I would be happy to reconsider my score if the authors address this concern during the discussion period.
---
Reply to Comment 1.1.1:
Comment: We thank the reviewer for their continued engagement and willingness to reconsider their evaluation. After reflecting carefully on the latest comments, we believe it is possible to address the remaining concerns raised regarding robustness. We’re grateful for this suggestion, which we agree will strengthen the paper, and hope these clarifications will encourage the reviewer to raise their recommendation into the acceptance range.
To begin, we briefly reiterate the core motivation of our paper: addressing critical gaps between theory and practice in algorithms-with-predictions. A significant gap is the widespread reliance on the maximum prediction error in prior work—a worst-case metric that is inherently impossible to estimate reliably. To clarify the distinction in our setting:
- **The max calibration error $\\alpha$ of a ML predictor is estimable**. As noted in our response to Reviewer wj06, $\alpha$ is defined as a maximum expected calibration deviation over the finite set of predictor outputs. Importantly, this quantity is not worst-case with respect to the underlying input space. In fact, an estimate of $\\alpha$ is a natural byproduct of post-hoc calibration procedures used in practice.
- In contrast, **the maximum prediction error of a ML predictor—as used in prior work—is not estimable given finite samples**, since it is defined as a supremum over the input space. To illustrate, consider two distributions that differ only in a single point label (one label 0 and the other labeled 1, for example). If the support of the distributions is continuous or large, no ML model can statistically distinguish between these distributions given finite samples. Thus, for any ML model, there are distributions where its maximum prediction error is arbitrarily large.
In light of the fact that knowledge of $\\alpha$ is a reasonable assumption in practice, the primary focus of our paper is strong average-case performance when given (1) query access to the ML predictor and (2) additional (attainable) calibration metrics. The second requirement clearly differentiates our approach from prior work. Nevertheless, directly addressing the reviewer's concern, we have found that it is indeed possible to incorporate worst-case robustness guarantees, which we will add to the final version of the paper:
- For ski rental, an analysis similar to that of Theorem 15 in Anand et al. (2020) shows that Algorithm 1 is $g(\alpha)$-robust, where $$g(\\alpha) = \\begin{cases} 1 + \sqrt{\\frac{1+\\alpha}{\\alpha}} &\text{if } \\alpha \\in [0, \\frac{1}{3}) \\\\ 2 &\text{if } \alpha \\in [\\frac{1}{3}, 1] \\end{cases}$$ (a decreasing function of $\\alpha$). This is because Algorithm 1 executes a worst-case 2-competitive strategy when $\\alpha \\geq \\frac{1}{3}$, and as noted in line 140 column 2, Algorithm 1 never buys skis before day $b\\sqrt{\\frac{\\alpha}{1+\alpha}}$ for $\\alpha < \\frac{1}{3}$. If $g(\alpha)$ is larger than some desired robustness threshold $\\beta$, one can artificially increase $\\alpha$, running the algorithm using a max calibration error bound of $\\alpha’ > \\alpha$ such that $g(\\alpha’) < \\beta$. As seen from the expected performance bounds in Theorems 3.1 and 3.3, this adjustment will come at the cost of average-case performance, highlighting the tradeoff between average and worst-case performance.
- For scheduling, we generalize the approach of Cho et al. (2022) by allowing for predictions from an arbitrary calibrated predictor. The error metric in this setting is not calibration error (see the response to Reviewer wjo6 about how we only require monotonic calibration), but rather the generalized false negative/false positive rates $\\epsilon_0$ and $\\epsilon_1$, which represent the discriminative power of the predictor. Since we recover the regret bounds from Cho et al. (2022), our approach inherits their robustness guarantees, which hold when $\\epsilon_0 = \\epsilon_1 = \\frac{1}{2}$, i.e., the predictions are truly random.
By justifying knowledge of the max calibration error $\\alpha$ in practice and giving explicit robustness guarantees, we directly address the reviewer’s remaining concerns and illustrate the fundamental tradeoff between robustness and average-case performance. We thank the reviewer again for their suggestions and hope these clarifications fully resolve the issue. | Summary: The paper initiates the study of the effect of calibration in algorithms with predictions through two case studies:
1. Ski Rental: The authors design an algorithm that achieves optimal prediction-dependent performance, bounding the expected performance using both the squared error and the calibration error. They proved that calibrated predictions can outperform the conformal prediction method for infinitely many instances.
2. Online Job Scheduling: They prove that a properly calibrated predictor with finer-grained confidence levels yields better performance bounds than prior work.
The theoretical findings are supported by experiments on real-world datasets, showing that the proposed algorithms leveraging calibrated predictions outperform the baselines.
Claims And Evidence: Most of the claims in the paper are convincing, but I have two concerns:
1. Clarification on Line 347-348 (Right-Hand Side): When you state that the bound is "tight," does this mean that there is a matching lower bound, or does it imply that the upper bound is optimal? A clearer explanation of what "tight" means in this context would be helpful.
2. Comparison with Conformal Prediction Methods: The claim that "there exist infinitely many families of distributions where calibrated predictions outperform conformal prediction methods" does not necessarily mean superiority. To make a stronger argument, you would need to show that the inverse does not hold—i.e., that there are no such infinite families where conformal prediction consistently outperforms calibrated predictions. Additionally, since the bound includes the squared loss, it is unclear whether calibration itself is responsible for the improved performance. A predictor with high squared error, even if well-calibrated, might still yield a poor bound. Authors might need to be careful to make a strong claim.
Methods And Evaluation Criteria: Yes, in theory, the expected competitive ratio is the most common objective and evaluation criterion for these types of algorithms. Additionally, the chosen dataset is appropriate and aligns well with the study's objectives.
Theoretical Claims: I checked the proofs in Section 3 and they seem to be correct. For Section 4, I briefly reviewed the proofs but did not check the details in depth.
Experimental Designs Or Analyses: The experimental design appears to be valid and well-structured. However, based on the figures, I am not fully convinced that the algorithm with calibrated predictors consistently outperforms the conformal prediction baseline.
Supplementary Material: No, I did not run the code.
Relation To Broader Scientific Literature: The paper initiate the study of calibrated predictors for algorithms with predictions, and provided interesting theoretical analysis for two case studies.
Essential References Not Discussed: To the best of my knowledge, the paper appropriately cites all essential related works.
Other Strengths And Weaknesses: Strengths:
1. The paper is innovative, being the first to study the effect of calibration in algorithms with predictions. The proposed algorithms and analysis are novel and interesting.
2. The writing is clear and well-structured.
Weaknesses:
1. The techniques and results for the two case studies feel somewhat disconnected. It remains unclear, at a high level, why and when calibration is beneficial for algorithms with predictions. A more detailed explanation and discussion would strengthen the paper.
2. The experimental results are not entirely convincing. As mentioned earlier, it is unclear whether the algorithm with calibrated predictors consistently outperforms the conformal prediction baseline. Additionally, it would be valuable to include experiments that vary the calibration error (while controlling for squared loss, if possible) to empirically demonstrate how calibration affects performance.
Other Comments Or Suggestions: 1. Line 779: Did you define K_1(f,D) in the paper?
Questions For Authors: Could you clarify the conclusion that the calibration-based algorithm outperforms the conformal prediction method? The theoretical results suggest that the conformal prediction approach fails in certain cases, but this does not necessarily imply that the calibration-based method is strictly superior in general. Could you provide additional theoretical justification to support this claim?
Additionally, I would appreciate further clarification on the concerns raised earlier.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We thank the reviewer for their thoughtful feedback! We’re encouraged that they find our application of calibration to algorithms with predictions innovative, and our algorithms and analysis novel and interesting. In addition to the modifications detailed below, we will correct the typo on line 776 for the camera-ready version of the paper.
**“Does the calibration-based algorithm outperform the conformal prediction method for ski rental?”**
We see the calibration-based and conformal prediction-based algorithms as two orthogonal approaches with neither being strictly superior. We solely aim to point out (e.g. in lines 42 column 2, 78 column 1, 244 column 1, and Theorem 3.7) that calibration offers advantages in situations where conformal predictors struggle: (1) when only binary targets are available for training an ML model, or (2) there is high variance in the target that is unexplained by the features. In general, the better method will depend both on the underlying ML model and the distribution over features and instances. This can be seen in the ablations for different models in the appendix, and we will modify the conclusion from lines 427-428 column 1 to better communicate this fact.
**“Lines 347-348 column 2: what does it mean that the bound is tight?”**
Thank you for pointing out this imprecise wording. It will be replaced by “the inequalities hold with equality.”
**“Why and when is calibration beneficial for algorithms with predictions?”**
This is a great question. Calibration is beneficial for algorithms with predictions in settings where (1) the goal is good performance over a distribution of instances, (2) there is a binary quantity of interest that is predictable, and (3) probabilistic estimates of this quantity are sufficient to make good decisions. Both case studies we consider fall under this framework. In ski rental, we provide a principled approach for decision making given a probabilistic estimate of whether a skier will ski for at least b days. For job scheduling, there is an optimal scheduling strategy based on the probabilities that each job is high priority.
To see why calibration is beneficial, notice that in a Bayesian sense, the best possible probabilistic estimate of a binary quantity $Y$ given any (potentially untrusted) prediction $f(X)$ of $Y$ is $\Pr(Y=1 \mid f(X))$. Computing these probabilities corresponds exactly to calibrating the original predictor $f$ over the input distribution, but this post-hoc correction is not always possible (for example, if the decision-maker does not have access to the full ML model and data). As a result, (approximate) calibration is a precondition for the decision-maker being able to generate reliable probabilistic estimates of the quantity of interest. If there are no calibration guarantees, we enter the classic realm of algorithms-with-predictions, where algorithms need to be robust against arbitrarily error-prone predictions. This is the reason calibrated predictions are often referred to as “trustworthy.” We agree that a discussion of this kind in Section 6 will help to unify and strengthen the paper, and we thank the reviewer for this recommendation.
**“Can experiments vary calibration error while controlling for squared loss?”**
Because calibration error is an additive component of the mean-squared error — see the response to Reviewer Buyh on their relationship for more details — varying calibration error necessarily changes the mean-squared error. This makes it difficult to design an experiment, such as the one that was suggested, that isolates the effects of calibration error vs overall predictor efficacy.
---
Rebuttal Comment 1.1:
Comment: I would like to thank the reviewers for answering my questions. I will keep my score. | null | null | null | null | null | null |
One Image is Worth a Thousand Words: A Usability Preservable Text-Image Collaborative Erasing Framework | Accept (poster) | Summary: This paper aims to solve the problem of concept erasing for images with visually undesirable or even harmful content. The authors first analyze the issues presenting in the prior works, which are actually caused by the sole use of text prompts. To overcome this, a new framework, called Co-Erasing, is proposed, which aims to integrate the images features with the text prompts. A refinement module is then proposed to better use the text-guided image concept.
Overall speaking, the motivation of this paper is interesting. The authors found the critical issues of priors work and propose a new method to conquer these issues. The idea of this paper also interesting.
Claims And Evidence: The authors have pointed out the limitations of previous works about the text-only erasing strategy and perform experiments to show how the proposed approach works and performs better than previous works.
Methods And Evaluation Criteria: - The proposed method is interesting. Instead of soly using the text prompts, this paper proposes to integrate the images with text embeddings first and then design a refinement module to extract the target concept. This design makes sense as the text prompts themselves do not consider the image content, which is actually essential to generate better target concept.
- The evaluation of this paper makes sense. The authors clearly show how the proposed method balances the efficacy and general usability.
Theoretical Claims: There are no theoretical proofs or analysis.
Experimental Designs Or Analyses: - In Sec. 5.3, the authors explicitly discuss how the text-guided refinement works? However, there is actually no deep analysis on this. The authors only show some contrast images and demonstrate that with the proposed approach, the results in terms of multiple metrics can be improved. I am supposed that there should be some feature analysis or statistically analysis to support the argument.
- According to the experiments, mixing the images features with the text embeddings is essential as shown in Table 1. It is good to see these experiments. However, the descriptions on is too simple. Have the authors analyze how the image modality helps in the proposed method?
Supplementary Material: No supplementary material provided.
Relation To Broader Scientific Literature: The key contributions of the paper are interesting. They are different from previous works.
Essential References Not Discussed: No
Other Strengths And Weaknesses: Other weaknesses:
- In the last part of the introduction section, the authors summarize three key contributions of this paper. The second one is a new framework and the third one is the refinement module. It seems that the refinement module is actually part of the overall framework. Should they be merged together?
- It is good to see some analysis in the appendix. It would be good to move this part to the main paper if there is extra space available.
Other Comments Or Suggestions: - The abstract of this paper is too long, which can be trimmed a little bit.
- The architecture figure in Fig. 7 is too simple, which does not bring too much information.
Questions For Authors: No other questions.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your valuable comments! Due to space constraints, we include `additional_tables.pdf` and figures at the following link: https://anonymous.4open.science/r/icml25_rebuttal-8608. References to $\textcolor{blue}{\text{Table}}$ and $\textcolor{blue}{\text{Figure}}$ in our responses correspond to the tables provided in this link.
> Q1 Feature or statistically analysis to support how text-guided works.
**A1**: We conduct a **feature space analysis** to provide deeper insight into how the proposed **text-guided refinement** works at the embedding level. Concretely, we extract CLIP embeddings of images and visualize their movement in the latent space before and after refinement using PCA projection. This visualization clearly shows that the refined features consistently move **closer to the text embedding**, indicating alignment with the semantic concept described in the prompt.
***p < 0.001 (paired t-test between w/o and with text-guided)
| Nudity | mean | std | min | max |
| ---------------- | --------- | ------ | ------ | ------ |
| w/o text-guided | 0.2360 | 0.0112 | 0.2006 | 0.2717 |
| with text-guided | 0.4365*** | 0.0178 | 0.3789 | 0.4915 |
| tench | mean | std | min | max |
| ---------------- | --------- | ------ | ------ | ------ |
| w/o text-guided | 0.2527 | 0.0209 | 0.1411 | 0.2898 |
| with text-guided | 0.4624*** | 0.0334 | 0.2739 | 0.5176 |
| church | mean | std | min | max |
| ---------------- | --------- | ------ | ------ | ------ |
| w/o text-guided | 0.2106 | 0.0111 | 0.1748 | 0.2460 |
| with text-guided | 0.3953*** | 0.0183 | 0.3345 | 0.4524 |
| Van Gogh | mean | std | min | max |
| ---------------- | --------- | ------ | ------ | ------ |
| w/o text-guided | 0.2542 | 0.0136 | 0.2139 | 0.3079 |
| with text-guided | 0.4651*** | 0.0208 | 0.4011 | 0.5435 |
> Q2 How the image modality helps?
**A2**: The **discrete nature of the text modality** often leads to ambiguity or under-specification, especially in generative tasks. In contrast, **images fill in semantic gaps left by sparse or ambiguous text**. To verity this, we use LLM to generate an expression set (including words and phrases) related to the concept *nudity*. With a technique similar to Textual-Inversion, we use model-generated images to retrieve top-5 related expressions from the set.
As shown in the examples below, the retrieved phrases from images (in $\textcolor{blue}{\text{Figure 2}}$) often reflect a **broader and more nuanced conceptual space** than the original seed terms (e.g., “nudity”, “sexy”). This suggests that image embeddings encode richer semantic representations than their originating textual prompts.
| Seed ID | 1987 | 743 | 1410 | 1499 |
| ------- | ----------------- | ----------------- | --------------- | -------------------- |
| Top-1 | body as sculpture | body expression | fine art nude | unclothed figure |
| Top-2 | a nude woman | emotive nudity | fashion nude | emotive nudity |
| Top-3 | emotive nudity | body as sculpture | high-art nudity | impressionistic nude |
| Top-4 | natural nudity | nude in motion | emotive nudity | a nude woman |
| Top-5 | concealed body | natural nudity | natural nudity | high-art nudity |
This demonstrates that **visual representations enable the model to recover latent semantics** that go beyond literal textual expansions.
> Q3 Merge the framework and text-guided refinement as one contribution, and figure 7 lacks information.
**A3**: The **refinement module** is a core component of Co-Erasing, therefore we now describe the **framework and its refinement module as a unified contribution**, which can further reflect the essential of our approach more accurately. In the final version, we will also make sure to **clarify and enrich all figures, including Figure 7**, to better convey the key information.
**A summary of responses**:
- **Additional Experiments**:
1. Integration with MACE for multi-concept erasure (a8WR)
2. Comparison with other methods (a8WR)
3. Defense against Ring-A-Bell attack (a8WR)
4. Exploration of optimal fusion of text and image vectors (a8WR)
5. Applying LoRA to reduce cost (uRE6, GDyf)
6. Erasure of more harmful concepts (GDyf)
7. Erasure of similar but untargeted concepts (uRE6)
- **Explanations of Method**:
1. Comprehensive analysis of limitations (a8WR)
2. Potential bias by different images of the same concept (a8WR)
3. Computational cost analysis (uRE6, GDyf)
4. Potential drawbacks and advantages of using model-generated images (a8WR, uRE6, VY4k)
5. Explanation of text-guided functionality (VY4k)
6. Explanation of image functionality (VY4k)
- **Organization**:
1. Reorganization of tables for clarity (a8WR)
2. Refinement of contributions and figures (VY4k)
---
Rebuttal Comment 1.1:
Comment: Thanks for the responses. My concerns have been solved. I lean towards an accept.
---
Reply to Comment 1.1.1:
Comment: We sincerely appreciate your time and effort during the review and discussion, as well as your acceptance of our paper. We will carefully incorporate all suggestions in the revision to improve our final version. | Summary: This paper introduces Co-Erasing, a text-image collaborative framework designed to address the challenge of generating undesirable content (e.g., NSFW, inappropriate styles) in text-to-image diffusion models. By leveraging both text prompts and self-generated images of the target concept, Co-Erasing aims to improve erasure efficacy while preserving usability. The framework incorporates a text-guided image concept refinement strategy to isolate relevant visual features, minimizing interference with benign content. Experiments on tasks like nudity removal, style erasure, and object deletion demonstrate that Co-Erasing outperforms state-of-the-art methods in balancing efficacy and usability.
Claims And Evidence: N/A
Methods And Evaluation Criteria: N/A
Theoretical Claims: N/A
Experimental Designs Or Analyses: N/A
Supplementary Material: N/A
Relation To Broader Scientific Literature: N/A
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: **Strengths**
1. The integration of text and image modalities addresses the inherent gap in text-only methods, enhancing the model’s ability to suppress unwanted content.
2. The text-guided image refinement module effectively focuses on target concepts, reducing collateral damage to benign generations.
Empirical Validation: Comprehensive experiments with multiple baselines (e.g., ESD, AdvUnlearn) and metrics (ASR, FID, CLIP) provide strong evidence of Co-Erasing’s superiority.
3. The framework’s applicability to diverse tasks (nudity, artistic styles, objects) highlights its potential for real-world content moderation.
**Weaknesses**
**Limited Generalization:** The evaluation is confined to specific tasks (e.g., nudity, Van Gogh style), leaving the framework’s effectiveness against broader harmful content (e.g., violence, hate speech) unproven.
**Adversarial Robustness:** The defense agains
t adversarial prompts is incomplete, as demonstrated by residual failures in Appendix C (e.g., unintended object reappearance).
**High Computational Cost:** Generating and processing large image datasets (e.g., 200 images per concept) increases training overhead, which may not be feasible for resource-constrained environments.
**Usability Trade-offs:** While FID/CLIP scores improve, qualitative results show occasional artifacts or semantic misalignment (e.g., Figure 11), indicating residual usability compromises.
**Theoretical Gaps:** The paper lacks a rigorous theoretical analysis of how text-image collaboration mitigates the knowledge gap, limiting its contribution to foundational understanding.
Other Comments Or Suggestions: While this paper presents a novel approach with promising empirical results, it requires significant revisions to address these above Weaknesses.
Questions For Authors: N/A
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your valuable comments! Due to space constraints, we include `additional_tables.pdf` and figures at: https://anonymous.4open.science/r/icml25_rebuttal-8608. References to $\textcolor{blue}{\text{Table}}$ and $\textcolor{blue}{\text{Figure}}$ correspond to those provided **in this link**. A summary of all responses can be found at the end of the response to Reviewer VY4k.
> Q1 Additional concepts including violence, hate speech.
**A1**: To address this concern, we conduct **additional** experiments including **violence, illegal activity, hate speech**. $\textcolor{blue}{\text{Table 18}}$ shows that Co-Erasing maintains strong performance, which confirms the generalizability of our framework and its potential applicability to a wider set of real-world moderation scenarios.
> Q2 Extra computational cost of generating image set.
**A2**: We address the concerns as follows:
(1) **Acceptable Cost of Image Generation**: While Co-Erasing introduces an additional step to generate concept images, this is done **prior to training**, incurring **no extra generation cost** during training or inference. The **peak memory usage** during image generation **never exceeds** that of model deployment. Therefore, as long as the model can be deployed, generating the image set remains feasible within the same resource constraints.
(2) **Plug-and-Play Design**: Co-Erasing is inherently **modular** and can be applied to different baseline methods with minimal overhead. For instance, when used with **SLD** (Safe Latent Diffusion), a training-free baseline, it introduces **virtually no additional computational cost**.
(3) **Low-Rank Adaptation (LoRA) for Training-Based Methods**: For fine-tuning-based methods like **ESD**, we **additionally** incorporate **LoRA** to reduce training overhead. $\textcolor{blue}{\text{Table 16}}$ shows that LoRA significantly lowers memory consumption while maintaining erasure performance. Specifically, memory consumption drops from ~17K MB to 8.16K MB, with minimal impact on effectiveness.
> Q3 Usability Trade-offs
**A3**: We agree that **artifact-free erasure with perfect semantic alignment** remains a challenging goal. As observed in prior works, there is often a **trade-off between erasure strength and usability preservation**.
In our experiments, we demonstrate that Co-Erasing achieves a **significant reduction in Attack Success Rate (ASR)** while maintaining **competitive or improved FID and CLIP scores**, indicating better preservation of overall generation quality. Although occasional artifacts may occur, our method **outperforms prior approaches** in balancing **effective concept removal** with **minimal impact on usability** as illustrated by **Figure 2** in the paper, where Co-Erasing approaches the **Pareto frontier**.
> Q4 Failure Cases Exist.
**A4**: Some failure cases do remain, particularly when the target concept shares visual features with benign or overlapping concepts. In such scenarios, adversarial prompts may still trigger partial or unintended reappearance of erased content, as illustrated in Appendix C. Nonetheless, Co-Erasing significantly reduces the model’s ability to generate the target concept across a wide range of prompts.
---
Rebuttal Comment 1.1:
Comment: Thank you very much for your reply. After carefully reading the reviews and rebuttals from other reviewers, my concerns have been resolved. Currently, there are no apparent deficiencies in the experiments of this paper. Judging from the motivation and the proposed solutions, both have been effectively verified by the experiments.
Though the method of the paper did not particularly impress me, a solid and comprehensive experiment deserves a "weak accept" rating. Therefore, I have revised my score to "weak accept".
---
Reply to Comment 1.1.1:
Comment: We are sincerely grateful for your comments and the improved rating. We will incorporate all the suggestions to improve our final version of the paper. | Summary: This paper proposes Co-Erasing, a framework for concept erasure in text-to-image diffusion models. Existing methods that rely solely on text-based erasure often struggle to balance efficacy (removing unwanted content) and usability (preserving benign generation quality) due to the inherent gap between text and image modalities. The proposed Co-Erasing framework incorporates both text and image modalities by using model-generated images as visual templates to guide the erasure process. Additionally, a text-guided image refinement module isolates relevant visual features, ensuring precise concept erasure while minimizing unintended degradation of benign outputs.
Claims And Evidence: The claims are clear.
Methods And Evaluation Criteria: N\A
Theoretical Claims: No
Experimental Designs Or Analyses: Good and Comprehensive.
Supplementary Material: Appendix A-B.3
Relation To Broader Scientific Literature: This paper is an improvement on the existing erasing concept method like ESD.
Essential References Not Discussed: No
Other Strengths And Weaknesses: Strengths: Co-Erasing integrates both text and image prompts, addressing modality gaps for more effective concept removal. It is evaluated on diverse concepts (e.g., nudity, artistic styles, objects), proving its adaptability to various generative constraints.
Weaknesses: Co-Erasing depends on model-generated images as erasure templates, which may not fully capture all nuances of the target concept. The additional step of generating images for erasure increases the overall computational cost compared to text-only approaches.
Other Comments Or Suggestions: Please see questions.
Questions For Authors: 1. Can Co-Erasing effectively erase more abstract or evolving concepts, such as misinformation or deepfake elements?
2. What optimizations can be introduced to reduce the computational overhead while maintaining the balance between efficacy and usability?
3. How does the method ensure that visually similar but benign content is not mistakenly erased ( risk of over-erasure)?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your valuable comments! Due to space constraints, we include `additional_tables.pdf` and figures at: https://anonymous.4open.science/r/icml25_rebuttal-8608. References to $\textcolor{blue}{\text{Table}}$ and $\textcolor{blue}{\text{Figure}}$ correspond to those provided **in this link**. A summary of all responses can be found at the end of the response to Reviewer VY4k.
> Q1 Potential drawbacks of using model-generated images instead of real images.
**A1**: Model-generated images offer several advantages over real images in the context of concept erasure, and potential drawbacks can be effectively mitigated:
(1) **Better Alignment with Model Knowledge**: Generated images are produced by the model itself and therefore **directly reflect the internal knowledge and distribution** we aim to erase. In contrast, real images may not align as well with how the model represents the concept internally, making them less effective for guiding targeted erasure.
(2) **Control and Filtering**: Prompt templates allow for **precise control over the appearance and context** of generated images, helping to exclude the untargeted concept. Furthermore, automatic filtering tools (e.g., **NudeNet**, **CLIP**, etc.) are applied to filter out low-quality or inappropriate images, ensuring the set remains clean and relevant.
> Q2 Generating images introduces extra computational cost compared to text-only methods. Also, any optimizations to reduce the computational overhead?
**A2**: We address the concerns as follows:
(1) **Acceptable Cost of Image Generation**: While Co-Erasing introduces an additional step to generate concept images, this is done **prior to training**, incurring **no extra generation cost** during training or inference. The **peak memory usage** during image generation **never exceeds** that of model deployment. Therefore, as long as the model can be deployed, generating the image set remains feasible within the same resource constraints.
(2) **Plug-and-Play Design**: Co-Erasing is inherently **modular** and can be applied to different baseline methods with minimal overhead. For instance, when used with **SLD** (Safe Latent Diffusion), a training-free baseline, it introduces **virtually no additional computational cost**.
(3) **Low-Rank Adaptation (LoRA) for Training-Based Methods**: For fine-tuning-based methods like **ESD**, we **additionally** incorporate **LoRA** to reduce training overhead. $\textcolor{blue}{\text{Table 16}}$ shows that LoRA significantly lowers memory consumption while maintaining erasure performance. Specifically, memory consumption drops from ~17K MB to 6.18K MB, with minimal impact on effectiveness.
> Q3 Potential influence on visually similar but benign content.
**A3**: We address the risk of over-erasure from both theoretical and practical perspectives:
(1) **Conceptual Justification**: Co-Erasing operates under this assumption: if the diffusion model to be erased can distinguish between two similar concepts, it can be fine-tuned to suppress one (the target) while preserving the other. By guiding the model to move away from the distribution of the target concept, we aim to minimize unintended effects on adjacent but benign concepts.
(2) **Empirical Validation**: To verify this in practice, we **further** conduct experiments on **visually similar yet untargeted concepts** in $\textcolor{blue}{\text{Table 17}}$. These tests evaluate whether the method preserves non-target content that shares overlapping features with the erased concept. Our results confirm that **Co-Erasing maintains semantics** compared to the baseline, avoiding significant degradation in generation quality for related but non-targeted categories.
> Q4: Erase misinformation or deepfake elements?
**A4**: Unfortunately, **Co-Erasing is not designed to erase abstract or evolving concepts** such as misinformation or deepfake elements. These types of content often lack a consistent or well-defined visual representation, making them fundamentally different from the **specific, visually grounded concepts** that Co-Erasing targets. In fact, addressing misinformation or deepfakes aligns more closely with the goals of **forgery detection or adversarial content analysis**, which typically involve **classification or verification tasks** rather than generative model editing. | Summary: This work is proposing a concept erasing method for diffusion models by exploiting images to aid text prompts during training. Image features related to text prompts that we wish to erase in the diffusion models are provided and then combined together after cross-attention layers so that the cross-attention layers can be tuned for better performance in concept erasing. The proposed method was evaluated for nudity, Van Gogh style, parachute object, church object removals. Self-generated images were also used for further performance improvement.
Claims And Evidence: The claims in this work were partially supported by a number of experiments. However, there are also a number of issues regarding the claims such as "outperforming SOTA erasure approaches" due to lack of experiments, baselines, and so on. I will discuss these issues below. One claim that I would like to particularly discuss in here is on Section 4.1. There were two claimed limitations and were discussed with experiments. However, it is unclear if the analyses are sound and accurate.
- Limitation 1: it was well-known that diverse red-teaming attacks can generate erased concepts, but it is unclear if it was because of the gap between texts and images. It could come from the models' incapability since different models using the same text may or may not generate the same images. Thus, it will be hard to argue that the innate gap between text and image can be the reason of the vulnerability of the models.
- Limitation 2: There are two issues - this experiment may simply show the limitation of the ESD model itself or the limitation of the way of augmenting texts (which will be still finite words!). Thus, for the former, more models should be investigated to support this claim. For the latter, more sophisticated method such as using LLMs could be used. See the below recent work:
- Byung Hyun Lee et al., Concept Pinpoint Eraser for Text-to-image Diffusion Models via Residual Attention Gate, ICLR 2025.
While the overall idea of using images in training concept erasures, Figure 12 seems to show that more images adversely work against better retention performance for remaining concepts. This probably shows a clear disadvantage of the proposed method since images often have other concepts that should not be removed as well as the concept to remove. This could be more serious for multiple concept erasing (see the below work), thus, it seems important to verify the proposed method for these cases.
- Shilin Lu et al., MACE: Mass Concept Erasure in Diffusion Models, CVPR 2024.
Methods And Evaluation Criteria: The main idea was using images to aid text prompts for concept erasing. However, there were a couple of works regarding it. While the proposed method is different from them, it will be appropriate to properly discuss and compare with them. See the below recent work:
- Masane Fuchi & Tomohiro Takagi, Erasing Concepts from Text-to-Image Diffusion Models with Few-shot Unlearning, BMVC 2024.
Theoretical Claims: N/A
Experimental Designs Or Analyses: This work should be evaluated for more datasets, baseline methods and more backbone networks. It is especially important to evaluate for the cases of having a series of concept erasing while retaining other concepts. See the below recent work:
- Shilin Lu et al., MACE: Mass Concept Erasure in Diffusion Models, CVPR 2024.
While Figure 9 looks nice, they are not useful enough to fully compare with other related works - usual tables with more detailed results will be needed. For example, see the Table 2 in the above work of (Lu et al., CVPR 2024), reporting the quantity of explicit content detected using the NudeNet detector on the I2P benchmark and the comparison of FID and CLIP on MS-COCO. Or see the Table 3 in that work on the assessment of Erasing 100 Artistic Styles. These are more informative over the current figure in this work. Thus, it seems important to demonstrate the capability of the proposed method using similar ways to these prior works + more recent works.
Supplementary Material: I have not read it, but it was good enough to read the main text to understand and assess this work.
Relation To Broader Scientific Literature: The idea of using images can also be similar to other machine unlearning works that focus on concept erasing since they are using both images and texts. It will be great if this work can discuss on those works and if possible, compare with some of them.
Essential References Not Discussed: See Masane Fuchi & Tomohiro Takagi, Erasing Concepts from Text-to-Image Diffusion Models with Few-shot Unlearning, BMVC 2024.
Other Strengths And Weaknesses: It is unclear if this work will work for multiple concept erasures while retaining other remaining concepts. It seems important to discuss and demonstrate the scalability.
It is unclear if this work will work well for quite different images of the same concept. Since only one image could be used, it could provide a serious bias - any discussion for this?
Other Comments Or Suggestions: Evaluating against red-team attacks seems important considering the limitation 1 in this work. See Ring-A-Bell (see below) or UnlearnDiff (Zhang et al., ECCV 2024) for more details.
- Yu-Lin Tsai et al., Ring-a-bell! how reliable are concept removal methods for diffusion models? ICLR 2024.
Questions For Authors: Could you explain why generated images were more effective over real images?
Was the sum of two latent vectors from text and image the best? Any other optimal way?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your valuable comments! Due to space constraints, we include `additional_tables.pdf` and figures at: https://anonymous.4open.science/r/icml25_rebuttal-8608. References to $\textcolor{blue}{\text{Table}}$ and $\textcolor{blue}{\text{Figure}}$ correspond to those provided **in this link**. A summary of all responses can be found at the end of the response to Reviewer VY4k.
> Q1 Vulnerability from text-image gap or model incapability?
**A1**: We believe the text-image gap **remains a key factor** to the vulnerability of diffusion models. Our reasoning is threefold:
(1) **Scaling doesn’t close the gap**: We further conduct erasure on Stable Diffusion XL, a stronger model with improved text-image alignment. $\textcolor{blue}{\text{Figure 1}}$ shows similar vulnerabilities, indicating that the gap is ubiquitous regardless of scale.
(2) **Attacks often rely on visual cues**. CCE[1] uses Textual Inversion from concept embeddings, and UnlearnDiff[2] optimizes prompts with target concept images, highlighting reliance on cross-modal cues.
(3) **Prior work on modality misalignment**. Studies[3] support that modality gaps in CLIP (used in Stable Diffusion) impacts downstream tasks.
[1]Circumventing Concept Erasure Methods For Text-to-Image Generative Models
[2]To Generate or Not? Safety-Driven Unlearned Diffusion Models Are Still Easy to Generate Unsafe Images ... For Now
[3]Mind the Gap: Understanding the Modality Gap in Multi-Modal Contrastive Representation Learning
> Q2 Limitation 2 only shows ESD, and text augmentation is too simple.
**A2**: We extend analysis to **SLD** (Safe Latent Diffusion) and **MACE** and apply LLM-based text augmentation[4]. $\textcolor{blue}{\text{Table 1}}$ shows **persistent text-based limitations** under more models and richer prompts.
[4]Concept Pinpoint Eraser for Text-to-image Diffusion Models via Residual Attention Gate
> Q3 Potential disadvantages on multiple concept erasing task.
**A3**: We agree multi-concept erasure is important. Since Co-Erasing is **plug-and-play**, we additionally integrate it with **MACE** and evaluate on multi-concept erasure. $\textcolor{blue}{\text{Table 2}}$ shows that Co-Erasing can complement MACE effectively.
> Q4 Differences with other works involving images.
**A4**: While other methods use images, **Co-Erasing differs in key ways**:
(1) **Data Efficiency**: Unlike [5], which uses **external real images**, Co-Erasing uses **self-generated images**, reducing cost and aligning better with model's internal knowledge. See **A1** (uRE6) and **A2** (VY4K) for details.
(2) **Preservation of Untargeted Concepts**:[5] does **not explicitly preserve** unrelated concepts, whereas Co-Erasing incorporates a text-guided refinement module to avoid unintended erasure.
(3) **Modularity**: Co-Erasing is **plug-and-play** with methods like MACE and SLD, whereas [5] lacks flexibility.
Additionally as shown in $\textcolor{blue}{\text{Table 3}}$, Co-Erasing **outperforms**[5] with a better trade-off.
[5]Erasing Concepts from Text-to-Image Diffusion Models with Few-shot Unlearning
> Q5 Potential bias when images of the same concept differ significantly and using only one image.
**A5**: Co-Erasing is robust to visual diversity across images of the same concept:
(1) We further analyze the distribution of image variations across concepts in $\textcolor{blue}{\text{Table 4}}$ and found **no strong relation** between visual diversity and performance drop, indicating Co-Erasing is **robust to image-level differences** within a concept.
(2) At each training step, one image is randomly selected from the generated set (typically 50+), which mitigates overfitting to any single image and helps capture a common representation of the target.
(3) **Text-guided refinement module** focuses on the semantic core of target concept, reducing impact from untargeted visual elements.
> Q6 Evaluation against red-team attack: Ring-A-Bell.
**A6**: We already evaluate against **UnlearnDiff** (UDA) in the paper. To further address this concern, we include **Ring-A-Bell** in $\textcolor{blue}{\text{Table 5}}$, which shows Co-Erasing can improve resistance against this attack.
> Q7 The reason why generated images perform better.
**A7**: Please see **A1** (uRE6) and **A2** (VY4K).
> Q8 Other potential merging methods of text and image latent vectors.
**A8**: Summation of text and image latent vectors follows **IP-Adapter**, widely adopted for integrating images into the generation process. To explore alternatives, we run experiments with different schedulers. $\textcolor{blue}{\text{Table 6}}$ shows slight performance gains. In future work we will further investigate optimal fusion designs.
> Q9 More informative result comparison.
**A9**: We show $\textcolor{blue}{\text{Table 7-15}}$, following MACE and AdvUnlearn[6], explicitly presenting quantitative results.
[6]Defensive Unlearning with Adversarial Training for Robust Concept Erasure in Diffusion Models | null | null | null | null | null | null |
MATH-Perturb: Benchmarking LLMs' Math Reasoning Abilities against Hard Perturbations | Accept (poster) | Summary: This paper constructs a new dataset by applying simple an hard perturbations to the hard problems in the original MATH dataset. Experimental results show drop in performance for almost all models.
## Update after rebuttal
I remain positive about the paper after reading author rebuttal.
Claims And Evidence: The claims are generally supported by evidence and convincing, though some interpretations of experimental results seem anecdotal.
Methods And Evaluation Criteria: Evaluation criteria make sense.
Theoretical Claims: Yes.
Experimental Designs Or Analyses: - Both train and test splits seem relatively small. Did you observe significant variance in the performance of the same model when running it multiple times?
- I am curious whether the issue in Figure 5 is repeatable or it just a one-off because of the specifics of the problem statement. Could you provide more details about your manual inspection of 20 error cases?
- Generally a lot of analysis seems anecdotal. Would it be possible to provide statistical evidence for the phenomena described?
- "We do not allow any tool usage including access to a code interpreter, as we find that many problems can be trivially solved by writing a brute-force search program." - it might still be good to evaluate with code interpreter, and then remove those problems that are trivially solvable with code as there reasoning is likely less necessary.
Supplementary Material: No
Relation To Broader Scientific Literature: The contributions are well positioned as they directly improve over prior work that considered only simple symbolic perturbations (e.g. GSM8K-Symbolic).
Essential References Not Discussed: --
Other Strengths And Weaknesses: I think the paper has a nice contribution as most of the existing work around this problem (generating perturbations of a dataset) falls short of creating interesting/hard perturbations.
Somehow I am not fully sure to what extent would I even consider these Hard perturbations as actual perturbations of the original dataset. Sure at the syntax level the modification is very small. But for example, in Figure 3, hard perturbation leads to a completely different solution so I would not consider these problems similar. So it's not that unexpected to me that LLMs perform worse there.
Other Comments Or Suggestions: Generally it would be good to have more details on how were the experiments on failure modes performed, and have more convincing argument that it's not just anecdotal evidence based on few examples.
Questions For Authors: Please see above.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your positive feedback on our work! **We evaluated 12 new long-CoT models that appeared near or after the ICML submission deadline.** The results [here](https://anonymous.4open.science/r/icml2025_13579_math_perturb_rebuttal-C0F8/) show no sign of saturation on MATH-P-Hard. We would like to provide detailed responses below:
---
> **Q1**: Both train and test splits seem relatively small. Did you observe significant variance in the performance of the same model when running it multiple times?
**A1**: **We did not observe significant variances in the performance.**
- Our Fig. 9 contains the error bars of the performance of multiple runs, which shows the standard deviation is less than 1% (note for Fig. 9: the Self-Consistency with $k=1$ corresponds to the standard evaluation.)
- For our new results on 12 long-CoT models, the averaged standard deviation of the performance of 3 independent runs is 0.91%.
- One may still be concerned by the size of our benchmark. For reference, we would like to point out that the functional variants subset of Putnam-AXIOM only contains 52 problems, GSM-Symbolic only contains 100 problems, and AIME 2024/2025 contains 30 problems.
---
> **Q2** I am curious whether the issue in Figure 5 is repeatable or it just a one-off because of the specifics of the problem statement. Could you provide more details about your manual inspection of 20 error cases?
**A2**: **The memorization issue is a frequently observed phenomenon in our experiments. We did not cherry-pick the example in Figure 5.** We understand that readers may have concerns about the proportions of memorization issues, so we have quantified them manually. We plan to open-source the benchmark so our claims can be publicly scrutinized.
We attach the raw logs of our manual inspections in the [anonymous github link](https://anonymous.4open.science/r/icml2025_13579_math_perturb_rebuttal-C0F8/). As the generated solutions are long and unformatted in Markdown, we omit them altogether with the problem statements and only include the problem ID, error type, and comment.
---
> **Q3** Generally a lot of analysis seems anecdotal. Would it be possible to provide statistical evidence for the phenomena described?
**A3**: **We have already taken extra caution before drawing any conclusion in the experiment section. To support each claim, we have provided quantitative numbers of different metrics as well as qualitative studies that require extensive human labor.** We hope our response to your Q2 can mitigate your concern. Besides this, could you specifically point out the claim that you think lacking statistical evidence? We are happy to address any further concerns.
---
> **Q4**: it might still be good to evaluate with code interpreter, and then remove those problems that are trivially solvable with code as there reasoning is likely less necessary.
**A4**: **We don’t think reasoning is less necessary for problems that can be trivially solvable with code.** Many number theory problems and counting problems can be solved via brute-force code solutions. However, for example, a counting problem may require the mathematical knowledge of **inclusion-exclusion principle** to solve, and a number theory problem may require knowledge of **finite group theory** to solve. The answers to these problems can often be produced by trivial brute-force codes, but they do require mathematical knowledge and reasoning ability.
---
> **Q5** Somehow I am not fully sure to what extent would I even consider these Hard perturbations as actual perturbations of the original dataset. .... So it's not that unexpected to me that LLMs perform worse there.
**A5**: **Unexpectedness of experimental results shouldn't undermine the contribution of the actual experiments.**
Our results may be well-expected from your high-level conceptual argument. Nevertheless, if our experiments suggested that “LLMs are strong enough to distinguish between different perturbation types and solve these problems perfectly”, this finding could also be well-expected from an opposite but compelling argument, e.g., LLM developers have intensively built training data to cover all the perturbation cases. **Therefore, curating the benchmark out and empirically verifying the hypothesis should be a valid and important contribution.**
**we believe hard perturbation is an important setting, especially when reasoning models are deployed for end users or agentic uses.** It is common for end users or agent systems to make slight changes to the inputs that fundamentally alter the questions. If the model fails to identify the changes and applies the memorized solutions, it may have bad consequences. We hope our benchmark can inspire future work in this direction.
---
**We sincerely hope that our responses can address your concerns, and we would greatly appreciate it if you would consider raising your score of our work to a clear accept given the responses.** | Summary: This paper proposes a new benchmark by modifying 279 MATH hard problems and evaluates the popular model on these questions. They also provide various analyses of the performance on these questions.
Claims And Evidence: Yes.
Methods And Evaluation Criteria: Yes.
Theoretical Claims: Not applicable.
Experimental Designs Or Analyses: Yes.
Supplementary Material: No supplementary materials.
Relation To Broader Scientific Literature: Provide the new evaluation benchmark.
Essential References Not Discussed: No.
Other Strengths And Weaknesses: Strengths:
1. The new math evaluation benchmark is valuable and needed by the community.
2. Creating and verifying problems manually is valuable and more reliable.
3. The motivation for modifying widely used MATH hard problems is well-founded.
4. The modification method of MATH-P-Hard is convincing.
5. The analysis of various phenomena is helpful.
Weakness:
1. The performance drop of SOTA models like Gemini and O1 is acceptable, indicating that the math-solving ability of SOTA LLMs is truly strong. This raises concerns that the new dataset may not be sufficiently difficult and could become outdated quickly, given the rapid advancements in math-focused LLMs.
Other Comments Or Suggestions: No.
Questions For Authors: 1. How do you view the concept of synthesized math problems? You may consider adding a discussion on this topic in the paper.
2. I find the boundary between ‘Perturbations’ and a new question to be somewhat vague. Your example, ‘From a line to a hyperbola,’ seems more like a completely new question rather than a perturbation. In my view, ‘Perturbations’ should focus more on adding disturbances to the problem, such as introducing irrelevant or misleading information. Defining perturbations in mathematics appears to be challenging.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your positive feedback on our work! **We evaluated 12 new long-CoT models that appeared near or after the ICML submission deadline.** The results [here](https://anonymous.4open.science/r/icml2025_13579_math_perturb_rebuttal-C0F8/) show no sign of saturation on MATH-P-Hard. We would like to provide detailed responses below:
---
>**Q1** The performance drop of SOTA models like Gemini and O1 is acceptable, indicating that the math-solving ability of SOTA LLMs is truly strong. This raises concerns that the new dataset may not be sufficiently difficult and could become outdated quickly, given the rapid advancements in math-focused LLMs.
**A1**:
Thank you for raising the concern! We would like to discuss with you our thoughts and emphasize our contributions as well:
- (1) **There are still around 20% of the problems (55 problems) that the SOTA long CoT models fail to solve.** So, one way to address the issue is to artificially **split the benchmark into two subsets**, for example, an “easy” set and a “difficult” set. The “difficult” subset can be used to evaluate SOTA long-CoT models while the “easy” subset can be used to evaluate small or short-CoT models. In that case, the SOTA performance on the “difficult” subset will be low, which leaves room for improvements and also saves evaluation cost.
- (2). One may still be concerned by the size of the “difficult” subset. For reference, the functional variants subset of Putnam-AXIOM [1] only contains 52 problems, and GSM-Symbolic [2] only contains 100 problems. AIME 2024/2025 contains 30 problems. **So we believe ~55 problems are an adequate number to claim sufficient contribution. These problems can serve as the seed to curate more problems.**
Reference:
- [1] Putnam-AXIOM: A Functional and Static Benchmark for Measuring Higher Level Mathematical Reasoning
- [2] GSM-Symbolic: Understanding the Limitations of Mathematical Reasoning in Large Language Models
---
> **Q2** How do you view the concept of synthesized math problems? You may consider adding a discussion on this topic in the paper.
**A2** Thank you for the suggestion! **In our next revision, we will add a short discussion of this future direction in the conclusion section.** We believe using synthesized math problems in training is a promising approach for improving the robustness against hard perturbations. For example, one can synthesize a training dataset with paired examples of (original problem, its hard perturbation) via hybrid methods that involve both state-of-the-art LLMs and expert-level human annotators.
---
> **Q3** I find the boundary between ‘Perturbations’ and a new question to be somewhat vague. Your example, ‘From a line to a hyperbola,’ seems more like a completely new question rather than a perturbation. In my view, ‘Perturbations’ should focus more on adding disturbances to the problem, such as introducing irrelevant or misleading information. Defining perturbations in mathematics appears to be challenging.
**A3**: We agree with you that giving a precise definition of “perturbation” may be challenging. In our paper, we use **“simple perturbation”** to refer to the cases where the reasoning patterns of the modified problem remain the same, which should be closer to the “perturbation” in your view.
In contrast, for **hard perturbation**, we agree that the modified problem is essentially a new problem in the sense that the two problems have different reasoning patterns. We still call the modified problem a perturbation of the original one because they look similar superficially. **We designed MATH-P-Hard in this way to deliberately elicit memorization behaviors of the models.**
Setting aside the debate of definitions, **we believe that hard perturbation is a valid and important setting, especially when reasoning models are deployed for end users or agentic uses**. It is common for end users or agent systems to make slight changes to the inputs that fundamentally alter the questions. If the model fails to identify the changes and applies the memorized solutions, it may have bad consequences. We hope our benchmark can inspire future work in this direction.
---
**We sincerely hope that our responses can address your concerns, and we would greatly appreciate it if you would consider raising your score of our work to a *clear accept* given the responses.** | Summary: This paper investigates the robustness of mathematical reasoning models when faced with out-of-distribution problem modifications. The authors introduce MATH-P-Simple and MATH-P-Hard, two benchmark datasets that test models under simple and hard perturbations, respectively. Their evaluation reveals significant performance drops on MATH-P-Hard, highlighting that models tend to blindly apply memorized problem-solving skills without assessing their applicability to modified contexts.
Claims And Evidence: The MATH-P-Hard introduces hard perturbations that alter the reasoning path, thereby increasing problem-solving difficulty. The authors evaluate instruction-tuned MLLMs and demonstrate that these models memorize problem-solving techniques from the training set rather than genuinely adapting to problem modifications. However, prior work, such as DeepSeek-R1 [1], suggests that reinforcement learning (RL) techniques can help models reduce memorization and explore reasoning paths more effectively. A key limitation of this study is that the authors do not evaluate RL-based models, leaving an open question regarding their effectiveness in addressing memorization biases in mathematical reasoning tasks.
Perturbation benchmark has been explored by the work [2].
[1]DeepSeek-AI, DeepSeek-R1: Incentivizing Reasoning Capability in LLMs via Reinforcement Learning.
[2] Chengke Zou et. al., DYNAMATH: A DYNAMIC VISUAL BENCHMARK FOR EVALUATING MATHEMATICAL REASONING ROBUSTNESS OF VISION LANGUAGE MODELS, ICLR2025.
Methods And Evaluation Criteria: The authors claim to have discovered a novel form of memorization, but it is unclear what distinguishes their findings from prior observations, such as those in [1], which already highlight that models memorize solution steps without truly understanding the underlying reasoning.
The authors should explicitly define what they mean by "problem-solving techniques" in line 432.
[1] Zhang, H., et al., A careful examination of large language model performance on grade school arithmetic. arXiv 2024.
Theoretical Claims: There are no theoretical claims.
Experimental Designs Or Analyses: If the authors use the same technique and data engine employed for MATH-P-Hard generation to create a training dataset, and then fine-tune MLLMs on this dataset, the issue of memorizing problem-solving techniques may likely remain a bottleneck of MLLMs.
Does exposure to perturbed training data actually improve generalization, or does it reinforce memorization biases?
To truly assess whether fine-tuning on such data mitigates memorization, an ablation study comparing models trained on perturbed vs. non-perturbed datasets would be necessary.
Supplementary Material: I reviewed Section C.
Relation To Broader Scientific Literature: This paper provides a valuable contribution by identifying new limitations in reasoning adaptability, but further research is needed to determine whether alternative training paradigms, such as RL or perturbation-based fine-tuning, can overcome these issues.
Essential References Not Discussed: Chengke Zou et. al., DYNAMATH: A DYNAMIC VISUAL BENCHMARK FOR EVALUATING MATHEMATICAL REASONING ROBUSTNESS OF VISION LANGUAGE MODELS, ICLR2025.
Other Strengths And Weaknesses: The paper is well-structured and the experiments are comprehensive and easy to follow.
The study provides valuable insights into model generalization and out-of-distribution reasoning.
Other Comments Or Suggestions: I have no further comments.
Questions For Authors: I have no further questions.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: > **Q1** The authors evaluate instruction-tuned MLLMs …
**A1**. We would like to first clarify that our dataset only contains textual input, and we evaluated on text-only LLMs, not Multimodal LLMs.
---
> **Q2**: A key limitation of this study is that the authors do not evaluate RL-based models...
**A2**: **We did evaluate RL-based models.**
- (1) We evaluated 3 long-CoT models: Gemini 2.0 flash thinking, o1-preview, and o1-mini. These models are believed to be tuned with RL, using similar techniques as Deepseek-R1. Please note that R1 (released on 2025/01/20) is considered concurrent work.
- (2) We additionally provided the evaluation results on the 12 new long-CoT models [here](https://anonymous.4open.science/r/icml2025_13579_math_perturb_rebuttal-C0F8), including R1.
- (3) Besides the long-CoT models, please note that Deepseek-Math-7B-RL and Qwen2.5-Math-7B-Instruct both underwent an RL tuning stage.
---
> **Q3**: Essential References Not Discussed: Perturbation benchmark has been explored by DYNAMATH [2].
**A3**: **We have already discussed and properly cited the DynaMath in our submission. The contributions of the two benchmarks do not conflict with each other:**
- DynaMath proposes 7 different perturbation types but most of them fall into the category of simple perturbations. In contrast, our paper studies hard perturbations.
- DynaMath focuses on multimodal mathematical reasoning settings and evaluates MLLMs, while our paper focuses on text-only settings.
---
> **Q4**: it is unclear what distinguishes their findings from prior observations, such as those in [1], which already highlight that models memorize solution steps without truly understanding the underlying reasoning.
**A4**: **Our contributions are orthogonal to [1], and our findings are different from GSM1K [1].** Specifically:
- (1) First of all, **the GSM1K benchmark [1] is already saturated**, with models achieving over 95% accuracy (see the online leaderboard in https://scale.com/leaderboard/math). **The leaderboard was officially deprecated in January 2025** by Scale AI, and the benchmark does not contain newly released RL-tuned models, such as Deepseep-R1.
- (2) The mechanisms of the memorizations are different: the authors of [1] stated their contribution as *“To measure the existing benchmark contamination on GSM8k, we created GSM1k, a held-out benchmark designed to match the difficulty and structure of GSM8k.”* In contrast, in our evaluation results, we showed that **naive memorization of the contaminated data is not a significant issue for the newly developed models**, and these models are already capable of generalizing to simply-perturbed problems. Instead, the memorization effects on MATH-P-Hard are caused by failing to recognize the essential differences between the perturbed problems and the original ones.
---
> **Q5**: The authors should explicitly define what they mean by "problem-solving techniques" in line 432.
**A5**: **We believe the term is already clear from the context.**
Cautions should be taken when giving a definition to such an abstract concept. By problem-solving techniques one can mean “the procedure of applying mathematical knowledge and mathematical operations” for solving a problem. This roughly corresponds to the steps of the chain-of-thought solution. Similar concepts are utilized in [[1]](https://arxiv.org/abs/2405.12205) and [[2]](https://arxiv.org/abs/2407.21009).
---
> **Q6** ... further research is needed to determine whether alternative training paradigms, such as RL or perturbation-based fine-tuning, can overcome these issues. ... an ablation study comparing models trained on perturbed vs. non-perturbed datasets would be necessary.
**A6**:
We agree that thorough studies on the effects of RL and perturbation-based fine-tuning datasets are necessary. This is an important follow-up but is **outside the scope of this work**. As a benchmark paper, our goal is to curate a high-quality dataset and identify new memorization issues as a current limitation of reasoning models, and encourage future studies.
---
> **Q7** ... Does exposure to perturbed training data actually improve generalization, or does it reinforce memorization biases?
**A7** Adopting the same technique to curate a training dataset with hard perturbation is a promising future direction. However, **to ensure high quality, our benchmark was curated by expert-level annotators,** which is *too costly* for constructing a large-scale training dataset. We encourage the community to explore hybrid methods to synthesize training datasets with both state-of-the-art LLMs and expert-level annotators. **Again, this is outside the scope of this work.**
---
**Given your review, we believe there were major misunderstandings on our work. We sincerely hope that our responses can resolve the misunderstandings and address your concerns, and we would greatly appreciate it if you would like to re-evaluate our work given the responses.** | Summary: The paper constructs MATH-Perturb to evaluate the math reasoning generalization of LLMs under simple and especially hard perturbations. The authors create MATH-P-Simple (279 problems) and MATH-P-Hard (279 problems) datasets from level-5 problems in the MATH dataset. Experiment results on 18 LLMs show significant performance drops on MATH-P-Hard, indicating they struggle with hard perturbations and are biased toward the original reasoning patterns. Failure mode analysis reveals that many of the errors can
be traced to a new form of memorization, where LLMs memorize the problem-solving techniques from the training set and blindly apply them without judging whether the modified settings are still suitable.
Claims And Evidence: I think the generalization of mathematical reasoning abilities, and even general reasoning abilities, which this paper focuses on, is worthy of exploration. The authors summarize the situation where LLMs can answer the original questions correctly and also handle simple variations of the original questions (such as variable substitution), but fail to solve the hard variations, as a **new form of memorization**.
I have some reservations about this claim:
- If it is considered a new form of memorization, it might be categorized as memorization of problem-solving abilities. It has learned the core abilities for such problems and can solve various variations of them, but is at a loss when facing more difficult problems or may still apply previous habitual assumptions.
- This kind of memorization might be normal, simply because the model lacks the ability to solve more difficult problems. For students, they may master easy questions but be unable to solve difficult ones.
- If it is possible to design problems that are **equivalent in question type and difficulty to MATH-P-Hard** but very different from the original questions (e.g. with a large edit distance). And if the models perform better on these problems than on MATH-P-Hard, it may indicate that they habitually use the solution approach of the original questions when solving MATH-P-Hard.
Methods And Evaluation Criteria: Yes, I think this benchmark is valuable.
Theoretical Claims: Yes, please refer to "Claims And Evidence" for details.
Experimental Designs Or Analyses: Yes, the experimental design is generally reasonable.
Supplementary Material: No Supplementary Material.
Relation To Broader Scientific Literature: Perhaps it would be beneficial to discuss or analyze some benchmarks[1] that focus on perturbations at the level of mathematical problem-solving tasks.
[1] Zhou et al. Is Your Model Really A Good Math Reasoner? Evaluating Mathematical Reasoning with Checklist. In ICLR 2025.
Essential References Not Discussed: No
Other Strengths And Weaknesses: ** Strengths**:
- This article is well-organized and easy to understand.
- The ideas discussed are of great value.
- The constructed dataset is also valuable, which is conducive for the community to compare different difficulty variants of the same or similar problems.
** Weaknesses and Questions**:
- When the model fails to solve difficult problems, is it simply due to the model's insufficient capabilities, or should it be attributed to the model's excessive memorization?
- I think there may be a lack of some more in-depth analysis, based on the existing benchmarks in the current community. For example, could it provide ideas or clues on how to achieve easy-to-hard generalization?
Other Comments Or Suggestions: None
Questions For Authors: ** Weaknesses and Questions**:
- When the model fails to solve difficult problems, is it simply due to the model's insufficient capabilities, or should it be attributed to the model's excessive memorization?
- I think there may be a lack of some more in-depth analysis, based on the existing benchmarks in the current community. For example, could it provide ideas or clues on how to achieve easy-to-hard generalization?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for your positive feedback on our work! **We evaluated 12 new long-CoT models that appeared near or after the ICML submission deadline.** The results [here](https://anonymous.4open.science/r/icml2025_13579_math_perturb_rebuttal-C0F8/) show no sign of saturation on MATH-P-Hard. We would like to provide detailed responses below:
---
> **Q1**: … This kind of memorization might be normal, simply because the model lacks the ability to solve more difficult problems. For students, they may master easy questions but be unable to solve difficult ones.
**A1**:
**We believe hard perturbation is a valid and important setting, especially when reasoning models are deployed for end users or agentic uses**. It is common for end users or agent systems to make slight changes to the inputs that fundamentally alter the questions. If the model fails to identify the changes and applies the memorized solutions, it may have bad consequences, even though one can argue this kind of memorization is normal. We hope our benchmark can inspire future work in this direction.
---
> **Q2**: If it is possible to design problems that are equivalent in question type and difficulty to MATH-P-Hard but very different from the original questions (e.g. with a large edit distance). And if the models perform better on these problems than on MATH-P-Hard, it may indicate that they habitually use the solution approach of the original questions when solving MATH-P-Hard.
**A2**: Thank you for the insightful suggestion! **We designed MATH-P-Hard to mimic the original problem formulations to deliberately elicit memorization behaviors of the models.** Designing problems that are equivalent in question type and difficulty to MATH-P-Hard but with large edit distances will lead to a good subset for *isolating* the memorization effect. We agree with you that if a model solves this type of problem correctly but fails on MATH-P-Hard, we can claim that the model possesses the skills to solve the harder problem but habitually uses the memorized approach due to the superficial similarity of the problem formulation to the original one. This is an interesting **follow-up direction**.
---
> **Q3**: Perhaps it would be beneficial to discuss or analyze some benchmarks[1] that focus on perturbations at the level of mathematical problem-solving tasks. [1] Zhou et al. Is Your Model Really A Good Math Reasoner? Evaluating Mathematical Reasoning with Checklist. In ICLR 2025.
**A3**: Thank you for the pointer! **We will cite and discuss the paper in our next revision.**
- The paper establishes a pipeline to generate perturbations of problems in 4*4 = 16 different variants, featuring 4 task generations (problem-solving, answerable judging, outcome judging, and process judging) and 4 reasoning robustness modifications (original problem, problem understanding, irrelevant disturbance, and scenario understanding). They focused on simpler GSM8K dataset and multimodal geometry datasets.
- Our paper focuses on dissecting “perturbation” into simple perturbations and hard perturbations, and investigates the proportion of the failures that are due to memorization. We selected MATH level-5, which is the harder high-school competition level.
---
> **Q4**: When the model fails to solve difficult problems, is it simply due to the model's insufficient capabilities, or should it be attributed to the model's excessive memorization?
**A4**: **We have discussed the failure modes in Section 3.2.** In short, the performance drops in MATH-P-Hard can be attributed to both insufficient capabilities to handle harder problems and memorization issues. The two failure modes often couple with each other. For stronger models, the general failure modes due to insufficient capabilities are largely reduced, making memorization issues more prominent.
---
> **Q5** I think there may be a lack of some more in-depth analysis, based on the existing benchmarks in the current community. For example, could it provide ideas or clues on how to achieve easy-to-hard generalization?
**A5**: We agree with you that the community currently lacks a more in-depth analysis of the existing benchmarks, which **motivates** our work.
There are some works focusing on easy-to-hard generation using MATH dataset (e.g. train on level 1-3 problems and test on level 4-5 problems) [1]. However, for this setting, there aren’t paired data with similar problem statements but different solutions and difficulty levels. **We believe our benchmark can serve as a testbed for future studies on easy-to-hard generalization and scalable oversights.**
- [1] Easy-to-Hard Generalization: Scalable Alignment Beyond Human Supervision. Zhiqing Sun, Longhui Yu, Yikang Shen, Weiyang Liu, Yiming Yang, Sean Welleck, Chuang Gan
----
**We sincerely hope that our responses can address your concerns, and we would greatly appreciate it if you would consider raising your score of our work to a *clear accept* given the responses.**
---
Rebuttal Comment 1.1:
Comment: Yeah, I think Q2 is a valuable follow-up work for MATH-Perturb. And I would raise my score to 4 as I think its current contribution is suitable for publication. | null | null | null | null | null | null |
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